Author Response

Reviewer #1 (Public Review):

This well-done platform trial identifies that ivermectin has no impact on SARS-CoV-2 viral clearance rate relative to no study drug while casirivimab lead to more rapid clearance at 5 days. The figures are simple and appealing. The study design is appropriate and the analysis is sound. The conclusions are generally well supported by the analysis. Study novelty is somewhat limited by the fact that ivermectin has already been definitively assessed and is known to lack efficacy against SARS-CoV-2. Several issues warrant addressing:

1) Use of viral load clearance is not unique to this study and was part of multiple key trials studying paxlovid, remdesivir, molnupiravir, and monoclonal antibodies. The authors neglect to describe a substantial literature on viral load surrogate endpoints of therapeutic efficacy which exist for HIV, hepatitis B and C, Ebola, HSV-2, and CMV. For SARS-CoV-2, the story is more complicated as several drugs with proven efficacy were associated with a decrease in nasal viral loads whereas a trial of early remdesivir showed no reduction in viral load despite a 90% reduction in hospitalization. In addition, viral load kinetics have not been formally identified as a true surrogate endpoint. For maximal value, a reduction in viral load would be linked with a reduction in a hard clinical endpoint in the study (reduction in hospitalization and/or death, decreased symptom duration, etc...). This literature should be discussed and data on the secondary outcome, and reduction in hospitalization should be included to see if there is any relationship between viral load reduction and clinical outcomes.

This is an important point and we thank the reviewer for raising it. We agree that there is a rich literature on the use of viral load kinetics in optimizing treatment of viral infectious diseases, and we are clearly not the first to think of it! We have added the following sentence in the discussion.

“The method of assessing antiviral activity in early COVID-19 reported here builds on extensive experience of antiviral pharmacodynamic assessments in other viral infections.”

We agree that more information is needed to link viral clearance measures to clinical outcomes. We have addressed this in the discussion as follows:

“Using less frequent nasopharyngeal sampling in larger numbers of patients, clinical trials of monoclonal antibodies, molnupiravir and ritonavir-boosted nirmatrelvir, have each shown that accelerated viral clearance is associated with improved clinical outcomes [1,4,5]. These data suggest reduction in viral load could be used as a surrogate of clinical outcome in COVID-19. In contrast the PINETREE study, which showed that remdesivir significantly reduced disease progression in COVID-19, did not find an association between viral clearance and therapeutic benefit. This seemed to refute the usefulness of viral clearance rates as a surrogate for rates of clinical recovery [16]. However, the infrequent sampling in all these studies substantially reduced the precision of the viral clearance estimates (and thus increased the risk of type 2 errors). Using the frequent sampling employed in the PLATCOV study, we have shown recently that remdesivir does accelerate SARS-CoV-2 viral clearance [17], as would be expected from an efficacious antiviral drug. This is consistent with therapeutic responses in other viral infections [18, 19]. Taken together the weight of evidence suggests that accelerated viral clearance does reflect therapeutic efficacy in early COVID-19, although more information will be required to characterize this relationship adequately.”

2) The statement that oropharyngeal swabs are much better tolerated than nasal swabs is subjective. More detail needs to be paid to the relative yield of these approaches.

The statement is empirical. We know of other studies in progress where there are high rates of discontinuation because of patient intolerance of repeated nasopharyngeal sampling. Not one of 750 patients enrolled to date in PLATCOV has refused sampling, which we believe is useful information for research involving multiple sampling. This is clearly a critical point for pharmacodynamic studies.

We agree that the optimal site of swabbing for SARS-CoV-2 and relative yields for the given test requirements (sensitivity vs quantification) need to be considered, although the literature on this is large and sometimes contradictory.

We have added the following line:

Oropharyngeal viral loads have been shown to be both more and less sensitive for the detection of SARS-CoV-2 infection. Although rates of clearance are very likely to be similar from the two body sites, this should be established for comparison with other studies.

3) The stopping rules as they relate to previously modeled serial viral loads are not described in sufficient detail.

The initial stopping rules were chosen based on previously modelled data (reference 11). We have added details to the text (lines 199-219):

“Under the linear model, for each intervention, the treatment effect β is encoded as a multiplicative term on the time since randomisation: eβT, where T=1 if the patient was assigned the intervention, and zero otherwise. Under this specification β=0 implies no effect (no change in slope), and β>0 implies increase in slope relative to the population mean slope. Stopping rules are then defined with respect to the posterior distribution of β, with futility defined as Prob[β<λ]>0.9; and success defined as Prob[β>λ]>0.9, where λ≥0. Larger values of λ imply a smaller sample size to stop for futility but a larger sample size to stop for efficacy. λ was chosen so that it would result in reasonable sample size requirements, as was determined using a simulation approach based on previously modelled serial viral load data [11]. This modelling work suggested that a value of λ=log(1.05) [i.e. 5% increase] would requireapproximately 50 patients to demonstrate increases in the rate of viral clearance of ~50%, with control of both type 1 and type 2 errors at 10%. The first interim analysis (n=50) was prespecified as unblinded in order to review the methodology and the stopping rules (notably the value of λ). Following this, the stopping threshold was increased from 5% to 12.5% [λ=log(1.125)] because the treatment effect of casirivimab/imdevimab against the SARS-CoV-2 Delta variant was larger than expected and the estimated residual error was greater than previously estimated. Thereafter trial investigators were blinded to the virus clearance results. Interim analyses were planned every batch of additional 25 patients’ PCR data however, because of delays in setting up the PCR analysis pipeline, the second interim analysis was delayed until April 2022. By that time data from 145 patients were available (29 patients randomised to ivermectin and 26 patients randomized to no study drug).”

4) The lack of blinding limits any analysis of symptomatic outcomes.

We added this line to the discussion:

“Finally, although not primarily a safety study, the lack of blinding compromises safety or tolerability assessments.”

5) It is unclear whether all 4 swabs from 2 tonsils are aggregated. Are the swabs placed in a single tube and analyzed?

The data are not aggregated but treated as independent and identically distributed under the linear model. 4 swabs were taken at randomization, followed by two at each follow-up visit. We have added line 183:

“[..] (18 measurements per patient, each swab is treated as as independent and identically distributed conditional on the model).”

Swabs were stored separately and not aggregated.

6) In supplementary Figure 7, both models do well in most circumstances but fail in the relatively common event of non-monotonic viral kinetics (multiple peaks, rebound events). Given the importance of viral rebound during paxlovid use, an exploratory secondary analysis of this outcome would be welcome.

Thank you for the suggestion. We agree, although the primary goal is to estimate the mean change in slope. Rebound is a relatively rare event and tends to occur after the first seven days of illness in which we are assessing rate of clearance.

Nevertheless, we agree that this is an important point. It remains unclear how to model viral rebound. In over 700 profiles now available from the study, only a few have strong evidence of viral rebound.

Reviewer #2 (Public Review):

This manuscript details the analytic methods and results of one arm of the PLATCOV study, an adaptive platform designed to evaluate low-cost COVID-19 therapeutics through enrollment of a comparatively smaller number of persons with acute COVID-19, with the goal of evaluating the rate of decrease in SARS-CoV-2 clearance compared to no treatment through frequent swabbing of the oropharynx and a Bayesian linear regression model, rather than clinical outcomes or the more routinely evaluated blunt virologic outcomes employed in larger trials. Presented here, is the in vivo virologic analysis of ivermectin, with a very small sample of participants who received the casirivimab/imdevimab, a drug shown to be highly effective at preventing COVID-19 progression and improving viral clearance (during circulation of variants to which it had activity) included for comparison for model evaluation.

The manuscript is well-written and clear. It could benefit however from adding a few clarifications on methods and results to further strengthen the discussion of the model and accurately report the results, as detailed below.

Strengths of this study design and its report include:

1) Selection of participants with presumptive high viral loads or viral burden by antigen test, as prior studies have shown difficulty in detecting effect in those with a lower viral burden.

2) Adaptive sample size based on modeling- something that fell short in other studies based on changing actuals compared to assumptions, depending on circulating variant and "risk" of patients (comorbidities, vaccine state, etc) over time. There have been many other negative studies because the a priori outcomes assumptions were different from the study design to the time of enrollment (or during the enrollment period). This highlight of the trial should be emphasized more fully in the discussion.

3) Higher dose and longer course of ivermectin than TOGETHER trial and many other global trials: 600ug/kg/day vs 400mcg/kg/day.

4) Admission of trial participants for frequent oropharyngeal swabbing vs infrequent sampling and blunter analysis methods used in most reported clinical trials

5) Linear mixed modeling allows for heterogeneity in participants and study sites, especially taking the number of vaccine doses, variant, age, and serostatus into account- all important variables that are not considered in more basic analyses.

6) The novel outcome being the change in the rate of viral clearance, rather than time to the undetectable or unquantifiable virus, which is sensitive, despite a smaller sample size

7) Discussion highlights the importance of frequent oral sampling and use of this modeled outcome for the design of both future COVID-19 studies and other respiratory viral studies, acknowledging that there are no accepted standards for measuring virologic or symptom outcomes, and many studies have failed to demonstrate such effects despite succeeding at preventing progression to severe clinical outcomes such as hospitalization or death. This study design and analyses are highly important for the design of future studies of respiratory viral infections or possibly early-phase hepatitis virus infections.

Weaknesses or room for improvement:

1) The methods do not clearly describe allocation to either ivermectin or casirivimab/imdevimab or both or neither. Yes, the full protocol is included, but the platform randomization could be briefly described more clearly in the methods section.

We have added additional text to the Methods:

“The no study drug arm comprised a minimum proportion of 20% and uniform randomization ratios were then applied across the treatment arms. For example, for 5 intervention arms and the no study drug arm, 20% of patients would be randomized to no study drug and 16% to each of the 5 interventions. Additional details on the randomization are provided in the Supplementary Materials. All patients received standard symptomatic treatment.”

2) The handling of unquantifiable or undetectable viruses in the models is not clear in either the manuscript or supplemental statistical analysis information. Are these values imputed, or is data censored once below the limits of quantification or detection? How does the model handle censored data, if applicable?

We have added lines 185-186:

“Viral loads below the lower limit of quantification (CT values ≥40) were treated as left-censored under the model with a known censoring value.”

3) Did the study need to be unblinded prior to the first interim analysis? Could the adaptive design with the first analysis have been done with only one or a subset of statisticians unblinded prior to the decision to stop enrolling in the ivermectin arm?

The unblinded interim analysis was done on the first 50 patients enrolled in the study. The study at that time was enrolling into five arms including ivermectin, casirivimab-imdevimab, remdesivir, favipiravir, and a no study drug arm (there were exactly 10 per arm as a result of the block randomization).

The main rationale for making this interim analysis unblinded was to determine the most reasonable value of λ (this defines stopping for futility/success), which is a trade-off between information gain, reasonable sample size expectations, and the balance between quickly identifying interventions which have antiviral activity versus the certainty of stopping for futility.

Once the value of 12.5% was decided, the trial investigators remained blinded to the results until the stopping rules were met and the unblinded statistician discussed with the independent Data Safety and Management Board who agreed to unblind the ivermectin arm.

4) Can the authors comment on why the interim analysis occurred prior to the enrollment of 50 persons in each of the ivermectin and comparison arms? Even though the sample sizes were close (41 and 45 persons), the trigger for interim analysis was pre-specified.

After the first interim analysis at 50 patients enrolled into the study, they were planned every additional 25 patients (i.e. very frequently). The trigger for the interim analysis was not 50 patients into a specific arm, but 50 patients in total, and thereafter were planned to occur with every 25 new patients enrolled into the study. In practice there were backlogs in the data pipeline (which we explain), and interim analyses occurred less frequently than planned- the second one being in April 2022.

5) The reporting of percent change for the intervention arms is overstated. All credible intervals cross zero: the clearance for ivermectin is stated to be 9% slower, but the CI includes + and - %, so it should be reported as "not different." Similarly, and more importantly for casirivimab/imdevimab, it was reported to be 52% faster, although the CI is -7.0 to +115%. This is likely a real difference, but with ten participants underpowered- and this is good to discuss. Instead, please report that the estimate was faster, but that it was not statistically significant. Similarly, the clearance half-life for ivermectin is not different, rather than "slower" as reported (CI was -2 to +6.6 hours). This result was however statistically significant for casirivimab/imdevimab.

Thank you for your comments. The confidence interval for casirivimab/imdevimab did not cross zero and was +7.0 to +115.1%, and we thank the reviewer for picking up the error in the results section (it was correct in the abstract) where it was written -7.0 to +115.1%. We have made this correction. Elsewhere, we have provided more precise language to discriminate clinical significance from statistical significance, as per the essential revisions.

6) While the use of oropharyngeal swabs is relatively novel for a clinical trial, and they have been validated for diagnostic purposes, the results of this study should discuss external validity, especially with respect to results from other studies that mainly use nasopharyngeal or nasal swab results. For example, oropharyngeal viral loads have been variably shown to be more sensitive for the detection of infection, or conversely to have 1-log lower viral loads compared to NP swabs. Because these models look for longitudinal change within a single sampling technique, they do not impact internal validity but may impact comparisons to other studies or future study designs.

We have added the following sentence to the discussion:

“Oropharyngeal viral loads have been shown to be both more and less sensitive for the detection of SARS-CoV-2 infection. Although rates of viral clearance are very likely to be similar from the two sites, this should be established for comparison with other studies.”

7) Caution should be used around the term "clinically significant" for viral clearance. There is not an agreed-upon rate of clinically significant clearance, nor is there a log10 threshold that is agreed to be non-transmissible despite moderately strong correlations with the ability to culture virus or with antigen results at particular thresholds.

We agree. We have addressed this partly in our response to Reviewer 1.

8) Additional discussion could also clarify that certain drugs, such as remdesivir, have shown in vivo activity in the lungs of animal models and improvement in clinical outcomes in people, but without change in viral endpoints in nasopharyngeal samples (PINETREE study, Gottlieb, NEJM 2022). Therefore, this model must be interpreted as no evidence of antiviral activity in the pharyngeal compartment, rather than a complete lack of in vivo activity of agents given the limitations of accessible and feasible sampling. That said, strongly agree with the authors about the conclusion that ivermectin is also likely to lack activity in humans based on the results of this study and many other clinical studies combined.

As above this has been addressed in our response to Reviewer 1.

Reviewer #3 (Public Review):

This is a well-conducted phase 2 randomized trial testing outpatient therapeutics for Covid-19. In this report of the platform trial, they test ivermectin, demonstrating no virologic effect in humans with Covid-19.

Overall, the authors' conclusions are supported by the data.

The major contribution is their implementation of a new model for Phase 2 trial design. Such designs would have been ideal earlier in the pandemic.

We thank the reviewer for their encouraging comments.

Author Response

Reviewer #1 (Public Review):

Auxin-induced degradation is a strong tool to deplete CHK-2 and PLK-2 in the C. elegans germ line. The authors strengthen their conclusions through multiple approaches, including rescuing mutant phenotypes and biochemical analyses of CHK-2 and PLK-2.

The authors overcame a technical limitation that would hinder in vitro analysis (low quantity of CHK-2) through the clever approach of preventing its degradation via the proteasome. In vitro phosphorylation assays and mass spectrometry analysis that establishes that CHK-2 is a substrate of PLK-2 nicely complement the genetic data.

The authors argue that the inactivation of CHK-2 by PLK-2 promotes crossover designation; however, the data only indicate that PLK-2 promotes proper timing of crossover designation.

We thank the reviewer for this point of clarification. While we believe that PLK activity is essential to inactivate CHK-2 and trigger CO designation, we agree that this has not been firmly established with the tools available to us, as elaborated below. We have revised the text to avoid overstating the conclusions.

It is not clear whether the loss of CHK-2 function with the S116A and T120A mutations is the direct result of the inability to phosphorylate these residues or whether it is caused by the apparent instability of these proteins, as their abundance was reduced in IPs compared to wild-type. Agreed. The instability of the mutant proteins was a source of significant frustration during the course of this work, and limits the strength of our conclusions.

The mechanism of CHK-2 inactivation in the absence of PLK-2 remains unclear, though the authors were able to rule out multiple candidates that could have played this role.

Reviewer #2 (Public Review):

In this manuscript, Zhang et al., address the role of Polo-like kinase signaling in restricting the activity of Chk2 kinase and coordinating synapsis among homologous chromosomes with the progression of meiotic prophase in C. elegans. While individual activities of PLK-2 and CHK-2 have been demonstrated to promote chromosome pairing, and double-strand break formation necessary for homologous recombination, in this manuscript the authors attempt to link the function of these two essential kinases to assess the requirement of CHK-2 activity in controlling crossover assurance and thus chromosome segregation. The study reveals that CHK-2 acts at distinct regions of the C. elegans germline in a Polo-like kinase-dependent and independent manner.

Strengths:

The study reveals distinct mechanisms through which CHK-2 functions in different spatial regions of meiosis. For example, it appears that CHK-2 activity is not inhibited by PLK's (1 and 2) in the leptotene/zygotene meiotic nuclei where pairing occurs. This suggests that either CHK-2 is not phosphorylated by PLK-2 in the distal nuclei or that it has a kinase-independent function in this spatial region of the germline. These are interesting observations that further our understanding of how the processes of meiosis are orchestrated spatially for coordinated regulation of the temporal process.

Weaknesses:

While the possibilities stated above are interesting, they lack direct support from the data. A key missing element in the study is the actual role of PLK-2 signaling in controlling CHK-2 activity and thus function. I expand on this below.

Throughout the manuscript, the authors test the role of each of the kinases (CHK-2 or PLK-1, or 2) using auxin-induced degradation, which would eliminate both phosphorylated and unphosphorylated pools of proteins. This experiment thus does not test the role of PLK-2 signaling in controlling CHK-2 function or the role of CHK-2 activation. To test the role of signaling from PLK-2 or CHK-2, the authors need to generate appropriate alleles such as phospho-mutants or kinase-dead mutants. The authors do generate unphosphorylatable and phosphomimetic versions of CHK-2, however, they find that the protein level for both these alleles is lower than wild-type CHK-2 (which the authors state is already low). The authors conclude that the lower level of protein in the CHK-2 phospho-mutants is because the mutations cause destabilization of the protein. I am sympathetic with the authors since clearly these results make interpretations of actual signaling activity more challenging. But there needs to be some evidence of this activity, for example through the generation of a phosphor-specific antibody to phosphorylated CHK-2. While not functional, at least the phosphorylation status of CHK-2 would provide more information on its spatial pattern of activation and inactivation. In addition, it would still be of interest to the readership to present the data on these phosphor-mutant alleles with crossover designation and COSA-1::GFP. Is the phenotype of the WT knockin, and each of the phosphomutant knock-ins similar to auxin-induced degradation of CHK-2?

We thank the reviewer for these comments. We have made several attempts over the past decade that have failed to elicit a CHK-2 antibody that works for either immunofluorescence or western blots, likely due to the very low abundance of CHK-2. This has discouraged us from investing yet more resources to try to develop a phospho-specific antibody. Moreover, our evidence suggests that phosphorylation may promote CHK-2 degradation. Since the phosphomutants of CHK-2 are not stable, we do not think knock-in of these phosphomutants will provide new insights.

Given that the CHK-2 phosphomutants did not pan out for assessing the signaling regulation of PLK-2 on CHK-2, to directly assess whether PLK-2 activity restricts CHK-2 function in mid-pachytene but not leptotene/zygotene, the authors should generate PLK-2 kinase dead alleles. These alleles will help decouple the signaling function of PLK-2 from a structural function.

Similarly, to assess the potentially distinct roles of CHK-2 in leptotene/zygotene and mid-pachytene it would be important to assess CHK-2 kinase-dead mutant alleles. At this time, all of the analysis is based on removing both active CHK-2 and inactive CHK-2 (i.e. phosphorylated and unphosphorylated pool) using auxin-induced degradation. The kinase-dead alleles will help infer the role of the kinase more directly. The authors can then superimpose the auxin-induced degradation and assess the impact of complete removal of the protein vs only loss of its kinase function. These experiments may help clarify the role of signaling outcomes of these proteins, vs their complete loss. For example, what does kinase dead PLK-2 recruitment to the synapsed chromosomes appear like? Are their distinct activities for active and inactive PLK-2 that are spatially regulated? The same can be tested for CHK-2.

A kinase-dead allele of plk-2 has been generated in previous work and we have used it for other purposes. However, the fact that CHK-2 and PLK-2 are required for homolog pairing and synapsis, which are prerequisites for crossover designation, precludes their use here.

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Reply to the reviewers

1. General Statements

We thank the reviewers for their thorough and insightful evaluations of our manuscript and for their constructive feedback, which have significantly improved the quality of our manuscript. We were pleased to read that all three reviewers found our work novel, interesting, and relevant. In this revised manuscript, we have done our best to address all of the points raised by the reviewers by performing new experiments and revising sections of the text, as requested.

2. Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

In this manuscript authors show that extracellular Mtb aggregates can cause macrophage killing in a close contact dependent but phagocytosis independent manner. They showed Mtb aggregates can induce plasma membrane perturbations and cytoplasmic Ca2+ influx with live cell microscopy. Next, the authors show that the type of cell death initiated by extracellular aggregates is pyroptosis and they partially supressed cell death with pyroptosis inhibitors. They also identified that PDIM, EsxA/EsxB and EspB all have a role in uptake-independent killing of macrophages even though their impact varies with respect membrane perturbation and Ca2+ influx. Finally, they used a small molecule inhibitor BTP15 to inhibit the effect of ESX-1 during the contact of the extracellular Mtb aggregates with the macrophages and they observed a substantial decrease in membrane perturbation and macrophage killing.<br /> The work describes a very interesting mechanism by which Mtb can kill macrophages that is possibly relevant in the context of infection.

1. In general, there are two main issues with the experiments and the interpretation: the lack of quantitative analysis showing that in a population of macrophages the ones that are in contact with the aggregates die whereas the ones that are not in contact remain alive. This is currently not shown, and it should be added in figure 1.

All our data are based on the visual inspection and annotation of time-lapse microscopy image series, from which it is conclusive that death happens more often among cells in contact with Mtb aggregates (see movies S3 and S6 for representative examples). However, we acknowledge the reviewer’s suggestion that quantitative data supporting this observation might help to convey this conclusion more effectively. Therefore, we have quantified the percentage of dead cells in: I) macrophages in uninfected controls; II) macrophages that establish contact with an Mtb aggregate; III) bystander macrophages that never contact an Mtb aggregate despite being in the same sample as the infected cells, in experiments with (figure 1D) or without (figure 1Q) cytochalasin D treatment. These data have been incorporated as two additional plots in figure 1 in the revised manuscript. We find that uninfected and bystander cells have similar survival probabilities over the time-course of an experiment, whereas most of the cells that physically interact with Mtb_aggregates die by the end of the experiment. To further validate these observations, we have also plotted the lifespans of infected cells vs. bystander cells without (figure S3A) and with (figure S3B) cytochalasin D treatment. In these plots, the lifespan of an individual cell is represented by a line; the fraction of the line coloured in black corresponds to the time spent as bystander and the fraction of the line in magenta corresponds to the time spent in contact with an _Mtb aggregate. We hope that these new data convincingly show that bystander cells (black lines) survive longer compared to cells that interact with Mtb aggregates (black-magenta lines).

1. The second is the cell death mode, as the markers used are very different and considering different outcomes (e.g., apoptosis vs. necrosis) are relevant for the infection it is unclear what is being measured here and the impact on bacterial replication.

As the reviewer points out, it has previously been shown that different cell death pathways can affect viability and propagation of intracellular bacteria (1, 2). Since in our experiments we are specifically analyzing extracellular bacteria, we cannot directly comment on how cell death affects intracellular bacterial replication. However, to address the reviewer’s comment, we have included additional data in figure S13A of the revised manuscript showing that specific inhibitors of cell death do not affect the growth or replication of extracellular Mtb. These results suggest that while these molecules do not affect Mtb growth per se, the suppression of these specific death pathways also does not significantly affect the microenvironment to alter Mtb growth (i.e., access to nutrients or molecules released by dead cells). In addition, we have included new data in figure S12 demonstrating the responsiveness of our isolated macrophages to the various cocktails of molecules typically used to induce apoptosis, pyroptosis, or necroptosis.

The authors are showing that infection with Mtb aggregates increase the rate of the macrophage killing but how does this impact infection dissemination and replication of the bacterial aggregates? Is it beneficial for the aggregates? Did the authors check the growth rate of Mtb along with cytochalasin D?

A previous study has shown that phagocytosis of Mtb aggregates leads to macrophage death more efficiently than phagocytosis of a similar number of individual bacteria (3). It has also been shown that Mtb growing on the debris of dead host macrophages forms cytotoxic aggregates that kill the newly interacting macrophages (3). These observations suggest a model in which host cell death induced by Mtb aggregates supports faster extracellular growth and propagation of infection (3). This study was cited in the Introduction section of our manuscript, and our data support these observations. In the revised manuscript, we show that single Mtb bacilli or Mtb aggregates induce macrophage death in a dose-dependent manner (figure S7A,B); however, bacterial aggregates kill more efficiently when compared to similar numbers of non-aggregated bacilli (figure S7A,B). We also show that infection with Mtb_aggregates leads to faster bacterial propagation compared to infection with similar numbers of individual bacteria (figure S7C,D). These observations, combined with our data showing that _Mtb aggregation also enhances uptake-independent killing of macrophages (figure 2), suggest that Mtb aggregates induce rapid host cell death, allowing the bacteria to escape intracellular stresses, grow faster outside host cells (figure S1B), and propagate to other cells. To address the reviewer’s concern whether cytochalasin D affects Mtb growth, the revised manuscript includes additional data confirming that cytochalasin D does not affect the growth of Mtb aggregates (figure S6).

1. How did the authors quantify the interactions of Mtb with macrophages in Figure 1D?

The interactions of Mtb with macrophages were quantified through manual annotation of the time-lapse microscopy image series. If the Mtb aggregates disaggregated upon interaction with the macrophage, resulting in redistribution of smaller aggregates of bacteria, we categorized them as “fragmented”. On the other hand, if the aggregates remained clustered, we categorized them as “not fragmented”. Representative snapshots of these two patterns are presented in figure 1E and 1F and we have included additional representative examples in movies S4 and S5 of the revised manuscript. These interactions are quantified and plotted in figure 1N of the revised manuscript (figure 1D in the original version).

1. Is it enough to conclude with one example of SEM that the mycobacteria with different fragmentation discriminates if the bacteria is intracellular or extracellularly localised? Can authors use an alternative quantitative method to confirm the localization of the bacteria by a quantification by 3D imaging of these two phenotypes with a cytoskeleton marker (or may be even with tdTomato-expressing BMDMs)?

In the revised manuscript, we provide additional examples of correlative time-lapse microscopy and SEM images (supplementary figure S5). As suggested by the reviewer, in the revised manuscript we further validate these conclusions using an alternative approach based on correlative time-lapse microscopy followed by confocal 3D imaging. After time-lapse imaging, we fixed the samples and labelled the plasma membrane of the macrophages with a fluorescent anti-CD45 antibody to define the cell boundaries and identify bacteria that are intracellular vs. extracellular. Representative images obtained using this approach have been added to figure 1 and additional examples are shown in supplementary figure S4 of the revised manuscript. The acquisition, processing, and analysis of these 3D images are time-consuming and prevent us from performing an exhaustive quantitative analysis. However, we are confident in our conclusions, since in all of the cells that we analyzed we found that aggregates that are not fragmented within 6 hours of stable interaction with macrophages are visible on the outer side of the plasma membrane.

1. How do we know if the cell is lysed at 30 h in Supplementary Figure 1, did the authors use a marker to detect the cell lysis or is it based on just the observation from the live cell imaging? Movies in supplementary are actually not very informative as there are many ongoing events and it is hard to visualise what the authors claim. A marker of cell death in the movies should be used.

In this study, we used brightfield time-lapse microscopy images to identify cell death. Dying macrophages rapidly change shape, lose membrane integrity, and stop moving. Moreover, the intracellular structures and bacteria also stop moving at the time of death of the host cell. While these events can be difficult to distinguish by examining individual snapshots, they are readily identifiable by careful frame-by-frame examination of time-lapse microscopy image series. To exemplify this process, in the revised manuscript we show in supplementary figure S2A how we identify macrophage cell death events. We also include Draq7 (a live cell-impermeable dye commonly used to identify dead cells by flow cytometry and microscopy) in the growth medium during time-lapse imaging in order to label dead macrophages. The timing of staining validates and confirms our strategy of using brightfield time-lapse images to define the time-of-death of individual cells. To further assist readers, in the revised manuscript we provide the time-lapse microscopy movie used to generate this figure (movie S4). Similar images and movies have also been added for cells treated with cytochalasin D (figure S2B; movie S7). As suggested by the reviewer, we also replaced figure S1A with a new figure that shows a representative example of an Mtb intracellular microcolony that, upon death of the host macrophage, grows and forms a large extracellular aggregate on the debris of the dead cell (Draq7-positive). Movie S2 was used to generate this figure. Finally, we replaced figures 1E,F with new figures incorporating the Draq7 staining to label macrophage cell death and we include the time-lapse microscopy movies used to generate these figures (movies S4, S5).

1. Total macrophage killing after contact in Figure 1L is around 12 hours, whereas it is observed that the macrophage death after contact with cytochalasin D treatment in Figure 1M is even longer than 24 hours. The viability at 12 hours in Figure1M is as fragmented Mtb survival in Figure1L, why there is a difference in timing with respect to macrophage killing?

We thank the reviewer for this interesting observation. Indeed, we find that macrophages treated with cytochalasin D do take longer to die upon establishing stable interaction with Mtb aggregates in comparison to untreated cells. Although we do not have a clear explanation for this difference in timing, we speculate that by inhibiting actin polymerization and consequently cell motility, cytochalasin D might slow the expansion of the macrophage plasma membrane and the establishment of a larger interface of contact between the cell and the bacterial aggregate, which could influence the timing of cell death.

1. Did authors perform statistical tests for Figure 1D and Figure 1N? p-values should be added.

Figure 1D (figure 1N in the revised manuscript) shows the percentage of interactions between macrophages and _Mtb_aggregates that do or do not lead to fragmentation of the aggregate. Each dot represents the percentage of these events in one experimental replicate. We included this plot to show that reproducibly in all our replicates approximately 20% of the interactions do not lead to fragmentation of the aggregate. Since the purpose of this plot is not to compare the “fragmented” and “non-fragmented” populations but rather to highlight the reproducibility of the phenomenon, we do not think it would be appropriate to add a p-value. However, figure 1N (figure 1Q in the revised manuscript) has been updated and modified to include statistical analysis and a p-value.

1. In Figure 3, do the observations indicated in the Figure 3 happen in all the macrophages that are in contact with aggregates? This is unclear and critical to support the conclusions. Do all the macrophages that are in contact with Mtb aggregates become Annexin-V positive? In Supplementary Figure 2 there is some information regarding this question, but it will be important to show it as a percentage.

In response to the reviewer’s suggestion, we have modified the figure to include quantitation of Annexin-V staining. Approximately 75% of the macrophages that interact with an Mtb aggregate show detectable local Annexin V-positive membrane domains at the site of contact with the aggregate during a typical 60 hour-long experiment. Since most of the macrophages show local Annexin V-positive membrane domains within the first 12 hours upon contact with an Mtb_aggregate (figure 3C), we used this criterion for comparison of different conditions or strains (for example, those shown in figure 6F). In addition, we added figure 3D, which shows the behaviour of 105 macrophages upon contact with _Mtb aggregates in a typical experiment. In this plot, each line represents the lifespan of an individual cell; the fraction of the line in black represents the time spent as bystander, the fraction of the line in magenta represents the time spent interacting with an Mtb aggregate, and the fraction in green represents the time upon formation of local Annexin V-positive membrane domains at the site of contact with the Mtb aggregate. We believe that this additional information further supports our conclusions that most of the cells in contact with an Mtb aggregate show local Annexin V-positive membrane domains and that cells that show this pattern die faster than cells that do not develop local Annexin V-positive membrane domains.

1. Did the authors try to stain Mtb aggregates alone with Annexin-V as a control over the duration of the imaging?

We thank the reviewer for suggesting this control. In supplementary figure S8C of the revised manuscript, we include a representative example of a time-lapse microscopy image series showing Mtb aggregates that never interact with a live macrophage althought they are adjacent to a dead cell. As observed in the Annexin V fluorescence images (yellow), these Mtb aggregates never become Annexin-V positive during the course of the experiment (60 hours).

1. In Figure 4, did the authors continue to image the cells interacting with Mtb aggregates that do not die after Ca2+ accumulation in Supplementary Figure 3D? Do these cells recover from the plasma membrane perturbation? Did the authors consider using another marker for plasma membrane perturbation together with BAPTA?

Unfortunately, we are not able to image macrophages stained with Oregon Green 488 Bapta-1 AM for more than 36 hours because they lose fluorescence over time, possibly due to partial dye degradation or secretion. Another issue is that macrophages do not establish synchronous interaction with Mtb aggregates (figure 3D; figure S3B). In order to pool together results from many cells, we analyze all the cells that interact with Mtb within the first 20 hours and we define as timepoint 0 the time at which each individual cell establishes interaction with the bacteria. To compare similar time windows for each cell, we use fluorescence values measured at 16 hours post-interaction with bacteria as a readout. This time window is sufficient to observe formation of local Annexin V plasma membrane domains and death in a relevant number of macrophages (figure 1P; figure 3D). Not all of the contacted cells die within the timeframe of our experiments; however, we believe that if we imaged cells that accumulate Ca2+ for longer durations, we would find that all such cells eventually die. This assumption is consistent with the observation that calcium chelation reduces inflammasome activation and death in macrophages in contact with Mtb aggregates (figure 5D; figure 4E).

With respect to the reviewer’s query whether cells recover from plasma membrane perturbation, in our time-lapse microscopy experiments, we observe that when macrophages form local Annexin V-positive plasma membrane domains at the site of contact with Mtb aggregates, they never revert to an Annexin V-negative status afterwards (figure 3D; movie S7; movie S8). Our SEM data show that Mtb aggregates colocalizing with Annexin V-positive domains are not partially covered by intact membrane, in contrast to those associated with Annexin V-negative macrophages, although they do present vesicles and membrane debris on their surface (figure 3F,G ). In the revised manuscript, we include additional fluorescence microscopy images showing that Annexin V-positive foci colocalize with markers for the macrophages’ plasma membrane (figure S8A,B) as well as with more distal areas of the bacterial aggregates, where we do not observe any positive plasma membrane staining (figure S8B). Similarly, although _Mtb_aggregates that are never in contact with macrophages never become Annexin V-positive (figure S8C), we see that upon macrophage death, aggregates in contact with dead cells retain some Annexin V-positive material on their surface (figure S8C; movie S8). Vesicle budding and shedding is a common ESCRT III-mediated membrane repair strategy that allows removal of damaged portions of the plasma membrane and wound resealing (4). Thus, we think that in our experiments the Annexin V-positive foci might represent both damaged membrane areas and released macrophage plasma membrane vesicles that stick to the hydrophobic surface of the bacterial aggregates. This means that the time of appearance of Annexin V-positive domains marks the time when the macrophage membrane experiences a damaging event. Interestingly, we do not observe a gradual increase in fluorescence intensity of the Annexin V-positive domains, but rather multiple single intensity peaks over time (movie S8). This might suggest that multiple discrete damaging events occur over time.

1. In Figure 5D-G it will be important if the authors include dots for each macrophage events for the contact conditions as well, as it was done for the bystander condition.

We apologize for using a too-pale shade of magenta in the earlier version of the manuscript, which apparently made the dots in these figures hard to visualize. In the revised manuscript, we use a darker shade of magenta to show the dots corresponding to the fluorescence values of the macrophages in contact with Mtb aggregates.

1. How did the authors discriminate between the macrophages that are in contact or not with Mtb aggregates after the staining with Casp-1, pRIP3 and pMLKL? Do the aggregates stay in contact even after the staining procedures? Representative images of the labelling should be included in this figure.

Before fixation, we make sure to remove the medium gently to avoid disrupting the interactions between cells and bacteria. This step most likely removes the floating bacterial aggregates that are not in stable contact with cells but apparently does not detach aggregates that stably interact with cells. Our correlative time-lapse microscopy and immunofluorescence images (figure 1; figure S4), as well as our correlative time-lapse microscopy and SEM images (figure S5; figure 3F,G), confirm that Mtb aggregates that interact with cells during time-lapse imaging are retained on the surface of those cells upon fixation and processing for immunofluorescence or electron microscopy. As we can observe in figure 5B (cell indicated by the white arrow), Mtb aggregates are retained on the debris of dead cells. In figure 5 we distinguish between “in contact” macrophages and “bystander” macrophages by inspecting brightfield images showing the cells and the respective fluorescence images corresponding to the bacteria. If the body of a macrophage identified in the brightfield image overlaps with a bacterial aggregate identified in the fluorescence channel, we define the macrophage as “in contact”; otherwise, it is annotated as “bystander”. We provide representative images in figure S12 and we clarify the definition of “in contact” and “bystander” in the figure legend of figure 5.

1. The labelling of Figure 5H needs to be corrected both in the text and in the figure legend.

We thank the reviewer for bringing our attention to this error, which has been corrected in the revised manuscript.

1. Pyroptosis inhibitors did reduce the percentage of cell death, but did it also reduce the number of Annexin-V positive domains? This is important as AnnexinV is a marker of apoptosis and the outcome for Mtb very different.

As pointed out by the reviewer, Annexin V staining is often used as a marker for apoptosis. Typically, apoptotic cells stain positive for Annexin V but negative for other membrane-impermeable markers such as propidium iodide, because they expose phosphatidylserine (bound by Annexin V) on the outer leaflet of the plasma membrane without losing plasma membrane integrity (5). Apoptotic cells often look round and their plasma membrane is stained homogeneously by fluorescently labelled Annexin V (5). In our experiments, we observe that macrophages in contact with Mtb aggregates become Annexin V-positive; however, this happens only at the site of contact with the bacteria (figure 3A; movie S7). Only when cells die and get stained by membrane-impermeable dies such as Draq7 do they also get stained with Annexin V over the entire membrane debris. We thus use Annexin V staining as a marker for membrane perturbation rather than for cell death. If we were using the Annexin V as a marker for cell death, we would expect to see a reduction in Annexin V-positive cells in samples treated with pyroptosis inhibitors. In these samples, we do observe a reduced percentage of cell death in comparison to untreated controls; however, we still observe a comparable percentage of macrophages that stain positive for Annexin V locally, i.e., at the site of contact with bacterial aggregates (supplementary figure S13B). In line with this observation, treated vs. untreated macrophages in contact with Mtb aggregates accumulate similar levels of intracellular calcium. These observations are consistent with our model suggesting that contact with Mtb aggregates induces membrane perturbation, calcium accumulation, inflammasome activation, and pyroptosis in contacted macrophages. Since the death inhibitors used in our study specifically target pyroptosis effectors, we do not expect them to affect upstream events such as membrane perturbation and calcium accumulation.

1. In Figure 6, The sections for Figure 6 are well described but kept relatively long with too many details, it will be helpful to the reader if the authors can combine the sections in one header.

We agree that the text linked to figure 6 is long. We tried to make these sections as concise as possible; however, we are concerned that combining all of the sections under a single header might be at the expense of clarity. Thus, unless the reviewer objects, we would prefer to maintain the use of multiple headers.

1. Figure 6F does not have a statistical test and p-value, it will be important to include the statistical test in the legend and p-values in the

As recommended by the reviewer, we have analyzed the results in figure 6F by using a one-way ANOVA test and we have added the calculated p-values to the figure.

Reviewer #1 (Significance):

Based on the literature, Mtb infection and replication can trigger different types of cell death and most of the studies have addressed cell death only as an outcome of intracellular replication. This study shows another form of host cell death, associated only to extracellular bacterial aggregates that are in contact with macrophages. Plasma membrane damage initiating pyroptosis has been defined in: "Plasma membrane damage causes NLRP3 activation and pyroptosis during Mycobacterium tuberculosis infection" by K.S. Beckwith et al. (2020). However, the effect of extracellular bacteria on plasma membrane damage was not addressed before and this paper is addressing an important observation with respect to Mtb evasion and dissemination. These observations represent a novel and interesting aspect in the induction of macrophage cell death by Mtb and potentially relevant for the disease. If the authors consider the comments listed above, this manuscript will be a novel and relevant addition to the field of host pathogen interactions in tuberculosis.

We thank the reviewer for their perspective and their positive comments about our work.

Reviewer #2 (Evidence, reproducibility and clarity):

In this work, Toniolo and coworkers use single-cell time-lapse fluorescence microscopy to show that extracellular aggregates of Mycobacterium tuberculosis can evade phagocytosis by killing macrophages in a contact-dependent but uptake-independent manner. The authors further show that this process is dependent on the functionality of the ESX-1 type VII secretion system and the presence of mycobacterial phthiocerol dimycocerosate (PDIM). In essence the authors show that M. tuberculosis can induce macrophage death from the outside of the cell, and dissect the different players that are involved in the process.

Major comments:

1. I was intrigued by all the different findings of this work, which was done by using bone marrow derived murine macrophages, however, my first question to the authors is how they imagine that this process will take under an in vivo situation? Do they have evidence that these mycobacterial clumps may form during the initial infection process in the lungs? It would be important to provide more insights and discussion into this question in order to see how relevant the described details are inside the host organism.

Formation of Mtb aggregates in tuberculosis lesions have been documented in several animal models (6, 7) and in humans (8–11). While it is unclear whether mycobacterial aggregates form during the earliest stages of infection, extracellular bacterial aggregates have been observed in animal models of infection within the first month post-infection, and they are often associated with necrotic foci. Moreover, masses of Mtb growing as pellicle-like aggregates are often observed on the surface of cavities in human tuberculosis patients. These observations confirm that Mtb aggregates can form during a tuberculosis infection and that a significant fraction of bacteria are extracellular during different stages of infection. As we observe that macrophages undergo contact-dependent uptake-independent death also in the absence of cytochalasin D in vitro, we assume that this may also happen in vivo when Mtb aggregates are formed or released outside host cells. This process may promote bacterial propagation at early stages of infection as well as at later stages when necrotic granulomas and cavities are formed.

In the revised manuscript we present and discuss our observations in the context of the in vivo phenotypes reported in the scientific literature and we include additional references showing that extracellular Mtb aggregates are often observed in vivo. We also propose this concept already in the Introduction section to better link our observations to possible in vivo scenarios.

Minor comments:

Line 91: here the authors list the different forms of cell death that is induced by MTB infection, and it would be important to add apoptosis as a reported mechanism as well (References: PMID: 23848406, PMID: 28095608)

As suggested by the reviewer, in the revised manuscript we have modified the Introduction section to include apoptosis as a Mtb-induced mechanism of macrophage death and we have cited the two publications recommended by the reviewer.

1. Line 95: The secretion of EspE was mainly described in M. marinum while in members of the M. tuberculosis complex no virulence phenotype was reported to the best of my knowledge.

In agreement with the reviewer’s comment, we have modified the sentence and removed EspE from the list of virulence factors.

1. Lines 98: In the cited papers it is described that PDIM is required for phagosomal damage/rupture, however, the methods used there do not allow to specifically report about translocation. The wording should be adapted.

We thank the reviewer for this insightful comment and we have modified the text accordingly.

1. Line 206: Here it is described that in Figure 3A the BMDMs were expressing tdTomato fluorescence and the bacteria GFP, and the same is also repeated in the Figure legend of Fig3A. However, on the images, BMDMs are shown green and bacterial clumps purple (as also indicated in the description directly on the images) Please check and explain/correct this discrepancy.

We apologize that the color scheme in figure 3A is confusing. In this figure we used tdTomato-expressing BMDMs and GFP-expressing bacteria; however, we have pseudo-colored the fluorescence images for the sake of consistency with the other figures in the manuscript, which always show bacteria in magenta. We have clarified this point in the figure legend of the revised manuscript.

1. Line 304: Here the authors could mention that this finding is similar to results found previously in reference PMID: 28095608 and opposite to the results reported previously in PMID: 28505176.

As recommended by the reviewer, we have added a sentence comparing our results with previous studies and we have cited the two references suggested by the reviewer.

1. Line 321: It should be mentioned that CFP10 (EsxB) can also be secreted without its EsxA partner (under certain circumstances, i.e. when the EspACD operon is not expressed due to a phoP regulatory mutation (PMID: 28706226)). However, in Figure S7 an EspAdeletion mutant shows loss of EsxB secretion. This should be checked and discussed how the data here compare with data and strains published previously.

We thank the reviewer for pointing out this interesting point. Our proteomics data revealed that both our esxA mutant and our espA mutants abolish secretion of both EsxA and EsxB, in line with previously published data (12–14). We do not know why the espA mutant behaves differently from the MTBVAC strain concerning secretion of EsxA and EsxB (although we note that regulatory mutations may have complex pleiotropic effects). In the revised manuscript, we have modified this section to include references highlighting that secretion of these proteins may be uncoupled in some circumstances.

1. The finding that EspB can substitute the loss of virulence due to loss of EsxA/ESAT-6 secretion is astonishing and also is different to previous observations that strain H37Ra and MTBVAC (two attenuated strains that have no or very little EsxA secretion due to a regulation defect of the espACD operon PMID: 18282096; PMID: 28706226). How does the hypothesis put forward by the authors match with these previously published data ?

We thank the reviewer for this interesting comment. We would like to clarify that we are not claiming that EspB and EsxA are in general redundant and that EspB can substitute EsxA as a virulence factor. In our experiments we show that EspB can induce contact-dependent uptake-independent death in macrophages in contact with Mtb aggregates in vitro even in the absence of EsxA; however, the precise role of EspB during infection in mice or humans remains to be elucidated and is outside the scope of this manuscript. A previous study comparing Mtb ESX-1 mutants with different secretion patterns linked EspB secretion to Mtb virulence in vivo (14); however, the behavior of an isogenic espB_deletion strain _in vivo was not reported. A M. marinum espB mutant was shown to have reduced virulence; however, in contrast to Mtb, deletion of espB also affects secretion of EsxA in this organism (15). As the reviewer points out, the Mtb strains H37Ra and MTBVAC do not secrete EsxA due to a mutated phoP gene. Previous literature has shown that espB expression is also dependent on PhoP (16). We thus speculate that these strains might behave similarly to our espA espB mutant strain in the context of contact-dependent uptake-independent induction of macrophage death, although we think that this point is outside the scope of our manuscript.

1. In the same context, it is to notice that the authors report in the paragraph between lines 310-330 about EsxA/EsxB secretion, however, looking at the Western blots of figure S7, there is no blot showing results using an antibody against EsxA. Given the previously published results that EsxA/EsxB secretion may also be disconnected (PMID: 28706226), the wording of the text in this paragraph should be adapted or the results from Western Blots using EsxA antibodies be added.

We agree with the reviewer’s comment. Unfortunately, we currently do not have access to a good antibody for EsxA. A commercial monoclonal antibody that was previously available for immunoblotting has been discontinued. We tried several other antibodies that were previously shown to work in M. marinum, but none of these antibodies were effective in M. tuberculosis. We agree that analysing secretion of EsxB alone might not be sufficient to support claims about EsxA secretion. For this reason, we performed quantitative proteome analysis of the secretome in all of the relevant mutant strains. In our revised manuscript, we are careful to make sure that whenever we refer to EsxA/EsxB secretion we always provide proteomics data to support our conclusions.

1. Line 395: Here the authors write that BTP15, a small molecule that in a previous study was shown to inhibit EsxA secretion at higher concentrations (starting from 1.5 uM and higher). However, no effect on the expression of EsxA was described for that compound in reference PMID: 25299337. Thus the corresponding sentence in line 395 needs to adapted to that situation.

We thank the reviewer for noticing this error, which we have corrected in the revised manuscript.

1. Moreover, most concentrations of the compounds used are reported in uM, except for BTP15. It would be easier for the reader if the concentration used for BTP15 could also be reported in uM.

As suggested by the reviewer, in the revised manuscript we report the concentration of BTP15 in μM.

1. Line 475 The comment on the pore forming activity has to be made with caution, as recombinant EsxA produced from E. coli cultures has been shown to often retain detergent PMID: 28119503 that may be responsible for pore forming activity of recombinant EsxA observed in quite some studies, whereas EsxA purified from M. tuberculosis cultures did not show the detergent, but still retained membranolytic activity. This point should be clarified and discussed, and the wording adapted, as EsxA is not a classical poreforming toxin, but excerts the membrane-lysing activity together with other partners (PDIM) in a yet unknown way upon cell contact.

We thank the reviewer for this comment. In the revised manuscript, we have modified the text accordingly and included the sugggested reference.

Reviewer #2 (Significance):

The findings in this work extend the current knowledge on cell infection by M. tuberculosis in a significant way and put extracellular M. tuberculosis clumps in a new context. These data obtained by single-cell time-lapse fluorescence microscopy also need to be discussed for predicting the relevance for an in vivo situation inside the host organism.

As suggested by the reviewer, in the revised manuscript we discuss additional examples from the literature showing that Mtb aggregates can form during infection and that many bacteria are extracellular and associated with necrotic foci during different stages of the disease in animal models of infection and in human patients. We believe that these previously published observations support the in vivo relevance of the process we observe in vitro.

Reviewer #3 (Evidence, reproducibility and clarity):

This is an excellent study distinguished by the volume of observations, rigor of analysis and clarity of presentation. The results are novel, biologically interesting and pathophysiologically important. The ability of aggregated M. tuberculosis to kill macrophages has been reported, but the understanding was that proliferation of Mtb within macrophages killed them. Here, the authors observe that macrophages are susceptible to pyroptotic death triggered by contact with extracellular Mtb aggregates, and that this is not recapitulated by contact with a comparable number of Mtb as single bacilli. The authors go some way to tracing the mechanism and uncover a complex inter-dependence on PDIM and on components of the mycobacterial ESX-1 secretory system.

The following comments will helpfully improve the study further.

Major points

1. The chief measurement in this study is death of individual macrophages as judged by the observer in videomicroscopy. However, the criteria for calling a macrophage "dead" are not defined with any morphological detail, beyond noting that the cell stops moving and lyses. Of course a cell will stop moving if it has lysed, but do not some if not most cells stop moving before they lyse? If so, lysis alone would seem to be the time-point marker for cell death. Yet from the images in Fig 1E and F, I cannot tell that the cells called "dead" have lysed. Watching the videos, the time of lysis is not clear to me. Eventually, shrunken cell bodies are obvious but it is not clear if these are residua of cells that had been said to "lyse" at an earlier time.

In this study, we used brightfield time-lapse microscopy images to identify cell death. Dying macrophages rapidly change shape, lose membrane integrity, and stop moving. Moreover, the intracellular structures and bacteria also stop moving at the time of death of the host cell. While these events can be difficult to distinguish by examining individual snapshots, they are readily identifiable by careful frame-by-frame examination of time-lapse microscopy image series. To exemplify this process, in the revised manuscript we show in supplementary figure S2A how we identify macrophage cell death events. We also include Draq7 (a live cell-impermeable dye commonly used to identify dead cells by flow cytometry and microscopy) in the growth medium during time-lapse imaging in order to label dead macrophages. The timing of staining validates and confirms our strategy of using brightfield time-lapse images to define the time-of-death of individual cells. To further assist readers, in the revised manuscript we provide the time-lapse microscopy movie used to generate this figure (movie S4). Similar images and movies have also been added for cells treated with cytochalasin D (figure S2B; movie S7). As suggested by the reviewer, we also replaced figures 1E,F with new figures incorporating the Draq7 staining to label macrophage cell death and we include the time-lapse microscopy movies used to generate these figures (movies S4, S5).

1. The use of BTP15 as a specific inhibitor of ESX-1 is problematic. The source of the compound is not stated.

The BTP15 molecule was kindly provided by Prof. Stewart Cole, the corresponding author of the article describing the identification of this compound and its effect on Esx-1 secretion (17). We have included this information in the Materials and Methods section.

1. The concentration used, 20 ug/mL, is well above the reported IC50 (1.2 uM) for its presumed target, a mycobacterial histidine kinase, and above the concentrations (0.3-0.6 uM) reported to inhibit Mtb's secretion of EsxA almost completely. It is concerning that the concentrations that were reported to work so well on the whole cell are lower than the IC50 for the presumed target, because uptake into Mtb and intrabacterial metabolism will typically lead to a lower potency for an inhibitor against the whole bacterium than against the isolated enzyme; and because 50% inhibition of an enzyme rarely gives a functional effect as complete as what is shown in the cited reference. In other words, it is not clear that the histidine kinase is the functionally relevant target of BTP15 in Mtb. The original report did not consider BTP15's possible effect on mammalian cells and the present authors likewise do not take that into consideration with respect to possible effects on the macrophages. No concentration-response or time course experiments with BTP15 are presented. Most important, unless I missed it, there is apparently no demonstration that the compound inhibited ESX-1-dependent secretion in the present authors' hands, no matter by what mechanism. Without this, I am reluctant to accept that the results with BTP15 demonstrate a dependence of extracellular-aggregate-induced macrophage death on ESX-1-mediated secretion from Mtb. I would recommend that the authors either provide a direct demonstration of BTP15's effect on ESX-1 dependent secretion at concentrations near those that worked on whole cells in the original report, or drop the BTP15 studies from the paper. That said, the genetic experiments remain unequivocal, so the paper's conclusions would not be affected.

We agree with the reviewer that in the original version of our manuscript we did not provide direct evidence demonstrating that BTP15 inhibits ESX-1 secretion and that it does not affect the host cells. We addressed the first issue by quantifying (by Western blot) the secretion of EsxB and EspB in Mtb cultures treated with different concentrations of BTP15. We show that BTP15 reduces secretion of these two proteins in a dose-dependent manner. These data have been included in figures S21A-B of the revised manuscript. In line with this observation, we also show that BTP15 reduces uptake-independent killing of macrophages by Mtb aggregates in a dose-dependent manner (figure 6H). To show that the dose-dependent effect observed in macrophages does not depend on a direct effect of BTP15 on the host cells, we treated Mtb with different concentrations of BTP15 for 48 hours and removed the compound by washing the bacteria prior to infection. We observe that Mtb aggregates that have been treated with BTP15 show reduced uptake-independent killing of macrophages, even when bacteria have been pre-treated and the small molecule is not present during the incubation with the cells (figure S21C). We hope that these additional results provide clear evidence that BTP15 reduces Mtb-mediated contact-dependent uptake-independent killing of macrophages by inhibiting ESX-1 secretion, consistent with our genetic data. We think these results are important because they provide a chemical validation of our genetic data. To the best of our knowledge, BTP15 is the only available compound known to inhibit ESX-1 secretion, and in the revised manuscript we confirm that this compound has the previously described effect on Mtb also in our hands. Unfortunately, we had to use concentrations higher than those previously reported to inhibit ESX-1 secretion in order to achieve the observed effects. As we had access only to prediluted aliquots that had been stored for a long time, we cannot rule out the posibility that the compound might have undergone partial degradation during storage.

1. The experiments, or at least the discussion, could consider what may distinguish single Mtb cells from aggregated Mtb in some way relevant to the present observations. The authors seem to assume that all the Mtb cells in their preparations are biochemically equivalent and that their distribution into single-cell or aggregate subpopulations is stochastic. What if it is deterministic instead? For example, what if these two subpopulations are defined by differential expression of PDIM, so that the greater macrophage-killing effect of aggregates than single cells in equivalent numbers reflects a greater amount of PDIM in the aggregates, rather than some sort of valency-of-contact effect? The authors could compare the PDIM-to-DNA ratio in the single cell and aggregated subpopulations, or at least discuss this possibility.

We thank the reviewer for proposing this extremely interesting idea. In the revised manuscript, we have added a discussion of this point (lines 487-489) and we have floated various possible explanations. However, we believe that experimental dissection of the underlying mechanism could be a very lengthy undertaking and we hope that the reviewer will agree that this is outside the scope of the current manuscript.

Minor points

1. Some of the experiments compare "low", "medium" and "high" numbers of Mtb, but I could not find a definition of these numbers.

We apologize for this oversight. In the revised manuscript, we have clarified the definition of these gates in the figure 2 legend.

1. There seem to be no positive or negative controls for any of the antibodies used for cell staining (anti-cleaved caspase 1, antiphospho RIP3, anti-phospho MLKKL).

As recommended by the reviewer, the revised manuscript includes controls for all of the antibodies used for immunostaining. In figure S12 we provide representative immunostaining images and fluorescence quantification of uninfected untreated macrophages (negative controls) and of uninfected macrophages treated with cocktails of molecules typically used to induce apoptosis, pyroptosis, or necroptosis (positive controls).

Reviewer #3 (Significance):

The results are novel, biologically interesting and pathophysiologically important.

We thank the reviewer for their appreciation of our findings.

References 1. H. Gan, et al., Mycobacterium tuberculosis blocks crosslinking of annexin-1 and apoptotic envelope formation on infected macrophages to maintain virulence. Nature Immunology 9, 1189–1197 (2008). 2. M. Divangahi, et al., Mycobacterium tuberculosis evades macrophage defenses by inhibiting plasma membrane repair. Nature Immunology 10, 899–906 (2009). 3. D. Mahamed, et al., Intracellular growth of Mycobacterium tuberculosis after macrophage cell death leads to serial killing of host cells. eLife 6, e22028 (2017). 4. A. J. Jimenez, et al., ESCRT Machinery Is Required for Plasma Membrane Repair. Science 343, 1247136 (2014). 5. M. van Engeland, L. J. W. Nieland, F. C. S. Ramaekers, B. Schutte, C. P. M. Reutelingsperger, Annexin V-Affinity assay: A review on an apoptosis detection system based on phosphatidylserine exposure. Cytometry 31, 1–9 (1998). 6. D. R. Hoff, et al., Location of Intra- and Extracellular M. tuberculosis Populations in Lungs of Mice and Guinea Pigs during Disease Progression and after Drug Treatment. PLOS ONE 6, e17550 (2011). 7. S. M. Irwin, et al., Presence of multiple lesion types with vastly different microenvironments in C3HeB/FeJ mice following aerosol infection with Mycobacterium tuberculosis. Disease Models & Mechanisms 8, 591–602 (2015). 8. Kaplan, G., et al., Mycobacterium tuberculosis Growth at theCavity Surface: a Microenvironment with FailedImmunity. Infection and Immunity 71, 7099–7108 (2003). 9. J. Timm, et al., A Multidrug-Resistant, acr1-Deficient Clinical Isolate of Mycobacterium tuberculosis Is Unimpaired for Replication in Macrophages. The Journal of Infectious Diseases 193, 1703–1710 (2006). 10. R. L. Hunter, Pathology of post primary tuberculosis of the lung: An illustrated critical review. Tuberculosis 91, 497–509 (2011). 11. G. Wells, et al., Micro–Computed Tomography Analysis of the Human Tuberculous Lung Reveals Remarkable Heterogeneity in Three-dimensional Granuloma Morphology. Am J Respir Crit Care Med 204, 583–595 (2021). 12. S. A. Stanley, S. Raghavan, W. W. Hwang, J. S. Cox, Acute infection and macrophage subversion by Mycobacterium tuberculosis require a specialized secretion system. Proc Natl Acad Sci USA 100, 13001 (2003). 13. S. M. Fortune, et al., Mutually dependent secretion of proteins required for mycobacterial virulence. Proc Natl Acad Sci U S A 102, 10676 (2005). 14. J. M. Chen, et al., Mycobacterium tuberculosis EspB binds phospholipids and mediates EsxA-independent virulence. Mol Microbiol 89, 1154–1166 (2013). 15. L.-Y. Gao, et al., A mycobacterial virulence gene cluster extending RD1 is required for cytolysis, bacterial spreading and ESAT-6 secretion. Mol Microbiol 53, 1677–1693 (2004). 16. V. Anil Kumar, et al., EspR-dependent ESAT-6 Protein Secretion of Mycobacterium tuberculosis Requires the Presence of Virulence Regulator PhoP. Journal of Biological Chemistry 291, 19018–19030 (2016). 17. J. Rybniker, et al., Anticytolytic Screen Identifies Inhibitors of Mycobacterial Virulence Protein Secretion. Cell Host & Microbe 16*, 538–548 (2014).

We are still rapidly discovering new species and beings that we did not know to exist before on our planet. Their evolutionary trajectory may have split but they are ultimately tied to us by ancestry. However, we often look at creatures, especially new ones, and label them as alien, unsightly, repulsive, gross, creepy, etc. This destructive rhetoric leads to an irreverence toward their being. We do not know what the blob may feel, think, or do so why do we create this disconnect between them and ourselves? Respect can still be present without a connection but may take more effort. We must put in this effort, however, as they are ultimately our neighbors (evolutionarily and physically).

This is abhorrence to the unknown is thought to be part of our psychology. We make patterns and molds in which to fit the world into. It makes internal processing much easier, especially when confronted with a dangerous situation. For example, when things, such as the sea-blob, go against our conceived notions of ocean animals we are more cautious as we don't know to internally lable them as "safe and cuddly" or "they will eat your arm off". (read: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4141622) I'm not a super big fan of this article as its very anthropocentric but it points to some ideas about patterns that have been thought to help us survive. While the above article may refute this, animals do a similar "patternization" of their surroundings. Its a shortcut to take in senses, really, but I think it often leads to, as Juliette said, schismogenesis. In my classes I haven't found much literature contradicting the "pattern" notions of sensing per psychology, as much as I don't like them. I'd be interested to see if other had come across any literature.

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Reply to the reviewers

Point by Point Description of Revisions

We thank the reviewers for their time, effort and constructive input. Below, our responses are bolded with yellow highlighting, while the reviewers’ comments are italicized.

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

Summary

The manuscript by Hays and colleagues described the spectrum of mutations that drive adaptation in nitrogen-limit environment by experimental evolution. The approach of serial transfer (fluctuating condition) allowed them to find that Ty insertion is the major mutation type for adaptive evolution. This was neither observed in nitrogen-limited condition when another experimental evolution approach, chemostat (non-fluctuating condition), was applied, nor in glucose-limited condition. The authors concluded that not only selection pressure itself but also how selection is applied are important to shape the adaptive events.

Major points

*Both serial transfer and chemostat are commonly used approaches of experimental evolution. In the manuscript, the authors refer serial transfer to "fluctuating" condition because the low nitrogen source would be consumed to none during the interval of transfers. I am wondering whether the authors have estimated the nitrogen uptake (consumption) during the transfer intervals and whether the nitrogen was exhausted within 48 hours. *

We appreciate the reviewer’s question, and although we did not directly measure nitrogen consumption throughout this specific experiment, ammonium was the limiting nutrient in the defined medium which has been previously used to achieve transient nitrogen starvation conditions in other yeast experimental evolutions (Blundell et al. 2019). In that previous work, it was confirmed that addition of ammonium above 0.04% (up to 0.15%) led to additional rounds of doubling – confirming that the amount of ammonium provided was in fact the limiting nutrient. Finally, we point out that the adaptive mutations recovered in this study predominantly impact genes known to affect nitrogen catabolism, as is expected under nitrogen-limited evolution conditions.

We’ve updated the methods section to ensure the rationale for this medium choice is clearly stated.

Since this is not precisely controlled by experiment design, the "fluctuating" condition itself may be not stable during the long-term evolution. For example, as population evolved, the rate and the amount of nitrogen uptake might change. I feel a better experiment setup for "fluctuating" condition is like 24 hour "low-nitrogen (ammonium)" - 24 hour "no ammonium" and so on. If the adaptive mutations (e.g. adaptive Ty) specifically respond to such "fluctuating" condition rather than chemostat, the authors can measure their fitness in nitrogen starvation condition, which is expected to be fitter than mutants observed only in chemostat (e.g. copy number variation of nitrogen transporters).

The reviewer correctly points out that nitrogen availability will change as the population adapts, and it is likely that some portion of the population become better at utilizing the newly available nitrogen upon transfer into fresh medium over time. This is in fact the intention of this experimental design. We have rephrased the text of the main paper to emphasize that our fluctuating conditions represent fluctuations in the nutrient availability in fresh medium upon transfer, and not strict oscillating nitrogen concentrations that cells experience locally throughout all generations.

We note that in the reviewer-proposed experimental design (using 2 stages of low- and no- nitrogen media), that the low-nitrogen condition would still exhibit the same population-dependent nitrogen usage dynamics as the population adapts over time. We chose our evolution conditions to apply a selective pressure for cells to become best adapted to the environmental fluctuations associated with this transfer regimen, and we have updated the main paper to clarify this point. We thank the reviewer for helping us clarify this important point.

The authors compared their results with published dataset using nitrogen-limitation chemostat and the mutation spectrum is different. In addition to the "fluctuating" and "non-fluctuating" difference as mentioned above, other factors need to be considered. First, the nitrogen-limited conditions in the two studies are different. The authors used 0.04% ammonium sulfate while Hong et al used "800 uM nitrogen regardless of the molecular form of the nitrogen", which may influence the mutation spectrum and need to be discussed. Second, bottlenecks were applied for each transfer in this study, in comparison with constant population size in chemostat, which will influence the efficiency of selection and further the evolutionary dynamics and outcomes. Thus, population size and bottlenecks need to take in to account to make comparisons of mutation spectrum.

We thank the reviewer for their point: we have expanded the section of the main text addressing the differences in how serial transfer and chemostat conditions are applied, the media differences necessitated by such and specifically how the conditions between our study and the Hong et al study differ. We believe the additional detail now better highlights our point that how selection is applied shapes adaptive events, and we thank the reviewer for their helpful input.

*The authors found that Ty mutagenesis accounts for a substantial number of adaptive mutations in nitrogen limitation. I am wondering for adaptive clones, whether Ty occurred independently or is more likely to co-exist with other drivers. *

We appreciate the reviewer’s question. In the clones with adaptive Ty insertions, the only co-occurring adaptive mutation is autodiploidization. There were no additional mutational classes that were adaptive and co-occur with adaptive Ty insertions in our dataset. However, many novel Ty insertions are neutral, and these DO co-occur with beneficial mutations. These data are captured in Figure 5A, and in detail in Supplemental File 1. The blue bar in the adaptive haploids reflect neutral-fitness Ty insertions that co-occur with other mutations that drive fitness increase. These are distinct from the Ty insertions that are themselves responsible for the fitness increase, which are captured in the orange bar. We have clarified the text surrounding the Fig 5A results to better emphasize these findings.

What is the distribution of number of clones with one, two, and multiple mutations? If there is co-existence of driver mutations, what is the relative contribution of each to adaptation? The phenotypic validation of Ty mutagenesis for adaptation is expected while it seems only one case was presented in Figure 2 (mep1Ty−731427).

Aside from diploidization events, only one clone with two nitrogen-adaptive mutations was identified in this study: a double mutant with mutations in both gat1 and tor1. Please see Supplemental File 1 (which is sortable) for a complete outline of all clones with mutations and fitness remeasurements. In the case of diploids that have additional beneficial mutations, those data are shown in Figure 3 with diploids indicated as well as the ploidy of the secondary beneficial mutation, and again in detail in Supplemental File 1.

The reviewer is correct in that only one Ty mutation was dissected and validated in Figure 2. However, we inferred adaptation by Ty insertion through the observation of parallel adaptation, and we fitness remeasurements of many independent Ty insertion mutants.

Statistical analysis needs to be reinforced in the manuscript, including but not limited to Figure 2 fitness comparison among clones with different genotypes, Figure 5 Ty enrichment comparison, etc.

We thank the reviewer for their helpful suggestion. We have updated figures and figure legends to more clearly include statistical comparisons between genotypes for Figures 2 and 5: specifically describing the analyses used and the associated p-values for differences between WT and adaptive alleles and significance of Ty class enrichments.

Minor points

We thank the reviewer for their detailed and careful edits below and have addressed them in the main text and figures as applicable.

"For diploids, we only sequenced those with estimated fitness greater than diploidy alone would provide." Main text clarified with additional explanation

"either through impacting alternate start (green triangle) or alternate stop sites (yellow and red triangles)." I do not see yellow and red triangles in Fig. 3. Legend updated to reflect current figure color palette.

Fig.2. FCY2 mutant fitness can be added as well?

Unfortunately, data for FCY2 backcrossed mutants were not generated

"while we found only 212 novel Ty insertions in 488 glucose evolved clones (Figure 5B)" The value in the text does not match the one in the figure.

We appreciate the reviewer’s attention to detail and have corrected the main text to match the correct value in Fig 5B.

In addition to adaptive Ty insertion, what is the genome-wide distribution or characteristics of other Ty, especially for nitrogen-limited condition? Is that distinct from glucose-limited condition?

Figure S5 addresses the major locations of Ty insertions upstream of tRNA genes, in both Glucose and Nitrogen limited evolutions, the insertion location previously published to be preferred; the only difference between glucose and nitrogen is that there are more in the nitrogen limited condition, though the profile of insertions upstream of tRNAs is essentially the same. In addition to insertions upstream on tRNAs, all other specific insertion locations are available in Supplemental File 1 and Supplemental File 4.

"Studies determining at which step(s) of the Ty life cycle nitrogen starvation shapes ty activity would be needed to determine the specific mechanism underlying the increase in transposon insertions." Here "ty" => "Ty"

Corrected! We thank the reviewer for their detailed reading.

Reviewer #1 (Significance (Required)):

The manuscript is a follow-up work of Levy et al. 2015 and Blundell et al. 2019. In general, the research is interesting and point out the important role of Ty for adaptive evolution in nitrogen-limited environment. It also compared the spectrum of adaptive mutations in response to nitrogen limitation by serial transfer (this work) and chemostat (especially the work of Gresham lab). The paper is well-written as well. Audience from the field of genetics, genomics and evolution will be interested in this work.

My field of expertise: genetics, experimental evolution, budding yeast

We thank the reviewer for their kind comments, constructive input, and generosity with their time.

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

Hays et al. sequence and analyze the mutational spectrum from a set of S. cerevisiae strains evolved in a nitrogen limiting environment, and detail genes that recurrently are found to be mutated in a fluctuating nitrogen limiting environment. These data are contrasted to evolution under glucose limited environments and non-fluctuating environments. Specifically, Hays et al. observe a high proportion of Ty element-mediated mutations arising from strains evolved under the fluctuating nitrogen limiting regime. Their fitness data are robust and clearly demonstrate that these mutations reproducibly lead to improved fitness under nitrogen limitation (based on the authors' defined criteria). Overall, the observed bias of the high proportion of Ty-mediated mutation in fluctuating nitrogen starvation is unexpected and an important finding. Further, the discussion was thoughtful and well executed in detailing interpretations of the data more broadly. We are generally positive about this work and find the analyses robust and convincing. The authors should address the concerns listed below prior to acceptance/publication.

We thank the reviewer for their kind words and enthusiasm for our study, we have worked to address their constructive feedback as detailed below.

Reviewer #2 (Significance (Required)):

Major comments to be addressed:

The claim that the 3' UTR Ty insertions in MEP1 are apparently gain of function is very interesting. The authors should consider performing RT-PCR or strand specific RNAseq to see whether the antisense transcript is reduced and the MEP1 transcript is increased in the presence of the 3' UTR insertion. This would provide much stronger support for their claim that MEP1 3' Ty insertions are gain of function. Orientation information is critical to provide!

We agree that these future directions are exciting and of extreme interest! We however believe they are out of the scope of this current study which already includes substantial data and analysis. We note that we did not claim that the 3’ UTR insertions are gain of function – instead, we suggested that “Ty insertions in the 3’ region unique to the MEP1 locus may affect fitness in nitrogen limitation via a mechanism different than the putative gain of function missense mutations in the coding region itself”. We did not speculate on the mechanism by which these insertions are adaptive, but it is an active line of research and we look forward to discovering the mechanism.

The authors seemed to miss a golden opportunity to measure Ty1 expression or transposition under fluctuating/non-fluctuating nitrogen starvation. Otherwise, the claims of increased Ty activity are unsupported. The authors measured an endpoint (Ty insertion), but this says nothing directly as to the rate of activity, although it is presumably correlated. However, based on the data one could argue activity may be equal in all environments, but the mutational events caused by Ty activity are uniquely selected for in fluctuating nitrogen starvation. As it stands, either model (increased activity vs. differential strength of selection) are equally likely. At a minimum, the authors should at least address this point.

We appreciate the reviewer bringing this concern to our attention: we address the reviewer’s concerns in 3 ways: First, we’ve rephrased to more explicitly consider the possibility that the observed difference in novel Ty insertions could be driven at the level of selection, not activity. Second, we’ve clarified the main text to greater emphasize our reasoning for why we speculate the inference of greater Ty activity under nitrogen starvation may be more likely based on the level of presumptive neutral Ty insertions being greater in nitrogen than in glucose (even after normalization for the number of evolved generations). Third, we’ve performed additional experiments that support that, at least with an artificial retrotransposition reporter construct, these starvation conditions show additional Ty activity in nitrogen compared to glucose (note, we have not carried out such experiments in chemostats, and do not currently have a functioning chemostat set up). We’re including these results below, though have not included them in the manuscript, as we intend to generate additional data for a subsequent study to make these claims more robust. We feel that adding them to this manuscript would make it less focused.

To assess Ty activity in yeast experiencing different nutrient conditions, we used a modified version of a plasmid-based Ty reporter created previously by Curcio and Garfinkel, 1991, PNAS 88(3):936-40. The original reporter construct used an inducible GAL promoter to initiate Ty transcription from the plasmid, and new Ty insertions confer the ability for the strain to grow on SC-His. To assess Ty activity induced by nitrogen limitation, we excised the GAL promoter and instead used the native Ty promoter from the insertion found at YPLWTy1-1. This Ty promoter was selected based on having recovered novel Ty insertions in evolved clones that originated from this locus.

Plasmid pGS234 was created by replacing the promoter containing XhoI fragment from pGTy1mhis3-AI with XhoI fragment containing promoter from chromosomal location of YPLWTy1-1.

Strains bearing the Ty reporter plasmid pGS234 were subjected to nitrogen limited media and glucose limited media to assess transposon activity in these conditions. We observe significantly more Ty activity from the reporter plasmid in nitrogen-limited conditions than in glucose limited conditions or in SC-ura medium (see Figure below).

Panel A: Bars represent average of three WT strains with transposon reporter plasmid; each value is number of colonies on SC-His medium with each His+ colony representing independent Ty transposition events. Strains were grown in SC-Ura and then shifted to M14, M3 or SC-Ura as a control for 48 hours and plated on SC-His plates.

Panel B. One WT strain with pGS234 was subjected to a fluctuation test (16x 5ml tubes) in M14 and M3 media. Each dot represents the number of colonies on each SC-His plate. Kruskal-Wallis chi-squared = 23.341, df = 1, p-value = 1.357e-06

In line with the above, we think the authors should soften some points in the discussion as it stands. For example: "The significant increase of Ty activity under this specific fluctuating nitrogen-starvation..." We feel the data does not exclusively support increased activity of Ty, that would require the aforementioned assays. As it stands, we feel this is more appropriate: ": "The significant increase of Ty insertions under this specific fluctuating nitrogen-starvation..."

We edited the main text to include this suggested language change.

Minor comments to be addressed:

Please provide a citation for the following statement "The single copy of Ty5 in the ancestor is known to be inactive and gives rise to no new insertions under either glucose or nitrogen limitation" - Voytas & Boeke. Nature 1992.

We appreciate the reviewer catching this, and the reference has been added.

We found the following to be a confusing sentence: "Indeed, if global Ty derepression reflects a host-parasite coevolution that minimizes host cost and maximizes potential for survival of both, the role of transposons in host evolvability is important (Levin and Moran 2011)."

We have clarified this sentence by editing it to: “Indeed, the role of transposons in host evolvability is important: global Ty derepression could reflect host-parasite coevolution towards a less parasitic lifestyle: resulting in minimal host cost and maximized potential for survival of both, especially under detrimental environmental conditions (Levin and Moran 2011)”

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

Hays et al. studied the genomic changes that lead to adaptation under fluctuating nitrogen starvation. In addition to loss of function alleles, the authors identified adaptive gain-of- function alleles. Furthermore, their results demonstrate that Ty and microhomology-facilitated mutations in several candidate genes contribute substantially (though not exclusively) to the adaptation under nitrogen-limited serial transfer. Importantly, a novel lineage tracking method provides high resolution fitness measurements.

We appreciate the reviewer’s helpful edits in clarifying and improving the manuscript, and appreciate their time and constructive input.

Despite the clear merits of the study, we also have a few relatively minor questions and suggestions

• Please elaborate on the criteria they used to identify adaptive loci. The fact that these mutations occurred repeatedly is highlighted on Table 1, but perhaps numbers could also be included in the text, to increase clarity.* We have added the pertinent numbers to the main text to accompany the values captured in Table 1 and Supplemental file 1 and further emphasize selection criteria outline in the main text.

• "Were also validated to a fitness effect of >0.01 in nitrogen-limited media". More details about the selection of this cut-off value need to be provided in either the text or the Methods section to increase clarity.*

We agree and have clarified the limit of detection used in the methods section.

• In Figure 3 it seems that the type of observed mutations was less important compared to the gene where the mutation occurred. Therefore, it seems that some genes, e.g. GAT1, contribute more to the observed fitness change. It would be beneficial if the authors discussed this observation.*

We thank the reviewer for their observation and have included some additional discussion in the main text around the per-locus fitness observations as shown in Figure 3.

• What was the reason to select samples from the 88th generation for glucose and from the 192nd generation for nitrogen, as presented in Figure 5? How does this affect the observations?*

We thank the reviewer for their question: these generations were determined to best capture peak adaptive diversity (as discussed in Blundell et al 2019), based on population barcode dynamics in the original evolutions (Levy et al 2015, Blundell et al. 2019). The challenge is balancing picking a time point late enough, such that there are sufficient numbers of adaptive clones within independent lineages, yet early enough that few mutations have occurred (ideally only a single adaptive mutation per sequenced clone) and that no very fit clones have taken over the population. Because the fitness effects of beneficial mutations in glucose limited media were larger than in nitrogen limited media it was necessary to choose a later timepoint in the Nitrogen limited evolutions, to allow for there to be a sufficient fraction of the population carrying adaptive mutations. We believe this peak diversity makes these samples the most relevant for broadly assessing the adaptive mutational spectra.

• The use of statistics is not always clear. Please provide a clear indication of the statistical methods/tests used, eg for Figure 5.*

We thank the reviewer for this important point and have updated figures 2 and 5 and their corresponding legends for clarity surrounding statistical analysis used.

• The authors could include a supplementary Table, summarising their findings on GAT1 locus, since the text is extensive and it is difficult to put all the information into perspective.*

We note that row one of Table 1 in the main text is exactly this overview of the mutations observed at the GAT1 locus. These mutations plus specific location and their fitness remeasurements are shown in Figure 3 panel A, and detailed descriptions of the mutations for each clone are also available in the sortable table in Supplemental File 1. For these reasons we’ve not included an additional GAT1-specific table.

• The introduction is extremely detailed and informative, but at the same time quite lengthy; shortening it and only keeping the most relevant parts may increase readability.*

We appreciate the reviewer’s perspective but have not made substantial changes to remove information from the introduction as we feel that each of the subsections of the introduction are necessary to provide the appropriate context to the study.

• More detailed figure legends (which should also include a brief mentioning of the statistics & sample size) would benefit comprehensibility. For example the black lines in Figure S4 are not described anywhere in the text.*

We agree and have added further description of statistics used in legends throughout. Description of the black lines in Figure S4 has been included.

• "Many of the 332 clones ... were beneficial" à rephrase.*

We have updated this sentence to clarify our intent.

Reviewer #3 (Significance (Required)):

Apart from the elegant characterization of adaptive mutations, perhaps the most important part of the study is that it highlights the importance of a particular selection regime. Together, the findings extend our knowledge on this important topic.

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Referee #2

Evidence, reproducibility and clarity

Hays et al. sequence and analyze the mutational spectrum from a set of S. cerevisiae strains evolved in a nitrogen limiting environment, and detail genes that recurrently are found to be mutated in a fluctuating nitrogen limiting environment. These data are contrasted to evolution under glucose limited environments and non-fluctuating environments. Specifically, Hays et al. observe a high proportion of Ty element-mediated mutations arising from strains evolved under the fluctuating nitrogen limiting regime. Their fitness data are robust and clearly demonstrate that these mutations reproducibly lead to improved fitness under nitrogen limitation (based on the authors' defined criteria). Overall, the observed bias of the high proportion of Ty-mediated mutation in fluctuating nitrogen starvation is unexpected and an important finding. Further, the discussion was thoughtful and well executed in detailing interpretations of the data more broadly. We are generally positive about this work and find the analyses robust and convincing. The authors should address the concerns listed below prior to acceptance/publication.

Significance

Major comments to be addressed:

The claim that the 3' UTR Ty insertions in MEP1 are apparently gain of function is very interesting. The authors should consider performing RT-PCR or strand specific RNAseq to see whether the antisense transcript is reduced and the MEP1 transcript is increased in the presence of the 3' UTR insertion. This would provide much stronger support for their claim that MEP1 3' Ty insertions are gain of function. Orientation information is critical to provide!

The authors seemed to miss a golden opportunity to measure Ty1 expression or transposition under fluctuating/non-fluctuating nitrogen starvation. Otherwise, the claims of increased Ty activity are unsupported. The authors measured an endpoint (Ty insertion), but this says nothing directly as to the rate of activity, although it is presumably correlated. However, based on the data one could argue activity may be equal in all environments, but the mutational events caused by Ty activity are uniquely selected for in fluctuating nitrogen starvation. As it stands, either model (increased activity vs. differential strength of selection) are equally likely. At a minimum, the authors should at least address this point.

In line with the above, we think the authors should soften some points in the discussion as it stands. For example: "The significant increase of Ty activity under this specific fluctuating nitrogen-starvation..." We feel the data does not exclusively support increased activity of Ty, that would require the aforementioned assays. As it stands, we feel this is more appropriate: ": "The significant increase of Ty insertions under this specific fluctuating nitrogen-starvation..."

Minor comments to be addressed:

Please provide a citation for the following statement "The single copy of Ty5 in the ancestor is known to be inactive and gives rise to no new insertions under either glucose or nitrogen limitation" - Voytas & Boeke. Nature 1992.

We found the following to be a confusing sentence: "Indeed, if global Ty derepression reflects a host-parasite coevolution that minimizes host cost and maximizes potential for survival of both, the role of transposons in host evolvability is important (Levin and Moran 2011)."

I think that it is kind of interesting that if you fall into the categories of being well groomed and polite then you could be seen as a stereotype. while I feel that while we shouldnt be restrained into any type of role or stereotype I also feel that it is strange to say that doing certain things someone does out of free will will make you a stereotype or almost like a traitor to your origins.

I wonder if we should specify these LibGuides - as I think the outcome of the LibGuide review may mean these could change??

!!!!

Henry David Thoreau from 1852

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

Summary: The authors use an unclassified quaranjavirus, Wǔh�n mosquito virus 6 (WuMV-6), to demonstrate the possibility of orthomyxvirid global transmission dynamic analyses. The focused surface protein analysis strongly indicates a vertebrate host for WuMV-6 in addition to the insect host. The analysis is then expanded to other quaranjaviruses, which differ considerably in their surface glycoproteins, indicating a complex evolution. Finally, the authors scientifically demonstrate that orthomyxovirids are undersampled and hence that this family will have to expand considerably in the future.

Major comments: none

We thank the reviewer for a succinct summary of our study and we are very glad the key messages were sufficiently clear.

Minor comments: The article lacks precision and hence some global edits are in order. Generally:

1. For clarity to the reader, please introduce the family Orthomyxoviridae, i.e., its current official composition (i.e., 9 genera, 21 species, and 22 viruses) so the reader is not confused by terms such as "quaranjavirus" or "isavirus" etc.).

This is a fair request though we would prefer to err on the side of caution with regards to the precise number of taxonomic ranks given the flux viral taxonomy has experienced and in light of the deluge of new taxa being discovered all the time. We refer to the “traditional” view of orthomyxovirid taxonomy at the genus level, encompassing the genera described up until 2011.

After that, please clearly indicate which viruses are classified and which ones are not. For instance, the main virus dealt with in this paper is unclassified, and so are Astopletus and Ūsinis viruses.

We do not think this is reasonable since virtually all RNA viruses discussed in the text are not classified and their status as such has little bearing on any of our findings.

Please ensure correct spelling, including diacritics, of the viruses and abbreviations throughout: Wǔh�n mosquito virus 6 (WuMV-6); H�běi orthomyxo-like virus 2 [note the deletion of one "virus"]; Wēnlǐng orthomyxo-like virus 2

Thank you for the comment, we have added the diacritics where we could identify them but may have missed some.

For orientation of the reader, please refer to family groups of viruses as -virids (e.g., "orthomyxovirids", "human coronavirids", "some rhabdovirids"). This way it is clear to the reader that, for instance, "quaranjaviruses" refers to a genus-level group

Thank you, we agree that this adds much needed precision in terminology.

"influenza" is a disease. There are several viruses that can cause influenza; they belong to four different genera. Please scan for "influenza" and replace each either with a virus name (for instance, in the abstract, "...RNA viruses containing influenza A virus" or with a genus name (e.g., "alphainfluenzaviruses")

Our apologies for that misnomer. The text has been corrected.

Please ensure the differentiation of taxa (concepts), such as species, and viruses (things). Orthomyxoviridae cannot infect anything, it can also not be sampled etc. Orthomyxovirids, the physical members of Orthomyxoviridae can infect things. Most instances of "Orthomyxoviridae" should be replaced accordingly.

Thank you for the comment, this has been corrected as suggested.

In particular:

1. The title doesn't make much sense. Orthomyxovirids are not taxonomically incomplete - they are things that we simply may not have samples or may have characterized incompletely. Also, the analyses are largely restricted to quaranjaviruses. Hence, I would suggest "...genome evolution, and broad diversity of quaranjaviruses"

Our apologies for the confusion. The analyses we carried out to quantify evolutionary orthomyxovirid diversity likely waiting to be discovered was carried out on all known (at the time) members of ____Orthomyxoviridae____ and thus the title must still refer to the entire family rather than quaranjavirids. We felt that the term “taxonomic incompleteness” imparts on the reader exactly what the reviewer refers to, namely that new taxonomic ranks are likely to come as more evolutionary diversity gets uncovered. Alternative and more precise formulations, like referring to evolutionary incompleteness or something similar, would miss the fact that it is taxonomy that discretises the otherwise continuous evolutionary change.

Abstract: genomes are not employed and do not make money. Please replace "employed" with "used"

We have to respectfully disagree since the definition of the word “employ” also includes the meaning “to make use of”.

Re: point 6 above, Introduction: species/families etc. cannot be discovered. They are being established by people for viruses that may be discovered. Please fix here and elsewhere (in most cases, "species" should be replaced with "viruses")

We agree that taxonomic ranks are designated and not discovered and have changed the text accordingly.

P3, second paragraph: please place "jingmenviruses" in quotation marks as this is not an official term (yet). Please add "potentially" ("as potentially causing human disease"). Even the authors only speak of an "association" and do not fulfill Koch's postulates

We have to respectfully disagree here too. “Jingmenviruses” as a term is unambiguous in referring to a group of related segmented flaviviruses even though the groups is not officially assigned a taxonomic rank. We have altered the text to add uncertainty to the claim that jingmenviruses cause disease in humans.

P3, top right column: "e.g., the tick-borne Johnston Atoll quaranja- and thogotoviruses" is ambiguous. Please change to "e.g., the tick-borne quaranja- and thogotoviruses" or list particular viruses and clarify which belong to which genus

Apologies for the confusion. We fixed this instance.

P3, right column "smaller number" - change to "lower number"

We have altered the offending sentence in response to reviewer 2 and this combination of words is no longer present.

P3, right column "or only the polymerase" - makes no sense to the reader as it has not been introduced; and grammatically needs to be improved as the polymerase is also encoded on a segment. Likewise, PB1 makes no sense to unacquainted reader - maybe add a few sentences to the intro right after the family introduction on general genome composition and that PB1 is part of the polymerase holoenyzme?

We have altered the offending sentence in response to reviewer 2 but we take the point. We’ve added detail about the RNA-directed RNA polymerase of orthomyxovirids to the introduction.

P4: the Ebola virus glycoprotein is called GP1,2 [with 1,2 in subscript] (also Figure 2 legend)

Respectfully, while the reviewer is technically correct in that the glycoprotein of Ebola virus is referred to as GP_1,2 in proteomics literature (the 1,2 referencing the protein held together by a cysteine bridge post-cleavage), calling it GP is not out of place in evolutionary studies and the term “Ebola virus GP” is unambiguous to the reader.

P4: please change "West Africa" to "Western Africa" (the designation of the area by the UN)

Unfortunately, while we agree that the reviewer is correct in that the UN refers to the region as “Western Africa”, references to the “West African Ebola virus epidemic” are ubiquitous in the literature and thus we do not see the reason to change the term here either.

P6: change "with Rainbow / Steelhead trout orthomyxviruses" to "with mykissviruses (rainbow trout orthomyxovirus and steelhead trout orthomyxovirus)" [note that virus names are not capitalized except for proper noun components; hence also "infectious salmon anemia virus, bottom right column]

While we recognise that viruses related to infectious salmon anaemia virus discovered in trout have received a separate taxonomic designation we feel very strongly about not mentioning it in our manuscript. Our fear is that “mykissviruses” have been designated too hastily on the basis of a handful of representatives and that relatives discovered in the future may show an indiscernible continuum between “mykissviruses” and isaviruses, invalidating the former as a valid term. We would therefore strongly prefer to keep references to specific viruses rather than a taxonomic designation that may disappear so that a future reader may have an easier time with our study.

P6, right column: please change "RNA-dependent" to the IUPAC/IUB-correct "RNA-directed"

Done.

Figure 2 is too small. I could not figure out B with or without my confocals... Likewise S2, S3 are way too small. In Fig 2 legend, please place "spike" into lower case

We understand the reviewer’s concern here but Figure 2B was a compromise between vertical space available on a page, the number of taxa in the PB1 tree, and what we thought important to communicate - the variation in segment number across orthomyxoviruses and mapping of PB1 diversity to gp64 diversity. This was done at the expense of individual taxon name visibility whilst fully zoomed out. To remedy this Figure 2B was rendered in 300 dpi resolution such that zooming in will show individual taxon names clearly. We ultimately hope to publish our study in an online-only journal where printing will not present an issue. Likewise for figures S2 and S3. We have changed “Spike” to be lower case in the legend.

Figure 3: correct spelling of virus names (from top to bottom): rainbow trout orthomyxovirus, infectious salmon anemia virus, influenza C virus, influenza D virus, influenza A virus, influenza B virus, Wēnlǐng orthomyxo-like virus 2, Dhori virus, Thogoto virus, Jos virus, Aransas Bay virus, ... Johnston Atoll virus, Quaranfil virus, H�běi orthomyxo-like virus 2, Hǎin�n orthomyxo-like virus 2, Wǔh�n mosquito virus 6. Also apply to S6 and others where applicable.

The names for viruses in Figure 3 were taken directly from their NCBI records and since we do not show their accessions there is no other way to disambiguate them to the reader. We have, however, added the necessary diacritics where appropriate.

[PS: based on the somewhat backward, non-UNICODE editorial manager system, I am worried that the diacritics in virus names above are not rendered corretly. If so, please look up the Pinyin spelling of Wuhan, Hainan, Wenling etc. - easiest way is to search Wikipedia for the terns and then identify the Pinyin spelling, which is typically pointed out]

CROSS-CONSULTATION COMMENTS

I think we (all reviewers) are all largely in agreement - this is a very useful study; the manuscripts just needs various adjustments. I agree with the requests of the other two reviewers.

Reviewer #1 (Significance (Required)):

The strength of the paper is that it provides a road map on how undersampled taxa may be analyzed and which kind of information can be gleaned from these analyses. The paper also demonstrates that the analysis of seemingly "unimportant" viruses can prove important. The limitation of the paper is that there is no true novel revelation here. The sampling sites of WuMV-2 GenBank records already suggest broad distribution, which often goes along with sequence diversity; the continued discovery of orthomyxovirids in metagenomic studies clearly implied undersampling (but it is nice to have this "gut feeling" scientifically fortified now). The paper is useful for evolutionary virologists, virus taxonomists, orthomyxovirid specialists, and invertebrate virologists.

We respectfully disagree with the reviewer and believe they may have missed an important point raised by our study. We do not claim that a global distribution of WuMV6 is what makes it remarkable but that its sampled diversity is 1) sufficient to calibrate molecular clocks (in our experience this is not always the case for arthropod viruses) and 2) that WuMV6 has reached its current global distribution ____recently____.

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

This is a nice example of bringing together a variety of data from metatranscriptomic studies to answer fundamental evolutionary questions in the field of viral evolution. There is a focus on a single virus family, and although some might see this as a little restrictive, I think the 'deep-dive' presented in this paper leaves space for a relatively detailed and comprehensive analysis. No doubt, other studies will gain inspiration from the approach presented here and expand this work to other viral groups.

Overall, the paper is very well written, and the figures are of a very high quality. It is a shame that there are only 3 main figures in the paper because the supplementary figures are well presented and informative.

We thank the reviewer for the kind words.

The manuscript discusses the importance of host quite a bit, and for that reason it would have been nice to try and incorporate the host of the various viruses into the figures somehow (perhaps as a supplementary, since the trees are already quite busy). This might help orientate the reader).

While we appreciate that host information is of interest, we foresee several issues. For one, we refer to broad host classes (essentially arthropod versus vertebrate) because they are largely determined by membrane fusion protein classes, the actual focus of our study, which exhibit strong phylogenetic signal. Secondly, host information in metagenomic studies can be imprecise, incorrect or unavailable.

I have some minor comments or suggestions for the authors to consider below. Note, please use line numbers in the future for your submissions.

A paragraph in the discussion laying out the limitations of this approach would be useful to the reader and would make this excellent paper even more robust.

Thank you for the suggestion. We presume the reviewer is referring to our interpolation of orthomyxovirid diversity and included a few sentences about the limitations of this approach in the Discussion.

Pg 3. The sentence starting 'The vast majority of known orthomyxoviruses use one...' should be made into two sentences to make it easier to read. A second sentence for the arthropod description is the obvious edit.

We appreciate the suggestion and have included it in the manuscript.

Pg 3. 'The number of segments of orthomyxoviruses with genomes known to be complete varies from 6 to 8'. Rephrase to - 'Orthomyxoviruses genomes are known to have 6-8 segments, but many metagenomically discovered viruses in this group have incomplete genomes...etc...',

Thank you for the suggestion, it has been included.

Figure 1 - what do the white triangles mean? Are these the directions of reassortment? This should be explained in the legend...

We apologise for the omission, this is now explained.

New Zealand is covered up by the circular tree. It looks like there is a point which is partially obscured.

The reviewer spotted a mistake on our part here. The figure included the coordinates for Wellington, New Zealand when the detection was actually in Wellington Shire, Australia. This has been fixed.

PD analysis - t I think you assume that viruses are static in this analysis. As we all know, they continue to mutate and eventually new species will evolve. Is it possible to consider the mutation rate in this analysis and the evolution of new variants/ eventually leading to new species? It might be complicated, and maybe a matter for future work, but it might be worth discussing this as a limitation at the very least. Especially when extrapolating to the future (although you do not extrapolate too far, so maybe this is not an issue here...). You could choose to discuss this in relation to the bird analogy (which was great), and compare the rate of mutation which will lead to the evolution of new species on a totally different time scale.

We appreciate the point raised by the reviewer and while we wholly agree that the possibility of new viral taxa arising over time is an important caveat, we felt the discussion ends up being rather short. On one hand taxa definitions for different viral groups can be different, and on the other speciation in RNA viruses is difficult to place in absolute time because of a phenomenon called time-dependence of evolutionary rates. Methods accounting for the latter using sophisticated models or external calibration points would seem to imply that speciation timescales exceed those of research.

Discussion: When discussing the hypothesis that WMV6 diversity is a result of repeat exposure to vertebrate hosts, can you also describe the alternative hypothesis here, and why the evidence leads you to put more weight on the former.

This is a fair question and we have mentioned an alternative hypothesis in the discussion that’s been brought up by our colleagues before. It’s a hypothesis that alternating between different hosts induces divergent selection pressures on gp64. We contend that since gp64 proteins are thought to use a highly conserved host receptor (NPC1) we think it likely that no major changes are required when switching hosts. We are open to discussing other alternatives if the reviewer has suggestions.

CROSS-CONSULTATION COMMENTS

Seems like we are all in agreement and that after some minor adjustments this will be an excellent contribution.

Reviewer #2 (Significance (Required)):

Please see my review above. I did not use your formatting suggestions since I only saw it upon completing my review.

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

Summary

This manuscript describes the use of data from metagenomic analyses to make inferences about the evolutionary and geographic history of the Orthomyxoviridae family of viruses and their hosts. Data from Wuhan Mosquito Virus 6 (WMV6) derived from various RNA-seq analyses is used to analyse loss and gain of virus segments over time, the time since the last common ancestor of these segments and the selection pressure acting on different genes. These results are used to hypothesise about which species have vectored this virus in the past and their geographic distribution. The additional phylogenetic diversity provided by characterisation of additional viruses of this species is quantified and projected into the future to demonstrate the value of further work in this area. The study also demonstrates more generally the benefit of additional sequencing and of characterising viruses in metagenomic datasets, even in cases where novel viruses are not identified.

Major Comments

The methodology in this manuscript appears to be sound and the results support the conclusions. Appropriate and detailed analyses have been performed and are described in detail. Code is provided to allow the results to be reproduced. The figures are informative and very well presented. I do not think any additional analyses are required.

We thank the reviewer for the kind words.

Minor Comments

The manuscript is a little hard to follow in places. I think a brief introduction of WHV6 in the introduction section would help with this - where has it been isolated previously and what is known about its evolutionary history (if anything), how is it related to other Orthomyxoviruses. This information is included later but it would improve the flow of the paper to include it in the introduction.

We apologise for the inconvenience and agree with the reviewer. We have improved the flow of the manuscript per reviewer suggestion.

I think including a little more about the Method in the Results section would also be helpful, to save the reader jumping back and forth in order to understand the results. For example, at the beginning of the results section, briefly detailing how many samples were included, their broad geographic location and what the analysis is intended to show (e.g. "three full length sequences isolated from China, seven from Australia [...], between 1995 and 2019, were used to generate a reassortment network, in order to show.....") would be helpful. Each of the subsections of the Results would benefit from something similar.

Apologies for the lack of clarity on our part. We have added more methodological information to each section in the results.

Although it is clear in the Materials and Methods which datasets have been included, it is less apparent why these were selected. For example, in Figure 1A there are five countries listed - are these countries for which a particularly large amount of full length sequences were available or for which any full length sequence is available? Similarly, for Figure 1B, are these all of the countries where a dataset has originated containing any segment of WHV6?

The confusion is entirely our fault as we have clearly not provided sufficient detail. This has been fixed now by explaining this better in the methods and Figure 1 legend.

In the Discussion, it is stated that the frequency and fast evolution of WMV6 place it uniquely to enable tracking of mosquito populations, however there is no evidence presented to support this - does WMV6 evolve faster or occur more frequently than other mosquito RNA viruses?

Our apologies for the jump in logic. We now expand on what we meant by the following sentence in the discussion: “In our experience, metagenomically discovered RNA viruses can be rare or, when encountered often, do not always contain sufficient signal to calibrate molecular clocks (Webster et al. 2015).”

CROSS-CONSULTATION COMMENTS

I also agree with the requests of the other two reviewers and that the manuscript will be in great shape once these are included.

Reviewer #3 (Significance (Required)):

This manuscript is very interesting, for the specific results presented here but, more importantly, in opening up further avenues for investigation. The study provides a proof of concept for using viruses derived from metagenomic data for specific and detailed evolutionary and ecological analyses of a single species. The scope of the analysis performed on WMV6 is not particularly broad, but it differs from the typical analysis of viruses in metagenomic datasets, which tends to focus on identification and characterisation of novel viruses only. I believe that this work is valuable to others working in the field, reveals additional potential in existing data and could provide inspiration for many future studies. To my knowledge, it is one of the first studies to focus on a single, fairly under-studied virus, and draw ecological conclusions based on only bioinformatic analyses.

I think the results presented here for WMV6 may be of interest to a specialised audience, but that the manuscript overall is valuable to a broad audience, including ecologists, evolutionary biologists and virologists conducting fundamental science research.

We appreciate the reviewer’s kind words.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors use an unclassified quaranjavirus, Wǔhàn mosquito virus 6 (WuMV-6), to demonstrate the possibility of orthomyxvirid global transmission dynamic analyses. The focused surface protein analysis strongly indicates a vertebrate host for WuMV-6 in addition to the insect host. The analysis is then expanded to other quaranjaviruses, which differ considerably in their surface glycoproteins, indicating a complex evolution. Finally, the authors scientifically demonstrate that orthomyxovirids are undersampled and hence that this family will have to expand considerably in the future.

Minor comments:

The article lacks precision and hence some global edits are in order. Generally:

1. For clarity to the reader, please introduce the family Orthomyxoviridae, i.e., its current official composition (i.e., 9 genera, 21 species, and 22 viruses) so the reader is not confused by terms such as "quaranjavirus" or "isavirus" etc.).

2. After that, please clearly indicate which viruses are classified and which ones are not. For instance, the main virus dealt with in this paper is unclassified, and so are Astopletus and Ūsinis viruses.

3. Please ensure correct spelling, including diacritics, of the viruses and abbreviations throughout: Wǔhàn mosquito virus 6 (WuMV-6); Húběi orthomyxo-like virus 2 [note the deletion of one "virus"]; Wēnlǐng orthomyxo-like virus 2

4. For orientation of the reader, please refer to family groups of viruses as -virids (e.g., "orthomyxovirids", "human coronavirids", "some rhabdovirids"). This way it is clear to the reader that, for instance, "quaranjaviruses" refers to a genus-level group

5. "influenza" is a disease. There are several viruses that can cause influenza; they belong to four different genera. Please scan for "influenza" and replace each either with a virus name (for instance, in the abstract, "...RNA viruses containing influenza A virus" or with a genus name (e.g., "alphainfluenzaviruses")

6. Please ensure the differentiation of taxa (concepts), such as species, and viruses (things). Orthomyxoviridae cannot infect anything, it can also not be sampled etc. Orthomyxovirids, the physical members of Orthomyxoviridae can infect things. Most instances of "Orthomyxoviridae" should be replaced accordingly.

In particular:

1. The title doesn't make much sense. Orthomyxovirids are not taxonomically incomplete - they are things that we simply may not have samples or may have characterized incompletely. Also, the analyses are largely restricted to quaranjaviruses. Hence, I would suggest "...genome evolution, and broad diversity of quaranjaviruses"

2. Abstract: genomes are not employed and do not make money. Please replace "employed" with "used"

3. Re: point 6 above, Introduction: species/families etc. cannot be discovered. They are being established by people for viruses that may be discovered. Please fix here and elsewhere (in most cases, "species" should be replaced with "viruses")

4. P3, second paragraph: please place "jingmenviruses" in quotation marks as this is not an official term (yet). Please add "potentially" ("as potentially causing human disease"). Even the authors only speak of an "association" and do not fulfill Koch's postulates

5. P3, top right column: "e.g., the tick-borne Johnston Atoll quaranja- and thogotoviruses" is ambiguous. Please change to "e.g., the tick-borne quaranja- and thogotoviruses" or list particular viruses and clarify which belong to which genus

6. P3, right column "smaller number" - change to "lower number"

7. P3, right column "or only the polymerase" - makes no sense to the reader as it has not been introduced; and grammatically needs to be improved as the polymerase is also encoded on a segment. Likewise, PB1 makes no sense to unacquainted reader - maybe add a few sentences to the intro right after the family introduction on general genome composition and that PB1 is part of the polymerase holoenyzme?

8. P4: the Ebola virus glycoprotein is called GP1,2 [with 1,2 in subscript] (also Figure 2 legend)

9. P4: please change "West Africa" to "Western Africa" (the designation of the area by the UN)

10. P6: change "with Rainbow / Steelhead trout orthomyxviruses" to "with mykissviruses (rainbow trout orthomyxovirus and steelhead trout orthomyxovirus)" [note that virus names are not capitalized except for proper noun components; hence also "infectious salmon anemia virus, bottom right column]

11. P6, right column: please change "RNA-dependent" to the IUPAC/IUB-correct "RNA-directed"

12. Figure 2 is too small. I could not figure out B with or without my confocals... Likewise S2, S3 are way too small. In Fig 2 legend, please place "spike" into lower case

13. Figure 3: correct spelling of virus names (from top to bottom): rainbow trout orthomyxovirus, infectious salmon anemia virus, influenza C virus, influenza D virus, influenza A virus, influenza B virus, Wēnlǐng orthomyxo-like virus 2, Dhori virus, Thogoto virus, Jos virus, Aransas Bay virus, ... Johnston Atoll virus, Quaranfil virus, Húběi orthomyxo-like virus 2, Hǎinán orthomyxo-like virus 2, Wǔhàn mosquito virus 6. Also apply to S6 and others where applicable.

[PS: based on the somewhat backward, non-UNICODE editorial manager system, I am worried that the diacritics in virus names above are not rendered corretly. If so, please look up the Pinyin spelling of Wuhan, Hainan, Wenling etc. - easiest way is to search Wikipedia for the terns and then identify the Pinyin spelling, which is typically pointed out]

CROSS-CONSULTATION COMMENTS

I think we (all reviewers) are all largely in agreement - this is a very useful study; the manuscripts just needs various adjustments. I agree with the requests of the other two reviewers.

Significance

The strength of the paper is that it provides a road map on how undersampled taxa may be analyzed and which kind of information can be gleaned from these analyses. The paper also demonstrates that the analysis of seemingly "unimportant" viruses can prove important. The limitation of the paper is that there is no true novel revelation here. The sampling sites of WuMV-2 GenBank records already suggest broad distribution, which often goes along with sequence diversity; the continued discovery of orthomyxovirids in metagenomic studies clearly implied undersampling (but it is nice to have this "gut feeling" scientifically fortified now). The paper is useful for evolutionary virologists, virus taxonomists, orthomyxovirid specialists, and invertebrate virologists.

The way we identify socially may be viewed entirely differently to different individuals depending on their understanding of the history /past surrounding your identity. You may have one understanding of the past surrounding who you are, for example you may view you identity positively after understanding your history, but someone else may view your social identity negatively because they interpret your past differently, or with bias.

Dear Alizeh, Sawdeh and Khurshid, I read your chapter twice carefully and I hope I have provided constructive feedbacks. In general, I can point out that while I was reading, I noticed your countless efforts in writing this chapter. Stay successful and talented.

Malvolio, despite being a character who should not be trifled with, falls for a poorly planned prank, first and foremost due to his desire for power (which is evident in his verbal juggling), which he believes will only come to him through his marriage to Olivia. Additionally, because Shakespeare wanted to mock the Puritan tendencies of the time, he purposefully created Malvolio to fall for this prank in this scene. A typical set of issues are brought up by the practical prank played on Malvolio, including identity instability, the significance of clothing in establishing one's identity and place, and the illusions and delusions we allow ourselves to fall into in the name of love. Malvolio succumbs to the seduction of romance just like everyone else, including Orsino and Viola. He is as romantic as anyone, despite his outward puritanism, albeit his idea of wedlocking Olivia is motivated more by social aspiration than by love. Malvolio's self-delusion is caused by his desire to surpass his class, but it also helps to explain why Sir Toby and the others find his fantasy so absurd. Malvolio is not a good match for Olivia due to both his undesirable demeanour and the fact that he lacks aristocratic blood. He is an ordinary person, whereas Olivia is a lady. They find it offensive that Malvolio would envisage Olivia and him getting married. We may remember how intrigued Olivia is when she learns from young Cesario, on whom she has a crush, that he is a "gentleman"—meaning that he is of noble birth—in an earlier scene. A noblewoman marrying a lower-class man would have been quite unusual in the class system of Shakespeare's day

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Reply to the reviewers

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

All the conclusions are based on solid evidence and convincing, and the methodology are in detail to follow or repeat. The writing of the manuscript is logical and easy to follow.

We thank the reviewer for these comments

1. The mutation experiments indicated that nkd enhanced the phenotype of scr, but there is no leaf phenotype variation in nkd muations, this is some way difficult to understand, it would much better if the authors can give much more explanation in the discussion.

We have added more discussion on this point. One possibility is that collectively the four genes function redundantly, however, due to the transcriptional negative feedback loop discovered here (Figure 3B), when NKD genes are mutated then SCR expression is enhanced, hence phenotypic perturbations are less likely to be observed than when SCR genes are mutated.

2.The word green millet in the first paragraph should be changed to green foxtail. Millet means domesticated small cereal grains, such as foxtail millet, finger millet, proso millet etc.

We thank the reviewer for this feedback and have made the suggested change.

Reviewer #1 (Significance (Required)):

The manuscript, which titled Mutations in NAKED-ENDOSPERM IDD genes reveal functional interactions with SCARECROW and a maternal influence on leaf patterning in C4 grasses by Hughes et al., first reported that SCR works regulating both leaf inner pattern and epidermal stomatal patterning in the C4 model plant green foxtail. The functional difference of this gene in Setaria from that in maize and rice indicated that the inner leaf cell patterning regulation of SCR is not a characteristic of C4 Species; this gave us insight understanding of the complex of C4 leaf cell patterning. In addition to this important discover, the authors found that mutations in NKD IDD genes enhance loss of function scr phenotypes in the leaves of C4 maize and Setaria but not in the C3 rice, indicating NKD IDD was involved in the leaf cell patterning in C4 species, but no in C3. They also identified a maternal effect on cell-type patterning in maize leaves that are initiated during embryogenesis.

We thank the reviewer for their kind comments and suggestions.

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

The leaf anatomy that distinguishes C4 from C3 plants has been known for decades, with veins in C4 plants separated by 1 to 3 (generally 2) mesophyll cells whereas those in C3 plants are considerably farther apart. This anatomical pattern appears to be critical for the function of the C4 pathway, which under some environmental conditions is a more efficient way to fix carbon than the C3 pathway. Despite the obvious importance of close vein spacing, the genetic mechanisms that control it have been surprisingly difficult to untangle. The statement on the bottom on p. 2 ("To date, very few regulators of cell-patterning in inner leaf tissues have been identified...") is an understatement. The paper by Hughes et al. offers a major step in uncovering the basis of C4 vein spacing.

We thank the reviewer for this feedback and agree that this work represents a major step forward in understanding C4 vein spacing.

The authors build on their previous work in Scarecrow-like proteins in maize and rice. In maize, SCR controls patterning of the mesophyll, whereas in rice it controls development of stomata. This paper pursues the possibility that the differences in SCR roles may have to do with interacting proteins. Based on work in Arabidopsis the authors focus on proteins with an indeterminate domain (IDD) and specifically on the NAKED ENDOSPERM genes.

The paper presents an analysis of an impressive set of mutants in three species. A major step in this paper is the comparison among three species of grasses - maize, rice, and Setaria - rather than the more common two species, usually maize and rice. Maize and rice differ in photosynthetic pathway but they also differ in many other traits that reflect the ca. 50 million years since their last common ancestor. Setaria is, like maize, C4 and the two species are more closely related to each other than either is to rice, although they represent two independent acquisitions of C4. This paper shows that SCR orthologs control stomatal patterning in both rice and Setaria implying that the stomatal function of SCR may be ancestral in the grasses and also is not directly connected to photosynthetic pathway.

The availability of allelic combinations of SCR and NKD in maize in particular permits the inference of possible maternal effect on the vein spacing phenotype, although exactly how this happens remains unclear.

The discussion provides a careful and logical assessment of the state of knowledge on SCR and IDD proteins in general, and the new data on SCR and NKD in particular. Many questions remain unresolved, and many additional experiments could be suggested. However, the power of the genetics and the phenotypic analysis together provide a novel direction for research on vein spacing. I will refrain in this review from suggesting what additional information would be nice to have since I think a review should assess the quality of the paper as it stands, not as it could be with months more of work.

My only really substantive suggestion is that the micrographs of the Setaria leaves need to be improved. Specifically, in Figure 6E it is hard to see the details of the fused veins. Either the section is too thick or the camera was not focused properly. Because this image in particular is central to the entire paper I would recommend aiming for the clarity of the images of Zea cross sections, which are fine.

We thank the reviewer for this suggestion. Obtaining leaf cross section micrographs from the Setaria scr1;scr2;nkd mutants was extremely challenging as the growth phenotype is so severe (Figure 5), meaning that the available leaves are small and extremely fragile. Multiple attempts to fix and section leaves using a microtome failed, with leaves consistently collapsing. In our hands, Setaria is not as amenable to fresh vibratome sectioning as maize, and combined with the additional challenges of handling the tiny triple mutant leaves mean that the resultant images are not of the same quality as the maize figures. We have included a supplemental figure (Figure S8) with additional examples of fused veins identified in our screening.

Very minor point: p. 3 - "double Zmscr1;Zmscr1h mutants" - what does the "h" in Zmscr1h refer to?

In this context h refers to this gene being a homeologous gene duplicate, as first explained in Hughes et al. (2019). We have included an explanation in the revision.

Reviewer #2 (Significance (Required)):

Strengths of the paper are 1) the inclusion of three species to help determine which aspects of the gene function may be ascribed to C4; 2) thoughtful and comprehensive genetic analysis; 3) careful sections of leaves; 4) outlines of the limitations of the approach. Limitations (several of which the authors acknowledge in the Discussion) include a general lack of molecular genetic data (protein interactions, DNA binding sites, RNA-seq, etc.). While this information would be great to have, I think the strength of the genetics is such that the paper will be foundational for future work in any case. The one bit of additional data that would be ideal would be information bearing on the two mechanistic hypotheses laid out on p. 10. The model that SCR and NKD promote cell division and specify mesophyll identity is the opposite of the model that SCR and NKD inhibit vein formation. An experiment that helped point the reader toward one or the other of these models would be very valuable.

We agree that an experiment that could distinguish these possibilities would be extremely valuable, and will undoubtedly be the subject of future experimentation.

The paper fills a critical gap. Little to nothing is known about how the internal anatomy of leaves is patterned and the data presented provide evidence that SCR and NKD are two important players. The paper also provides a conceptual advance in offering a couple of genes and some plausible mechanisms of how they might function.

The audience will be primarily developmental geneticists and physiologists. The paper addresses an important problem that is of broad interest to developmental biologists and is potentially important for global agriculture.

We thank the reviewer for their kind comments and suggestions.

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

The manuscript of Hughes et al. aimed to demonstrate the functional interactions between Naked-Endosperm IDD genes and the transcription factor SCARECROW and a maternal effect on leaf patterning in C4 grasses. To this end, the authors conducted a greenhouse and labor experiment to create mutants of related genes and assess the expression of these genes through qRT-PCR combined with fluorescence microscopic images in Rice, Maize, and Setaria. They found an increase in the proportion of fused veins with no intervening mesophyll cells in scr;nkd mutants in C4 species (Maize and Setaria) but not in C3 species (rice). In the end, they revealed a maternal effect of derived NKD on patterning cells in leaf primordia during embryogenesis.

Major comments - Optional: the authors should have conducted a whole transcriptome experiment through RNA-seq on the mutants as compared to the controls to check if these genes were significantly up-related followed by qRT-PCR for validation. By doing so, the authors should be able to get a broad overview of all key plays involved in leaf patterning.

We agree with the reviewer that it would be useful to have this data, and such an approach will undoubtedly inform future research.

• Optional: although the authors may evoke the statistical significance of observing fused veins in mutants sr;nkd, the presence of fused veins in one mutant Svscr1;Svscr2 and Zmscr1-m2;Zmscr1h-m1 may contradict the claim that the authors made regarding the association between scr and nkd. Moreover, the sampling size is not also large enough to draw a substantial conclusion.

We disagree with the reviewer that our sampling size is not large enough to draw a substantial conclusion. In maize we surveyed 11 quadruple mutants and 588 veins. Although this phenotype is occasionally seen in Zmscr1;Zmscr1h mutants, it is far more penetrant in Zmscr1;Zmscr1h;Zmnkd1;Zmnkd2 quadruple mutants and easily distinguished by eye when viewing each mutant, the statistical analysis only serves to make this point. In Setaria we agree that the differences are less stark, and the sampling size is necessarily lower due to the challenges of working with the triple mutant leaves which are extremely small and fragile (far more so than the maize quadruple mutant leaves). We have already included discussion as to why the phenotype may be less penetrant in setaria. Together we think that the fact the direction of the phenotype matches that of maize is convincing evidence that the increase in fused veins is a real consequence of combining the scr and nkd mutations.

• There are two copies of nkd in maize but only one copy in rice and Setaria. Does the presence of two copies in maize has any evolutionary or functional meaning? Does the presence and absence of one or two copies has any effect on leaf patterning? It would be interesting to discuss this in the discussion section.

We thank the reviewer for this comment and have added discussion of this in the manuscript. This situation is common in maize, which underwent a more recent whole genome duplication since its divergence from rice and setaria. Most of these gene-pairs function redundantly, however, there is evidence of functional divergence in terms of expression in some gene-pairs. We have added a sentence in the results explaining why we think the presence of two NKD gene copies in maize is unlikely to have functional significance in this case.

• The methods section is not easy to read for a non-specialized audience. I suggest providing an explanation of the abbreviations used to describe mutants.

We thank the reviewer for this suggestion and have made the suggested change.

• For the results section, you should provide a table summarizing the differences between mutants and controls regarding the leaf structure.

We have added such a table at the end of the results section and referred to it in the discussion.

Minor comments: - "Zmscr1-m2;Zmscr1h-m1 seed were" seeds instead

We have made the suggested change.

• "Loss of NKD gene function enhances SCR mutant phenotypes in maize and setaria" This section is confusing because several perturbations were observed in triple mutants of Setaria and quadruple mutants of Maize as compared to their double mutants (Svscr1;Svscr2 and Zmscr1;Zmscr1h). You should rewrite this subtitle for clarity.

We have changed this sub title to read “In maize and setaria, but not in rice, nkd loss of function mutations enhance scr mutant phenotypes”

• "The accumulation of transcripts in the ground meristem cells" How do you estimate the accumulation of transcripts? What do you mean by the accumulation of transcripts? What do you consider transcripts?

We use this term as opposed to ‘gene expression in the ground meristem cells’ because we do not know whether the presence/absence/level of detectable RNA is regulated by transcriptional or post-transcriptional mechanisms.

Reviewer #3 (Significance (Required)):

The manuscript of Hughes et al. is very interesting in the context of C4 photosynthesis research because there are many transcription factor candidates involved in the development of C4 leaf anatomy but few of them have been validated. However, a whole comparative transcriptome of mutants and controls should provide a broad overview and probably new insight into key players involved in leaf patterning.

We agree with the reviewer that this would be of great interest, but we feel it is beyond the scope of this study and will be a productive avenue of future research.

This study goes far beyond the simple validation by outlining the potential interactions between transcription factors. The authors made a substantial effort by combining gene expression results with visual data that strengthen the quality of this manuscript. Therefore, this manuscript is very interesting for the C4 research communities and for the field of developmental biology.

We thank the reviewer for their kind comments and suggestions.

A plant biologist working on the evolution and regulation of morphological characters using transcriptomics and genomics.

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Reply to the reviewers

Reviewer #1

Major comments: The main conclusions of this work are that promoters of the different classes of genes display differing usage of GTFs and cofactors to promote transcription and likely recruit polymerase by different mechanisms. The in vivo experiments using factor depletion offer strong evidence that certain factors including TBP/TRF2 are differentially required for transcription at the housekeeping/developmental gene classes. The in-depth analysis of different promoter types combined with the genetic approaches outlined above provide compelling mechanistic insights into promoter-specific engagement of regulatory factors. In general, the data supports the authors' suggestions.

One important shortcoming of these experiments is in the in-vitro DNA binding analysis of GTFs at differing core promoter contexts. The lack of GTFs binding to the housekeeping promoters may be a reflection of low intrinsic transcription activity. If the housekeeping promoters don't assemble active transcription complexes in this in vitro system but the developmentally-regulated promoters do, then a simple comparison of proteins bound to each promoter type is potentially misleading as to the factors required for transcription. For example, results of the in-vivo analysis suggest that the +1 nucleosome is an important factor in the positioning of the transcription start site at housekeeping promoters, therefore the use of chromatinized templates rather than naked DNA would likely better reflect the intrinsic binding properties of factors at promoters.

We thank the reviewer for highlighting that the in vivo experiments constitute strong evidence for the differential requirements of certain factors at different promoter types and that our work provides compelling mechanistic insights into promoter-specific engagement of regulatory factors. We are also grateful to the reviewer for pointing out that we had not sufficiently clearly explained the aim and rationale of the initial in vitro DNA binding analyses (Figures 1 & 2). These which were not meant to assess different factor requirements but to assess if short core-promoter DNA is sufficient recruit transcription-related proteins, as had been reported for TATA promoters, and whether different core-promoter types differ in this ability. We therefore based the in vitro DNA binding assays on the fact that 121bp-short TATA core-promoter DNA is able to recruit and assemble the PIC even in the absence of activators, i.e. when the core promoters are transcriptionally inactive, and assayed all other core-promoter types under identical conditions. Interestingly, while the TATA core promoters enrich for canonical PIC components as expected, housekeeping promoter DNA does not, suggesting that the core-promoter DNA fragments’ abilities to recruit and assemble the PIC differs.

We agree with the reviewer that one could possibly find conditions in which the different promoter types are active in vitro, e.g. by providing activators or chromatinized templates, and we hope that our explanations above clarify why this has not been the goal of these analyses. As the reviewer pointed out, we assay functional requirements of various TFs and GTFs in vivo in the remainder of the manuscript. We revised the manuscript to improve clarify the aim and scope of these sections (pages 4-9) and are grateful to the author for allowing a discussion of this topic as alternative (see below), many thanks

One way to address this issue is to test transcription activity of the promoters used in the mass spec analysis. After incubation of promoters with extract, add NTPs and quantitate the basal transcription activity of each type of promoter. If they are the ~same - great. If not, at a minimum, the authors need to acknowledge this as a limitation of the study. The suggested transcription experiment is a simple extension of the work already completed.

As outlined above, we deliberately assay all core promoter types under identical conditions, such that differences in protein binding reflect the different DNA fragments distinct functional properties. Please also note that while all core-promoter fragments are transcriptionally inactive, they can be activated by input from a strong enhancer (please see Supplementary Figure 2C; housekeeping and developmental core promoters can be induced to comparable levels, and thus weaker binding of GTFs to housekeeping promoters is not a reflection of weaker inducibility or activity).

We note that all statements and claims are strictly in line of what we tested, namely the core promoter DNA’s ability to recruit transcription-related proteins in vitro. However, we agree with the reviewer that the notion that the core promoters are assayed under identical conditions but are not active is important and discuss it in the main text (pages 8 – 9) and the ‘limitations of this study’ section.

The authors suggest from the depletion experiments of TBP/TRF2 that the factors are functionally redundant since the level of transcription for target genes recovers after prolonged depletion, though there is not specific functional evidence to support this claim. A suggested experiment to test the functional redundancy of TBP/TRF2 at subsets of genes is to assess the levels of proteins and/or protein binding to promoters after factor depletion. For instance, is there a global upregulation/stabilization of TBP after TRF2 depletion? Or is there an increase in TBP binding at promoters? These can be addressed by western blot for overall protein levels and ChIP-seq or similar method to assess binding to promoters, which are fairly straightforward experiments given that the cells lines have already been produced.

We thank the reviewer for suggesting potential compensatory mechanism regarding the redundancy of TBP and TRF2 at a subset of tested promoters. To address the question regarding the stability of TBP or TRF2 in the absence of one or the other, we have performed label-free quantitative mass spectrometry on the TRF2-AID cell line and examined TBP levels (Supplementary Figure 4E). We do not see a stabilization of TBP upon the depletion of TRF2 with auxin. The apparent functional redundancy (e.g. Fig. 4J) thus indeed suggests that there might be increased TBP binding. Unfortunately, we are not able to directly test this experimentally due to a lack of resources. We now add a discussion of the potential compensatory mechanisms to the main text (page 14), many thanks.

A discussion would be appreciated on the generality of the suggested mechanism in metazoans. For example, is DREF conserved only in insects but could other eukaryotes use a similar mechanism at housekeeping genes?

We agree that some of the specific TFs don’t have one-to-one orthologs outside insects, yet that other prominent features of Drosophila housekeeping promoters are shared more widely. We now discuss the parallel between dispersed patterns of initiation at different promoter types across species, including Drosophila housekeeping and vertebrate CpG island promoters. We also provide an outlook towards future functional, biochemical and structural studies that might reveal more diverse transcription initiation mechanisms at the different promoter types in our genomes (pages 23-24).

Minor comments: The manuscript is very difficult to read. One major problem is the large number of figures - many of which are not essential for understanding the results. I strongly suggest that the authors think carefully about which figures to include in the manuscript and keep only the most important.

We agree that the manuscript is complex with six main figures and several different approaches, including biochemistry and mass spectrometry but also genomics and bioinformatics. In addition, the manuscript includes in vitro tests of DNA-protein binding and in vivo assays to probe functional requirement (by depletion) and sufficiency (by recruitment). These different assays assess different properties and complement and validate each other, which is why we feel they are required. We hope that the clarification of the different aspects and their purpose makes the manuscript more easily accessible, many thanks.

Second, the legends on many of the graphs are very tiny and difficult to read.

We have revised the figures to improve font size and readability of the figures, many thanks.

Third, it would greatly help readability if the main figures and legends were imbedded in the manuscript and if the supplemental figures + legends were in a separate document. We have now included the main figures and legends into the manuscript, thanks.

Fig 4E: very difficult to understand what was done.

We now add further explanations to the figure legend to describe the different promoter groups compared in the analysis of ChIP-seq coverage of TBP and TRF2. Fig 4A vs G: why are ~ the same number of genes affected by TRF2 vs TBP + TRF2 depletion? I got the impression from the text that there should be a large difference in the number of affected genes.

We had the same prior expectation, but indeed observed a similar number of downregulated genes upon TRF2 depletion versus TBP and TRF2 double depletion. This may partly be technical, e.g. relating to clonal selection of the different AID-cell lines or thresholding effects, but is likely explained by the relatively few TBP dependent genes (200) that don’t contribute substantially to the larger group of TRF2 dependent genes (3826). The observed number 3935 is 98% of the sum, even ignoring potential overlap. We now clarified this in the text. Fig 5A and similar figures: include the number of affected genes in the figure.

We added the number to the figure, thanks. Fig S2C: hard to understand what was done from the legend.

We have added additional explanations to the figure legend, thanks. Fig S2F and similar figures: hard to distinguish the legend and the green colors used. Proofreading: Add citation for Cut&run in the methods.

We did not analyze CUT&RUN data, however ATAC-seq and ChIP-seq data sets are cited.

In supplemental Fig1a, the percentage of "INR only" is greater than 100%.

We thank the reviewer and fixed the typo.

Supplemental Fig 1a legend-should 170,000 protein coding genes read "17,000"? Santana et al. reference on pg 8 should read 2022.

We thank the reviewer and fixed the typos Readability: The categorizations of genes classes based on core promoter elements is somewhat unclear-from 1a, is it the case that all TATA contain INRs? A different way of representing the data to capture overlaps in motifs other than a pie chart may better convey these motif relationships. Work could be done to increase clarity in general on the promoter motif subtypes used and how mutually exclusive these elements are in the tested subsets.

We thank the reviewer for the suggestion. We have added a heatmap in Supplementary Figure 1A showing the percent match score to motif PWMs across Drosophila promoters. As the reviewer suspects, most developmental core promoters have a high-scoring INR motif and some have an additional TATA box or DPE motif. We have also revised the remainder of the text and rewritten the methods section regarding the motif analysis (pages 36 to 38) to improve clarity. Many thanks. Figure 5: authors state "all protein coding genes" are downregulated with TFIIA depletion, though it appears some transcripts are unchanged or upregulated in 5B/C. Suggest change in language.

We thank the reviewer for this comment. Less than 70 genes are not downregulated upon TFIIA depletion, and manual inspection shows that these genes include intronic non-coding RNAs such as tRNAs that hinder accurate PRO-seq quantification. However, we agree with the reviewer and revised the text to reflect that essentially all promoters are downregulated, affecting all promoter types. A discussion on the developmental context of the S2 cell line seems appropriate. If S2 cells represent a late stage developmental cell line, would the authors expect the relative utilization of cofactors to be the same/different in other cellular contexts?

We thank the reviewer for this comment. We indeed expect the relative utilization of cofactors to be the same I most cellular contexts and now added a discussion with relevant references (page 23), many thanks.

Reviewer #2

1. The DNA affinity purification method is excellent as a discovery method, but it has some potential caveats. One is that it cannot capture remodeling events that could potentially remove otherwise stably bound factors to allow for transient PIC assembly and gene activation. It is possible that some of the insulator factors such as BEAF-32 and Ibf1/2, which selectively bind housekeeping sequences, could prevent or reduce binding by PIC factors. This could occur if BEAF-32 and/or Ibf1/2 inhibit PIC assembly if bound to DNA and if these factors bind housekeeping promoters with high affinity and slow off-rates. That is, in live cells, a competition could exist between binding of these enriched housekeeping factors and PIC assembly. By contrast, this caveat is not relevant at developmental promoters due at least in part to low/sub-nM TBP binding affinity. Ultimately, this is a minor concern but the authors should address in the article to inform readers about potential limitations of the experiments.

We thank the reviewer for highlighting that DNA affinity purification is an excellent discovery method and for pointing out important differences between such in vitro assays and the in vivo situation. We agree and interpret our results from the DNA affinity purification carefully and specifically regarding differences observed for different types of core promoters under identical experimental conditions. We now highlight these differences more clearly throughout the relevant sections on pages 4-8 and expand the discussion of this issue in the ‘limitations of the study’ section. Many thanks.

1. More information about how the PRO-seq spike-ins were implemented is recommended. For example, were they fit to a linear regression of read counts/chromosome between all samples, or did they take all hg19 reads as raw fold-change of all samples compared to a control replicate?

We thank the reviewer for addressing the insufficient information provided about the spike-ins used for PRO-seq. We have added this information to the materials and methods section: We calculated the ratio of spiked-in reads representing the percentage of reads mapping to the human genome over all reads. This ratio was used to determine a scaling factor representing the fold-change of total transcriptional output between the auxin-treated sample and the control samples.

1. Figure S1C should be cited (not S1B) to support the statement "Mutating either the TATA box or DRE motifs reduced TBP or DREF binding to control levels..."

We thank the reviewer for this correction and implemented the correct panel citation.

The authors could note that TATA box mutants still show slight enrichment for TBP compared to negative controls.

We now note this in the figure legend and explain that it is consistent with TBP binding to non-TATA-box developmental core promoters (Figure 2 B & E).

In Figure 2A, it would help to remind readers here that TATA, DPE, INR = developmental and TCT, Ohler1/6, DRE = housekeeping.

We thank the reviewer for this suggestion and implement it

Figure S2A shows only 121bp and 350bp DRE core promoters but the text refers to 450bp and 1000bp sequences as well. Can the authors show representative results from these longer sequences?

We thank the reviewer for pointing out these inconsistencies, which we now fixed by revisions to the text and supplementary figures.

1. In comparing data in Fig 2B and 2E, it seems the statement "the ChIP signals reflected the differential binding preferences observed in vitro for the respective promoter subtypes" should be modified. It is true to an extent but it is more nuanced than indicated by the text.

We have reworded the section and now discuss the observed trends for GTFs and TFs.

In Fig S2I, Ohler1 + Ohler6 and TCT are difficult to distinguish because of color scheme choice.

We agree and now explain in the figure legend that the brighter green corresponds to the Ohler1/6 promoters and the darker green to the TCT promoters, we have additionally edited the legend for better color visibility, many thanks.

In Fig 3F, perhaps add that Gld has TATA and Fit2 has DRE?

We now indicate the presence of TATA-box and DRE motifs in the figure, thanks.

Fig 5D: legend is cut off in the Figure. We thank the reviewer for this comment and now fixed the cropped legend. 11. Fig S2B needs more description and clarification in the main text and the legend. We now deleted Fig.S2B. 12. Page 8, 2nd paragraph "avoiding potential" should be replaced with "minimizing" or similar. We thank the reviewer for this comment and have changed the word choice. 13. Page 16, penultimate paragraph: "Essentially" should be replaced with "Essentiality"

We thank the reviewer for this comment and correct the wording.

Reviewer #3

1. The authors perform a k-means clustering of PWM match scores within 17,000 promoter sequences. They describe in the Methods section that this data revealed 9 groups of promoters. However, although it is likely that several of these promoters contain matches for multiple core promoter motifs, the promoter classes are simply named DRE-promoters, TATA-promoters, TCT-promoters, etc., disregarding any combinatorial association. Furthermore, the clustering data is not visualized to support this naming. The authors should at least provide a heatmap showing the PWM match scores for these clusters and indicate which promoters were used. This is crucial for interpretation of results. We thank the reviewer for pointing out the description of the motif analysis lacked clarity and that the clustering of Drosophila promoters should be visualized. We agree and now provide the k-means clustering heatmap of all 17118 protein coding gene promoters, visualizing the position-weight-matrix (PWM) scores matches for the different promoter motifs in Supplementary Figure 1A. This visualization confirms the reviewer’s suspicion that core-promoter motifs often co-occur in the same core-promoter. For example, TATA promoters typically contain TATA-boxes and INR motifs, etc, which is now clearly seen in the newly provided heatmap. We have also revised the main text, figure legends and have rewritten the method section (pages 36-38) to clarify the analysis of motifs throughout the manuscript. Many thanks.

2. Relatedly, this paper uses a seemingly over-simplified terminology to describe promoters as housekeeping or developmental. While this terminology has been used in several studies from the Stark lab, this is not well supported by data and the usage of this terminology will likely lead to confusion among readers. Here, housekeeping seems to refer solely to the presence of a motif match in the promoter sequence rather than to ubiquitous expression across cell types. Similarly, developmental promoters seem to refer to anything that is not housekeeping. Are S2 cells best reflecting the activity of developmental genes? What about genes that are not expressed as part of a specific developmental trajectory, but still cell-type restricted? Since focus here is on the behavior of promoters with respect to their core promoter elements, why not just refer to them according to their promoter elements? A good example where the developmental versus housekeeping distinction is not useful is the authors' desire to generalize differences observed in Figure 2B, in which it is quite obvious that there is no clear developmental versus housekeeping split. Rather the data demonstrate that TATA-containing and DRE-containing promoters behave differently.

We thank the reviewer for raising a concern about the terminology of functionally distinct promoter types in Drosophila. The use of functionally distinct promoter types enriched in different motifs is built on extensive evidence by our lab and others (e.g. the Ohler or Kadonaga groups) that found extensive agreement between promoter sequence, promoter function, initiation pattern, gene annotation, and ubiquitous vs. cell-type-restricted activities. Ubiquitously active housekeeping promoters tend to contain the TCT, DRE and Ohler 1/6 motifs, while cell-type-restricted developmental promoters tend to contain TATA-box, DPE and INR motifs (Arnold & Zabidi, Nat Biotech 2017, Haberle et al. Nature 2019, Ngoc et al. Genetics 2019, Ohler et al. Genome Biol 2002, Ohtsuki et al. Genes & Dev 1998, Rach et al. Plos Genetics 2011).

We find that the terminology is simple and thus accessible for the non-specialist reader. We agree with the reviewer that clarity is key and revise the introduction of the terminology to clarify that it is based on multiple lines of evidence. We also clarify that Figure 2B – in contrast to the reviewer’s claim – does support a clear developmental versus housekeeping split (please see the dendrogram on top of the heatmap). We now clarified this in the main text and legend to Figure 2B, many thanks.

1. The authors state that the "prevalent model" in the community is that PIC assembly is the same at all promoters. This is not true. For instance, it is well established that certain core promoter elements have a strong positional effect on TSS selection, while dispersed promoters lack strong positional features. What is less known is how the dispersed pattern, e.g. of non-TATA promoters, arises. The authors should more clearly specify the unknowns and the novel findings of their paper.

We agree with the reviewer that certain core promoter elements have strong positioning effects on TSS selection and that these occur in promoters with focused initiation patterns such as TATA promoters and developmental non-TATA promoters (e.g. promoters with INR and/or DPE motifs). We also agree that it is unclear how dispersed patterns at housekeeping promoters arise, especially because the initiation sites don’t co-occur with the TF motifs present in these promoters (e.g. DRE or M1BP motifs; see Figure 6A).

However, the question we address goes beyond TSS selection: we have not seen any study of PIC recruitment and assembly at any promoter with dispersed initiation pattern and the idea of a single uniform Pol II PIC assembly has been the predominant view of transcription initiation during the past two decades (Schier & Taatjes, Genes & Dev 2020). Here, we provide evidence that protein recruitment and GTF usage differs between promoter types, which has mechanistic implications beyond TSS choice alone. In particular, we show that at least two modes of transcription initiation exist that differ between focused developmental and dispersed housekeeping promoters, whereby the developmental promoter DNA directly engages the Pol II PIC via TBP and TFIID, while the housekeeping promoter DNA does not and instead, housekeeping promoters recruit TFs, which recruit COFs and TFIIA. This is exciting and inconsistent with uniform GTF recruitment and assembly, and we hope that this work motivates the study of these different PIC assembly mechanisms at different promoter types.

One of the major claims made by the authors in the paper is that PIC is recruited directly or indirectly depending on the presence of TATA or DRE. However, their approach seems to pick up a lot of indirect bindings, especially for TATA. This raises concerns of potential biases, which if addressed would strengthen the author's claims. The results do not exclude that TFIIA is directly recruited to TATA but might simply reflect stronger binding to other factors compared to DRE. It is also puzzling that DRE is the only one selected for further validation as it appears to have the lowest affinity for PIC binding and the focus on Ohler1/6 motifs in the final model. Disclaimer, this reviewer is not an expert on DNA-affinity purification assays.

We thank the reviewer for pointing out that we had not sufficiently clearly explained the DNA affinity purifications. They were performed under identical conditions for all promoter types, such that the differential binding to TATA vs DRE promoters reflects the respective promoter DNA’s affinity to various transcription-related proteins – they are key results of our work. Please note that, despite the high number of TATA interactions, many of these interactors are expected and reflect the binding of multi-subunit protein complexes such as the Mediator and TFIID (please see Figure 2B) and reflect the fact that we did not purify the PIC nor reconstitute it from purified components but determine nuclear proteins that bind to TATA-box promoter DNA. We now introduce and discuss these aspects more clearly.

It is possible that the fewer interactors found for housekeeping promoters stem from lower affinity of the PIC, the lack of chromatin, or the stable binding of sequence-specific binders such as DREF, BEAF-32 and M1BP in our assay (please see our response to reviewer 2 above). As these result from identical experiments under identical conditions, the fewer interactors for housekeeping promoters are also an important result that likely reflects lower affinity or more transient binding. We now clarify these results and their interpretation in the main text and discuss differences between this assay and transcription in vivo in the “limitations of the study” paragraph.

As the reviewer might appreciate, the follow up experiments, including the creation of AID cell lines, PRO-seq, etc., are a lot of work such that we did them for promoters at the two extreme ends of the spectrum and their respective DNA-binding factors TBP and DREF identified in Figure 1. We think that these representatives sufficiently strongly demonstrate that PIC assembly and factor requirement is distinct for different promoter types, many thanks.

Their final model is supported by results by Baumann et al (2018), which directly shows binding and interactions between M1BP, putzig, gfzf and TRF2. However, these factors bind to Ohler1, while most of the work within this study (Figures 1, 3) focused on DRE. How do DRE-containing promoters fit with the final model? Currently, these promoters are not even represented in the model figure.

We thank the reviewer for pointing out that the final model highlights the Ohler 1 motif but omits the DRE motif. Based on the functional analyses shown in Figure 6 (pages 19-21), we think that the different motifs function equivalently in recruiting housekeeping cofactors and activating housekeeping transcription and have now included DRE motifs in the final cartoon. Our original choice was indeed based on the fact that previous reports from Baumann et al 2018 corroborate our findings for M1BP. As DRE promoters also recruit and depend on TRF2 (Hochheimer et al. Nature 2002), we now show a model by which housekeeping DRE promoters recruit a TRF2 containing PIC through TFIIA, but would like to stress that both likely function equivalently, leading to dispersed initiation. We also revised the data presentation and the final discussion regarding these promoters, many thanks.

Minor comments

1. The TSS patterns of promoters were evaluated using STAP-seq (in vitro data) and developmental CAGE data. For the purpose of the paper and to match the in DNA-affinity purification data better, it would be more reasonable to make use of S2 cell CAGE data (e.g. Rennie et al, 2018 PMID: 29659982).

We thank the reviewer for bringing up this point. For figure 6 we have used CAGE data from Drosophila embryos instead of S2 cells in order to capture a larger proportion of expressed developmental genes and their promoters, rather than just the ones that are expressed in S2 cells. As promoter motifs are found in stereotypical positions in relation to the TSS (Ohler et al. Genome Biol 2002) and because non-S2-cell core promoters can be activated in STAP-seq (Arnold 2017; Haberle 2019), our use of CAGE data from Drosophila embryos allows us to base all subsequent analyses on many more core promoters and also exclude any cell-type specific effects that may arise in TSS selection.

Previous models on TSS selection within non-TATA promoters have highlighted the dinucleotide frequency of +1 nucleosomal DNA as a strong positional feature. Here, the authors investigate this model using a rather weak analytical approach. We know that nucleosomes can vary between cells (fuzzy positioning). Variability across promoters may cause larger variability in relative TSS positioning. Hence, what is observed here as a TSS spread relative to the +1 nucleosome positioning might in fact be caused by averaging. A more suitable approach would be to analyze the positional cross-correlation between TSS locations (e.g. revealed by CAGE reads) and nucleosomal positions (e.g. revealed by MNase-seq reads). This would better support claims regarding specific TSS positioning with respect to nucleosome positioning.

We agree that the analysis of cross correlation between TSS locations and nucleosomal positions at individual promoters would provide a more precise measure of TSS positioning relative to the nucleosome. We had originally chosen a visualization that more directly assesses whether the +1 nucleosome determines the TSSs by centering on the predicted +1 positions. In response to this comment, we have performed two additional analyses: a cross-correlation analysis on CAGE and Mnase-seq read coverage in relation to the dominant CAGE TSS (new Supplementary Figure 6I) and a TSS-centric analysis of Mnase-seq coverage (new Supplementary Figure 7. Both analyses agree with the original analysis and we thank the reviewer for pointing out how to strengthen this analysis.

The cross-correlation analysis reveals a peak in the mean correlation score 125 base pairs downstream of housekeeping TSS (at TCT, Ohler1 and DRE) promoters but not downstream of developmental promoters (TATA-box, DPE and INR), in line with housekeeping TSS being positioned upstream of the +1 nucleosome.

The analysis assessing +1 nucleosome positions as derived from MNase-seq coverage relative to the position of the dominant TSS reveals the expected phasing of downstream nucleosomes in housekeeping promoters but not at developmental promoters. Many thanks.

It is interesting that tethering of housekeeping-associated coactivators leads to a higher positional dispersion compared to the result of developmental-associated coactivators. However, the positional TSS dispersion of housekeeping promoters seems to always be larger than that of developmental promoters regardless of coactivator recruitment. Can the authors explain these results?

We agree that CAGE data typically show TSS dispersion at housekeeping promoters, yet this reflects the promoters’ transcriptionally active states during which endogenous TFs and coactivators are present. Our analyses are based on short, transcriptionally inactive core promoters that can be activated by cofactor recruitment, leading to the observed outcomes. We now clarify this in the manuscript and highlight that the differences in focused versus dispersed patterns occur even on the very same DNA sequences upon the recruitment of developmental or housekeeping activators (e.g. Fig. 6F).

The authors seem to suggest that positional dispersion of TSSs within housekeeping promoters is due to stochastic initiation after non-positional specific PIC recruitment mediated via certain co-activators. If TSS selection is truly stochastic, why do these promoters then have dominant TSSs?

We thank the reviewer for pointing out that our phrasing might have suggested that TSS selection was entirely random or stochastic, which is neither true for STAP-seq nor for endogenous CAGE data. In fact, not all positions have the same probability to initiate transcription, but certain positions or nucleotides seem to be inherently favored. We speculate that favorable positions relate to the local DNA structure, the energy barrier landscape for both DNA helix melting to occur and for the first phospho-diester bond to form (e.g. Dineen, D. et al. NAR 2009 and Vanaja, A. et al. ACS Publications 2022). We now added this discussion and the corresponding references to our manuscript (page 21).

The authors find Chromator as a likely cofactor for indirect recruitment of TFIIA to housekeeping promoters. BEAF-32 is another factor the authors highlight as being enriched at housekeeping promoters (DRE promoters). Both of these factors have previously been considered insulator proteins or architectural proteins involved in the formation of chromatin folding (Ramirez et al, 2018, PMID: 29335486; Wang et al, 2018. PMID: 29335463). Could the authors comment on this link with their own findings?

We thank the reviewer for addressing the importance of chromatin topology in the light of our findings, which we now discuss in the main text (pages 22-23).

1. Can the authors justify PWM match thresholds used and why these were changed from Haberle et al 2019?

We thank the reviewer for pointing out that these changes had not been justified. We adjusted them to be more stringent (e.g. DPE) or sensitive (e.g. TATA-box) exclusively for the motif enrichment analysis, which we did outside the rule-based promoter-annotation effort. These adjusted thresholds reflect the motifs vastly different information contents, which is low for DPE and high for TATA-box motifs.

Figure related comments/concerns: • General: Sometimes wrong ordering of figure panels with regards to their first mention in the main text, varying font sizes, and minimal figure legends that are often inconsistent (e.g. PRO-seq is sometimes specified when used, but not always) • Typo: Supp Fig 1: INR only 121.37% • Fig 1E not explained, what does x axis describe and how is it calculated? • Figure 2C-D: The CAGE signal is poorly visualized in panel C, it also poorly describes that this is supposedly done using a pool of promoters. Where is the 450bp blot (it seems plausible that the 450bp fragment could actually facilitate a luciferase signal in Fig S2-B)? How was this pool selected, is it exclusively based on DRE-containing promoters? • Fig 2D: apparent gel leakage and loading on the second panel is low. Preferably, provide positive control on the same gel. • Figure 4C: all classes are negatively affected by TRF2 depletion, thus enrichment (4B) makes little sense here • Figure 5C: Missing axis labels • Figure 6F: A y scale would help here

We thank the reviewer for these recommendations and have implemented all of them.

reply to Ryan Randall and Matt Stine at https://hcommons.social/@ryanrandall/109677171177320098

@mstine@mastodon.sdf.org @ryanrandall It won't go as far back as we may like, but I'm hoping Mark Bernstein's upcoming talk will help to remedy some of the lost knowledge: https://lu.ma/2u5f7ky0

In part I blame Vannevar Bush for erasing so much history in As We May Think (1945).

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)):

Summary:

In this study, mice were exposed to a specific form of so-called Intermittent Fasting (IF) and the effects of IF on adult neogenesis in the hippocampus were determined. The specific IF protocol used had no effect on activation, proliferation, or maintenance of adult Neural Stem Cells (aNSCs) and displayed a decrease in number of new neurons in the neurogenic niche but only after 1 month of the IF protocol. These results contrast previously published results from multiple studies that concluded that IF promotes survival of new neurons and by extension promote adult neurogenesis. The unresponsiveness of aNSCs or their immediate cell progeny, the Intermediate Neural Progenitors (IPCs), to IF is a novel finding. The authors make several relevant points in the discussion about the publication bias towards positive results (or omission of negative results), which may reinforce established dogmas. However, the presented results did not convincingly demonstrate that the absence of effects of IF on aNSCs or adult neurogenesis is simply not a result of a specific IF paradigm, which is not robust enough to elicit changes in adult neurogenesis. In other words, there is a lack of positive controls and alternative protocols that would rule out that the observed absence of effects is not a consequence of type II error (the error of omission), or more colloquially, a consequence of false negatives.

We thank the reviewer for acknowledging the importance and novelty of our findings. On them being the result of a specific IF paradigm, we must point out that we used the same IF paradigm as in previous studies that had shown changes in neurogenesis upon IF. We do not claim that IF is unable to increase neurogenesis in all conditions, but report that IF is not a reliable method to increase adult neurogenesis (in particular, every-other-day intermittent fasting with food re-administration in the evening). We have repeated the experiment multiple times in different strains, always with enough animals to make our experiments conclusive and we never observed an increase in adult neurogenesis, effectively ruling out that our results are a false negative. Of note, even if other protocols might indeed increase neurogenesis (which we never claimed cannot) that would not make our results a false negative.

Major Comments:

1. Protocol-driven absence of effects: The absence of IF effects on aNSCs and IPCs observed in this study does not lend it the authority to conclude that aNSCs are resilient to IF or all IF paradigms and protocols. The absence of IF effects on aNSCs and neurogenesis could be specifically related to the chosen IF paradigm. Indeed, not all previous studies that observed IF-driven effects on adult neurogenesis used the same "night-time every-other-day fasting" protocol chosen in this study. For example, Brandhorst et al., 2015 (cited in this paper) used 4 days of IF 2x per month and observed an increase of DCX+BrdU+ cells. On the other hand, certain previous studies used the same or similar IF protocol used here, but often with longer duration or with a post-fasting ad libitum feeding period, which may be responsible for the pro-neurogenic or pro-survival effects. In fact, the authors acknowledge this in the discussion (page 7, lines 289-290 and 292-294). Why would the authors then not include similar feeding/IF paradigm in their study and determine if these would generate effects on survival of new neurons but also on aNSCs and/or IPCs?

As just stated above, we never claimed that aNSCs are resilient to all IF paradigms. We refer to fasting in general in the introduction but quickly focus on every-other-day fasting throughout the paper and directly compare our results only to similar IF paradigms. We chose the most commonly used IF paradigm that had been shown to increase adult neurogenesis. As the reviewer points out, we speculate in the discussion that a refeeding period may explain the differences between our results and others. This is because a post-fasting ad libitum period was introduced in the study published in Dias et al. 2021. We are currently analysing a new experiment in which we replicate the IF protocol in that study, which we will include in our revised version.

In addition, the authors acknowledge that the chosen IF paradigm may have affected the stress levels or behaviour of mice (page 9, lines 372-378). Why did they not test if their IF protocol does not increase stress or anxiety of mice by simple behaviour tests such as open field or elevated T maze?

While testing all possible causes for the lack of positive results in our experiments is not viable, we do agree with the reviewer that stress levels might indeed influence the outcome of the experiments. We will collect blood from ad libitum-fed and fasted mice to analyse the levels of stress hormones (e.g. corticosterone). The results will be included in our revised version. These measurements will give us a more accurate reading of stress levels than behavioural tests. Of note, regardless of the outcome of this experiment, our conclusions will remain identical. We will not be able to compare stress levels with previous publications, as they were not tested. And if the protocol did increase stress levels, it would still argue that IF is not a reliable method to increase neurogenesis (as presumably might or might not increase stress to levels that affect neurogenesis).

Alarmingly, the used IF protocol does not result in changes in final weight or growth curves (S.Fig.2), which is surprising and raises a question the used IF protocol is robust enough or appropriate.

We were also surprised by the lack of change in the final weight our IF mice respect to control. Differences in final weight between different labs despite using the exact same protocol are one of the reasons why we conclude that this IF paradigm is not a robust intervention. However, we are not the first ones to report little or no difference in weight upon IF in C57BL6/J mice (Goodrick et al., 1990 and Anson et al., 2003) and this would not be a reason to dismiss the experiment since the benefits in crucial circulating factors induced by IF seem to be independent of weight loss (Anson et al., 2003).

Finally, the authors acknowledge that their own results do not support well-established findings such as aging-related reduction in number of aNSCs (page 4, lines 177-179). This again questions whether the selected protocols and treatments are appropriate.

As we already discuss, we believe this might be due to a difference between strains in the time when aNSC numbers decline. Nevertheless, we will complement our current data by counting the number of aNSCs at 1 and 3 months post-tamoxifen (3 and 5 month old mice) using GFAP, Sox2 and Nestin triple stainings (as suggested by another reviewer).

Lack of topic-specific positive controls: The authors successfully demonstrated that the used IF protocol differentially impacts the adipose tissue and liver, while also inducing body weight fluctuations synchronized with the fasting periods. However, these peripheral effects outside the CNS do not directly imply that the chosen IF protocol is robust enough to elicit cellular or molecular changes in the hippocampus. The authors need to demonstrate that their IF protocol affects previously well-established CNS parameters associated with fasting such as astrocyte reactivity, inflammation or microglia activation, among other factors. In fact, they acknowledge this systemic problem in the discussion (page 8, lines 359-360).

We fully agree with the reviewer in that even though the chosen IF protocol induces peripheral effects, it is not robust enough to elicit cellular or molecular changes in the hippocampus, and this is precisely the message of our paper. We have looked for references showing the influence of IF on astrocyte reactivity or microglia activation, but the studies we found so far look at the effects of IF and other forms of fasting in the CNS in combination with pathologies such as Alzheimer’s disease, Multiple Sclerosis, physical insults or aging (Anson et al., 2003; Chignarella et al., 2018; Rangan et al., 2022; Dai et al., 2022. Reviewed in Bok et al., 2019 and Gudden et al., 2021). Fasting seems to reduce astrocyte reactivity, inflammation or microglia activation in these pathological situations respect to the same pathology in ad libitum mice, but its effect in control, healthy mice is far less clear. In fact, the only reference that we could find where healthy mice were included in the analysis showed that these benefits only happened in the context of the injury (Song et al., 2022).

Problematic cell analyses: Cell quantification should be performed under stereological principles. However, the presented results did not adhere to stereological quantification. Instead, the authors chose to quantify specific cell phenotypes only in subjectively selected subsets of regions of interest, i.e., the Subgranular Zone (SGZ). This subjective pre-selection may have been responsible for the absence of effects, especially if these are either relatively small or dependent on anatomical sections of SGZ. For example, IF may exert effects on caudal SGZ more than on rostral SGZ. But if the authors quantified only (or predominantly) rostral SGZ, they may have missed these effects by biasing one segment of SGZ versus other. The authors should apply stereological quantification at least to the quantification of new neurons and test if this approach replicated previously observed pro-survival effects of IF. Also, the authors should describe how they pre-selected the ROI for cell quantification in greater details.

We did analyse only the more septal region of the hippocampus, which we will make clear in the text. As also suggested by other reviewers, we will include stereological counts of the neuronal output of aNSCs in the revised version. As for selecting the SGZ for aNSC counts, this is the standard in the field, as one of the criteria to identify aNSCs is precisely the location of their nucleus in the SGZ. Neuroblasts and new neurons were counted both in the SGZ and the granule cell layer. There was no subjective pre-selection of areas of interest since we counted the whole DG in each section and not a specific random region.

Alarming exclusion of data points: There appears to be different number of data points in different graphs that are constructed from same data sets. For example, in the 3-month IF data set in Figure 4, there are 14 data points for the graph of Ki67+ cells (Fig.4B), but 16 (or 17) data points for the graph of DCX+ cells (Fig.4D). How is that possible? If data points were excluded, what objective and statistical criteria were applied to make sure that such exclusion is not subjective and biased? In fact, the authors state that "Samples with poor staining quality were also excluded from quantifications" (page 12, line 528-529). Poor preparation of tissue is not only suboptimal but not a valid objective reason for data point exclusion. This major issue needs to be explained and corrected.

As we disclose in the methods, those stainings that did not work were excluded. This was done always before counting. Different samples were used in different counts because of the variability of staining quality between different antibodies. We will look back into the samples that failed in at least one of the stainings and exclude them from all counts, so that only samples for which all stainings worked are considered. These revised graphs will be provided in our revised version of the manuscript.

Different pulse-and-chase time-points: One of the reasons why this study has found that aNSCs may not be responsive to IF could be the use of less appropriate pulse-and-chase time-points either after EdU or after Tamoxifen for cell lineage tracing. The authors observed that IF has negative effects on new neurons initially (Fig.4F). Similarly, it is well established that voluntary physical exercise affects SGZ adult neurogenesis only during the first 2 weeks. After this period, the neurogenic effects of exercise are diminished beyond observational detection (i.e., van Praag's and Kempermann's papers in the past 25 years). These two arguments suggest that the observed absence of aNSC responsiveness might be a consequence of the chosen EdU administration and the EdU pulse should not be administered 15 days after Tamoxifen/IF protocol start but earlier, in the first week of the IF protocol. In fact, the decreased number of new neurons during the initial IF phase may not be only a consequence of reduced survival but of higher aNSC quiescence during the first week of the IF protocol.

We fully agree with the reviewer that BrdU or EdU pulses can give a biased view of the effects of any intervention on neurogenesis and that the EdU and Tamoxifen protocols would not allow us to detect an increase in neurogenesis during the first few days of IF. We cannot rule out that IF has a transient effect on aNSCs at some point of the treatment, but this hypothetical effect does not seem to have any consequences on neuronal output or aNSC maintenance. As for the effects on neurogenesis in the longer IF treatments, we used the same EdU protocol as in previous publications: administration after 2/3 months of IF and analysis after one month of chase.

Discussion needs more specificity and clarity: The authors claim that the absence of IF effects on neurogenesis is multi-layered (including the influence of age, sex, specific cell labelling protocols etc.) but they do not specifically address why certain studies did find IF-driven neurogenic effects while they did not. In addition, some statements and points in the discussion are not clear. For example, when the authors refer to their own experiments (page 8, lines 331-334), it is not clear, which experiments they have in mind.

We will double check our discussion and improve its clarity and direct comparison to other studies.

Minor comments:

1. Change in the title: The authors have shown that a very specific IF protocol does not affect aNSCs but initially decreases number of new neurons in SGZ. The title should reflect this. For example, it could state "Specific (night-time every-other-day) fasting does not affect aNSCs but initially decreases survival of new neurons in the SGZ".

We find our title, together with the abstract, clearly and faithfully represent our findings and would rather prefer to keep our current title unmodified.

Data depiction: Data in 3 datasets were found not normally distributed (Fig. S5A, B and S6A) and were correctly analysed with non-parametric tests. However, the corresponding graphs wrongly depict the data as mean +/- SD while they should depict median +/- IQR (or similar adequate value) because non-parametric statistical tests do not compare means but medians.

We thank the reviewer for spotting this, we will correct the graphs in Fig. S5A, B and S6A.

Statistical analysis: For ANOVA, the F and p values are not listed anywhere. The presented asterisks in the graphs are only for non-ANOVA or ANOVA post-hoc tests. This does not allow to judge statistical significance well and should be corrected.

Again, thanks for spotting this, we will include them.

Asymmetric vs Symmetric cell divisions: Representative images in Fig.2B suggest that IF may affect the plane of cell division for the Type-1 aNSCs. The plane of cell division is an indirect indicator of symmetric vs asymmetric (exhaustive vs maintaining) modes of cell division. Is it possible, IF influences this, especially during the first week of IF (see major comment 5)?

This is an interesting hypothesis. However, since we do not see any effects on aNSC maintenance, it is unlikely that IF produces any long-lasting effects on the mode of division of aNSCs. In general, we did not notice a difference in the plane of division of aNSCs between control and IF mice, although we did not systematically test for this (would require specific short EdU pulses to capture aNSCs in M-phase). In Figure 2B, the two stem cells shown in the control are unlikely to be the two daughter cells after the division of one aNSC, as one of them is positive and the other negative for Ki67. We only pointed to the second one to show a Ki67-negative aNSC. We will emphasize this in the figure legend.

Improved and more accurate citations: Some references are not properly formatted (e.g., "Dias", page 7, line 288). Some references are included in generalizing statements when they do not contain data to support such statements. For example, Kitamura et al., 2006 did not determine the number of new neurons (only BrdU+ cells) in the SGZ, yet this reference is included among sources supporting that IF "promote survival of newly born neurons" (page 2, line 60). Authors should be more careful how the cite the references.

Thanks for spotting these mistakes, we will correct them and check again all our references. As for the sentence where the Kitamura paper is cited, most of the other references also use only BrdU+ cells while concluding that IF enhances the survival of new neurons. We will change new neurons for new cells to reflect this, which we already bring up in the discussion (see also extended discussion in previous BioRxiv version).

How do the authors explain that they observe 73-80% caloric restriction and yet the final body weight is not different between IF and control animals? Would it suggest that the selected IF protocol or selected diet are not appropriate (see major point 4)?

We also found this surprising and were expecting a change in overall activity in IF mice, which we did not observe. Many factors might play a role, like, as the reviewer suggests, changes in stress levels, which we will measure and show in the revised version.

Given that aNSCs rely more on de novo lipogenesis and fatty acids for their metabolism as shown by Knobloch et al., Nature 2013 and given the interesting changes in RER with the IF shown in this study, it would be interesting to see whether there are differences in Fasn expression in aNSCs between control and IF animals (see minor point 4).

This is an interesting suggestion but given that we see no effect on aNSCs, we find it’s unlikely and unnecessary to test for Fasn expression differences in our IF protocol.

Determining apoptosis in the SGZ by picnotic nuclei (Figure S6A) should be supplemented by determining the number and/or proportion of YFP+ cells positive for the Activated Caspase 3.

We previously found that counting picnotic nuclei is a more accurate and sensitive readout of cell death in the DG, as cells positive for caspase 3 are extremely rare due to the high efficiency of phagocytosis of apoptotic cells by microglia (see Urbán et al., 2016).

Reviewer #1 (Significance (Required)):

General assessment:

This study concludes that aNSCs do not respond to the intermittent fasting. This expands and supplements previous findings that suggest that the intermittent fasting promotes adult neurogenesis by increasing survival and/or proliferation in the Subgranural Zone. The study is well designed, however, over-extends its conclusions beyond a specific fasting paradigm and does not acknowledge serious limitations in the experimental design and analyses. In fact, until major revision is done, which would rule out that the absence of effects of fasting on aNSCs is not due to false negative results, many conclusions from this study cannot be accepted as valid.

Advance:

As mentioned above, the study has a potential to advance our understanding of how fasting affects neurogenesis and fills the knowledge gap of how fasting specifically affects the stem cells. However, unless the study addresses its limitations, its conclusions are not convincing.

Audience:

This study would be particularly interesting for the niche readers from the neurogenesis field. However, the study can also be interesting for researchers in metabolomics and dietology.

My expertise:

adult neurogenesis, neural stem cells, dietology, metabolism

We disagree with the reviewer and find our conclusions well balanced, as we acknowledge our results are to be compared only with similar IF protocols. We also do not believe our results can be attributed to a false negative, as we consistently observe the same with different strains and protocols, always with sufficient animals to make our counts conclusive.

We nevertheless thank the reviewer for assessing our paper and for the advice to improve it. We hope that the reviewer will maintain the same level of scrutiny and scepticism with all IF-related papers.

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

In this manuscript, Gabarro-Solanas et al. question the suitability of IF (Intermittent fasting - non-pharmacological strategy to counteract ageing, which has been previously shown to increase the number of adult-born neurons in the dentate gyrus of mice) as a pro-neurogenic intervention, since IF treatment did not stimulate adult hippocampal neurogenesis, neither at the stem cell level nor on immature and/or dividing neurons. The Authors used a tamoxifen inducible transgenic model (Glast-CreERT2;RYFP mice) to trace neural stem cell lineage and found that IF did not enhance neural stem cell proliferation, nor the abundance of immature, DCX+ neurons. Three-months of IF failed to increase the number of new adult-born neurons (NeuN+/YFP+), while one month of IF significantly reduced the number of new adult-born neurons.

The study appears technically sound, including many different approaches in order to reach its conclusions.

For instance, tamoxifen has been reported to impair various physiological processes, including neurogenesis (Smith et al., 2022), and most studies on adult hippocampal neurogenesis use the C57BL/6J strain of mice; hence, the use of Tamoxifen or that of the GlastCreERT2;RYFP model may have underscored these observations. However, to account for this potentially confounding factor, the Authors characterised the effect of their IF treatment in C57BL/6j mice, also reporting no evident effects of IF as a pro-neurogenic intervention.

I think the study was carefully planned and the analyses well done. Several possible variables were considered, including sex, labelling method, strain, tamoxifen usage or diet length. Several controls were performed in other organs and tissues (liver, fat) to establish the fasting protocol and to check its effects.

Data are presented in a clear way. Quality of images is high level.

In general, it appears as a highly reliable paper reaching an authoritative conclusion for the absence of effect of IF on adult neurogenesis.

Major comments:

I think that the key conclusions are convincing and no further experiments are required.

The methods are presented in such a way that they can be reproduced, and the experiments adequately replicated with proper statistical analysis.

We thank the reviewer for the encouraging remarks and the appreciation of our efforts.

Minor comments:

Prior studies are referenced appropriately, both regarding the IF protocols and the adult neurogenesis modulation.

Line 288 - a reference is incomplete (Dias); integrate with: (Dias et al., 2021)

We will re-format the reference, thanks for spotting the mistake.

There is one concept that is not expressed in the manuscript. Maybe it is not strictly necessary, but I think can be useful to mention it here. It is the fact that most information currently available strongly indicates that adult neurogenesis in humans is not present after adolescence. Of course the research described here is carried out on mice, and in the manuscript it is stated many times that adult hippocampal neurogenesis is strongly decreasing with age, also due to age-related stem cell depletion. Yet, it seems that in humans the exhaustion of such a process can start after adolescence. We know that a sort of controversy is currently present on this subjects, because DCX+ neurons can be detected in adult and old human hippocampi. Yet, it is also clear that there is no substantial cell division (stem cells are depleted) to sustain such hypothetical neurogenesis. Hence, it has been hypothesized that non-newlyborn, "immature" neurons can persist in the absence of cell division, as it has been well demonstrated in the cerebral cortex (see La Rosa et al., 2020 Front Neurosci; Rotheneichner et al., 2018, Cereb Cortex).

This point can be important in the case someone want to use dietary approached such as IF (or any other pharmacological treatment) to stimulate neurogenesis in humans.

We agree with the reviewer and also find this a very interesting and timely topic. However, we find it a bit far from our results and would prefer not to comment on it in the context of the current paper.

Reviewer #2 (Significance (Required)):

The significance of this study relies on the fact that adult neurogenesis field (AN) has been often damaged by the search of "positive" results, aiming at showing that AN does occur "always and everywhere" and that most internal/external stimuli do increase it. This attitude created a bias in the field, persuading many scientists that a result in AN is worthy of publication (or of high impact factor publication) only when a positive result is found.

Personally, I found particularly meaninful the last sentences of the Discussion (reported below), which might seem "off topic" in a research paper, while - I think - underline the real significance of the manuscript:

"In addition, publication bias might be playing a role in skewing the literature on fasting and neurogenesis towards reporting positive results.

In some reviews, even studies reporting no effect are cited as evidence for improved neurogenesis upon IF. Reporting of negative results, especially those challenging accepted dogmas, and a careful and rigorous evaluation of the publications cited in reviews are crucial to avoid unnecessary waste of resources and to promote the advancement of science."

Reviewer field of expertise - keywords: adult neurogenesis, brain structural plasticity, non-newly born immature neurons, comparative neuroplasticity.

We are very happy that the reviewer shares our concern with the biased publication of positive results in the field. We hope our work (and that of Roberts et al., 2022) will encourage other labs to publish their negative results.

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

In this manuscript, Gabarro-Solanas et al. investigate the effects of intermittent fasting (IF) on adult hippocampal neurogenesis in young adult mice. IF has been reported to increase the number of adult-born neuron in the hippocampus, a region that is important for learning and memory. However, it is not well understood what stages of adult neurogenesis are regulated by IF. To address this, the authors utilized lineage tracing and label retention assays in mice undergoing an IF diet. The authors used 2 months old Glast-CreERT2;RYFP mice in combination with Edu label retention to characterize adult NSCs and placed these mice on 1 and 3 months of IF. Despite seeing a decrease in neural stem cell proliferation with age, the authors did not observe a change due to diet. The authors then used immunohistochemistry to characterize changes in cell proliferation, neuroblasts, and new neurons following 1 month and 3 months of IF. Only 1 month of IF seemed to decrease the number of new neurons; however, by 3 months the neuronal output was the same. There were no differences in neuroblasts or cell proliferation due to diet. Gabarro-Solanas et al. conclude that IF transiently and mildly inhibits neurogenesis. Due to contradicting results, the authors then try to determine what variables (sex, labeling method, strain, tamoxifen usage, or diet length) could be affecting their data. The authors saw no substantial differences due to any of their variables.

Major Points

1. The authors analyze NSCs homeostasis and neurogenesis in young adult mice and do not observe any significant changes with their chosen alternate day intermittent fasting paradigm. However, a lot of the data and cell counts appears to be highly variable between animals in the same group. At times, there is an order of magnitude difference between the highest and lowest counts (e.g. Figure 2C,E). According to the method section, it appears that the authors predominantly analyzed a single DG (section?) for most immunostainings, which may explain the large variability in their data. If this is indeed the case, it is insufficient to quantify only a single section for each animal. The authors should quantify several DG sections for each mouse from a pre-defined range along the rostral-caudal axis of the hippocampus in accordance with a standard brain reference atlas. There are also several quantifications, especially of Ki67 where several individuals appear to have no Ki67+ (Figure 3B, 6D) NSCs. These findings are surprising given the still young age of these mice and may be another reflection of the limited brain sections that were analyzed.

The counts are indeed very variable. The counts were made on 1 to 4 DG sections (counted in full), depending on the staining. We will more clearly disclose this information in the revised version. In addition, we will re-count the neuronal output after fasting using stereology. Regarding the very low number of Ki67+ aNSCs, our counts are lower than those in other publications because we are much more stringent with our aNSC identification. Instead of using merely Sox2 (which also labels IPCs), we rely on the presence of a radial GFAP+ process.

There appear to be significant cutting or imaging artifacts across most fluorescent images further raising concerns regarding the accuracy of the quantifications (e.g. Figure 3D, 4C,E, 6B) and publication quality of the images and data. Importantly, uneven section thickness, either from cutting artifacts or imaging issues, may lead to inaccurate cell quantifications a could, possibly, account for the high variability. This issue would further exacerbate concerns regarding the quantification of a single DG section for each animal.

We only processed those samples that passed our QC after sectioning, meaning any unevenly cut brains were never considered (or stained). The stitched images do show artifacts (lower signal in the image junctions), particularly in the NeuN staining. However, this did not affect quantifications, as the measured levels were always clearly above the threshold to consider a cell positive, regardless of the position within the image. The images were cropped to improve the visualisation of NSCs, and to avoid the display of empty tiles. A low magnification image will be provided in the revised version to show that there were no staining artifacts.

It is unclear how NSCs were counted in the B6 mice (Fig 6D,E). The authors only provide a description for the Glast-CRE mice, where they used YFP labeling and GFAP. We assume they performed Sox2/GFAP or Nestin labeling, however, this is not clear at all. The authors should describe their methodology and provide representative images.

We used GFAP, location and morphology to count aNSCs in non-YFP mice. We will make this clear in the text and will also add one more count using Sox2, GFAP and Nestin to identify aNSCs.

NSC populations represent a heterogenous group of stem cells with different replicative properties. As such, the Glast-Cre approach used for the majority of this study may represent a specific subset of NSCs. In line with the previous point, we recommend the authors complement their NSC counts with Sox2/GFAP and Nestin immunostainings.

aNSCs labelled with Glast-Cre are the great majority of aNSCs (>90%) in both ad libitum fed and fasted mice. The data will be included in the revised version. Nevertheless, we will add counts using Sox2, GFAP and Nestin for key experiments.

Stress is a significant negative regulator of neurogenesis. Is it possible that the IF mice display higher stress level which could counteract any beneficial effects of the IF intervention. The authors should provide some measures of stress markers to rule out this potential confounding factor in their IF paradigm.

This is a great suggestion. We will collect blood from control and fasted mice and measure the levels of stress factors (e.g. corticosterone). We will include the data in our revised version.

Minor Point

1. The authors state that "Experimental groups were formed by randomly assigning mice from different litters within each mouse strain and all experiments were conducted in male and female mice". Given that neurogenesis, especially at young ages, is highly sensitive to the exact age of the mice, the authors should provide a rationale why animals from different litters instead of littermate controls were used in these experiments.

Littermate controls were always used in the experiments. But also, more than one litter was used for each experiment, since one litter was never generating enough mice for the experiments. We will clarify this point in text.

Currently, the statistical tests are only described in the method section, however it would be helpful if this information to be integrated into the figure legend as well. Additionally, the authors provide individual data points for some but not all bar graphs (eg Figure 1D).

We will consider including the statistical information in the figure legend, provided there is not a maximum length for figure legends. In the case of figure 1D, data points are not shown because of how the food intake was calculated: as an average per cage instead of per animal (included in the materials and methods). We therefore do not consider it useful to show the datapoints in the final version of the manuscript, but will provide them for the reviewer.

Cell counts per AU is a rather unorthodox unit. With a representative selection of tissue for each animal, the authors could avoid the need to normalize to the DG length and may be able to extrapolate an estimate of cell counts for the entire DG instead.

Thanks for the suggestion. Our arbitrary units (AU) were in fact already equivalent to cells per mm of DG, and we have updated our graphs to reflect this.

In Figure 4D, the authors highlight a few NSC with arrowheads. At a quick glance this is rather confusing as it appears that the authors only counted 3 NSCs in each picture. It may be a better option to show a zoomed in picture to highlight an example of a representative NSC.

Examples of representative NSCs are already shown in Fig 2. With this image, we intended to show a larger number of NSCs. We realise the arrows only pointed to some of them, making the message confusing. We will consider removing them from the figure in the revised version.

In Supplementary Figure S6, the authors should complement the quantification of the nuclei with representative images.

We will include representative images in Figure S6.

For the daytime IF, did the authors assess weights, food intake, RER as well liver/fat measurements similar to night-time IF? If so, this data should be provided in the supplement.

We do have data for the daytime IF in the metabolic cages, which was taken from mice housed in groups (during the preliminary phase of our study). We also have the weight and data on neurogenesis, which we will show as a supplement.

Reviewer #3 (Significance (Required)):

The authors are commended for compiling a manuscript on what is commonly considered 'negative data', that, at the same time, are also contradicting independent reports on the effects of IF on neurogenesis. The studies outlined in this manuscript are comprehensive and mostly well designed. Given the broad, growing interest in dietary restriction as an aging intervention the study is timely.

We thank the reviewer for the positive assessment of the significance of our work.

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

Summary:

In this manuscript, Gabarró-Solanas et al. tested the effect of intermitted fasting (IF, every-other-day fasting) on adult neural stem cells and neurogenesis. They demonstrate that the paradigm they have used does not affect NSC activation or maintenance, and does also not promote neurogenesis. As previous reports showed increased neurogenesis with IF, the authors controlled for various parameters such as mouse strain, sex, and diet length. They also used different methods of identification of newborn neurons, such as tamoxifen-induced lineage-tracing versus birth-dating with thymidine-analogues to substantiate their findings.

Major comments:

This study is very well done with carefully designed and controlled experiments. The manuscript reads nicely and the data are presented in a clear way, making it easy to follow. The authors have done a "tour-de force" to rule out confounding factors that might influence their findings that IF does not affect NSCs nor neurogenesis.

The claims and conclusions are supported by the data. The methods are clearly described and should allow to reproduce the data independently. The number of replicates (i.e. the number of mice analyzed) is impressive and statistical analysis is adequate.

The major findings, namely that the chosen IF does not affect NSCs and neurogenesis is not in line with some previous studies. Despite a careful ruling out of potentially confounding factors (see also "significance" below), it remains unclear why other studies have found an increase in neurogenesis with IF. As each of these studies has some specific experimental design, it is difficult to judge these data in the context of previous data without going through all the details of the other studies. It would thus be a great help for the reader if the authors could provide a table or schematic, which lists the major parameters of each of these studies, such as detailed paradigm of IF, age of mice at start, sex, duration of the intervention, method of identification of NSCs and neurogenesis etc.

This is a very good suggestion, and we had already created such a table. We, however, consider that it might be better suited for a review on the effects of IF on neurogenesis than for this work. We will include the table in our response to the reviewers together with our revised version.

Two points that the authors have not discussed might also be worth mentioning in the discussion part:

1.) The mice in the night-time IF were single caged, could there be a potential negative effect on neurogenesis that would mask the presumably beneficial effect of IF? Although the controls were also single caged, the stress of social isolation might play a role?

The mice were only single caged for the metabolic phenotyping, but not for the neurogenic counts. We will make this clearer in the text. In any case, we do agree that stress might play a role and we will measure stress levels in the control and fasted mice and will include this data in the revised version.

2.) The IF mice gained the same weight over time (Fig. S2), but had a ~20% reduction in overall calory intake. This would be explainable by a reduction in energy expenditure, but the overall activity was also not significantly changed (Fig. S1). Can the authors speculate why they reach the same weight with less calories?

We also found this surprising and were expecting a reduction in the overall activity of the fasted mice. We do not have an explanation for this discrepancy, but perhaps stress levels might explain part of it (we will check stress levels in the revised version). We will also look at whether energy expenditure and activity levels changed over time.

Minor comments:

1.) It would be nice to replace the arbitrary units (AU) in the graphs were this is used (e.g. Fig. 2F, 3C, 4B, D and F etc) to the actual number of cells per a certain µm DG, so that the number of cells can be put in context and compared between the figures.

Yes, our AU already corresponded to mm and we will update our figures accordingly.

2.) Fig 3 D: can the authors also show the Ki67 channel to illustrate how it looks after a 3 month IF?

We find it does not help much, as Ki67+ cells are mostly IPCs and that data is already shown in Fig. 4A. We will nevertheless include the image in our response to the reviewers together with our revised version.

3.) Fig.4E: the NeuN staining looks strangely interrupted, this might be due to tile-stitching? In that case, it would be better to either only show one segment or to try to get a better stitching algorhythm.

It is indeed because of the tile-stitching and uneven illumination. However, this did not affect the counts, as already discussed in the response to reviewer #3 (major point #2).

4.) Fig.6 D shows a minus axis in Y-axis, this should only been shown from 0 to positive values, as it is a percentage of cells and cannot be negative.

True, thanks for spotting this. We will correct the graphs in the revised version.

5.) Fig.6 B: the same problem with the NeuN staining as mentioned under point 3. This should be improved.

As with point 3, the stitching did not affect the quantification. We find it more accurate to show the image with the stitching, as that was the one used for quantification. We will provide a new picture with lower magnification to better show the quality of the staining.

6.) Fig. S6B: maybe add a comment in the result part or in the figure legend that a 10 day chase after an EdU pulse is not the classical protocol to look at mature NeuN positive neurons. But apparently enough newborn neurons were already NeuN positive for this quantification.

We fully agree 10 days is not the standard for neuronal identification. We did find neurons after the 10-day chase but in low numbers. We will add a comment in the text of the revised version to clarify this.

7.) The authors refer to personal communications with M. Mattson and S. Thuret to underline that circadian disruption is not enough to explain the differences (line 367 onwards). Can they refer the reader to published data instead?

While the results are published in their papers, the methods did not specify the time at which the food was added/removed for the IF protocol. That is why we refer to personal communication.

Further showing that disruption of circadian rhythms is not enough to explain the difference in outcome of the IF protocol, we will show the data for the 1-month daytime IF, which again does not increase adult neurogenesis (reviewer #3, minor point #6).

Reviewer #4 (Significance (Required)):

Given the great interest in the seemingly positive effects on health of IF in general, and also for increasing neurogenesis, it is important to better understand the mechanism of this intervention. The study by Gabarró-Solanas et al. clearly demonstrates that IF is not a universal, "works all the time" way of increasing neurogenesis. The study is very well done, with well controlled and measured parameters. It shows that a physiological interference such as IF might depend on many factors and might be less robust across laboratories than anticipated. This study is a very good example that all the details of the experimental settings need to be taken into consideration and are ideally reported with every IF study. It is also a good example how to follow up "no effect" data in a way that they are conclusive.

The significance of this study is to point out that IF as a strategy to increase neurogenesis needs to be reconsidered. It raises the questions how IF can be beneficial in some studies and not in others, asking for more experiments to better understand the detailed mechanisms of IF action. In a systematic approach, this study rules out some of the potentially confounding factors and shows that at least with the chosen IF paradigm, these factors are not the reason for not seeing increased neurogenesis. The study is thus of clear interest for the neurogenesis field and will also need to be considered by the broader field of IF research, although it speaks against the beneficial effects of IF. It might have the potential to bring together the different study authors who did or did not see increased neurogenesis with IF and discuss together the non-published details of their study design to advance the field.

We thank the reviewer for the positive assessment of our work and for acknowledging its importance for the broader field of IF research.

List of references used in the response to reviewers:

Anson, R. M. et al. Intermittent fasting dissociates beneficial effects of dietary restriction on glucose metabolism and neuronal resistance to injury from calorie intake. Proceedings of the National Academy of Sciences 100, 6216–6220 (2003).

Bok, E. et al. Dietary Restriction and Neuroinflammation: A Potential Mechanistic Link. International Journal of Molecular Sciences 20, 464 (2019).

Cignarella, F. et al. Intermittent Fasting Confers Protection in CNS Autoimmunity by Altering the Gut Microbiota. Cell Metabolism 27, 1222-1235.e6 (2018).

Dai, S. et al. Intermittent fasting reduces neuroinflammation in intracerebral hemorrhage through the Sirt3/Nrf2/HO-1 pathway. Journal of Neuroinflammation 19, 122 (2022).

Dias, G. P. et al. Intermittent fasting enhances long-term memory consolidation, adult hippocampal neurogenesis, and expression of longevity gene Klotho. Mol Psychiatry 1–15 (2021).

Goodrick, C. L., Ingram, D. K., Reynolds, M. A., Freeman, J. R. & Cider, N. Effects of intermittent feeding upon body weight and lifespan in inbred mice: interaction of genotype and age. Mechanisms of Ageing and Development 55, 69–87 (1990).

Gudden, J., Arias Vasquez, A. & Bloemendaal, M. The Effects of Intermittent Fasting on Brain and Cognitive Function. Nutrients 13, 3166 (2021).

Lee, J., Seroogy, K. B. & Mattson, M. P. Dietary restriction enhances neurotrophin expression and neurogenesis in the hippocampus of adult mice. Journal of Neurochemistry 80, 539–547 (2002).

Rangan, P. et al. Fasting-mimicking diet cycles reduce neuroinflammation to attenuate cognitive decline in Alzheimer’s models. Cell Reports 40, 111417 (2022).

Roberts, L. D. et al. The 5:2 diet does not increase adult hippocampal neurogenesis or enhance spatial memory in mice. 2022.10.03.510613 BioRxiv Preprint (2022).

Song, M.-Y. et al. Energy restriction induced SIRT6 inhibits microglia activation and promotes angiogenesis in cerebral ischemia via transcriptional inhibition of TXNIP. Cell Death Dis 13, 449 (2022).

Urbán, N. et al. Return to quiescence of mouse neural stem cells by degradation of a proactivation protein. Science 353, 292–295 (2016).

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Gabarro-Solanas et al. question the suitability of IF (Intermittent fasting - non-pharmacological strategy to counteract ageing, which has been previously shown to increase the number of adult-born neurons in the dentate gyrus of mice) as a pro-neurogenic intervention, since IF treatment did not stimulate adult hippocampal neurogenesis, neither at the stem cell level nor on immature and/or dividing neurons. The Authors used a tamoxifen inducible transgenic model (Glast-CreERT2;RYFP mice) to trace neural stem cell lineage and found that IF did not enhance neural stem cell proliferation, nor the abundance of immature, DCX+ neurons. Three-months of IF failed to increase the number of new adult-born neurons (NeuN+/YFP+), while one month of IF significantly reduced the number of new adult-born neurons.

The study appers technically sound, including many different approaches in order to reach its conclusions. For instance, tamoxifen has been reported to impair various physiological processes, including neurogenesis (Smith et al., 2022), and most studies on adult hippocampal neurogenesis use the C57BL/6J strain of mice; hence, the use of Tamoxifen or that of the GlastCreERT2;RYFP model may have underscored these observations. However, to account for this potentially confounding factor, the Authors characterised the effect of their IF treatment in C57BL/6j mice, also reporting no evident effects of IF as a pro-neurogenic intervention. I think the study was carefully planned and the analyses well done. Several possible variables were considered, including sex, labelling method, strain, tamoxifen usage or diet length. Several controls were performed in other organs and tissues (liver, fat) to establish the fasting protocol and to check its effects. Data are presented in a clear way. Quality of images is high level. In general, it appears as a highly reliable paper reaching an authoritative conclusion for the absence of effect of IF on adult neurogenesis.

Major comments:

I think that the key conclusions are convincing and no further experiments are required. The methods are presented in such a way that they can be reproduced, and the experiments adequately replicated with proper statistical analysis.

Minor comments:

Prior studies are referenced appropriately, both regarding the IF protocols and the adult neurogenesis modulation. Line 288 - a reference is incomplete (Dias); integrate with: (Dias et al., 2021) There is one concept that is not expressed in the manuscript. Maybe it is not strictly necessary, but I think can be useful to mention it here. It is the fact that most information currently available strongly indicates that adult neurogenesis in humans is not present after adolescence. Of course the research described here is carried out on mice, and in the manuscript it is stated many times that adult hippocampal neurogenesis is strongly decreasing with age, also due to age-related stem cell depletion. Yet, it seems that in humans the exhaustion of such a process can start after adolescence. We know that a sort of controversy is currently present on this subjects, because DCX+ neurons can be detected in adult and old human hippocampi. Yet, it is also clear that there is no substantial cell division (stem cells are depleted) to sustain such hypothetical neurogenesis. Hence, it has been hypothesized that non-newlyborn, "immature" neurons can persist in the absence of cell division, as it has been well demonstrated in the cerebral cortex (see La Rosa et al., 2020 Front Neurosci; Rotheneichner et al., 2018, Cereb Cortex). This point can be important in the case someone want to use dietary approached such as IF (or any other pharmacological treatment) to stimulate neurogenesis in humans.

Significance

The significance of this study relies on the fact that adult neurogenesis field (AN) has been often damaged by the search of "positive" results, aiming at showing that AN does occur "always and everywhere" and that most internal/external stimuli do increase it. This attitude created a bias in the field, persuading many scientists that a result in AN is worthy of publication (or of high impact factor publication) only when a positive result is found.

Personally, I found particularly meaninful the last sentences of the Discussion (reported below), which might seem "off topic" in a research paper, while - I think - underline the real significance of the manuscript: "In addition, publication bias might be playing a role in skewing the literature on fasting and neurogenesis towards reporting positive results.

In some reviews, even studies reporting no effect are cited as evidence for improved neurogenesis upon IF. Reporting of negative results, especially those challenging accepted dogmas, and a careful and rigorous evaluation of the publications cited in reviews are crucial to avoid unnecessary waste of resources and to promote the advancement of science."

Reviewer field of expertise - keywords: adult neurogenesis, brain structural plasticity, non-newly born immature neurons, comparative neuroplasticity.

This quote addresses our society's ever-changing nature, and the need for our teaching methods to change as a result. The way that our current educational institutions are structured are a sort of "one-size-fits all". However, it only fits a select group and does not take into account that people think and learn differently.

I agree with the author that if the next generation can be made to understand and change perceptions, it will require teachers and parents to show respect for different groups in society by example, and I think it is beneficial for children to learn about groups that are different from their own social class. Changing teaching styles is also an important point, as mentioned in the article that there needs to be different learning styles for students, so teachers need to learn more diverse teaching styles to improve the quality of teaching.

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Reply to the reviewers

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

Marta Sanvicente-García et al and colleague developed a comprehensive and versatile genome editing web application tool and a nextflow pipeline to give support to gene editing experimental design and analysis.

The manuscript is well written and all data are clearly shown.

While I did not tested extensively, the software seems to work well and I have no reason to doubt the authors' claims.

I usually prefer ready to use web applications like outknocker, they are in general easier to use for rookies (it would be good if the author could cite it, since it is very well implemented) but the nextflow implementation is anyway well suited.

We have been able to analyze the testing dataset that they provide, but we have tried to run it with our dataset and we have not been able to obtain results. We have also tried to run it with the testing dataset of CRISPRnano and CRISPResso2 without obtaining results. The error message has been in all the cases: “No reads mapping to the reference sequence were found.”

Few minor points:

Regarding the methods to assess whether the genome editing is working or not, I would definitely include High Resolution Melt Analysis, which is by far the fastest and probably more sensitive amongst the others.

Following the Reviewer 1 suggestion, we have added this technique in the introduction: “Another genotyping method that has been successfully used to evaluate genome editing is high-resolution melting analysis (HRMA) [REFERENCE]. This is a simple and efficient real-time polymerase chain reaction-based technique.”

Another point that would important to taclke is that often these pipelines do nto define the system they are working with (eg diploid, aploid vs etc). This will change the number of reads needed ato unambigously call the genotypes detected and to perform the downstream analysis (the CRISPRnano authors mentioned this point).

In the introduction, it is already said: " it is capable of analyzing edited bulk cell populations as well as individual clones". In addition, following this suggestion we have added in the help page of CRISPR-A web application and in the documentation of the nextflow pipeline a recommended sample coverage to orient the users on that.

I am also wondering whether the name CRISPR-A is appropriate since someone could confuse it with CRISPRa.

CRISPR-A is an abbreviation for CRISPR-Analytics. Even if it is true that it can be pronounced in the same way that CRISPRa screening libraries, it is spelled differently and would be easily differentiated by context.

CROSS-CONSULTATION COMMENTS

Reviewer 2 made an excellent work and raised important concerns about the software they need to be addressed carefully.

In the meantime we had more time to test the software and can confirm some of the findings of Reviewer 1:

1) We spent hours running (unsuccessfully) CRISPR A on Nextflow. The software does not seem to run properly.

2) No manual or instruction can be found on both their repositories (https://bitbucket.org/synbiolab/crispr-a_nextflow/

https://bitbucket.org/synbiolab/crispr-a_figures/)

We have added a readme.md file to both repositories and we hope that with the new documentation the software can be downloaded and run easily. We have also added an example test in CRISPR-A nextflow pipeline to facilitate the testing of the software. Currently, the software is implemented in DLS1 instead of DLS2, making it impossible to be run with the latest version of nextflow. We are planning to make the update soon, but we want to do it while moving the pipeline to crisprseq nf-core pipeline to follow better standards and make it fully reproducible and reusable.

Few more points to be considered:

• UMI clustering is not proper terminology. Barcode multiplexing/demultiplexing (SQK-LSK109 from Oxford Nanopore).

We have added more details in the methods section “Library prep and Illumina sequencing with Unique Molecular Identifiers (UMIs)” to clarify the process and used terminology: “Uni-Molecular Identifiers are added through a 2 cycles PCR, called UMI tagging, to ensure that each identifier comes just from one molecule. Barcodes to demultiplex by sample are added later, after the UMI tagging, in the early and late PCR.”

We had already explained the computational pipeline through which these UMIs are clustered together to obtain a consensus of the amplified sequences in “CRISPR-A gene editing analysis pipeline” section in methods:

“An adapted version of extract_umis.py script from pipeline_umi_amplicon pipeline (distributed by ONT https://github.com/nanoporetech/ pipeline-umi-amplicon) is used to get UMI sequences from the reads, when the three PCRs experimental protocol is applied. Then vsearch⁴⁸ is used to cluster UMI sequences. UMIs are polished using minimap2³² and racon⁴⁹ and consensus sequences are obtained using minialign (https://github.com/ocxtal/minialign) and medaka (https://github.com/nanoporetech/medaka).”

We also have added the following in “CRISPR-A gene editing analysis pipeline” methods section to help to understand differences between the barcodes that can be used: “In case of working with pooled samples, the demultiplexing of the samples has to be done before running CRISPR-A analysis pipeline using the proper software in function of the sequencing used platform. The resulting FASTQ files are the main input of the pipeline.”

Then, SQK-LSK109 from Oxford Nanopore is followed through the steps specified in methods: “The Custom PCR UMI (with SQK-LSK109), version CPU_9107_v109_revA_09Oct2020 (Nanopore Protocol) was followed from UMI tagging step to the late PCR and clean-up step.”

Finally, we want to highlight that, as can be seen in methods as well as in discussion, UMIs are used to group sequences that have been amplified from the same genome and not to identify different samples: “Precision has been enhanced in CRISPR-A through three different approaches. [...] We also removed indels in noisy positions when the consensus of clusterized sequences by UMI are used after filtering by UBS.” As well as in results (Fig. 5C).

• Text in Figure 5 is hard to read.

We have increased the letter size of Figure 5.

• They should test the software based on the ground truth data

We have added a human classified dataset to do the final benchmarking. And we can see that for all examined samples CRISPR-A has an accuracy higher than 0.9. As has been shown in the figure with manual curated data, CRISPR-A shows good results in noisy samples using the empiric noise removal algorithm, without need of filtering by edition windows.

• The alignment algorithm is not the best one, I think minimap2 would be better for general purpose (at least it work better for ONT).

As can be seen in figure 2A, minimap is one of the alignment methods that gives better results for the aim of the pipeline. In addition, we have tuned the parameters (Figure 2B) for a better detection of CRISPR-based long deletions, which can be more difficult to report in a single open gap of the alignment.

• The minimum configuration for installation was not mentioned (for their Docker/next flow pipeline).

Proper documentation to indicate the configuration requirements for installation has been added to the readme.md of the repository·

• Fig 2: why do they use PC4/PC1?

Principal Component Analysis is used to reduce the number of dimensions in a dataset and help to understand the effect of the explainable variables, detect trends or samples that are labeled in incorrect groups, simplify data visualization… Even PC4 explains less variability than PC2 or PC3, this helps us to understand and better decipher the effect of the 4 different analyzed parameters even if the differences are not big. We have decided to include as a supplementary figure other PCs to show these.

• There are still typos and unclear statements thorughout the whole manuscript.

One more drawback is that the software seems to only support single FASTQ uploading (or we cannot see the option to add more FASTQ).

In the case of paired-end reads instead of single-end reads, in the web application, these can be selected at the beginning answering the question “How should we analyze your reads? Type of Analysis: Single-end Reads; Paired-end Reads”. In the case of the pipeline, now it is explained in the documentation how to mark if the data is paired-end or single-end. It has to be indicated in “input” and “r2file” configuration variables.

In the case of multiple samples, and for that reason multiple FASTQ files, there is the button to add more samples in the web application. In the pipeline, multiple samples can be analyzed in a single run by putting all together in a folder and indicating it with variable “input”.

Since usually people analyze more than one clone at the time (we usually analyze 96 clones together) this would mean that I have to upload manually each one of them.

All files can be added in the same folder and analyzed in a single run using the nextflow pipeline. Web application has a limit of ten samples that can be added clicking the button “Add more”.

Also, the software (the webserver, the docker does not work) works with Illumina data in our hands but not with ONT.

This should be clarified in the manuscript.

If a fastq is uploaded to CRISPR-A, the analysis can be done even if we haven't specifically optimized the tool for long reads sequencing platforms. We have checked the performance of CRISPR-A with CRISPRnano nanopore testing dataset and we have succeeded in the analysis. See results here: https://synbio.upf.edu/crispr-a/RUNS/tmp_1118819937/.

Summary of the results:

Sample

CRISPRnano

CRISPR-A

'rep_3_test_800'

42.60 % (-1del); 12.72 % (-10del)

71% (-1del);

16% (-10del)

– 36 (logo)

'rep_3_test_400'

37.50 % (-1del); 15.63 % (-10 del)

65% (-1del);

28% (-10del)

– 38 (logo)

'rep_1_test_200'

39.29 % (-1del); 8.33 % (-17del)

10del; 17del; 1del

'rep_1_test_400'

80.11 % (-17 del)

del17; del20; del18; del16;del 16

'rep_0_test_400'

80.11% (-17 del)

del17; del20; del 18; del16; del16

'rep_0_test_200'

71.91% (-17 del)

del17; del18

As we can see from these exemple, CRISPR-A reports all indels in general without classifying them as edits or noise. Since nanopore data has a high number of indels as sequencing errors the percentages of CRISPR-A are not accurate. Eventhat, CRISPR-A reports more diverse outcomes, which are probably edits, than CRISPRnano.

Therefore, we have added the following text in results:

“Even single-molecule sequencing (eg. PacBio, Nanopore..) can be analyzed by CRISPR-A, targeted sequencing by synthesis data is required for precise quantification.”

Reviewer #1 (Significance (Required)):

As I mentioned above I think this could be a useful software for those people that are screening genome editing cells. Since CRISPR is widely used i assume that the audience is broad.

There are many other software that perform similarly to CRISPR-A but it seems that this software adds few more things and seems to be more precise. It is hard to understand if everything the author claims is accurate since it requires a lot of testing and time and the reviewing time is of just two weeks. But 1) I have no reason to doubt the authors and 2) the software works

Broad audience (people using CRISPR)

Genetics, Genome Engineering, software development (we develop a very similar software), genetic compensation, stem cell biology

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

Summary:

CRISPR-Analytics, abbreviated as CRISPR-A, is a web application implementing a tool for analyzing editing experiments. The tool can analyze various experiment types - single cleavage experiments, base editing, prime editing, and HDR. The required data for the analysis consists of NGS raw data or simulated data, in fastq, protospacer sequence and cut site. Amplicon sequence is also needed in cases where the amplified genome is absent from the genome reference list. The tool pipeline is implemented in NextFlow and has an interactive web application for visualizing the results of the analysis, including embedding the results into an IGV browser.

The authors developed a gene editing simulation mechanism that enables the user to assess an experiment design and to predict expected outcomes. Simulated data was generated by SimGE over primary T-cells. The parameters and distributions were also fitted for 3 cell lines to make it more generalized (Hek293, K562, and HCT116). The process simulated CRISPR-CAS9 activity and the resulting insertions, deletions, and substitutions. The simulation results are then compared to the experimental results. The authors report the Jensen-Shannon (JS) divergence between the results. The exact distributions that served as input to the JS are not well defined in the manuscript (see below).

To clarify the used distributions in the JS divergence calculation, we have changed the following piece of text in section “Simulations evaluation” of methods:

“ Afterward, we tested the performance on the fifth fold, generating the simulated sequences with the same target and gRNA as the samples that belong to the fifth fold, in order to calculate the distance between these. The final validation, with the mean parameters of the different training interactions, was performed on a testing data set that was not used in the training. Validation was done with samples that had never taken place in the training process. Jensen distance is used to compare the characterization of real samples and simulated samples since this is the explored distance that differentiates better replicates among samples. In order to obtain the different distributions, the T cell data, including 1.521 unique cut sites, was split into different datasets based on the different classes: deletions, insertions and substitutions. For each of these classes, giving as input the datasets with only that class, we obtained the distribution for size and then for position of indels. The same was done for the other three cell lines: K562, HEK293 and HCT116, which included 96 unique cut sites, with three replicates each. The whole datasets (with 1521 and 96 unique cut sites) were split into five-folds (4 for training and one for test) and validation, in order to train and validate the simulator. Using the parameters obtained during the training-test iterations (the average value of the 5 iterations), we generate simulated sequences with the same target and gRNA as the samples that are assigned to the test subset to calculate the Jensen-Shannon (JS) divergence between the simulated and real samples of that subset. Finally, the same was performed for validation. The input for the distance calculations were the generated simulated subset and its real equivalent (same target and gRNA) distributions of the classes. ”

The authors also report an investigation of different alignment approaches and how they may affect the resulting characterization of editing activity.

The authors examine three different approaches to increase what they call "edit quantification accuracy" (aka, in a different place - "precise allele counts determination" - what is this???): (1) spike-in controls (2) UMI's and (3) using mock to denoise the results. See below for our comments about these approaches.

Moreover, the authors developed an empirical model to reduce noise in the detection of editing activity. This is done by using mock (control), and by normalization and alignment of reads with indels, with the notion and observation that indels that are far from the cut site tend to classify as noise.

The authors then perform a comparison between 6 different tools, in the context of determining and quantifying editing activities. One important comparison approach uses manually curated data. However - the description of how this dataset was created is far from being sufficiently clear. The comparison is also performed for HDR experiment type, which can be compared only to 2 other tools.

We have changed alleles by editing outcomes in the title section “Three different approaches to increase precise editing outcomes counts determination” trying to be more clear.

There is already a section in methods “Manual curation of 30 edited samples” explaining how the manual curation was done.

We see the potential contribution aspects of the paper to be the following:

1. NextFlow pipeline implementation is an important engineering contribution. Same is true for the interactive web application
2. The option to simulate an experiment to assess it is a nice feature and can help experiment design
3. Identification of amplicons when not provided as input
4. CRISPR-A seeks substitutions along the entire amplicon sequence and is less dependent on the quantification window and on the putative cutsite
5. Analysis of the difference, in edit activity, comparing different cell lines
6. CRISPR-A supports the use of UMIs
7. Interesting sequence pattern insights - like "...found certain patterns associated with low diversity outcomes: free thymine or adenine at the 3' nucleotide upstream of the cut site that leads to insertions of the same nucleotide, a free cytosine at the same place that leads to its loss, and strong micro-homology patterns that lead to long deletions " We further comment on the soundness of these contributions in our comments below and on their significance in our comments related to the general potential significance of the paper.

Major comments:

• Upon attempting to run an analysis from the web interface (https://synbio.upf.edu/crispr-a) and using: fastq of Tx and mock (control), the human genome and the gRNA sequence provided as input for the protospacer field, our run was not successful. In fact the site crashed with no interpretable error message from CRISPR-A. We have improved the error handling together with the explanations in the help page, where you will find a video. Hopefully these improvements will avoid unexpected crashings.

• Moreover, there should be more clear context. There is no information regarding the type of experiments that can be analyzed with the tool. We figure it is multiplex PCR and NGS but can the tool also be used for GUIDESeq, Capture, CircleSeq etc.? Experiments that could be analyzed are specified in Results: “CRISPR-A analyzes a great variety of experiments with minimal input. Single cleavage experiments, base editing (BE), prime editing (PE), predicted off-target sites or homology directed repair (HDR) can be analyzed without the need of specifying the experimental approach.” We have also specified this in the nextflow pipeline documentation as well as in the web application help page.

• No off target analysis. Only on-target The accuracy of the tool allows checking if edits in predicted off-target sites are produced, this being an off-target analysis with some restrictions, since just variants of the predicted off-target sites are assessed. Translocations or other structural off-targets will not be detected by CRISPR-A since the input data analyzed by this tool are demultiplexed amplicon or targeted sequencing samples.

• No translocations and long/complex deletions The source of used data as input does not allow us to do this. There are other tools like CRISPECTOR available for this kind of analysis. We have added this to supplementary table 1.

• We view the use of a mock experiment as control as a must for any sound attempt to measure edit activity. This is even more so when off-target events need to be assessed (any rigorous application of GE, certainly any application aiming for clinical or crop engineering purposes). We therefore think that all investigation of other approaches should be put in this context. We agree with the necessity of using negative controls to assess editing. For that reason we have included the possibility of using mocks in the quantification. In addition, there are few tools that include this functionality.

• It's a nice feature to have simulated data, however, it is not a good approach to rely on it. As can be seen in the manuscript we highlight the support that simulations can give without pretending to substitute experimental data by just simulated data. Simulated data has been useful in the development and benchmarking of CRISPR-A, but we are aware of the limitations of simulations. Here some examples from the manuscripts explaining how we have used or can be used simulated data:

“Analytical tools, and simulations are needed to help in the experimental design.”

“simulations to help in design or benchmarking”

“We developed CRISPR-A, a gene editing analyzer that can provide simulations to assess experimental design and outcomes prediction.”

“Gene editing simulations obtained with SimGE were used to develop the edits calling algorithm as well as for benchmarking CRISPR-A with other tools that have similar applications.”

Even simulated data has been useful for the development and benchmarking of CRISPR-A, we have also used real data and human validated data.

• In p7 the authors indicate the implementation of three approaches to improve quantification. They should be clear as to the fact that many other tools and experimental protocols are also using these approaches. for example, ampliCan, CRipresso2 and CRISPECTOR all take into account a mock experiment run in parallel to the treatment. Even in page 7 (results) we don’t mention the other tools that also use mocks for noise correction, we detail this information in Supplementary Table 1. CRISPResso2 was not included since they can run mocks in parallel but only to compare results qualitatively, i.e. there is not noise reduction in their pipeline. It has been added to the table.

• Figure1: ○ The figure certainly provides what seems to be a positive indication of the simulations approach being close to measured results. Much more details are needed, however, to fully understand the results.

We have added more details.

○ Squema = scheme ??

We have changed the word “schema” by diagram.

○ What was the clustering approach?

As is said in the caption of Figure 1 the clustering is hierarchical: “hierarchical clustering of real samples and their simulations from validation data set.” And we have added that “The clustering distance used is the JS divergence between the two subsets.”

○ What is the input to the JS calculation? What is the dimension of the distributions compared? These details need to be precisely provided.

The distribution has two dimensions, sizes and counts or positions and counts.

As said before, to clarify the used distributions in the JS divergence calculation, we have changed the following piece of text in section “Simulations evaluation” of methods:

“ Afterward, we tested the performance on the fifth fold, generating the simulated sequences with the same target and gRNA as the samples that belong to the fifth fold, in order to calculate the distance between these. The final validation, with the mean parameters of the different training interactions, was performed on a testing data set that was not used in the training. Validation was done with samples that had never taken place in the training process. Jensen distance is used to compare the characterization of real samples and simulated samples since this is the explored distance that differentiates better replicates among samples. In order to obtain the different distributions, the T cell data, including 1.521 unique cut sites, was split into different datasets based on the different classes: deletions, insertions and substitutions. For each of these classes, giving as input the datasets with only that class, we obtained the distribution for size and then for position of indels. The same was done for the other three cell lines: K562, HEK293 and HCT116, which included 96 unique cut sites, with three replicates each. The whole datasets (with 1521 and 96 unique cut sites) were split into five-folds (4 for training and one for test) and validation, in order to train and validate the simulator. Using the parameters obtained during the training-test iterations (the average value of the 5 iterations), we generate simulated sequences with the same target and gRNA as the samples that are assigned to the test subset to calculate the Jensen-Shannon (JS) divergence between the simulated and real samples of that subset. Finally, the same was performed for validation. The input for the distance calculations were the generated simulated subset and its real equivalent (same target and gRNA) distributions of the classes. ”

○ What clustering/aggregation approach did the authors use here (average dist, min dist, dist of centers?)

Hierarchical clustering.

○ 5 pairs were selected out of how many? Call that number K.

We have 100 samples in the validation set. Following the suggestion of indicating the total number of samples in the testing set, we have added this information to the figure caption.

○ What does the order of the samples in 1C mean? Is 98_real closer to 22_sim than to 98_sim? If so then state it. If not - what is the meaning of the order? Furthermore - how often, over K choose 2 pairs does this mis-matching occur for the CRISPR-A simulator??

Exactly, it is a hierarchical clustering, where samples are sorted by JS divergence. It was already stated in Results: “In addition, on top of comparing the distance between the experimental sample and the simulated, we have included two experimental samples, SRR7737722 and SRR7737698, which are replicates. These two and their simulated samples show a low distance between them and a higher distance with other samples.” As well as in Figure 1 caption: “For instance, SRR7737722 and SRR7737698, which cluster together, are the real sample and its simulated sample for two replicates.” Then, since these samples are replicates, its simulations will come from the same input and is expectable to find low distance between these two real samples as well as between both of them and their simulation. We have stated it in the discussion.

• "From the characterized data we obtained the probability distribution of each class" (page 3) - How is this done? how many guides? how many replicates? what is class? where do you elabore regarding it? how you obtain the distributions? More details of the methods need to be provided. Added in methods.

• The 96 samples used for development here - where are they taken from? This should be indicated in the first time these samples are mentioned. Namely - bottom of P6 Added: “The 96 samples, from these cell lines, are obtained from a public dataset BioProject PRJNA326019.”

• CRISPECTOR is not mentioned in the comparison in the section: "CRISPR-A effectively calls indels in simulated and edited samples" (Table S2). Is there a specific reason for having left it out? CRISPECTOR, as well as ampliCan, is not in Table S2, since in this table is shown detailed data from Figure 2. CRISPECTOR is compared with CRISPR-A in figure 5, where the different approaches to enhance precision, like using a negative control, are explored.

• In the section "Improved discovery and characterization of template-based alleles or objective modifications" - part of the analysis was made over simulated data and then over real data. The authors state "it is difficult to explain the origin of these differences...". Thus, needs to be investigated in more detail ... :) (P5) Moreover - the performance over real data is, at the end of the day, the more interesting one for comparison purposes. We have added this sample to the human validated dataset to understand better what was happening in this case and the results and pertinent discussion have been added in the manuscript: “CRISPResso2 is detecting a 2% more of reads classified as WT. These 2% correspond with the percentage classified as indels by CRISPR-A. In total, the percentage difference between CRISPResso2 and CRISPR-A template-based class is 0.6%, higher in CRISPR-A. CRISPR-A percentage is closer to the ground truth data than CRISPResso2.”

• We found no explanation of "spike-in"/"spike experimental data" across the entire article. There is some general language about lengths but the scheme is still totally unclear. We have indicated in methods section when we were talking about the spike-in controls.

• Description of the 96 gRNAs? Is this data from REF26? If so - where do you state this? If so - how do the methods described herein avoid the unique characteristics of the data of REF26? We have added the reference: “The 96 samples, from these cell lines, are obtained from a public dataset BioProject PRJNA326019.” In addition, there are other sources of data, simulations and now even human validated data.

• "distance between the percentage of microhomology mediated end-joining deletions of samples with the same target was calculated and the mean of all these distances was used to reduce the information of the 96 different targets to a single one." (P6) What is the exact calculation used? which distance? How was clustering performed? What is the connection for gene expression? The used distance was euclidean distance and the clustering was performed using hierarchical clustering. We have added this information to the manuscript. Regarding the connection of gene expression, we are exploring the correlation of two phenotypes: the gene expression of the proteins differentially related with NHEJ and MMEJ pathways, and the gene editing landscape (indel patterns that are related with MMEJ and those that are more prone to be generated with NHEJ). We have tried to improve this explanation in the manuscript.

• "we have fitted a linear model to transform the indels count depending on its difference in relation to the reference amplicon" (P7) - needs more explanation. Is this part of the pipeline? We have explained better how we have fitted the linear model in methods: “A linear regression model was fitted to obtain the parameters of Equation 1 using spike-in controls experimental data (original count, observed count and size of the change in the synthetic molecules). We have used the lm function from R. Parameter m in Equation 1 is equivalent to the obtained coefficient estimate of x which was 0.156 and n is the intercept (n=10). ”.

The model is optionally used as part of the pipeline as explained at the end of section “CRISPR-A gene editing analysis pipeline” to correct amplification biases due to differences in amplicon size. Then, what is part of the pipeline is the use of this model to make the transformation of counts from the observed counts to the predicted original counts. This is done with Equation 1 and can be found in the pipeline (VC_parser-cigar.R).

• What is it "...manually curated data set"? (page 8) This is explained in “Manual curation of 30 edited samples” in methods.

• Section "CRISPR-A empiric model removes more noise than other approaches" - with what data were the comparisons performed? Moreover, how were the comparison criteria selected (efficiency and sensitivity)? The literature already used several approaches to compare data analysis tools for editing experiments. See for example ampliCan, Crispresso (1 and 2) and CRISPECTOR. Maybe the authors should follow similar lines. The data used in this comparison comes from the reference 26:“26. van Overbeek, M. et al. DNA Repair Profiling Reveals Nonrandom Outcomes at Cas9-Mediated Breaks. Mol. Cell 63, 633–646 (2016).” We have added it to the manuscript.

The values of efficiency and sensitivity were not used directly for the comparison. We wanted to firstly evaluate our own algorithm. For that we obtained the values of efficiency and sensitivity for the previous mentioned dataset. These values were chosen to firstly have an idea of firstly, how much noise the algorithm is able to detect, and secondly, how much of it is able to be reduced after the Tx vs M process. That established a framework of comparison in which we can then compare directly the reported percentage of edition of the different tools.

Regarding the approaches used to compare data analysis tools for editing experiments, we are going to explain why we haven’t followed similar lines or how we have now included it:

In the case of ampliCan, the comparison that they do is with a synthetic dataset with introduced errors:

"synthetic benchmarking previously used to assess these tools (Lindsay et al. 2016), in which experiments were contaminated with simulated off-target reads that resemble the real on-target reads but have a mismatch rate of 30% per base pair".

In CRISPResso2, they benchmarked the efficiency against an inhouse dataset but this dataset is not published. Finally, for the benchmarking of CRISPECTOR, a manual curated dataset is used as a standard: "Assessment of such classification requires the use of a gold standard dataset of validated editing rates. In this analysis, we define the validated percent indels as the value determined through a detailed human investigation of the individual raw alignment results". In this sense, we have added a human validated dataset to do something similar to complement the analysis that we had already done.

In the end, we consider that simulated or synthetic datasets, as those used by ampliCan or CRISPResso2, does not capture the complete landscape of confounding events that can be detrimental to the analysis results. Similar limitations are found in the use of a gold standard dataset of validated editing rates, since the amount of reads or samples that can be validated by humans is not big since it is time consuming. In addition, humans can also make errors and have biases. Eventhogh, we have found very valuable talking into consideration adding a human validated dataset to complete our exploration.

• In the section "CRISPR-A empiric model removes more noise than other approaches" the authors state, incorrectly, that CRISPECTOR only reports the percentage of editing activity per site (there is much more information reported in the HTML report, including the type of edit event detected - deletion, of various lengths, insertions, substitutions etc). (P8) We thank the reviewer for the observation, as indeed the state is incorrect. What we wanted to express is that with CRISPECTOR we cannot trace individually each of the called indels, as any sort of excel or file with this content is given in the output. Therefore we cannot investigate which events have been corrected. To be precise in our statement we changed this sentence to the following:

“CRISPECTOR, although providing extensive information on the statistics and information about the indels, is not possible to track the reads along their pipeline, thus we cannot know which have been corrected and which have not.”

• Section "CRISPR-A noise subtraction pipeline" describes a pretty naive method for noise subtraction (P12). Should be rigorously compared, for Tx vs Mock experiments, to CRISPECTOR and to CRISPResso2. In the section "CRISPR-A empiric model removes more noise than other approaches", we perform an exhaustive comparison with a dataset that contains 288 Mock Files vs 864 Tx files. This can be better appreciated in the, now included, figure Sup. 13A. CRISPResso2 was intentionally left out since their pipeline does not use a model to reduce noise but other approaches like reducing the quantification window.

• "recalculated using a size bias correction model based on spike-in controls empiric data.." (P14). Where is the formula? The formula comes from Equation 1. Now it is correctly referenced.

• Section "Noise subtraction comparison with ampliCan and CRISPECTOR" - fake mock was generated for comparison. We consider the avoidance of a Mock control in experiments designed to measure editing activity to not be best practice. It is OK to support this approach in CRISPR-A. However - the comparison to tools that predominantly work using a Mock control (including ampliCan and CRISPECTOR) should be done with actual Mock. Not with fake Mock .... (P15) We understand the claims of the reviewer for this point as the use of a “fake” mock may not be the best practice for general comparisons. Nevertheless here what we wanted to compare is the difference in the edition percentages using mock and not using it. Since to make a run for on-target data CRISPECTOR requires a mock, the only way to replicate the conditions of “no mock” was to use a synthetic file with the same characteristics of the treated files in terms of depth, but with no edition/noise events to avoid any correction outside this framework. The other run was made with the 288 real Mocks. This was a solution ad Hoc for CRISPECTOR, with ampliCan we used only real mock since they allow to make runs without a mock for on-target.

We changed the word fake for synthetic in the Noise subtraction comparison with ampliCan and CRISPECTOR section:

“As for CRISPECTOR, since it requires a mock file to perform on-target analysis, synthetic mock files were generated”.

Minor comments:

• "Also, most of these tools lack important functionalities like reference identification, clustering, or noise subtraction" - bold part incorrect for CRISPECTOR, although it is not aiming only for CRISPECTOR In supplementary table 1, it is already elucidated which are the functionalities that each tool has. We have also added more context to that statement to highlight the differences between different tools:

“Even not all of them have the same missing functionalities, as can be seen in the Supplementary table 1, CRISPR-A is the only tool that can identifies the amplicon reference from in a reference genome, correct errors through UMI clustering and sequence consensus, correct quantification errors due to differences in amplicon size, and includes interactive plots and a genome browser representation of the alignment.”

• "Same parameters and probability distributions were fitted for three other cell lines: Hek293, K562, and HCT11626, to make SimGE more generalizable and increase its applicability" (page 3) - how was fitted? It was fitted in the same way as the t-cell samples as specified in methods. We have detailed more methods explaining how SimGE is built.

• What is the "nature of modification"? (P5) We have changed nature by type for a better understanding.

• In the section "CRISPR-A effectively calls indels in simulated and edited samples" (P5) towards the end, the authors write that the CRISPR-A algorithm did not give good results for a few examples. They then state that this was corrected and then yielded good results. There is no explanation of what correction was done, if it was implemented in the code and how to avoid/detect it in further cases. The problem was that the used reference sequence was too short. There is no modification in CRISPR-A code, we have just used the whole amplicon reference sequence obtained with the amplicon reference identification functionality of CRISPR-A. We have tried to explain it better in the manuscript: “Once the reference sequence is corrected used is the one corresponding to the whole reference amplicon, obtained with CRISPR-A amplicon sequence discovery function, CRISPR-A shows a perfect edition profile”

• Cell culture, transfection, and electroporation - explanation only for HEK293, what about the others? (P15) We already had explained it for HEK293 and for C2C12, that are the experiments done by use. In the case of the analysis of the three cell lines and 96 targets we reference the source of the data as this data was not produced in our lab.

• Typos and unclear wording: ○ "obtention" (P8) → changed by obtaining

○ "mico" >> micro (P 7,10) → changed

○ "Squema" >> scheme (Fig.1) → changed

○ "decombuled" (P10) → changed by separated

○ "empiric" >> empirical (P8 and other places) → changed

○ "Delins" (P14) → this is not a typo, it is used to indicate that a deletion and insertion has take place (http://varnomen.hgvs.org/recommendations/DNA/variant/delins/)

○ "performancer" (P9) → Change to performance

○ Change word across all article - "edition" to "editing" → changed. In the case of edition windows it has been changed by quantification windows.

○ "...has enough precision to find" (P6) not related to "results" section → We have moved to discussion.

• Comments on figures: ○ Fig. 2C:

■ No CRISPECTOR in the analysis

It is not included because for on-target analysis this tool requires a mock control sample. For this reason, it is compared in Figure 5D, where samples using negative controls are compared, and in Figure 5E where all tools and their different analysis options are compared.

■ It is simulated data only

Yes, it is. Comparison with real data is done in Figure 2D and 2E. And now we also have added a ground truth data in our comparisons obtained from human validation of the classification of more than 3,000 different reads.

■ It is not violin plot as mentioned in the description

It is a violin plot, but in general there is not much dispersion of the data points making the density curves flat.

○ Fig 3A - Is it significant? Yes, it is. We have added this information in the caption of the figure.

○ Fig. 4:

■ A

• Each row/column is a vector of 96 guides? No, as it is said in the caption of the figure, it is the “mean between the distances calculated for each of the 96 different targets.”

• How is the replicate number decided? Is it a different experiment by date? What is separating between experiments? Rep numbers? All this information should be found in the referenced paper from which this dataset comes from as already referenced.

■ B - Differential expression:

We have realized that the caption was not correct, missing the explanations for Fig. 4B and all the following ones moved to a previous letter.

• How? did you measure RNA? It is already stated in methods that RNAseq data was obtained from SRA database and the analysis was done using nf-core/rnaseq pipeline: “RNAseq differential expression analysis of samples from BioProject PRJNA208620 and PRJNA304717 was performed using nf-core/rnaseq pipeline⁵².”

• Is the observed data in the figure sufficiently strong in terms of P-value? Yes, at is it is highlighted in the plot with ** and ***. We have also added the p-value in the cation of the figure.

• Where is the third cell-line? As mentioned in the text, we have just chosen the cell lines that show us higher differences in the the percentage of MMEJ: “HCT116 than in K562, which are the cell lines with the major and minor ratios of MMEJ compared with NHEJ, respectively”.

○ Fig.13 - There is no A and B as mentioned in the text

We thank the reviewer for the observation as we mistakenly uploaded the wrong figure. We corrected it.

Reviewer #2 (Significance (Required)):

We repeat the aspects of contribution, as listed in the first part of the review, and comment about significance:

• NextFlow pipeline implementation is an important engineering contribution. Same is true for the interactive web application

  Significant engineering contribution. Nonetheless, we were not able to run the analysis. So - needs to be checked.

Hopefully now that the documentation is properly added to the repository it will be easier to run analysis.

• The option to simulate an experiment to assess it is a nice feature and can help experiment design

  An important methodology contribution

• Identification of amplicons when not provided as input

  Not important in the context of multiplex PCR and NGS measurement assays, as amplicons will be known. Not clear what other contexts the authors were aiming at.

It is useful to save time, no need to look for the sequence of each amplicon and add it as input. Also, it can help to detect unspecific amplification, since all amplicons of the same genome can be retrieved from the discovery amplicon process. In addition, we have already found one example where this avoids getting incorrect results: “Once the reference sequence used is the one corresponding to the whole reference amplicon, obtained with CRISPR-A amplicon sequence discovery function, CRISPR-A shows a perfect edition profile”. We have added this to the discussion of the manuscript.

• CRISPR-A seeks substitutions along the entire amplicon sequence and is less dependent on the quantification window and on the putative cutsite

  Importance/significance needs to be demonstrated

In figure 3 are shown the results of template-based and substitutions detection. CRISPR-A is a versatile and agnostic tool for gene editing analysis. This means that it can be prepared for the analysis of gene editing of future tools, since the cut site or other elements of experiment design are not required. In addition, it has been shown that when a mock is used its performance is comparable to filtering by edition windows, avoiding the loss of edits when the cut site is slided.

• Analysis of the difference, in edit activity, comparing different cell lines

  Significant contribution. However - the methods need to be much better explained and the results better described in order for this to be useful to the community.

We have made an effort to try to be more clear in the description of the results.

• CRISPR-A supports the use of UMIs

  Mildly significant technical contribution. However - only addresses on-target. Also addressing off-target would have been significant.

The use of UMIs is something that has never been done before in this context. Sequencing biases are not taken into account and editing percentages are reported as observed. Being able to differentiate between different molecules at the beginning of the amplification sequence, allows a higher precision avoiding under or overestimation of each of the species in a bulk of cells.

In the case of off-targets, can be for sure done using sequencing the predicted off-target sites. In addition, there are other methods, like GuideSeq that can be used to discover off-targets, but this kind of data is out of the scope of CRISPR-A. Even that, we are aware of the importance of being able to analyse off-targets when in a context of a broad analysis platform and we will take these into consideration when participating in the building of crisprseq pipeline from nf-core.

• Interesting sequence pattern insights - like "...found certain patterns associated with low diversity outcomes: free thymine or adenine at the 3' nucleotide upstream of the cut site that leads to insertions of the same nucleotide, a free cytosine at the same place that leads to its loss, and strong micro-homology patterns that lead to long deletions "

  As stated - interesting.

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:

CRISPR-Analytics, abbreviated as CRISPR-A, is a web application implementing a tool for analyzing editing experiments. The tool can analyze various experiment types - single cleavage experiments, base editing, prime editing, and HDR. The required data for the analysis consists of NGS raw data or simulated data, in fastq, protospacer sequence and cut site. Amplicon sequence is also needed in cases where the amplified genome is absent from the genome reference list. The tool pipeline is implemented in NextFlow and has an interactive web application for visualizing the results of the analysis, including embedding the results into an IGV browser. The authors developed a gene editing simulation mechanism that enables the user to assess an experiment design and to predict expected outcomes. Simulated data was generated by SimGE over primary T-cells. The parameters and distributions were also fitted for 3 cell lines to make it more generalized (Hek293, K562, and HCT116). The process simulated CRISPR-CAS9 activity and the resulting insertions, deletions, and substitutions. The simulation results are then compared to the experimental results. The authors report the Jensen-Shannon (JS) divergence between the results. The exact distributions that served as input to the JS are not well defined in the manuscript (see below).

The authors also report an investigation of different alignment approaches and how they may affect the resulting characterization of editing activity. The authors examine three different approaches to increase what they call "edit quantification accuracy" (aka, in a different place - "precise allele counts determination" - what is this???): (1) spike-in controls (2) UMI's and (3) using mock to denoise the results. See below for our comments about these approaches. Moreover, the authors developed an empirical model to reduce noise in the detection of editing activity. This is done by using mock (control), and by normalization and alignment of reads with indels, with the notion and observation that indels that are far from the cut site tend to classify as noise. The authors then perform a comparison between 6 different tools, in the context of determining and quantifying editing activities. One important comparison approach uses manually curated data. However - the description of how this dataset was created is far from being sufficiently clear. The comparison is also performed for HDR experiment type, which can be compared only to 2 other tools. We see the potential contribution aspects of the paper to be the following:

1. NextFlow pipeline implementation is an important engineering contribution. Same is true for the interactive web application
2. The option to simulate an experiment to assess it is a nice feature and can help experiment design
3. Identification of amplicons when not provided as input
4. CRISPR-A seeks substitutions along the entire amplicon sequence and is less dependent on the quantification window and on the putative cutsite
5. Analysis of the difference, in edit activity, comparing different cell lines
6. CRISPR-A supports the use of UMIs
7. Interesting sequence pattern insights - like "...found certain patterns associated with low diversity outcomes: free thymine or adenine at the 3' nucleotide upstream of the cut site that leads to insertions of the same nucleotide, a free cytosine at the same place that leads to its loss, and strong micro-homology patterns that lead to long deletions " We further comment on the soundness of these contributions in our comments below and on their significance in our comments related to the general potential significance of the paper.

Major comments:

• Upon attempting to run an analysis from the web interface (https://synbio.upf.edu/crispr-a) and using: fastq of Tx and mock (control), the human genome and the gRNA sequence provided as input for the protospacer field, our run was not successful. In fact the site crashed with no interpretable error message from CRISPR-A.
• Moreover, there should be more clear context. There is no information regarding the type of experiments that can be analyzed with the tool. We figure it is multiplex PCR and NGS but can the tool also be used for GUIDESeq, Capture, CircleSeq etc.?
• No off target analysis. Only on-target
• No translocations and long/complex deletions
• We view the use of a mock experiment as control as a must for any sound attempt to measure edit activity. This is even more so when off-target events need to be assessed (any rigorous application of GE, certainly any application aiming for clinical or crop engineering purposes). We therefore think that all investigation of other approaches should be put in this context.
• It's a nice feature to have simulated data, however, it is not a good approach to rely on it.
• In p7 the authors indicate the implementation of three approaches to improve quantification. They should be clear as to the fact that many other tools and experimental protocols are also using these approaches. for example, ampliCan, CRipresso2 and CRISPECTOR all take into account a mock experiment run in parallel to the treatment.
• Figure1:
  • The figure certainly provides what seems to be a positive indication of the simulations approach being close to measured results. Much more details are needed, however, to fully understand the results.
  • Squema = scheme ??
  • What was the clustering approach?
  • What is the input to the JS calculation? What is the dimension of the distributions compared? These details need to be precisely provided.
  • What clustering/aggregation approach did the authors use here (average dist, min dist, dist of centers?)
  • 5 pairs were selected out of how many? Call that number K.
  • What does the order of the samples in 1C mean? Is 98_real closer to 22_sim than to 98_sim? If so then state it. If not - what is the meaning of the order? Furthermore - how often, over K choose 2 pairs does this mis-matching occur for the CRISPR-A simulator??
• "From the characterized data we obtained the probability distribution of each class" (page 3) - How is this done? how many guides? how many replicates? what is class? where do you elabore regarding it? how you obtain the distributions? More details of the methods need to be provided.
• The 96 samples used for development here - where are they taken from? This should be indicated in the first time these samples are mentioned. Namely - bottom of P6
• CRISPECTOR is not mentioned in the comparison in the section: "CRISPR-A effectively calls indels in simulated and edited samples" (Table S2). Is there a specific reason for having left it out?
• In the section "Improved discovery and characterization of template-based alleles or objective modifications" - part of the analysis was made over simulated data and then over real data. The authors state "it is difficult to explain the origin of these differences...". Thus, needs to be investigated in more detail ... :) (P5) Moreover - the performance over real data is, at the end of the day, the more interesting one for comparison purposes.
• We found no explanation of "spike-in"/"spike experimental data" across the entire article. There is some general language about lengths but the scheme is still totally unclear.
• Description of the 96 gRNAs? Is this data from REF26? If so - where do you state this? If so - how do the methods described herein avoid the unique characteristics of the data of REF26?
• "distance between the percentage of microhomology mediated end-joining deletions of samples with the same target was calculated and the mean of all these distances was used to reduce the information of the 96 different targets to a single one." (P6) What is the exact calculation used? which distance? How was clustering performed? What is the connection for gene expression?
• "we have fitted a linear model to transform the indels count depending on its difference in relation to the reference amplicon" (P7) - needs more explanation. Is this part of the pipeline?
• What is it "...manually curated data set"? (page 8)
• Section "CRISPR-A empiric model removes more noise than other approaches" - with what data were the comparisons performed? Moreover, how were the comparison criteria selected (efficiency and sensitivity)? The literature already used several approaches to compare data analysis tools for editing experiments. See for example ampliCan, Crispresso (1 and 2) and CRISPECTOR. Maybe the authors should follow similar lines.
• In the section "CRISPR-A empiric model removes more noise than other approaches" the authors state, incorrectly, that CRISPECTOR only reports the percentage of editing activity per site (there is much more information reported in the HTML report, including the type of edit event detected - deletion, of various lengths, insertions, substitutions etc). (P8)
• Section "CRISPR-A noise subtraction pipeline" describes a pretty naive method for noise subtraction (P12). Should be rigorously compared, for Tx vs Mock experiments, to CRISPECTOR and to CRISPResso2.
• "recalculated using a size bias correction model based on spike-in controls empiric data.." (P14). Where is the formula?
• Section "Noise subtraction comparison with ampliCan and CRISPECTOR" - fake mock was generated for comparison. We consider the avoidance of a Mock control in experiments designed to measure editing activity to not be best practice. It is OK to support this approach in CRISPR-A. However - the comparison to tools that predominantly work using a Mock control (including ampliCan and CRISPECTOR) should be done with actual Mock. Not with fake Mock .... (P15)

Minor comments:

• "Also, most of these tools lack important functionalities like reference identification, clustering, or noise subtraction" - bold part incorrect for CRISPECTOR, although it is not aiming only for CRISPECTOR
• "Same parameters and probability distributions were fitted for three other cell lines: Hek293, K562, and HCT11626, to make SimGE more generalizable and increase its applicability" (page 3) - how was fitted?
• What is the "nature of modification"? (P5)
• In the section "CRISPR-A effectively calls indels in simulated and edited samples" (P5) towards the end, the authors write that the CRISPR-A algorithm did not give good results for a few examples. They then state that this was corrected and then yielded good results. There is no explanation of what correction was done, if it was implemented in the code and how to avoid/detect it in further cases.
• Cell culture, transfection, and electroporation - explanation only for HEK293, what about the others? (P15)
• Typos and unclear wording:
  • "obtention" (P8)
  • "mico" >> micro (P 7,10)
  • "Squema" >> scheme (Fig.1)
  • "decombuled" (P10)
  • "empiric" >> empirical (P8 and other places)
  • "Delins" (P14)
  • "performancer" (P9)
  • Change word across all article - "edition" to "editing"
  • "...has enough precision to find" (P6) not related to "results" section
• Comments on figures:
  • Fig. 2C:
• No CRISPECTOR in the analysis
• It is simulated data only
• It is not violin plot as mentioned in the description
  • Fig 3A - Is it significant?
  • Fig. 4:
• A
• Each row/column is a vector of 96 guides?
• How is the replicate number decided? Is it a different experiment by date? What is separating between experiments? Rep numbers?
• B - Differential expression:
• How? did you measure RNA?
• Is the observed data in the figure sufficiently strong in terms of P-value?
• Where is the third cell-line?
  • Fig.13 - There is no A and B as mentioned in the text

Significance

We repeat the aspects of contribution, as listed in the first part of the review, and comment about significance:

• NextFlow pipeline implementation is an important engineering contribution. Same is true for the interactive web application
  • Significant engineering contribution. Nonetheless, we were not able to run the analysis. So - needs to be checked.
• The option to simulate an experiment to assess it is a nice feature and can help experiment design
  • An important methodology contribution
• Identification of amplicons when not provided as input
  • Not important in the context of multiplex PCR and NGS measurement assays, as amplicons will be known. Not clear what other contexts the authors were aiming at.
• CRISPR-A seeks substitutions along the entire amplicon sequence and is less dependent on the quantification window and on the putative cutsite
  • Importance/significance needs to be demonstrated
• Analysis of the difference, in edit activity, comparing different cell lines
  • Significant contribution. However - the methods need to be much better explained and the results better described in order for this to be useful to the community.
• CRISPR-A supports the use of UMIs
  • Mildly significant technical contribution. However - only addresses on-target. Also addressing off-target would have been significant.
• Interesting sequence pattern insights - like "...found certain patterns associated with low diversity outcomes: free thymine or adenine at the 3' nucleotide upstream of the cut site that leads to insertions of the same nucleotide, a free cytosine at the same place that leads to its loss, and strong micro-homology patterns that lead to long deletions "
  • As stated - interesting.

I have always believed that individualism is a very selfish behavior pattern. I agree that individualism can make one's life better, or let one have a higher quality of life. But people live in a collective. In a collective, too strong individualism may harm the interests of the collective. There is an old Chinese saying that when there is no lip, the teeth will be very cold. It means that the collective is the umbrella of the individual. Individualism can exist, but I think we should put collective interests first.

I think another relevant thing here is what the student's goal is. We talked a bit about this in class, but some students just want to get the paper/assignment done in the shortest time and with the least effort. They probably won't use this process because it's not a requirement like it was in high school. They may not even consider that it's worth writing the best paper they can and considering strategies to help them do so.

Reviewer #2 (Public Review):

By now, the public is aware of the peculiarities underlying the omicron variants emergence and dissemination globally. This study investigates the mutational biography underlying how mutation effects and epistasis manifest in binding to therapeutic receptors.

The study highlights how epistasis and other mutation effect measurements manifest in phenotypes associated with antibody binding with respect to spike protein in the omicron variant. It rigorously tests a large suite of mutations in the omicron receptor binding domain, highlighting differences in how mutation effects affect binding to certain therapeutic antibodies.

Interestingly, mutations of large effect drive escape from binding to certain antibodies, but not others (S309). The difference in the mutational signature is the most interesting finding, and in particular, the signature of how higher-order epistasis manifests in the partial escape in S309, but less so in the full escape of other antibodies.

The results are timely, the scope enormous, and the analyses responsible.

My only main criticisms walk the stylistic/scientific line: many of the others have pioneered discussions and methods relating to the measurement of epistasis in proteins and other biomolecules. While I recognize that the purpose of this study is focused on the public health implications, I would have appreciated more of a dive into the peculiarity of the finding with respect to epistasis. I think the authors could achieve this by doing the following:

a) Reconciling discussions around the mutation effects in light of contemporary discussions of global epistasis "vs" idiosyncratic epistasis, etc. Several of the authors of the manuscript have written other leading manuscripts of the topic. I would appreciate it if the authors couched the findings within other studies in this arena.

B)While the methods used to detect epistasis in the manuscript make sense, the authors surely realize that methods used to measure is a contentious dimension of the field. I'd appreciate an appeal/explanation as to why their methods were used relative to others. For example, the Lasso correction makes sense, but there are other such methods. Citations and some explanation would be great.

Lastly (somewhat relatedly), I found myself wanting the discussion to be bolder and more ambitious. The summary, as I read it, is on the nose and very direct (which is appropriate), but I want more: What do the findings say for greater discussions surrounding evolution in sequence space? For discussions of epistasis in proteins of a certain kind? In, my view, this data set offers fodder for fundamental discussion in evolutionary biology and evolutionary medicine. I recognize, however, the constraints: such topics may not be within the scope of a single paper, and such discussions may distract from the biomedical applications, which are more relevant for human health.

But I might say something similar about the biomedical implications: the authors do a good job outlining exactly what happened, but what does this say about patterns (the role of mutations of large effect vs. higher-order epistasis) in some traits vs others? Why might we expect certain patterns of epistasis with respect to antibody binding relative to other pathogenic virus phenotypes?

In summary: rigorous and important work, and I congratulate the authors.

Author Response

Reviewer #3 (Public Review):

In this manuscript, Kim et al. use a deep generative model (a Variational Auto Encoder previously applied to adult data) to characterize neonatal-fetal functional brain development. The authors suggest that this approach is suitable given the rapid non-linear development taking place in the human brain across this period. Using two large neonatal and one fetal datasets, they describe that the resultant latent variables can lead to improved characterization of prenatal-neonatal development patterns, stable age prediction and that the decoder can reveal resting state networks. The study uses already accessible public datasets and the methods have been also made available.

The manuscript is clearly written, the figures excellent and the application in this group novel. The methods are generally appropriate although there are some methodological concerns which I think would be important to address. Although the authors demonstrate that the methods are broadly generalisable across study populations - however, I am unsure about the general interest of the work beyond application of their previously described VAE approach to a new population and what new insight this offers to understanding how the human brain develops. This is a particular consideration given that the major results are age prediction (which is easily done with various imaging measures including something as simple as whole brain volume) and recapitulation of known patterns of functional activity in neonates. As such, the work will be of interest to researchers working in fMRI analysis methods and deep learning, but perhaps less so to a wider neuroscience/clinical readership.

Specific comments:

1) (M1) If I understand correctly, the method takes the functional data after volume registration into template space and then projects this data onto the surface. Given the complexities of changing morphology of the development brain. would it not be preferable to have the data in surface space for standard space alignment (rather than this being done later?). This would certainly help with one of the concerns expressed by the authors of "smoothing" in the youngest fetuses leading to a negative relationship between age and performance.

While projecting onto the cortical surface has its advantages, as suggested here18, several studies have also shown that with careful registration, such as in the current study, volumetric registration can yield comparable performance19. Regardless, we did attempt to directly generate cortical surfaces for our fetuses. We refer the reviewer to our response to the RE-M2 [page 9].

Regarding the “smoothing” effect in the youngest fetuses, we want to clarify that the smoothing effect in the scans of young fetuses is not unique to the choice of registration method. In other words, the same smoothing effect must be seen with cortical registration as well. Regarding this perspective, we kindly refer the reviewer to our response to RE-M1 [page 7]. Regarding the specific change made in the revised manuscript, we kindly refer to our response to R1-m5 [p21] or [page 9 line 191-213] in the main manuscript.

2) (M2) A key limitation which I feel is important to consider if the method is aiming to be used for fetuses is the effects of the analysis being limited only to the cortical surface - and therefore the role of subcortical tissue (such as developmental layers in the immature white matter and key structures like the thalami) cannot be included. This is important, as in the fetal (and preterm neonatal) brain, the cortex is still developing and so not only might there be not the same kind of organisation to the activity, but also there is likely an evolving relationship with activity in the transient developmental layers (like the subplate) and inputs from the thalamus.

The reviewer raises an important point. We agree with the reviewer that the subcortical region plays a critical role in fetal and newborn neurodevelopment. Unfortunately, our current VAE model cannot utilize such information without a major change in the model structure. We added this as a limitation of our study and discussed why our VAE model, in its current form, did not include subcortical areas. Please see our detailed response to RE-M1 [page 4] or [page 25 line 558-570] in the main manuscript.

3) (M3) As the authors correctly describe, brain development and specifically functional relationships are likely evolving across the study time window. Beyond predicting age and a different way of estimating resting state networks using the decoding step, it is not clear to me what new insight the work is adding to the existing literature - or how the method has been specifically adapted for working with this kind of data. Whilst I agree that these developmental processes are indeed likely non-linear, to put the work in context, I think the manuscript would benefit from explaining how (or if) the method has been adapted and explicitly mentioning what additional neuroscientific/biological gains there are from this method.

We appreciate the reviewer’s critical insights. In the revised paper, we included additional results that, we hope, can address the reviewer’s concerns. We believe that the strength of the VAE model is that, relative to linear models, it can be more generalizable across different datasets and ages (adult vs. full-term babies vs. preterm babies vs. fetuses). In the original manuscript, this was supported by the superior age prediction performance of the VAE over linear models when applied to different datasets covering the fetal to neonatal periods. Age prediction could also be done using other imaging modalities, as the reviewer pointed out. However, we do not think this undermines the potential impact of having the ability to accurately estimate age based on functional connectivity patterns. Brain function-structure relationships may not exactly be one-to-one20. It is entirely possible that for one disease, brain functional connectivity alterations precede structural changes such that delayed growth trajectories will first manifest in the functional space. There are also certain aspects of brain function that cannot be mapped directly to its structural characteristics (i.e., structural connectivity patterns). For example, brain changes its functional connectivity patterns dynamically over different brain states (resting vs. task-engaging)21, mental disorders (depression22, anxiety23, Schizophrenia24), cognitive traits25, 26, and individual uniqueness25, etc. Therefore, we believe that estimating the functional age of fetuses and neonates given their functional connectivity profiles may provide a biomarker for tracking neurodevelopment trajectories, allowing clinicians to identify deviations early and intervene in a timely manner if necessary. For these reasons, we believe that superior age prediction performance of the VAE model compared to linear models is scientifically significant.

The value of the VAE lies in its ability to capture FC features that are otherwise not modeled by linear strategies. For example, here, we showed that only the VAE model can extract latent variables representing brain networks that are similar across different datasets. In contrast, linear models, showed higher network pattern similarity between full-term and preterm infants within the dHCP dataset. This suggests that the VAE model can be a very useful tool for capturing common brain networks in datasets acquired using different recording parameters and preprocessing steps. Moreover, the VAE representations predicted age with higher accuracy compared to linear representations. Together, these findings show that the methodology is effective in extracting functionally relevant features of the brain. Please see RE-M1 [page 3] and R1-m13 regarding the specific changes made in the revised manuscript.

4) (M4) The unavoidable smoothing effect of VAE is very noticeable in the figures - does this suggest that the method will be relatively insensitive to the fine granularity which is important to understand brain development and the establishment of networks (such as the evolving boundaries between functional regions with age) - reducing inference to only the large primary sensory and associative networks? This will also be important to consider for the individual "reconstruction degree" - (which it would likely then overstate - and would need careful intersubject comparison also) if it was to be used as a biomarker or predictor of cognition as suggested by the authors.

Regarding the first concern, yes. Greater smoothing will tend to yield less granular network patterns; this is true for all representational models (not only VAE, but also models like ICA or PCA). This effect becomes ever more pronounced when representations consist of fewer components (e.g., IC50); the smoothing effect becomes stronger, leading to coarser brain patterns (see Fig. 3 in the revised manuscript). In this regard, higher number of components is desired, but on the flipside, IC maps with higher components are generally less interpretable. In short, there will always be trade-offs between interpretability and spatial resolution. Also, higher components tend to cause over-fitting issue, as shown in our age prediction performance across different datasets (worse performance in the IC300 vs. IC50). In this sense, what matters for the representations is how informative each latent variable (or component) is. In the revised Fig. 2, we showed that latent variables from the VAE model were more informative in representing rsfMRI than linear representations. It is also noteworthy that the smoothing effect of the VAE is comparable to IC300 (similar effect to manual smoothing at the level of FWHM=5mm; revised Fig. 3). Given above results, we believe the VAE model may be more suitable for investigating finer scale of brain networks, than linear models. The above perspective was updated in the revised manuscript as [page 23 line 506-511]:

"Another interesting observation was that the smoothing effect of the VAE is comparable to IC300 (similar effect to manual smoothing at the level of FWHM=5mm; Fig. 3). Given the above, we believe the VAE model may be more suitable for investigating finer scale of brain networks, than linear models. Perhaps, the VAE model with a greater number of latent variables (e.g., 512 or 1024 instead of 256 in the current VAE) can be utilized to find brain networks at finer scale."

On top of the points raised above, network mapping with linear models is limited when it comes to mapping the spatial evolution of brain networks over aging due to their linear nature. This limitation can be observed in the ICA study with dHCP dataset (Fig. 4 in 7). On the other hand, thanks to its nonlinearity nature, the VAE model may have a potential to observe the spatial gradient of brain network over aging, while this expectation needs confirmation. To that end, we revised our discussion to reflect our perspective. We refer the full change made in the revised manuscript to our response to R1-m13.

Author Response

Reviewer #1 (Public Review):

The manuscript by Shaikh and Sunagar addresses the question of the origin of spider venom proteins. It has been known for many years that an important component of spider venoms is a diverse group of small proteins known as disulfide-rich peptides (DRPs). However, it has not been clear whether this group of proteins has a common origin or evolved convergently in different lineages. The authors collected sequences of the genes encoding these proteins from publicly available genomes of spiders from a range of families. They aligned the sequences using the structural cysteines as guides and carried out a phylogenetic analysis of the different sequences, ultimately classifying the different proteins into over 50 super-families. One thing that is not clear from the text or from the references cited (I am not an expert on spider venom) is how many of these superfamilies were known before and how many are novel. There is also no clear indication of what criteria were used to define a subset of sequences as a superfamily. Nonetheless, the authors show that all these superfamilies have a single common ancestor, predating the divergence of araneomorphs and mygalomorphs and that the DRPs underwent independent diversification in each of these two lineages.

We have identified 78 novel superfamilies in this study and 33 were previously identified (Pineda et al. 2020 PNAS). We had previously described information in lines 90, 101 and 106 regarding the description of novel superfamilies from previous studies and the ones described in this study.

Line 90 “Recently, using a similar approach, 33 novel spider toxin superfamilies have been identified from the venom of the Australian funnel-web spider, Hadronyche infensa (9).”

Line 101 “This approach enabled the identification of 33 novel toxin superfamilies along the breadth of Mygalomorphae (Figures S1 and S2).”

Line 106 “Moreover, analyses of Araneomorphae toxin sequences using the strategy above resulted in the identification of 45 novel toxin superfamilies from Araneomorphae, all of which but one (SF109) belonged to the DRP class of toxins (Figures S3 and S4).”

Spider toxin superfamilies have been named after gods/deities of death, destruction and the underworld based on nomenclature introduced by Pineda et al. (2014 BMC genomics). We have now included this explanation in the manuscript under the methods and results sections. We have also provided additional details pertaining to this nomenclature in Table S1.

The authors also looked at selective forces acting on the sequences using dN/dS analyses. They reach the conclusion that there are different modes of selection acting on different sequences based on their role - defensive or predatory venoms - building on previous work by the lead author on venom sequence evolution in diverse animals.

All in all, this is an admirable piece of molecular evolution work, providing new data on the evolution of spider venom proteins. There are some confusions in terminology that need to be cleared up, and somewhat more context needs to be given for non-specialists as detailed in the points below:

We thank the reviewer for their constructive and critical suggestions, as well as the kind words of encouragement. Their suggestions have helped us in significantly improving the quality of our work.

Suggestion 1) Common names of the main spider infraorders should be given.

We thank the reviewer for their helpful input. We have now introduced spider infraorders with well-known spiders and their common names under the introduction section. Furthermore, we have also included a schematic representation of the spider phylogeny, and highlighted lineages under investigation as Figure 1.

Suggestion 2) Opisthothelae is not the common ancestor of Mygalomorphae and Araneamorphae, but the clade that encompasses those two clades. This incorrect statement appears in several places. Further on, it is stated that Opisthothelae is the common ancestor of all extant spiders. This is wrong both from a terminological point of view (a clade cannot be ancestral to another clade) and from a factual point of view, since there are extant spiders not included in Opisthothelae.

We thank the reviewer for pointing out this oversight. We have now corrected it to suborder Opisthothelae as the clade encompassing Mygalomorphae and Araneomorphae spiders.

Suggestion 3) Several proteins and proteins families are mentioned without being introduced, e.g. knottin. Please provide short descriptions.

We have now provided a short introduction to terms such as Knottin.

Reviewer #2 (Public Review):

This interesting study looks into the evolution of putative spider venom toxins, specifically disulfide-rich peptides (DRPs). The authors use published sequence data to gain new insights into the evolution of DRPs, which are the major component of most spider venoms. Through a series of sequence comparisons and phylogenetic analyses they identify a substantial number of new spider toxin superfamilies with distinct cysteine scaffolds, and they trace these back to a primitive scaffold that must have been present in the last common ancestor of mygalomorph and araneomorph spiders. Looking at the taxonomic distribution of these putative venom DRPs, they conclude that mygalomorph and araneomorph DRPs have evolved in different ways, with the former being recruited into venom at the level of genera, and the latter at the level of families. In addition, they perform selection analyses on the DRP superfamilies to uncover the surprising result that mygalomorph and araneomorph DRPs have evolved under different selective regimes, with the evolution of the former being characterised by positive selection, and the latter by purifying (negative) selection.

However, I don't think that in the current state of the manuscript these conclusions are robustly supported for several reasons. First, it seems that not all previously published data were included in the phylogenetic analyses that were used to identify new superfamilies of DRPs.

We have, indeed, analysed all spider toxin sequences available to date. We have relied on the signal and propeptide regions for identifying novel superfamilies, which is an accepted convention: Pineda et al. (2014 BMC Genomics); Pineda et al. (2020 PNAS).

Although many additional superfamilies can be identified, we have only retained those sequences for which there were at least 5 representatives for the identification of toxin superfamilies, and 15 representatives for selection analyses to ensure robustness. This filtering step ensured that the generated alignments, phylogenetic trees, and evolutionary assessments were robust and devoid of noise that stems from single-representative groups. Adding in those sequences would have enabled us to identify many more superfamilies, solely based on the signal and propeptide examination, but it wouldn’t have been possible to support them with other lines of evidence that were provided for all other superfamilies in this study, jeopardising the overall quality of the manuscript. Nonetheless, there is strong evidence that the left-out sequences are also related to the ones analysed in this study (Figure S10). In future, when more transcriptomes are sequenced, it would be possible to designate these newer toxin superfamilies with much stronger support.

Second, much of the data were obtained from whole-body transcriptome data, which leaves a degree of uncertainty that these data indeed derive from the venom glands that produce the toxins.

We respectfully disagree with the reviewer that ‘much of the data’ are from the whole-body transcriptomes. Nearly all sequences in our study are sourced from Pineda et al. (2014 BMC Genomics and 2020 PNAS), Sunagar et al (2013 Toxins), Cole and Brewer (2020 bioRxiv) and transcriptome sequence assembly data from established online repositories NCBI (NR and TSA) and ENA. All the above-mentioned studies (KS is a part of many of these) under their methods section clearly state that the transcriptomes were generated using mRNA isolated from venom gland tissue (BioProject accessions: PRJEB14734; PRJEB6062; PRJNA189679, PRJNA587301 and PRJNA189679, where source tissue type is designated as venom gland).

We would like to direct the reviewer’s attention to the following excerpts from reference papers from which data for this study has been sourced:

1. Pineda S et al. (2020 PNAS): “Three days later, they were anesthetized, and their venom glands were dissected and placed in TRIzol reagent (Life Technologies). Total RNA from pooled venom glands was extracted following the standard TRIzol protocol.”
2. Sunagar et al (2013 Toxins): “Paired venom glands were dissected out and pooled from nine mature females on the fourth day after venom depletion by electrostimulation. Total RNA was extracted using the standard TRIzol Plus method ...”
3. Cole and Brewer (2020 bioRxiv): “... the venom glands of each ctenid were dissected out, whole RNA was isolated from the venom glands …”

We would also like to point out that hexatoxins are widely studied and are some of the most well-understood spider venom toxins. Many representatives have been functionally characterised and shown to be potent in affecting prey and predatory species [Sunagar et al (2013 Toxins); Pineda et al. (2014 BMC Genomics and 2020 PNAS); Volker, et al. (2020 PNAS) - KS is a part of most of these studies as well]. However, the current technologies do not permit the high-throughput screening of the enormous diversity of toxins in spiders, which is why not every toxin sequence identified from the venom gland is functionally characterised. Nonetheless, venom researchers will not contest the role of these highly expressed venom gland proteins in envenoming, especially given that they share significant sequence identities with toxins that are functionally well-characterised.

The only exception to the above is non-ctenid araneomorph toxin superfamily sequences, which are retrieved from whole-body transcriptomes (Cole and Brewer; 2020 bioRxiv). The authors of the paper indicated these as putative toxins. As explained above, homologs of these peptides are well-characterised to be venom toxins. Additionally, in our phylogenetic trees (Figures 3, 4, S6 and S9), they are nested within the toxin clades, reaffirming their identity.

Third, the taxonomic representation of mygalomorph and araneomorph diversity in this study is so sparse that it becomes impossible to distinguish whether toxin recruitments have happened at the level of genera, families, or even higher-level taxa.

We respectfully disagree with this suggestion. The taxonomic breadth investigated in this study isn’t sparse. Analysed sequences belong to groups across the breadth of the spider phylogeny. To address this criticism, we are now including a schematic representation of spider phylogeny, where lineages under investigation are highlighted (Figure 1A). Given this broader taxonomic breadth, all of our interpretations are parsimoniously extendable to their common ancestors. For instance, we establish the common origin of all DRPs in the members of these widespread spider families. Therefore, not including sequences from other sister groups will not invalidate this hypothesis, and the most parsimonious explanation will be that the missing members too are likely to have DRPs in their venom (which is also a common understanding of the spider venom research). Whether DRPs dominate the venoms of these missing groups will only come to light upon investigation, but their presence in the venom is highly likely. Moreover, please do note that we have analysed nearly all sequences available in the literature to date.

As for the recruitment of the toxin superfamily at the taxon level, we would like to point out the phylogenies in Figures 2 and 3 that clearly show the differential recruitment events. We would also like to point out lines 120 and 136 state that this may not only be a result of recruitment and could arise from differential rates of diversification (also evident in other analyses presented in Figures 5 and Tables S2 and S3).

Line 120 “Interestingly, the plesiotypic DRP scaffold seems to have undergone lineage-specific diversification in Mygalomorphae, where the selective diversification of the scaffold has led to the origination of novel toxin superfamilies corresponding to each genus (Figure 2).”

Line 136 “However, we also documented a large number of DRP toxins (n=32) that were found to have diversified in a family-specific manner, wherein, a toxin scaffold seems to be recruited at the level of the spider family, rather than the genus. As a result, and in contrast to mygalomorph DRPs, araneomorph toxin superfamilies were found to be scattered across spider lineages (Figure 3; Figure S6; node support: ML: >90/100; BI: >0.95).”

Adding any number of missing lineages will neither change the fact that araneomorphs ‘appear’ to have recruited these superfamilies at the genera level, nor the family-level recruitment of toxin superfamilies in a large number of examined mygalomorphs.

We have now introduced a new figure (Figure 7) that highlights the different scenarios that explain the observed differences in the evolution of mygalomorph and araneomorph spider toxins. We have also included additional text in the manuscript to explain this better.

Fourth, only a selection of DRP superfamilies was used for natural selection analyses, without the authors explaining how this selection was made. Yet, they attempted to draw general conclusions about toxin evolution in mygalomorphs and araneomorphs, even though most of the striking differences they found were restricted to just two mygalomorph genera, and one family of araneomorphs.

From our experience and previous reports [Sunagar and Moran (2015, PLoS genetics); Sunagar, et al. (2012, MBE); Yang, Z. (2007, MBE)], the unavailability of enough sequences from datasets results in inaccurate estimation of omega values. For instance, if there are only a couple of sequences in a superfamily, both of which are slightly different from one another, then even these minor differences in them would be exaggerated. Hence, we have resorted to performing selection analysis on datasets for which there are at least 15 sequences. No doubt that this conservative approach reduces the number of datasets analysed, but it also ensures that our findings are well-supported. We have now clarified this in our manuscript under the methods section.

However, we did previously include sequences from all toxin superfamilies described to date in our alignment figure (Fig S10) and analysed their signal and propeptide regions. They were only excluded from selection analyses. It can be seen that they too are DRPs, but they belong to distinct superfamilies from the ones being described here.

If these concerns are addressed this study can shed important new light on venom toxin evolution in one of the most diverse venomous taxa on Earth.

We thank the reviewer for their constructive inputs and suggestions which have enabled us to make this manuscript more accessible to a wider audience.

Reviewer #3 (Public Review):

This work aims to elucidate the evolutionary origins of disulfide-rich spider toxin superfamilies and to determine the modes of natural selection and associated ecological pressures acting upon them. The authors provide a compelling line of evidence for a single evolutionary origin and differing factors (e.g., prey capture strategies and methods of anti-predator defense) that have shaped the evolution of these toxins. Additionally, the two major spider infraorders are claimed to have experienced differing selective pressures regarding these toxins.

The results presented here are novel and generally well-presented. The evidence for a single origin of DRP toxins in spiders is exciting and changes the paradigm of spider venom evolution.

The data are well analyzed, but the methods lack enough detail to reproduce the results. More information regarding the parameters passed to each software package, version numbers of all software employed, and models of molecular evolution employed in phylogenetic analyses are among the necessary missing information.

We thank the reviewer for their kind words and constructive and critical suggestions. Their suggestions have contributed towards improving the quality of our work. Upon their suggestion, we have now expanded the methods section to include more details.

The differences in the evolutionary pressures between mygalomorphs and RTA-clade spider DRP toxins are clear, but expanding RTA results to all araneomorphs may be overreaching. Additional araneomorph sequence data is available, despite the claims within this manuscript (e.g., see Jiang et al.. 2013 Toxins; He et al.. 2013 PLoS ONE; and Zobel-Thropp et al.. 2017 PEERJ). These papers include cDNA sequences of spider venom glands and contain representatives of inhibitory cysteine knot toxins, which are DRP toxins. These data would greatly enhance the strengths of the results presented herein.

In response to the expansion of RTA results to araneomorphs, we would like to point out that RTA comprises about 50% of the diversity recorded in Araneomorphae. The araneomorph data analysed in our study covers a range of araneomorph family divergence time Agelenidae (<70 MYA), Pisauridae (<50 MYA) and Theridiidae (~200 MYA, Magalhaes 2020, Biological Reviews 95.1). We report a strong signature of purifying selection influencing the evolution of araneomorph toxin SFs, despite the long evolutionary time separating them (50 - 200 MYA). We firmly believe that further addition of toxin sequence data from other groups will not deviate from the general trend of molecular evolution observed in both these lineages across such large period of time; barring certain certain exceptions (such as SF13 a defensive toxin identified from Hadronyche experiencing purifying selection; Volker, et al. 2020 PNAS).

We had initially excluded non-ctenid datasets from our analyses on account of poor sequence annotation and lack of representative sequence data. However, we have now incorporated Dolomedes mizhoanus (DRP) (Jiang et al. 2013 Toxins) and Latrodectus tredecimguttatus (non-DRP) (He et al. 2013 PLoS ONE) toxin dataset into our analyses, following reviewer’s suggestion. This has led to identification of 5 novel superfamilies, providing additional support to our spider venom evolution hypothesis.

"Individuals are social animals who are influenced by social preferences, social networks, social identities, and social norms: most people care about what those around them are doing and how they fit into their groups..."

https://www.theguardian.com/global/2019/nov/24/fear-of-missing-out-fomo-making-decision-biology-fobo-christmas-turkey#:~:text=Indecision%20when%20the%20decision%20is,or%20fear%20of%20missing%20out.

This idea is one which we are all familiar with: the fear of missing out, more commonly known as FOMO. The referenced article extends this idea beyond to FOBO, or the fear of better options. This is a great example exhibiting the rationale behind why many of us tend to think socially, as we are afraid of missing out on the better choices that may be presented to us. Consequentially, in decision-making, we may rely on others' decisions, as we are all aware, whether consciously or subconsciously, that collective thinking is "smarter".

!- integrating : individual and collective wellbeing - David Loy offers a clear explanation of the entangled nature of self-and-other - we begin the journey of self improvement due to problems in our personal lives, that is the motivation - but as we continue the journey, we may discover that it is our separation from others and from nature herself that is the cause of our dis-satisfaction - David quotes Joanna Macy, who said that "the world has a role to play in our awakening"

!- Micheal Hudson : debt writedown - At a certain point, Governments of 3rd world countries who are so debt trapped may simply decide to write down the debts and start over - They may reach a point where instead of servicing the debt of the 1%, they decide its not worth it and save their own economies, freeing themselves from World Bank and IMF debt conditions - It's just as radical a move as your suggestion to stop tax evasion by closing down all offshore banks

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Reply to the reviewers

Dear Editor,

Please find below our detailed responses (in black font) to the Reviewer's comments (in blue). In addition, and to the request of Reviewer #1, we added a PDF file called “Reply to the reviewers MS data” that shows MS/MS and quantification information of representative peptides which were selected based on their (different) caspase/control abundance ratios. We thank the reviewers for their time and valuable comments.

NOTE: our original reply includes several tables and graphs that were not incorporated into our reply shown below

Reviewer #1

Page 4 - In contrast to the hindrance of N-terminal amine ionization by Nt-acetyl groups concluded by the authors, previous studies reported an improved MS-scoring if α-amino-acetylated (tryptic) peptides by the higher numbers of b and y fragment ions observed as compared to α-amino-free (tryptic) peptides (e.g. (Staes et al., 2008)). It is rather the lack of any N-/C-terminal charged residue in case of Lys-N type N-termini which makes LATE less suitable for studying N-terminal protein acetylation.

We thank the reviewer for this comment. In the HYTANE and LATE workflows, only peptides with modified N-termini (by dimethylation or acetylation) are observed after negative selection, hence we argue that the important comparison here is between Nt-acetylated peptides and Nt-dimethylated peptides with (as in HYTANE) or without basic residue (as in LATE). While we are aware of the study by Staes et al 2008 (PMID: 18318009), we do not believe it contradicts our claim as it discusses the difference between Nt-acetylated peptides and peptides with free N-termini.

As we indicated in the manuscript (page 5 in the last sentence of 1st paragraph), we observed less overall peptide identifications in LATE, which was expected due the lack of basic C-term residue. The reduction of identification was more pronounced for Nt-acetylated peptides. However, this still does not exclude LATE as a useful tool for identification of such peptides.

Of note, the overall fragmentation coverage we obtained by LATE and HYTANE for Nt-acetylated and Nt-dimethylated peptides was similar. See the figure below.

Hence, following Cho et al 2016 (PMID: 26889926), we suggest that the difference in ionization of Nt-dimethylated peptides vs Nt-acetylated peptides is the more dominant factor in peptide identifications.

Figure 1:relative Ion coverage for modified peptides in LATE and HYTANE

Page 4 - Besides indication the retained N-termini with high relative caspase-3/control abundance ratio's as putative caspase-3 proteolytic products, also indicate that unique peptides were retained, as many such singletons were reported in previous (caspase-focussed) degradomics studies making use of differential proteomics (e.g. (Van Damme et al., 2005)). Therefore the cut-off ratio of 2 rather seems unsubstantiated, unless the cellular proteomes of so-called control cells were affected by caspase activation. As such, showing some representative MS-spectra of neo-N-termini would be informative.

We thank the reviewer for this comment. We agree that caspase-3 cleavage generates many singletons. This is indeed what we observed in the in vitro experiment as shown in Figure 2B by the long straight lines at Log2(caspase-3/control) >10. We also add here histograms of the obtained ratios that we hope will make this clearer. We chose a cut-off of 2 due to the basal activity of proteases (including caspase-3) as we did not add caspase-3 inhibitors to the cell lysate. In addition, peptides derived from the putative caspase-3 cleavages in the in vitro experiment were required to be identified only in the caspase-3-treated samples (i.e. to appear only with the heavy labeling). Minor changes to Figure 3 legend have been introduced accordingly. As can be seen in the table below, with a cut-off ratio of 2 (Log2=1) and selection of cleavage sites after D or E we identified >98% of the cleavage sites that were identified only in the caspase-3 treated samples (column text in blue). This rate did not change when the cut-off was set to 8 (Log2=3). Therefore, we have chosen to maintain our selection criteria and cut-off ratio as used before for both experiments.

Figure 2: Histograms of Log2(Caspase/control) ratios indicating the large number of singleton peptides (marked with arrows)

Table 1: In vitro experiment selection ratio

Method

Cutoff

Time

Sites

Sites identified only caspase-3 treated samples

% of caspase-treated only sites (singleton)

Sites D/E with light

Sites after D/E no light

% of singleton

LATE

Log2=1

18H

936

906

96.8%

798

786

98.5%

LATE

Log2=2

18H

884

866

98.0%

767

759

99.0%

LATE

Log2=3

18H

819

810

98.9%

722

716

99.2%

HYTANE

Log2=1

18H

1186

1159

97.7%

1037

1032

99.5%

HYTANE

Log2=2

18H

1128

1110

98.4%

998

993

99.5%

HYTANE

Log2=3

18H

1035

1025

99.0%

924

919

99.5%

LATE

Log2=1

6H

755

732

97.0%

656

645

98.3%

LATE

Log2=2

6H

711

700

98.5%

630

623

98.9%

LATE

Log2=3

6H

671

666

99.3%

601

597

99.3%

HYTANE

Log2=1

6H

1028

988

96.1%

899

890

99.0%

HYTANE

Log2=2

6H

955

931

97.5%

851

844

99.2%

HYTANE

Log2=3

6H

882

871

98.8%

795

791

99.5%

LATE

Log2=1

1H

445

423

95.1%

380

372

97.9%

LATE

Log2=2

1H

411

402

97.8%

361

355

98.3%

LATE

Log2=3

1H

386

380

98.4%

344

338

98.3%

HYTANE

Log2=1

1H

593

559

94.3%

513

506

98.6%

HYTANE

Log2=2

1H

544

532

97.8%

488

482

98.8%

HYTANE

Log2=3

1H

508

498

98.0%

461

455

98.7%

In the cell-based experiments of caspase-3, we induced apoptosis on both cell types (over-expressing caspase-3 and the control). Therefore, in this case, as the reviewer has also mentioned, a cut-off of 2 is appropriate because the control cells are also affected by caspase activation. Following the reviewer’s request we have added (in a separate PDF file) several representative MS/MS spectra of neo-N-term peptides and their corresponding quantification data.

Page 4 - replace 'without labelling of lysine residues (epsilon-amines)' to 'without notable labelling of lysine residues (epsilon-amines)', as residual labelling of lysine side-chains was observed. Also in case of the latter, do note that reduced MS-ionization potential might impact labelling efficiency calculation, and chromatographic detection of labelling efficiency should be considered to conclusify this finding.

We thank the reviewer for this comment. We have changed the sentence as requested (Page 4 marked in red). Regarding the labeling efficiency calculations, it is true that ionization potential might affect them. We used a common way to test this aspect (see e.g. Hurtado Silva et al 2019 (PMID: 30934878)) and we are not aware of any reduction in ionization potential following lysine dimethylation. Although we did not study this aspect thoroughly, we frequently observe the opposite: that dimethylation improves MS detections.

Page 6 - The experimental setup comparing caspase-3 overexpressing and ABT-199 induced versus ABT-199 induced cells will be highly biased as it will not be able to detect efficient caspase-3 cleavages (Plasman et al., 2011), as such cleavage events are complete and thus do not require any additional overexpressed capase-3. I see this as an important flaw and the authors should demonstrate that the list also includes efficient caspase-3 cleavages.

We thank the reviewer for highlighting this important aspect. We agree that with our setup, we can miss some efficient cleavages of caspases-3. We acknowledged this caveat in the original text (page 6), but chose to perform our experiments this way in order to highlight cleavages that are affected by caspase-3 expression. To address the reviewer’s comment we have added new experiment and data on caspase cleavages that occur following ABT-199 treatment in HCT116 cells without overexpression of caspase-3. The focus of this experiment was on the relatively short time points following the ABT-199 treatment when no cell death is observed based on XTT assay (see Supplement Figure 6B). This experiment was used to prove that neo-Nt-acetylation of NACA is an early event in apoptosis (Figure 5 E-F page 12). We also used this experiment as an indication of the appearance of efficient cleavages. As can be seen from Supplement Table S10, if we consider all 3 time points of the ABT-199 treatment, we quantified 106 cleavages with free neo-Nt that were cleavages after D and were identified only in the ABT-treated samples. We refer to such cleavages, which appeared prior to noticeable cell death, as "efficient cleavages". Out of these efficient cleavages, 82 were also identified and quantified in the cell-based experiment with overexpression of caspase-3. Twenty efficient cleavages show a high ratio (≥2) in both experiments. Fifty six efficient cleavages had a high ratio in the new experiment and ratio below 2 in the cell-based experiment with overexpression of caspase-3. This supports our original claim regarding efficient cleavages and addresses the reviewer’s concern regarding our ability to identify efficient caspase-3 cleavages with the experimental setup of HCT116 cells overexpressing caspase-3.

Page 12 - The setup doesn't permit ORF N-terminal stability per se, rather the cleavage susceptibly of N-termini holding (a) putative caspase-3 cleavage site(s). Please adjust accordingly. Again since the setup might have missed efficient cleavages, the assessment might be biased.

Thanks for the comment. As requested, the word “stability” has been deleted. As discussed above, we demonstrate that our setup does allow the identification of efficient cleavages and hence our basis for believing that the assessment is not biased. Please also refer to our reply to the next comment.

The claim that Nt-acetylation is protective for caspase-3 cleavage should be validated by monitoring cleavage efficiency of an Nt-acetylated versus an Nt-free variant (e.g. by introducing a Pro residue at AA position 2, or comparing cleavage efficiencies in corresponding NAT knockdown versus control cells) of an identified caspase substrate (i.e. a substrate holding a caspase-3 cleavage site in its N-terminal sequence) versus its Nt-free counterpart

Thanks for raising this point. The reviewer's suggestions have some caveats: a mutation at a protein’s N-terminus in order to generate an Nt-free variant can alter its stability or function and NAT knockdown might have a profound biological impact on the cells. Therefore we chose a different way to study this aspect by selecting from our data ORF N-terminal peptides that were identified with both free N-termini and acetylated N-termini (i.e. the same peptide was identified in some PSMs as acetylated and in other as dimethylated). We managed to find 136 ORF N-terminal peptides that were quantified in both forms, and out of these, 122 contained Asp or Glu residues (the putative caspase cleavage motifs). We added the comparison of the abundance ratios of these peptides in Figure 4C (see also below). It shows a remarkable difference between the groups when the Nt-acetylated peptides ratios did not change as a result of caspase-3 overexpression while the peptides with free Nt were identified mostly in the control cells (negative Log2(caspase-3/control)). Comparison of the 14 ORF Nt-peptides that do not have Glu or Asp in their sequence shows no difference (see below).

Figure 3: Abundance ratio distributions of the ORF Nt peptides identified with both Nt-acetylated and free Nt in HCT116 cells overexpressing caspase-3 and in the control. A. Comparison of peptides that contain putative caspase cleavage in their sequence (D or E) B. comparison of peptides without putative caspase cleavage

These results provide additional support for the notion of the protective or shielding effect of Nt-acetylation against caspase-3 cleavage.

Page 12 - Since post-translational Nt-acetylation of neo-N-termini could be reproduced in vitro in the non-dialyzed sample, enzymatic over chemical Nt-acetylation should be demonstrated (e.g. by the use of a (bisubstrate) NAT inhibitor).

We think this is an interesting idea for future work. Yet, in our opinion, the fact that only very few neo-Nt-acetylated peptides were affected in vitro and that a similar trend of few selected neo-Nt-acetylation targets was shown in the cell-based experiments indicates that this process is enzymatic and not chemical in nature.

Other concerns:

Abstract - The abstracts holds complex/incorrect sentence constructions (e.g. simply indicate 'Protein N-termini', '... undergo ... processing by proteases' (currently: 'not be processed by proteases').

Thanks for pointing this out. We have changed the abstract accordingly.

Abstract - 'To expand the coverage of the N-terminome' only applies when this is used in conjunction with other negative enrichment strategies as by itself, LATE doesn't intrinsically provide a better coverage of the N-terminome (this is also noted at page 2).

We thank the reviewer for pointing this out. We have changed the abstract accordingly.

Change 'that cannot be identified by other methods' to 'that cannot be identified by other negative selection methods'

Thanks for pointing this out. We believe that our description here is appropriate as we explicitly state “some of which cannot be identified by other methods”.

Page 1 - Suggestion to change 'Proteases are typically described as degradative enzymes' to 'Proteases used to be described as degradative enzymes'

Changed as suggested.

Page 1 - Not really correct how written; 'N-terminomics methods highlight the N-terminal fragment of every protein (N-terminome)'

Changed as suggested.

Page 2 - Positive selection techniques .... Enrichment of unblocked (or Nt-free) N-termini

We are not sure what the reviewer had in mind here but have added the text in the brackets

Page 2 - Besides altering charge, Nt-acetylation also alters hydrophobicity ...

Changed as suggested.

Page 2 - remove 'to better chart'

Changed as suggested.

Page 2 etc. - Do note that caspase-3 can potentially activate downstream caspases in vitro

Following this comment, we have added a sentence on Page 5 with this reservation

Page 3 - functional crosstalk between proteolysis and neo-Nt-acetylation has already been demonstrated in the case of co-translational acting methionine aminopeptidases and chloroplast N-terminal acetyltransferases. Adjust accordingly.

We thank the reviewer for highlighting this aspect, although we used the term “neo-Nt-acetylation” which we used to mark that this is not the common (co-translational) acetylation. To assure that this is more clear we have added the words “post-translational” to better define the novelty of our findings.

Page 3 - when discussing the identification of ORF N-termini, note that some of the strategies of which note when used to enrich for in vivo blocked N-termini, can also be used without blocking/labelling of Lys residues, and thus trypsin will also result in Lys-ending peptides. This is important to consider in this context.

Following the reviewer's remark we have changed the sentence so it now states: “Many of these N-terminomics methods……”

Page 3 - remove the following sentence part; '... or run individually which can be useful for quantifying naturally modified N-termini.', since also a differential/labelled proteomics setup enables such assessment. Related to this, the authors should comment on the observation that much fewer (i.e. less than 40%) Nt-acetylated N-termini were identified by LATE as compared to HYTANE. How is this reflected in the number of PSMs? Probably these difference are further intensified when considering PSMs.

We have changed the sentence as suggested.

Regarding the reduction of Nt-acetylation, we thank the reviewer for this question as it led us to find typos in the numbers in Figure 1E which are now corrected. These typos did not change the overall observation that with LATE we identify fewer Nt-acetylated peptides than Nt-free (dimethylated) peptides. As the reviewer anticipated (see below), the reduction in LATE-based “contribution” to the identification of Nt-acetylated peptides as opposed to the identification of dimethylated peptides, is pronounced when considering PSMs but this is not much different than the peptide-based data. Therefore, we prefer to keep the current presentation of Figure 1E.

Figure 4: Comparison of HACAT cells N-terminal peptides identification with LATE and HYTANE when considering peptide sequences and PSMs. Peptides identified with both methods are in green and those that are unique to one method are in blue. Shared peptides were determined based on the sequence of the first 7 amino acids of the identified peptides. A. comparison for peptides with dimethylated N-terminal (free Nt) B. comparison for Nt-acetylated peptides.

Page 6 - Informative to indicate how many of the in silico predicted putative DEVD P4-P1 cleavages were actually present in the list of 2049 putative cleavages identified.

In our dataset, we identified 17 cleavages after DEVD motif. 11 were identified only with HYTANE, 3 were identified by both methods, and 3 more were identified only with LATE. Of note, it seems that in large-scale proteomic studies of apoptosis, the number of caspase cleavages after DEVD motif is quite low. For example, in the CASBAH database (PMID: 17273173__) __there are 10 reports of such cleavage out of 391 reported sites, and in DegraBase (PMID: 23264352) that combined many different apoptotic experiments there are 64 reported DEVD sites out of a total of 6896 P1-Asp sites.

Page 6 - Unclear if any of the of 2049 putative cleavages, included non-canonical P1 cleavages besides the P1 Asp and Glu cleavages identified.

These are 2049 putative cleavage sites with P1 Asp or Glu. We have changed the text to make it clearer.

Page 6 - Were the 'regular' cells mock transfected?

No. The control cells used for the cell-based experiments were the non-transfected cells from the same culture of HCT166. We chose this option to guarantee that exactly the same cells that were grown in the same dish went through the same FACS sorting as a control.

Page 6 -Important to note that an ORF can have multiple N-termini besides neo-N-termini (e.g. in the case of alternative translation initiation)

Thanks for the great point. We have added an indication if the neo-N-termini site has been reported as an alternative translation initiation site to all of the results of the cell-based experiments (Supplementary Tables S4, S5, S6, S9). We also changed the Figures and text accordingly. Our analysis of reported/unreported neo-N-temini is based on the TopFind database which includes information about alternative translation initiation sites from TISdb. Of note, since our focus is on caspase cleavages and we further select putative cleavages based on D/E in P1 and fold change, out of 973 peptides that we reported as putative caspase cleavage (Table S6) only one is in the vicinity of an alternative initiation site.

Page 6 - The authors should be more careful with generalization when comparing LATE and HYTANE (and other degradomics approaches) as in this study LATE was only applied for the identification of caspase-3 neo-N-termini, which by its extended substrate specificity might hold specific features enabling the preferred detection by one technique over the other. Also note that as compared to less recent studies, evidently the MS instrument used is a key factor in the increase in cleavages reported in the current study.

It is conceivable that caspase cleavage may differ from other proteases and thus theoretically work better with LATE, but we fail to see why this would also be the case for other N-terminomics method (like TAILS, Subtiligase, CoFRADIC, ChaFRADIC etc). We showed that LATE provides additional ORF Nt peptides identifications and demonstrated its effectiveness in E. coli (Supplement Figure S2) also, which has a proteome with a different amino acid composition to the human proteome. Furthermore, using LATE in the cell-based experiment led to the identification of many neo-Nt-peptides that do not match caspase cleavage patterns (as indicated for both HYATNE and LATE in Figures 3E and 3F). We reviewed the text again, and believe that we have used a fair description of the results especially when we compared them to previous studies.

Page 9 - The authors should provide some info/supporting statistics in the text regarding the new putative substrates showing GO-enrichments (compared to which control?) similar to previously reported caspase-3 substrates.

The results of the GO enrichment analysis are presented in Fig. S8 and details about how the test was performed are provided in the Materials & Methods. In the revised version, we are including the numerical data that include results of the statistical tests per GO term as Table S12. The enrichment analysis was performed with respect to the whole human proteome.

Page 11 - Indicate that the 11 neo-N-terminal peptides of which note are the neo-Nt-peptides matching (signal peptide) cleavages indicated in the Uniprot database. Were any corresponding di-methylated neo-N-termini of these cleavages identified? In case of the 'other' proteolytic cleavages of which note, refer to these as not-annotated in UniProt.

We thank the reviewer for pointing this out. We have added an indication that this analysis is based on UniProt annotations. Yes, all of the reported 11 neo-Nt-Acet peptides shown in Figure 4 were also found as neo-Nt-DiMet peptides.

Page 11 - post-translational Nt-acetylation is abundant in plant and the responsible NAT has been identified, please reference these studies as well.

We thank the reviewer for pointing this out regarding page 11. A relevant reference has been added in Page 11. In the discussion, we already referenced Nt-acetylation in plants in the discussion as well (see page 14).

Page 12 - Define 'undoubtedly dependent on caspase-3 cleavage'

We thank the reviewer for pointing this out. The word ‘undoubtedly’ has been deleted.

Page 14 - The NAA30 discussion is not really relevant for the discussion of the post-translational Nt-acetylation of mitochondrial neo-N-termini.

We thank the reviewer for pointing this out. This sentence has been deleted.

Viewing the harsh in vitro caspase-3 cleavage condition used, namely 1 µg caspase 3 over 20 µg protein, the P1 specificities of all identified neo-N-termini should clearly be shown.

The P1 specificities of all neo-N-termini found in the in vitro experiment are listed in the supplementary tables S2 and S3. For the reviewer’s convenience, we are providing the table with the P1 specificities below:

Since acetylation of serine and threonine residues are reported forms of post-translational modification, and many so-called past-translational Nt-acetylated neo-N-termini harbour such AA residues in their N-terminal sequence, b-ion coverage for these neo-N-termini should be provided/inspected.

We are not sure that we understand this comment. O-Acetylation of amino acids refers to their side chain. Since we are using Di-methylation labeling in both HYTANE and LATE, if we have a peptide with O-acetylated Ser or Thr at its first position, it is possible to distinguish it from the same peptide with Nt-acetylation by MS1 as illustrated in the following table for a hypothetical peptide SAAANPELKR (mass is MH+1)

Regardless we include in the manuscript MS/MS spectra of NACA Neo-Nt-acetylated peptide by HYTANE and LATE

Reviewer #2

Major suggestions:

• The LATE method relies on digestion with LysN. Can the authors comment on the digestion efficiency of the samples where the LATE workflow was applied?

The LysN digestion details that we used were based on vendor (Promega) instructions combined with details from the Nature Protocol paper by Giansanti et al 2016 (PMID: 27123950__)__ that describes optimized digestion protocol for LysN. We tested LysN efficiency in terms of the identification of missed cleavage and found that it performed very well with a missed-cleavage rate of

• The authors state that the number of peptides with acetylated N-termini was lower compared with HYTANE. Yet, the Nt-acetylation can occur co-translationally in approximately 85% of human proteins.

Did the authors consider optimizing the method (e.g. by fractionating the sample) for better identification of such peptides?

We thank the reviewer for this important comment. We are certain that it is possible to improve the output of LATE by fractionation and/or optimization by changes to the LC gradient as it is well established for most, if not all, bottom-up proteomics methods. In this work, we concentrated more on the proof of concept of the methodology and hence chose to work without fractionation. We performed one attempt to optimize the LC gradient but found that the results were not significantly different, and we thus used the same LC-MS methods that have been optimized for trypsin.

Regarding the reduced identification of Nt-acetylated peptides, as we state in the manuscript following Cho et al 2016 (PMID: 26889926), we believe that this is mainly due to the reduced ionization efficiency of Nt-acetylated peptides compared to Nt-dimethylated peptides which is more pronounced when a C-terminal positive charge is missing (due to LysN digestion).

Also, were the results of the study compared with searches done using other proteomic pipelines (e.g. FragPipe)?

Unfortunately, when we started this project, MS-Fragger did not support LysN as the digesting enzyme. At the time TPP also provided better visualization and quantification support than FragPipe. Recently, we found that MSFragger is faster while providing similar identifications but we are not convinced of the quantification output via FragPipe. In addition, we performed comparisons of Comet to X!Tandem and while the searches took longer than with Comet, the total number of IDs did not improve significantly.

Can the authors provide details on the settings used for searches done in COMET, especially for the samples treated with LysN?

The settings are provided in Table S10 in the supplementary information (Page 14 of the PDF file).

"Fractions containing relatively pure caspase-3 were pooled together and dialyzed against 20 mM HEPES 7.5, and 80 mM NaCl. Aliquots of the protein were stored at -80{degree sign}C"

o What exactly is meant by 'relatively pure'?

We apologize for the inaccurate description. The relevant text has been updated (Page 17) and now explains that this was based on Coommasse stain SDS-PAGE.

Minor suggestions:

• Please check the link for the Github as this reviewer could not open it.

We thank the reviewer for pointing this out. We corrected the link. In any case, the relevant scripts can be found here: https://github.com/OKLAB2016

• Please correct the spelling.

The manuscript was proofread.

Comments regarding figures:

• Figure 2:

o All figures comparing LATE and HYTANE utilize color green for LATE. Yet, in figure 2G, HYTANE is depicted in green-like color. Please consider staying consistent with the color scheme.

We thank the reviewer for this comment. Done as suggested.

Reviewer #2 (Significance (Required)):

Significance:

• The LATE method provides an excellent way to study proteases in vitro or in cell-based experiments. It enables deep investigation of N-terminome based on a simple and cost-effective workflow that utilizes digestion with LysN followed by chemical derivatization of α-amines. This approach allows for the identification of N-terminal peptides that may escape detection by other N-terminomics methods. With LATE, proteases' cleavage sites that might not so far be reporter due to technical limitations, can be studied and characterized. Hence, LATE is a useful addition to the N-terminomic toolbox.

We thank the reviewer for the positive comments and general assessment of LATE.

Reviewer #3

In this manuscript, Hanna et al. report LATE, an N terminomics method similar to N-TAILS and HYTANE, with modifications that enhance or change coverages of the N-terminal proteome in proteomics datasets. LATE relies on selective N-terminal modification of protease-treated, LysN digested samples, enabling internal peptides to be depleted based on the presence of the unblocked lysine epsilon amine. Using LATE in comparison with HYTANE, the authors identified a large number of both known and unknown caspase-3 cleavage sites, both in vitro and in vivo. Because LATE enables identification of both proteolytic neo-N termini and natively blocked N termini such as those that are acetylated, the authors were able to discover a number of post-translationally acetylated proteolytic neo-N termini. This finding points to potential functional cross talk between apoptotic proteolysis and Nt-acetylation. Overall, this is a very nice manuscript that adds a valuable new tool to the N-terminal proteomics toolbox. However, the manuscript could be improved by addressing the following questions and comments.

We thank the reviewer for this assessment.

1. One of the benchmark points used to describe the need for a new technology such as LATE is the idea that there are 134 putative caspase-3 substrates in the human proteome, of which only about half can be identified based on ArgC cleavages. However, the 134 substrates seem to include only those that have the exact canonical DEVD motif. Many more substrates than this are already known for caspase-3. For example, >900 caspase-3 substrates were identified by Araya et al. alone. It might make more sense to apply a position-specific scoring matric to the human proteome to predict a maximum number of possible caspase-2 cleavage sites and how many would be expected to be identified using other technologies. Otherwise, please provide a rationale for why these 134 putative caspase-3 sites are representative.

The reviewer is correct. Indeed, most of the identified caspase-3 cleavage are not exact matches to the DEVD motif. We used the DEVD as an example to illustrate the added value of using lysine-based digestion together with ArgC. We obtained a similar trend with some variations when we tested the feasibility of the identification of the human ORF Nt-peptides, E. coli ORF Nt-peptides and more. We are quite confident that any prediction will show a relatively similar distribution. To demonstrate this, we show here the relative contribution of each method for the identification of any peptide that begins after Asp in the human proteome.

While the distributions are not identical, they are very similar, and the specific additions from LATE (LysN) are between 20% to 22% out of the total and it can help to expand the coverage by 42% to 45%.

It is definitely plausible and have been previously demonstrated that selective N-terminal demethylation can be achieved under the right reaction conditions, and I do not doubt that it has been achieved here. However, I do not understand how the authors were able to conclude that alpha-amines are blocked with 95% efficiency and lysines are blocked at

This is a very good point. The reviewer is correct and indeed we don’t have a way to establish if the dimethylation is on the side chain amine of lysine or on its N-terminal amine. A partial support for our claim is from labeling experiments that we (and others) conducted with tryptic and LysC peptides that clearly demonstrate that under the specified labeling conditions, 95% of the N-terminal amines are labeled and not the lysine side chain amines. However, at the end of the day, this does not change the outcome of LATE.

Related to the above comment, Table S10 seems to indicate that MS/MS data from LATE were searched with dimethylation as a fixed modification at the N terminus. Were LATE samples searched with different parameters to generate Figure 1C? Are the dimethylated Ks identified mostly from missed cleavages and therefore not at the N terminus?

We thank the reviewer for pointing this out. The search parameters used for the generation of Figure 1C have been added to Table S10. The reviewer is correct, the few dimethylated Ks identified in the search used for Figure 1C are mostly from missed cleavages.

For both the in vitro and in vivo experiments, how many of the new caspase-3 cleavage sites occurred in proteins that were not previously known to be caspase substrates?

In the in vitro experiments, we identified cleavages of 372 proteins that were not reported as caspase-3 substrates based on the databases we used as references. A line specifying this number was also added to text on page 7. In the cell-based experiment, we identified putative caspase-3 cleavages of 67 proteins that were not reported so far as caspase-3 substrates. This information has been added to the main text on page 10. We have added columns indicating the known/unreported protein substrates to Tables S2, S3, S4, S5, and S6.

For the experiment in cells, can the authors explain the rationale for comparing cells in which apoptosis is induced with ABT-199 to ABT-199-treated cells with caspase-3 overexpression? What is the advantage over comparing ABT-199 treated cells to untreated cells

Great question. An N-terminomics study of “common” apoptosis would lead mainly to the identification of effector caspases (caspase-3 and -7) substrates. Our aim was to focus mostly on the caspase-3 cleavages that occur in the cell during apoptosis. In choosing this gain-of-function approach we were motivated by the idea that it couldprovide new insights that would otherwise go undetected when using knockout or other loss-of-function approaches. The advantage of this system over comparing ABT-199 treated to non-treated cells (which we have now added as well) is that it can enhance the identification of caspase-3 specific cleavages.

Can the authors discuss the timescale of cell death in ABT-199 treated cells vs. ABT-199 treated caspase-3-overexpressing cells. Ideally, data showing cell viability over time (e.g. Cell Titer Glo or MTT assays) would be presented, but if the authors could at least describe whether apoptosis is accelerated in the caspase-3 overexpressing cells, it would be helpful.

Great suggestion. Following the reviewer’s suggestion we have characterized the effect of caspase-3 overexpression of the cells by XTT assay, and indeed caspase-3 overexpressing cells do show accelerated cell-death in response to ABT199 compared to non-transfected cells. These results are now presented as Supplement Figure S6B and are mentioned in the results section.

The authors say that in their experimental design, they expect to see no difference between ABT-199 only and ABT-199/caspase-3 overexpression for substrates that are cleaved efficiently by endogenous caspases. If the new caspase-3 substrates are not cleaved efficiently by endogenous caspase-3, this seems to call into question their physiological relevance. Can the authors explain more thoroughly how these new substrates fit into the apoptotic program?

We thank the reviewer for raising this issue. We are aware that our original cell-based experimental design may have some limitations, yet we chose this gain-of-function setup in order to identify caspase-3 substrates in a cell-based system. We believe that this setup does allow identification of substrates that are efficiently cleaved by endogenous caspase-3, such as cleavage and acetylation of NACA at Ser34 (and neo-Nt-acetylation after caspase-3 cleavage in general). To study the physiological relevance of the neo-Nt-acetylation, we have added to the revised manuscript a time-course N-terminomics characterization of early apoptosis events conducted in HCT116 cells (without caspase-3 overexpression). The results of these experiments are now shown in Figure 5C and also in the Supplementary Table

The authors convincingly show that cleaved NACA is a neo-substrate for Nt-acetylation, suggesting functional crosstalk between proteolysis and acetylation. However, it is not clear if this acetylation event has a functional consequence, so it seems inaccurate to say at the top of page 3 that "This is the first demonstration of functional crosstalk between neo-Nt-acetylation and proteolytic pathways."

The author is correct. We changed the text accordingly.

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Reply to the reviewers

Manuscript number: RC-2022-01588

Corresponding author(s): Erh-Min, LAI

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The authors thank the reviewers for the positive and valuable comments, which have helped us to improve the quality of this work. We have addressed all comments by providing additional data and/or explanation with a detailed point-by-point response. The revised manuscript included new data: 1) viable cell counts of growth inhibition assay (Fig. 2A), 2) Quantitative data of microscope data (Fig. 2C, Fig. 4), 3) quantitative data of interabacterial competition (Fig. 5A, 5B), western blotting data of growth inhibition (Fig. S1A and S1B), secretion assay of single glycine-zipper mutants (Fig. 5C), and inclusion of full gel of western blot results (Fig. S3 and S5). By integrating these new results, we have substantially strengthened the findings that a glycine zipper motif of a type VI secretion effector T6SS Tde1contributes to its translocation across the cytoplasmic membrane of target cells.

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

Summary: In this manuscript, Ali et al. propose that a glycine zipper motif located at the N-terminus of the Agrobacterium tumefaciens T6SS DNase effector, Tde1, can transport the toxin across the cytoplasmic membrane and into the cytoplasm, where its target is found. To support these claims, they perform a series of secretion, competition, toxicity, and fluorescence microscopy assays showing that a mutation in two glycine residues affects toxicity of the effector during competition and its ability to enter a target cell, but not its secretion through the T6SS or its binding to the adaptor protein Tap1. The concept brought forth in this study is quite interesting and important - the notion that T6SS effectors have domains that aid in their transport into the cytoplasm of the target cell. This is similar to a recent finding that a domain common to bacterial pyocins and T6SS effectors can mediate DNase toxin transport through the target cell's cytoplasmic membrane (Atanaskovic et al., mBio, 2022); the authors should mention and discuss this recent work. Nevertheless, it is my impression that the results do not fully support the conclusions and proposed mechanism, even though the general idea seems correct.

Ans: We thank this reviewer found this work interesting and important. We hope the revised manuscript including the new data and careful interpretation have substantialized the conclusions and proposed mechanisms. We also included the excellent work by Atanaskovic et al., 2022 and discussed the findings in the revision (see lines 344-349).

Major comments:

• An experiment that directly demonstrates the ability of the glycine zipper to mediate transport of a toxin across a membrane would greatly support and solidify the conclusions of this work. For example, showing the ability of a purified protein to enter spheroplasts or liposomes in a glycine zipper dependent fashion. Currently, the authors perform experiments that can only indirectly support the proposed function of the glycine zipper to enable the effector to cross the membrane, and as detailed below, some of these experiments are over-interpreted in my opinion. Ans: We agree that the direct evidence for the ability of the glycine zipper to mediate Tde1 transport across target cell membrane is to perform the in vitro translocation assay. Unfortunately, the attempts to purify sufficeint amounts of full-length or N-termial version of Tde1 have not been successful. Therefore, we are unable to perform this experiment. Accoringly, we have tried our best to carefully interpret the data and rephrase the statements accordingly.

• Lines 153-159: It is not clear how much these results are relevant to the activity of the glycine zipper motif during effector delivery by the T6SS. If I understand correctly, the described experiments are of over-expression of the proteins in the E. coli cytoplasm, where glycine zipper-dependent membrane permeability and toxicity are detected. However, one would expect that if the effector is to be transported from the periplasm to the cytoplasm during T6SS delivery, then the glycine zipper should function from the periplasmic face of the cytoplasmic membrane, and not from its cytoplasmic face, as is the case in these experiments. Is it possible that the observed toxicity and membrane permeability be the result of over-expression in the "wrong place"? Ans: The reviewer is right that Tde1 should permealize cytoplasmic membrane from periplasmic side upon injection from the attacker based on our proposed model. The purpose of ectopic expression of Tde1 and its variant in E. coli is to dissect the region and motif of Tde1 DNase-independent toxicity and the ability in enhancing membrane permeability regardless of which sides of cytoplasmic membrane the Tde1 mediates toxicity and permeability. The results of glycine zipper-dependent toxicity and membrane permeability provide a ground work for the experiments of secretion and interabacterial compeittion in the context of active T6SS action to determine the role of glycine zipper in Tde1 export and translocation.

• Fig. 4B: This figure appears to be very important, and the authors base a large part of their main conclusion regarding the role of the glycine zipper in membrane crossing on it. However, some controls are missing and part of the results observed in the figure do not match their description in the text. • Lines 233-237 - While the authors state in the text that GFP and mCherry signals did not overlap in E. coli cells co-cultured with Agrobacterium cells expressing Tde1(M)-GLGL, I see many double-colored cells in this sample (bottom panels in Fig. 4B). Actually, all cells appear to have both green and blue colors, except for a few cells that are only green but that also seem to be dead judging by their ghostly appearance in the phase contrast channel.

Ans: We thank the reviewer pointed this out. By looking at this particular image more carefully, it is striking that the majority of cells seem to emit both green and blue colors from this Tde1(M)GLGL sample. We have performed a total of three indepenent experiments for this translocation assay and all results except this particular sample in this particular experiment are consistent in all three independent experiments. Honestly, we could not explain this result and a possibility is this sample might be accidentally mixed with another sample. Because this is the only sample with inconsistent result with another two independent experiments, we decided NOT to use the results from this independent experiment and instead performed another independent experiment. We now have included the quantitative data from three effective independent experiments and show the representative images in Figure 4.

How is it that all cells in the bottom panels are blue (indicating that they are E. coli target cells)? Shouldn't a large portion of the cells be Agrobacterium cells that should not be blue, since these are added at the beginning of the competition assay at a 10:1 ratio in their favor? Ans: As explained above, we have no defined answer and decided to perform additional repeats, which are consistent with results of another two independent experiments.

It is quite remarkable that so much GFP signal is transported into the E. coli target cells so that it is so clearly visible under the microscope. How do the authors know that the GFP signal overlapping with the mCherry is really inside the cell and not outside (for example, proteins secreted to the media that attach to the cell envelope)? Will the GFP signal remain if trypsin is added to the media before visualization under the microscope? Ans: Indeed, our quantitative data show there are ~50% cells have GFP overlapping with mCherry in the translocation positive samples. The signals should be inside the cells because no overlay signals were observed from N-Tde1GLGL or Tde1(M)GLGLeven though they are secreted.

Can the authors quantify the ratio of E. coli cells that have overlapping green and blue colors over several experiments for each sample, to show that this phenomenon repeats and is statistically significant? Ans: Yes, see quantitative data in Figure 4.

Can the authors explain why at least some of these E. coli cells should not be dead due to the toxicity mediated by the third effector of the Agrobacterium T6SS, Tae? Ans: In Agrobacterium tumefaciens C58, Tde1/2 are the major effectors contributing to antibacterial activity. Tae effector has little impact on interbacterial competition outcome (see previous publications Ma et al., 2014 doi: 10.1016/j.chom.2014.06.002.; Yu et al., 2020 doi.org/10.1128/JB.00490-20)

Why were the microscopy competitions performed differently than the regular competition assays? Why wasn't AK media used in these competitions? How active is the T6SS under these conditions compared to the AK media? Ans: We have tried to use AK medium for the translocation assay but only very weak fluorescent signals can be observed likely due to the low expression when grown on this nutrient poor medium. In order to correlate the results of the compeittion assay with translcoation experiment, we have performed E. coli killing assay using LB medium that is used for translocation experiment now. For the interbacterial competition against agrobacterial siblings, we still used AK medium for competition because no detectable interbacterial compettion activity could be observed between two A. tumefaciens strains on LB agar. As reported earlier, stronger interbacterial competition outcome was detected from co-culture on AK than other nutrient rich medium while the secretion activity grown in AK medium is lower (Yu et al., 2020 doi.org/10.1128/JB.00490-20). These results indicate that the factors other than secretion activity also impacted recipient cell susceptibity, which however is not the main focous of this work.

In the N-Tde1 sample, many Agrobacterium cells appear to have the GFP signal in foci rather than distributed throughout the cell (as it is in other samples), while the E. coli cells have a uniform and strong GFP signal. Can the authors comment on that? Ans: Thanks the reviewer for raising this question.We are also curious about the Tde1 glycine zipper-dependent GFP foci and now include this potential explanation in the Discussion of revised manuscript (line 387-406). To this end, we do not have an answer for it. Because glycine zipper repeats are known to interact with membrane, it is possible that Tde1 proteins may preferntially bind to microdomain of cytoplasmic membrane, which was recently found in A. tumefaciens (Czolkoss et al., 2021). We also found that Tde1 proteins (either tagged with HA or GFP) are proned for truncation when they are ectopically expressed in E. coli or when Tdi1 is absent or not equivalent. Thus, it is possible that Tde1-GFP proteins are truncated after translocation into E. coli cells, in which most GFP signals are emitted from free GFP instead of Tde1-GFP. The stability of free GFP derived from translocated Tde1-GFP may also explain the high percentage of E. coli cells exhibiting overlayed GFP/mCherry signals.

It might be easier for readers to visualize this figure and see the signal distribution in the different cells if the authors show a zoomed in version in the main text, and provide the wide field images as a supplementary figure. Ans: We have tried to include zoom-in images but the resolution is not good. We have improved the quality of images in the Figure 4 and believe the images are clear to see individual and overlayed fluorescence signals.

• Fig. 5C-D: The reduced expression and secretion of the GLGL mutant is considerable. How can the authors rule out that this reduction was the cause for the reduced observed toxicity of the mutant in 5A-B? Moreover, the results show that the GLGL double mutant is hampered in expression, secretion, and DNase activity, and it negatively affects overall T6SS activity. Since this mutant was used throughout the paper, and in the absence of a direct assay showing membrane transport mediated by the glycine zipper motif, the claim of the role of this motif in membrane crossing is not well substantiated by the results. If the authors were to show that the single glycine mutants used in Fig. 5D, which are stable and have an intact DNase activity, behave as claimed in the final conclusion sentence (lines 279-283), then the conclusions will be better substantiated by the results. Ans: Thank you very much for suggesting this important experiment. We have now constructed the single G39L and G43L variants expressed together with Tdi1 in A. tumefaciens tdei mutant for both secretion and interbacterial competition assays (see description in lines 259-280 and Fig. 5). As shown in Figure 5, both G39L and G43L variants are expressed and secreted at similar or even higher levels than wild type Tde1 but have no detectable antibacterial activity against either E. coli or A. tumefaciens 1D1609. This result substantializes the role of this glycine zipper motif in translocation.

Minor comments:

• Line 93: I am not sure that Ntox15 should still be referred to as a "novel" domain.

Ans: despite the evidence of this domain as DNase, the name of Ntox15 is used. We think to keep this nomenclatture as it will be easier to be ditinquished from other nuclease or toxin domain.

• Line 105: The section's heading does not actually describe its content. The results here only show toxicity upon over-expression of the effector or its mutant forms in E. coli. Therefore, this cannot be referred to as a "prey cell" since the effector was not transported into it during competition. Moreover, the results in Fig. 5A do not support DNase-independent toxicity during competition. Ans: The heading is changed to “Tde1 exhibits DNase-independent growth inhibition in E. coli” (line 115).

• Please consider making all of the symbols in the growth assays semi-transparent. It is impossible to discern between the different, overlapping curves. Ans: The growth curve results are improved by changing line colors and reducing size bars (Fig. 1B, 1C; Fig. 2A, 2D)

• Please consider making the size bars in all microscopy images more pronounced. They are barely visible in their current form. Also, it would be better to show images of the same magnification/zoom for the different samples, since the current presentation shows cells from different samples at different sizes, and it can be confusing to the readers. Ans: Amended (Fig. 2C; Fig. 4).

• In Fig. 1B and in Fig. 2A the authors show that expression of Tde1(M) in cells is toxic, yet in Fig. 2D they see no toxicity. Can the authors please comment on this discrepancy? Ans: Fig. 2D showed the viability of E. coli cells after Tde1 variants were induced for 1 hr before ONPG uptake assay to indicate the increased membrane permeability is not due to cell death. In Fig. 1B, the growth inhibition of Tde1(M) is also not evident at 1 hr. So, the results are consistent.

• I am not convinced that the assay in Fig. 2E can be used to determine bacteriostatic/bacteriolytic effect. It is not clear how such a distinction can be made from OD measurements, since an increase in OD can result from the entire population growing after removal of the stressor, or just part of the population that did not lyse/die. To make such a claim, the authors can spot bacteria on repressing media at different timepoints after protein induction, and then determine CFU.

Ans: The increased OD600 value during recovery could be caused by either resumed cell division or cell elongation. Based on the newly added growth inhibition assay of all Tde1 variants which we showed nice correlation between CFU counting and OD600value (Fig. 2A, S2) and no increased cell size/length of E. coli cells expressing N-Tde1 or Tde1(M), we think the recovered OD600 value is supportive of N-Tde1 or Tde1(M) exhibiting bacteriostatic toxicity. In addition to that, our interbacterial competition data showed that Tde1(M)-Tdi1 which is still having intact glycine zipper doesn’t show significant detectable killing, supporting the bacteriostatic function of Tde1 glycine zippers. In fact, we performed this experiment based on Mariano et al.(Nat. Commun. 2019 doi: 10.1038/s41467-019-13439-0), which showed the recovery of OD600 value after removal of inducer as the evidence that the Ssp6 toxin is not bacteriolytic.

• Fig. 3A: A control is missing. To verify that the N-terminal part of Tde1 is not promiscuously interacting with proteins, the authors should include a control sample testing its inability to precipitate a protein other than Tap1 in the same experiment. Ans: Our previous study has showed that Tde1 can co-immunprecipiate Tap1 but not a non-T6SS protein RpoA (Bondage et al., 2016 doi:10.1073/pnas.1600428113), indicating that Tde1 is not promiscuously interacting with proteins. Considering the tight biochemical interaction between Tap1 with N-Tde1 but not C-Tde1 that correlate with their ability for secretion upon loading onto VgrG1, N-Tde1 is unlikely to bind proteins non-specifically. This is also supported by the non-specific protein bands from cellular fractions recognized by anti-Tap1 are not co-immunoprecipitated by any of Tde1 variants (Fig. S3). We could repeat the experiments to include additional proteins as negative controls but we chose to use time for other more critical experiments during the limited revision time.

• Fig. 3B: the blots are very "dirty". It is not clear how the authors were able to determine expression and precipitation of some truncations (for example, C2-Tde1 in the E. coli IP panel looks like a background band found in other lanes too).

Ans: We agree that western blots of co-IP experiments in E. coli are not very clear due to the weak signals of some Tde1 variants and background. As pointed out by the reviewer 3, this result is not conclusive and rovide little additional information other than the co-IP results from A. tumefaciens. Because the interaction between Tde1 variants and Tap1 when expressed in E. coli are not physiologically relevant and not the main focus of this work, we have removed the E. coli co-IP results from this manuscript as suggested by the reviewer 3.

• Lines 222-225 (Fig. 4A): I can't see C-1-Tde1(M)-sfGFP in the cellular blot. All the bands in this lane look like background bands that are also present in all other lanes. Therefore, I am not sure how the conclusion regarding this truncation's ability to be secreted was reached. Ans: We agree that C1-Tde1(M)-sfGFP is barely detectable due to its weak signal overlapping with cross-reacted bands. Since several attemps to improve the western blot quality by changing antibody and pre-blocking with protein lysages of vector control strain did not produce convincing results for detection of C1-Tde1(M)-sfGFP, we have rephrased the description of this result as “However, C1-Tde1(M)-sfGFP protein signal could not be unambiguously determined in the cellular fraction due to the overlapping of its predicted protein band with cross-reacted proteins, and no corresponding C1-Tde1(M)-sfGFP band was detected in the extracellular fraction.” (line 234-237).

• Fig. 4A: the protein names above the lanes should include the sfGFP that is fused to them. Ans: Amended.

• It would be preferable to show quantitative competition assays with statistics rather than pictures of a plate showing a single competition result, if conclusions or observations on minor differences in toxicity are made (for example, line 253: "The killing activity of Δtdei(Tde1GLGL-Tdi1) was largely compromised"). Since the authors performed each competition assay more than once, these data should be available to them. Ans: Amended. We have repeated the interbacterial competition experiments including single G39L and G43L variants for multiple biological repeats (see detailed in legends of Fig. 5A, 5B). The quantitative data with statistical analysis were added, which show no statistical difference of any glycine zipper mutants as comapred to Tde1(M) or when expressed in the T6SS mutant. Thus, there are no detectable antibacterial activity of glycine zipper mutants against either E. coli or A. tumefaciens siblings.

• Fig. 5A: The author claim at the beginning of the manuscript (first results section heading: "Tde1 can cause DNase-independent growth inhibition of prey cells") that the N-terminal region of Tde1 is toxic on its own in the prey cell, yet in this competition assay Tdi1(M) shows no toxicity against the E. coli target cells. In the microscopy assay (Fig. 4B), it appears that a lot of Tdi1(M) enters the prey cell, since we can visualize it under the microscope. Can the authors clarify this discrepancy and explain why they do not expect to see target killing by this mutant even though they claimed it is toxic earlier? Ans: As describbed in earlier response, N-Tde1 amd Tde1(M) toxicity can exhibit toxicity by ectopic expression in E. coli. We mainly used this ectopic expression assay to dissect the region and motif contributing the toxicity. Compared to the interbacterial competiton process where Tde1(M) may only transiently permealze cytoplasmic membrane transiently as the final destination is cytoplasm where wild type Tde1 but not Tde1(M) exerts DNase toxicity. Thus, the toxicity of N-Tde1 and Tde1(M) can be only observed when the proteins are continuously produced in the cytoplasm. The role of N-Tde1, specifically the glycine zipper motifs, is to mediate Tde1 translocation across inner membrane, instead of exerting toxicity during the context of interbacterial competition.

• Fig. 5B: the GLGL mutant seems to have some residual toxicity, not dissimilar to what is shown in 5A. Why are these similar results interpreted differently (in 5A they are "largely compromised", while in 5B "killing activity... was not detectable")? Also, why was Tde(M)1-Tdi1 used in Fig. 5A but Tdi1(M) without the immunity gene used in Fig. 5B? Ans: As described above, to better quantify the interbacterial competition outcomes, we have repeated the interbacterial competition experiments and used Tde(M)1-Tdi1 instead of Tdi1(M) for at least three biological replicates. The quantitative data with statistical analysis were carried out to clarify this ambiguity (Fig. 5A, 5B).

• Fig. 5: Does the remaining third effector, Tae, not play a role in these competition assays? If, as shown in Fig. 5C, the entire T6SS is less active when a GLGL mutant is expressed, couldn't the different in toxicity shown in Figs. 5A-B be the result of lack of Tae secretion and toxicity?

Ans: As decribed above, Tae effector has little impact on interbacterial competition outcome. The quantatitive interbacterial competition results (Fig. 5A, 5B) also clarify the ambiguity because single G39L and G43L variants are expressed and secreted at similar or even higher levels than wild type Tde1 but have no detectable antibacterial activity against either E. coli or A. tumefaciens 1D1609.

• Lines 359-362: T6SS effectors that bind the inner Hcp tube were suggested to be only partially folded. Ans: Amended.

Reviewer #1 (Significance (Required)):

The concept of T6SS effectors providing their own mechanism of transport from the cytoplasm to the periplasm is very interesting. It will appeal to audience in a wide range of microbiology disciplines, including those interested in toxins, membrane transport, and even translational applications. A similar concept was recently proposed and demonstrated for a domain that is also found in T6SS effectors (Atanaskovic et al., mBio, 2022).

Expertise: I have been studying the different aspects of T6SS for the past decade.

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

This manuscript is focused on understanding how the Agrobacterium tumefaciens T6SS effector, Tde1, is translocated across the cell envelope of target cells and how this effector binds to the adapter Tap1. The authors show that GxxxG motifs in the N terminal region of Tde1 are required for delivery into the cytoplasm of target cells and permeabilising the cytoplasmic membrane. Given that these GxxxG motifs resemble glycine zipper structures that are found in proteins involved in membrane channel formation, the authors propose that these Tde1 motifs are involved in channel formation in the target cell. The authors also show that the N terminal region of Tde1 binds to Tap1 to facilitate loading onto the T6SS machinery but that the GxxxG motifs are not involved in this binding. Overall the manuscript was easy to read and followed a logical presentation of the findings. There are a few major comments that this reviewer has below - addressing these would allow the authors' claims to be more robustly supported. Ans: Thank you very much for the positive comments and valuable suggestion. We hope the revised manuscript including the new data and careful interpretation have substantialized the conclusions and proposed mechanisms.

Major comments:

1. Fig 1B: Why is this such a short growth experiment (5 hrs total with 2 hr pre and 3 hrs post induction)? Reporting on a growth experiment would normally be at least until the cells reach stationary phase but here the cells are still clearly in exponential phase. This reviewer would query what happens to growth rate in later exponential growth and into stationary phase? Is the toxic effect lessened in later stages of growth? Ans: We have indeed performed the growth curve analysis with longer time period. However, we noted that the growth at later time points are not always consistent and our interpretation is that the continuous expression of toxins may lead to the selection of mutants. Since the 3 or 4 hr time period already showed the toxicity phenotype, we have focused on this time frame for the growh experiments.

2. It is indeed surprising that C2-Tde1(WT) does not inhibit growth despite it having a functional DNase domain and being expressed in the cytoplasm. Did the authors confirm that this protein variant was expressed by Western blot or other means? This should be done to confirm that this variant is indeed not impacting upon growth instead of it not impacting growth simply because it is not being expressed.

Ans: Amended. All Tde1 variants including C2-Tde1 are expressed (data included in Fig S1)

1. The letters used to report significance are not clear to this reviewer. The authors say that "The significant differences were shown by the different letters (p value

For all fluorescence microscopy experiments how many fields of view were imaged for each biological replicate? Were the fields selected at random or was the field selection biased to what was present in the field before taking the image? The answers to all of these questions should be stated in the methods. Also the microscopy data presented in the manuscript is not quantitative. Quantification of the number of cells with PI vs Hoechst signal (in Fig 2C) and mcherry vs gfp signal (in Fig 4B) for all fields of view and for all biological replicates would be very informative and convince the reader that the authors have not just "cherry picked" the images they are showing in the manuscript. This could be performed manually or the authors could use the freely available image analysis program Fiji (https://imagej.net/software/fiji/) to perform these analysis in a semi-automated manner.

Ans: The number of images and experiments were now described in the figure legends and the quantititive data are included (Fig. 2C).

1. For the co-IP experiments in Fig 3 where interaction between HA tagged Tde1 and Tap1 is demonstrated the authors should also show that Tap1 does not interact with a different HA-tagged protein i.e. that the interaction is specific to Tde1 and not the HA motif. Ans: All Tde1 variants were tagged with HA. As shown in Fig. 3A, Tap1was not co-precipitated by C2-Tde1 and C1-Tde1(M), indicating that Tap1 specifically interacts with N-terminal region of Tde1.

For all Western blot images there should be at least 2 protein standard markers present in each individual blot - i.e. for Fig 3A and B the bottom panel showing Tap1 detection only has the 35 kDa marker, it should have at least one more marker in it. The same is true for other panels in Fig 2, 3 and 4. Having at least two molecular weight markers in a panel is now standard for most journals when presenting Western blot images. Ans: Amended. We have now included the full gel of western blot results in Fig. S3 and S5 of those shown in main figures.

For the competition assay serial dilution images in Fig 5A-B the images are a nice way to visually represent the experimental outcome but they should accompany graphs showing the competitive index of CFU/ml of the input prey and attacker vs the output prey and attacker for all biological replicates. This will convince the reader that the authors had equivalent amounts of the prey and the attacker going into the experiment and also that all attackers grew at the same rate and so were equally able to target the prey cell. This quantification could also provide more convincing out competition of ID1609 prey by C58 attacker (Fig 5B). Ans: Amended. As indicated above, we have repeated the interbacterial competition experiments for at leaset three biological replicates and show that quantitative data with statistical analysis (Fig. 5A, 5B).

Minor comments:

Line 40: should read "...demonstrate that the effector itself..." Ans: The sentence has been rephrased (line 40) .

Line 41: "...we propose..." instead of "...we proposed..." since present tense makes more sense for this statement.

Ans: Amended (line 42).

Line 51: "Each specialized protein secretion system" instead of "Each of...." Ans: Amended (line 52).

Line 76: "A glycine zipper structure..."

Ans: Amended (line 83).

Line 79: "For example..."

Ans: Amended (line 86).

Lines 96-100: The present tense should be used here as the current usage of past tense implies that this has been done in previous work and not in the current study - eg "we revealed", "we showed" would be better as "we reveal", "we show".

Ans: Thanks for the advice. We have made changes throughout the manuscript.

Fig 5B - The competition assay serial dilution images look a bit blurry, are there images the authors could use that are not blurry?

Ans: Amended. As indicated above, we now show quantitative data with statistical analysis (Fig. 5A, 5B).

Reviewer #2 (Significance (Required)):

This work is significant in as while there is a great deal known about how T6SS effectors cause toxicity there is less known about how these effectors are loaded onto the T6SS machinery and very little known about how T6SS effectors are able to translocate across the cytoplasmic membrane of target cells to reach a cellular component that is in the cytoplasm. This work would be of wide general interest to researchers in the T6SS field as well as those interested in bacterial secretion systems.

Reviewer expertise key words: Molecular microbiology, T6SS, interbacterial competition

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

EVIDENCE, REPRODUCIBILITY AND CLARITY

Summary:

In this work, Ali et al. demonstrate that the N-terminal GxxxG motif of the T6SS DNase effector Tde1 of Agrobacterium tumefaciens is required for interbacterial intoxication. Using a combination of cell viability, reporter, and microscopy assays, the authors demonstrate that over-expression of the N-terminus of Tde1 results in inner membrane permeability. Moreover, the authors show that both the interaction between Tde1 and its adaptor Tap1 as well as the T6SS-mediated secretion of Tde1 are dependent on the N-terminus of Tde1. Finally, using a combination of in vitro and in vivo experiments, the authors determine that the N-terminal GxxxG motif is essential to Tde1-dependent interbacterial killing by enabling effector entry into competing bacterial cells.

Major comments:

If N-tde1 is 1-97 aa, the predicted size is 9 kDa, but it shows up as ~17 kDa? Can the authors comment on this? Does N-tde1 or tde1 dimerize? Ans: The theoretical Mw of N-Tde1-HA is 10.64 KDa, which indeed migrated at higer position ~17 kDa. It is notable that full-length Tde1 with theoretical 29.5-kDa migrated slower in SDS-PAGE with a observed size ~36 kDa as observed previously (Ma et al., 2014 doi:10.1016/j.chom.2014.06.002). Similarly, the full-length HA-tagged Tde1(M) with theoretical 30.89 kDa migrated at a position ~38 kDa. Since the protein samples analyzed by SDS-PAGE including reducing agent, we cannot exclude the possibility that Tde1 or N-Tde1 may form dimer or oligomer that was disrupted by SDS-PAGE but it appears not forming dimer on SDS-PAGE.

I have many concerns with the data and conclusions drawn from the data in Fig. 3B. I recommend removing it since (1) the data are not accurately represented in the text and (2) it is difficult to ascertain whether biologically relevant conclusions can be drawn from what happens with Agrobacterium proteins in E. coli. Below is a summary of my concerns regarding this section: I disagree with the authors' statements in lines 191-198. Their pulldown with E. coli is not consistent with their pulldown in C58. In fact, given the expression problems of some of the constructs in E. coli, I believe the data shown in Fig. 3B is inconclusive. The amount of Tap1 that co-IP'ed with N-Tde1GLGL and Tde1(M) is very low even though the expression levels of N-Tde1GLGL and Tde1(M) were relatively strong. Therefore, I do not feel confident concluding that these proteins "interact". Secondly, Tde1(M)GLGL was not expressed in E. coli, so no conclusions can be drawn. Moreover, the C1 and C2 variants were also not expressed well, so I believe the authors' statement in line 191-192: "Similar to the results in A. tumefaciens, the N-Tde1 and Tde1(M) interacted with Tap1 but not the C-terminal variants", is unjustified. You cannot rule out that C1 and C2 do not interact with Tap1 because C1 and C2, like Tde1(M)GLGL, were not expressed well in E. coli. Ans: We agree with the reviewer that the E. coli co-IP result is not conclusive due to the low expression and instability of proteins mostly during the process of cell lysis and purification, and it provides little additional information other than data from co-IP in A. tumefaciens. Because the interaction between Tde1 variants and Tap1 when expressed in E. coli are not physiologically relevant and not the main focus of this work, we have removed the E. coli co-IP results from this manuscript.

Lines 211-214: It looks like C1-Tde1(M) inhibits T6SS secretion. I am aware that in Agrobacterium, it has been shown that effector loading is essential for secretion, but then why does the pTrc200 secrete Hcp? Also, in Fig. 4B, a strain expressing C1-Tde1(M) now secretes Hcp. Ans: Thanks for noting our previous finding that Tde loading is critical for secretion. Our data are indeed supportive of the effector loading in activating T6SS as only very low levels of Hcp secretion could be detected from the strain containing vector only or C1-Tde1(M). In our previous paper (Wu et al., 2020 https://doi.org/10.15252/embr.201947961), there is either little or no detection of Hcp secretions when effectors are not loaded, indicating that effector loading is important but not essential for Hcp secretion. Because overexpression of VgrG can also activate T6SS secretion in the absence of effector loading (Bondage et al., 2016 doi:10.1073/pnas.1600428113), we think the low level secretion under certain conditions could be caused by some cells with higher levels of VgrG protein concentration but more work is required to elucidate the underlying mechanisms.

Minor comments:

Fig. 2B could benefit from better labeling to indicate that most strains lack lacY. Also, why is BW25113 WT showing such a low OD420 if it has LacY? Or is WT without lacZ? Please clarify.

Ans: We apologize for not labeling clearly. The BW25113 strain lacks lacZ, therefore all the ∆lacY strains were complemented with a plasmid encoding lacZ (pYTA-lacZ). We have now added the labels to avoid confusion (Fig. 2B).

Reviewer #3 (Significance (Required)):

SIGNIFICANCE

It has been known for over a decade that T6SS effectors have both periplasmic and cytosolic targets (e.g., cell wall and DNA). However, it remains unclear (1) where within the target cell are T6SS effectors are delivered and (2) once delivered, how do effectors reach their intracellular target site. In this work, Ali et al. demonstrate that for Tde1, the N-terminal GxxxG motif is essential for Tde1 to reach its target (DNA). The authors identified Tde1 homologs in several bacteria, suggesting that this model may be relevant across a wide range of bacteria. Additional research is needed to (1) determine whether Tde1 is originally secreted into the periplasm and (2) understand how non-Tde1/non-GxxxG effectors reach their target site.

Author Response

Reviewer #2 (Public Review):

This is an interesting study investigating the effects of sensory conflict on rhythmic behaviour and gene expression in the sea anemone Nematostella vectensis. Sensory conflict can arise when two environmental inputs (Zeitgeber) that usually act cooperatively to synchronize circadian clocks and behaviour, are presented out of phase. The clock system then needs to somehow cope with this challenge, for example by prioritising one cue and ignoring the other. While the daily light dark cycle is usually considered the more reliable and potent Zeitgeber, under some conditions, daily temperature cycles appear to be more prominent, and a certain offset between light and temperature cycles can even lead to a breakdown of the circadian clock and normal daily behavioural rhythms. Understanding the weighting and integration of different environmental cues is important for proper synchronization to daily environmental cycles, because organisms need to distinguish between 'environmental noise' (e.g., cloudy weather and/or sudden, within day/night temperature changes) and regular daily changes of light and temperature. In this study, a systematic analysis of different offsets between light and temperature cycles on behavioural activity was conducted. The results indicated that several degrees of chronic offset results in the disruption of rhythmic behaviour. In the 2nd part of the study the authors determine the effect of sensory conflict (12 hr offset that leads to robust disruption of rhythmic behaviour) on overall gene expression rhythms. They observe substantial differences between aligned and offset conditions and conclude a major role for temperature cycles in setting transcriptional phase. While the study is thoroughly conducted and represents and impressive amount of experimental and analytical work, there are several issues, which I think question the main conclusions. The main issue being that temperature cycles by themselves do not seem to fulfil the criteria for being considered a true Zeitgeber for the circadian clock of Nematostella.

Major points:

Line 53: 'However, many of these studies did not compare more than two possible phase relationships.....'. Harper et al. (2016) did perform a comprehensive comparison of different phase relationships between light and temperature Zeitgebers (1 hr steps between 2 and 10 hr offsets), similar to the one conducted here. I think this previous study is highly relevant for the current manuscript and -- although cited -- should be discussed in more detail. For example, Harper et al. show that during smaller offsets temperature is the dominant Zeitgeber, and during larger sensory conflict light becomes the dominant Zeitgeber for behavioural synchronization. Only during a small offset window (5-7 hr) behavioural synchronization becomes highly aberrant, presumably because of a near breakdown of the molecular clock, caused by sensory conflict. Do the authors see something similar in Nematostella? Figure 3 suggests otherwise, at least under entrainment conditions, where behaviour becomes desynchronized only at 10 and 12 hr offset conditions. But in free-run conditions behaviour appears largely AR already at 6 hr offset, but not so much at 4 and 8 hr offsets (Table 2). So there seems to be at least some similarity to the situation in Drosophila during sensory conflict, which I think is worth mentioning and discussing.

We have added a more detailed discussion of our results in the context of Harper et al. 2016 (L468-476).

Line 111: The authors state that 14-26C temperature cycle is 'well within the daily temperature range experienced by the source population'. Too me this is surprising, as I was not expecting that water temperature changes that much on a daily basis. Is this because Nematostella live near the water surface, and/or do they show vertical daily migration? Also, I do not understand what is meant by '...range of in situ diel variation (of temperature)'. I think a few explanatory words would be helpful here for the reader not familiar with this organism.

In fact, one of our motivations for studying temperature is that Nematostella naturally experience extreme temperature variation. The data we cite (Tarrant et al. 2019) are from in-situ water measurements. Nematostella live in extremely shallow water (in salt marshes), and the local population in Massachusetts experience wide swings in temperature due to the temperate latitude.

We have added this information to the Introduction (L88-90), and we also added a discussion of Nematostella’s ecology in the Discussion section (L591-654).

Lines 114-117: I was surprised that clock genes can basically not be synchronized by temperature cycles alone. Only cry2 cycled during temperature cycles but not in free-run, so the cry2 cycling during temperature cycles could just be masking (response to temperature). Later the authors show robust molecular cycling during combined LD and temperature cycles (both aligned and out of phase), indicating that LD cycles are required to synchronize the molecular clock. Moreover, a previous study has demonstrated that LD cycles alone (i.e., at constant temperature) are able to induce rhythmic molecular clock gene expression (Oren et al. 2015). Similarly, the free running behaviour after temperature cycles does not look rhythmic to me. In Figure 2A, 14-26C there is at best one peak visible on the first day of DD, and even that shows a ~6 phase delay compared to the entrained condition. After the larger amplitude temperature cycle (8:32C) behaviour looks completely AR and peak activity phases in free-run appear desynchronized as well (Fig. 2B). Overall, I think the authors present data demonstrating that temperature cycles alone are not sufficient to synchronize the circadian clock of Nematostella. One way to proof if the clock can be entrained is to perform T-cycle experiments, so changing the thermoperiod away from 24 hr (e.g., 10 h warm : 10 h cold). If in a series of different T-cycles the peak activity always matches the transition from warm to cold (as in 12:12 T-cycles shown in Fig. 1A) this would speak against entrainment and vice versa.

Thank you for these thoughtful comments and constructive suggestions. We have conducted an additional experiment, which provides further evidence that temperature cycles can, in fact, synchronize the circadian clock. To do this, we measured the behavior of animals entrained in cycles with a short (12h) period, half the length of a circadian period. This takes advantage of a phenomenon called “frequency demultiplication”, in which organisms in 12h environmental cycles display both 12h and 24h components--essentially, the clock perceives every other cycle as a “day” (Bruce, 1960; Merrow et al., 1999). The important thing is that the 24h behavioral component can only occur if the signal is entraining a circadian clock—otherwise, we would only observe a directly-driven 12h behavior pattern.

We first show that this phenomenon occurs with 6:6 LD cycles—which we expected, because we know light is a zeitgeber. We then show that animals entrained to a temperature cycle with a 12h period also display 24h behavioral rhythms—and in fact the 24h component is stronger than the 12h component. We believe this is strong evidence that temperature is a bona fide zeitgeber in this system. This experiment is now explained in the Results (L127-154) and in Figure 2–Figure supplement 1.

In terms of our original data, the reviewer is correct that the statistically-detectable free-running rhythms were weak and not visually obvious). Our confidence in thermal entrainment came from the fact that some individual animals had 24h rhythmicity in free-run, even if the signal was weak in the mean time series—this suggested that temperature must be at least capable of synchronizing internal clocks. It is also important to note that even light-entrained rhythms are “noisy” in cnidarians, which is why we were not surprised that the signal was weak. We have added a discussion of this observation in L601-612.

Lines 210-226: As mentioned above, I think it is not clear that temperature alone can synchronize the Nematostella clock and it is therefore problematic to call it a Zeitgeber. Nevertheless, Figure 3A, B, D show that certain offsets of the temperature cycle relative to the LD cycle do influence rhythmicity and phase in constant conditions. This is most likely due to a direct effect of temperature cycles on the endogenous circadian clock, which only becomes visible (measureable) when the animals are also exposed to certain offset LD cycles. My interpretation of the combined results would be that temperature cycles play only are very minor role in synchronizing the Nematostella clock (after all, LD and temperature cycles are not offset in nature), perhaps mainly supporting entrainment by the prominent LD cycles.

With our new data (see previous point), we believe we can safely say that temperature is a zeitgeber. We are not totally clear on what is meant by “a direct effect of temperature cycles on the endogenous circadian clock.” We argue that, because we see changes in free-running behavior during certain offsets, the timing of temperature cycles must affect the internal clock in a way that persists during constant conditions—it can’t just be a direct (clock-independent) effect of temperature.

Gene expression part: The authors performed an extensive temporal transcriptomic analysis and comparison of gene expression between animals kept in aligned LD and temperature cycles and those maintained in a 12 hr offset. While this was a tremendous amount of experimental work that was followed by sophisticated mathematical analysis, I think that the conclusions that can be drawn from the data are rather limited. First of all, it is known from other organisms that temperature cycles alone have drastic effects on overall gene expression and importantly in a clock independent manner (e.g., Boothroyd et al. 2007). Temperature therefore seems to have a substantially larger effect on gene expression levels compared to light (Boothroyd et al. 2007). In the current study, except for a few clock gene candidates (Figure 2C), the effects of temperature cycles alone on overall gene expression have not been determined. Instead the authors analysed gene expression during aligned and 12 h offset conditions making it difficult to judge which of the observed differences are due to clock independent and clock dependent temperature effects on gene expression. This is further complicated by the lack of expression data in constant conditions. I think the authors need to address these limitations of their study and tone down their interpretations of 'temperature being the most important driver of rhythmic gene expression' (e.g., line 401). At least they need to acknowledge that they cannot distinguish between clock independent, driven gene expression and potential influences of temperature on clock-dependent gene expression rhythms. Moreover, in their comparison between their own data and LD data obtained at constant temperature (taken from Oren et al. 2015), they show that temperature has only a very limited effect (if any) on core clock gene expression, further questioning the role of temperature cycles in synchronising the Nematostella clock. Nevertheless, I noted in Table 3 that there is a 1.5 to 3 hr delay when comparing the phase of eight potential key clock genes between the current study (temperature and LD cycles aligned) and LD constant temperature (determined by Oren et al.). To me, this is the strongest argument that temperature cycles at least affect the phase of clock gene expression, but the authors do not comment on this phase difference.

We agree with these points about the limitations of our study, and have revised the manuscript to phrase our conclusions more carefully. We still think it is reasonable to observe that temperature was a stronger drive of gene expression than light in our study, but this may not be true in other contexts.

In terms of the comparison with Oren et al. 2015, we didn’t want to over-interpret these results because there are other differences between the studies (L1181-1185), including the use of a different source population. In addition, we would prefer denser sampling (2h time points rather than 4h) and larger sample sizes to make claims about phase differences.

Network analysis: This last section of the results was very difficult to read and follow (at least for me). For example, do the colours in Figure 6A correspond to those in Figure 6B, C? A legend for each colour, i.e., which GO terms are included in each colour would perhaps be helpful. As mentioned above, I also do not think we can learn a lot from this analysis, since we do not know the effects of temperature cycles alone and we have no free-run data to judge potential influence on clock controlled gene expression. Under aligned conditions genes are expressed at a certain phase during the daily cycle (either morning to midday, or evening to midnight), which interestingly, is very similar to temperature cycle-only driven genes in Drosophila (Boothroyd et al. 2007). Inverting the temperature cycle has drastic effects on the peak phases of gene expression, but not so much on overall rhythmicity. But since no free-run data are available, we do not know to what extend these (expected) phase changes reflect temperature-driven responses, or are a result of alterations in the endogenous circadian clock.

We have revised and streamlined this section and Fig. 6, including removing panel 6C. The colors do correspond across panels in the figure. For space, GO terms of select modules are included in Fig. 6, and GO results for all modules are included in the Supplemental Data and discussed in the Results.

It is true that we can’t distinguish temperature-driven versus clock effects here, and it does seem like many modules simply follow the temperature cycle (which we say in this section). The most interesting finding from this section is probably that the co-expression structure (correlations between rhythmic genes) are substantially weakened during SC, and we do discuss certain modules of genes that lose or gain rhythmicity. We have revised this section to focus on the main points and have cut several of the less pertinent results.

Reviewer #3 (Public Review):

This article reflects a significant effort by the authors and the results are interesting.

For the third set of experiments, are temperature and light really out of synch? While peak in temperature no longer occurs along with lights on, we do still have two 24 hour cycles where changes in the environmental cues still occur simultaneously (lights on with peak in temperature, lights off with min in temperature). I wonder what would happen if light remained at a 24 hour cycle and temperature became either sporadic (randomly changing cycles) or was placed on a longer cycle altogether (temperature taking 20 hours to increase from min to max, and then another 20 hours to go from max to min).

Thank you for your interesting suggestions for future experiments. This point is addressed in our revisions responding to Reviewer #1, who requested a discussion of the phrase “sensory conflict.” We agree that the binary “in-sync vs. out-of-sync” may be too simplistic. Our original conception of sensory conflict was a situation in which light and temperature provide different phase information, as informed by experiments with only light (prior literature) or only temperature (this work).

In our revised manuscript, we discuss the idea that “sensory conflict” is not always a useful framework because there are many possible relationships between light and temperature. Although our 12h offset is certainly less “natural” than our aligned time series, it may be useful to think of them simply as 2 different possible light and temperature regimes in which the two signals interact, rather than abstract ideals of “aligned” or “misaligned.”

An area that could significantly benefit a broader readership would be to improve overall clarity of figures and rethink if all the results are necessary to convert the key findings of the paper. As written, the results sections is somewhat confusing.

We have revised Figs. 1 and 6 for clarity, and we have also shortened the network analysis portion of the Results.

Evaluation 3

Ratings and predictions

Ratings (1-100)

• Overall assessment: 65 Confidence: Medium
• Advancing knowledge and practice: 70 Confidence: Medium
• Methods: Justification, reasonableness, validity, robustness: Not qualified
• Logic & communication: 80 Confidence: Medium-to-high
• Open, collaborative, replicable: Not qualified
• Relevance to global priorities: 80 Confidence: High

Journal predictions (1-5)

• What ‘quality journal’ do you expect this work will be published in? 3.5 Confidence: Medium
• On a ‘scale of journals’, what tier journal should this be published in? 3.5 Confidence: Medium

Written report

I am a political scientist specializing in science policy (i.e., how expertise and knowledge production influences the policymaking process and vice-versa), with a focus on “decision making under conditions of uncertainty,” R&D prioritization, and the governance of systemic and catastrophic risk. With respect to the various categories of expertise highlighted by the authors, I can reasonably be considered a “policy analyst.”

Potential conflict of interest/source of bias: one of the authors (Dr. Anders Sandberg) is a friend and former colleague. He was a member of my PhD dissertation committee.

A quick further note on the potential conflict of interest/bias of the authors (three of the four are associated with ALLFED, which, as the authors note, could stand to benefit financially from the main implication of their analysis - that significant funding be allocated to resilient food research in the short-term). In my opinion, this type of “self-advocacy” is commonplace and, to some extent, unavoidable. Interest and curiosity (and by extension, expertise) on a particular topic motivates deep analysis of that topic. It’s unlikely that this kind of deep analysis (which may or may not yield these sorts of “self-confirming” conclusions/recommendations) would ever be carried out by individuals who are not experts on - and often financially implicated in - the topic. I think their flagging of the potential conflict of interest at the end of the paper is sufficient - and exercises like this Unjournal review further increase transparency and invite critical examinations of their findings and “positionality.”

I am unqualified to provide a meaningful evaluation of several of the issues “flagged” by the authors and editorial team, including: the integration of the sub-models, sensitivity analysis, and alternative approaches to the structure of their Monte Carlo analysis. Therefore, I will focus on several other dimensions of the paper.

Context and contribution

This paper has two core goals: (1) to explore the value and limitations of relative long-term cost effectiveness analysis as a prioritization tool for disaster risk mitigation measures in order to improve decision making and (2) to use this prioritization tool to determine if resilient foods are more cost effective than AGI safety (which would make resilient food the highest priority area of GCR/X-risk mitigation research). As I am not qualified to directly weigh in on the extent to which the authors’ achieved either goal, I will reflect on the “worthiness” of this goal within the broader context of work going on in the fields of X-risk/GCR, long-termism, science policy, and public policy - and the extent to which the authors’ findings are effectively communicated to these audiences.

Within this broader context, I believe that these are indeed worthy (and urgent) objectives. The effective prioritization of scarce resources to the myriad potential R&D projects that could (1) reduce key uncertainties, (2) improve political decision-making, and (3) provide solutions that decrease the impact and/or likelihood of civilization-ending risk events is a massive and urgent research challenge. Governments and granting agencies are desperate for rigorous, evidence-based guidance on how to allocate finite funding across candidate projects. Such prioritization is impeded by uncertainty about the potential benefits of various R&D activities (partially resulting from uncertainty about the likelihood and magnitude of the risk event itself - but also from uncertainty about the potential uncertainty-reducing and harm/likelihood-reducing “power” of the R&D). Therefore, the authors’ cost-effectiveness model, which attempts to decrease uncertainty about the potential uncertainty-reducing and harm/likelihood-reducing “power” of resilient food R&D and compare it to R&D on AGI safety, is an important contribution. It combines and applies a number of existing analytical tools in a novel way and proposes a tool for quantifying the relative value of (deeply uncertain) R&D projects competing for scarce resources.

Overall, the authors are cautious and vigilant in qualifying their claims - which is essential when conducting analysis that relies on the quasi-quantiative aggregation of the (inter)subjective beliefs of experts and combines several models (each with their own assumptions).

Theoretical/epistemic uncertainty

I largely agree with the authors’ dismissal of theoretical/epistemic uncertainty (not that they dismiss its importance or relevance - simply that they believe there is essentially nothing that can be done about it in their analysis). Their suggestion that “results should be interpreted in an epistemically reserved manner” (essentially a plea for intellectual humility) should be a footnote in every scholarly publication - particularly those addressing the far future, X-risk, and value estimations of R&D.

However, the authors could have bolstered this section of the paper by identifying some potential sources of epistemic uncertainty and suggesting some pathways for further research that might reduce it. I recognize that they are both referring to acknowledged epistemic uncertainties - which may or may not be reducible - as well as unknown epistemic uncertainties (i.e., ignorance - or what they refer to as “cluelessness”). It would have been useful to see a brief discussion of some of these acknowledged epistemic uncertainties (e.g., the impact of resilient foods on public health, immunology, and disease resistance) to emphasize that some epistemic uncertainty could be reduced by exactly the kind of resilient food R&D they are advocating for.

Presentation of model outputs

When effectively communicating uncertainties associated with research findings to multiple audiences, there is a fundamental tradeoff between the rigour demanded by other experts and the digestibility/usability demanded by decision makers and lay audiences. For example, this tradeoff has been well-documented in the literature on the IPCC’s uncertainty communication framework (e.g., Janzwood 2020). What fellow-modelers/analysts want/need is usually different from what policymakers want/need. The way that model outputs are communicated in this article (e.g. 84% confidence that the 100 millionth dollar is more cost-effective) leans towards rigour and away from digestibility/usability. A typical policymaker who is unfamiliar with the modeling tools used in this analysis may assume that an 84% probability value was derived from historical frequencies/trials in some sort of experiment - or that it simply reflects an intersubjective assessment of the evidence by the authors of the article. Since the actual story for how this value was calculated is rather complex (it emerges from a model derived from the aggregation of the outputs of two sub-models, which both aggregate various types of expert opinions and other forms of data) - it might be more useful to communicate the final output qualitatively.

This strategy has been used by the IPCC to varying levels of success. These qualitative uncertainty terms can align with probability intervals. For example, 80-90% confidence could be communicated as “high confidence” or “very confident.” >90% could be communicated as “extremely confident.” There are all sorts of interpretation issues associated with qualitative uncertainty scales - and some scales are certainly more effective than others (again, see Janzwood 2020) but it is often useful to communicate findings in two “parallel tracks” - one for experts and one for a more lay/policy-focused audience.

Placing the article’s findings within the broader context of global priorities and resource allocation

Recognizing the hard constraints of word counts - and that a broader discussion of global priorities and resource allocation was likely “out of scope” - this article could be strengthened (or perhaps simply expanded upon in future work) by such a discussion. The critical piece of context is the scarcity of resources and attention within the institutions making funding decisions about civilization-saving R&D (governments, granting organizations, private foundations, etc.). There are two dimensions worth discussing here. First, R&D activities addressing risks that are generally considered low-probability/high-impact with relatively long timelines (although I don’t think the collapse of global agricultural would qualify as low-risk - nor is the likely timeline terribly long - but those are my priors) are competing for scarce funding/attention against R&D activities addressing lower-impact risks believed to be shorter-term and more probable (e.g., climate change, the next pandemic, etc.). I think most risk analysts - even hardcore “long-termists” - would agree that an ideal “R&D funding portfolio” be somewhat diversified across these categories of risk. It is important to acknowledge the complexity associated with resource allocation - not just between X-risks but between X-risks and other risks.

Second, there is the issue of resource scarcity itself. On the one hand, there are many “high value” candidate R&D projects addressing various risks that societies can invest in - but only a finite amount of funding and attention to allocate between them. So, these organizations must make triage decisions based on some criteria. On the other hand, there are also a lot of “low” or even “negative value” R&D activities being funded by these organizations - in addition to other poor investments - that are providing little social benefit or are actively increasing the likelihood/magnitude of various risks. I believe that it is important in these sort of discussions about R&D prioritization and resource scarcity to point out that the reosource pool need not be this shallow - and to identify some of the most egregious funding inefficiencies (e.g., around fossil fuel infrastructure expansion). It should go without saying— but ideally, we could properly resource both resilient food and AGI safety research.

Evaluator details

1. Name: Scott Janzwood
2. How long have you been in this field? 10 years
3. How many proposals and papers have you evaluated? ~25 proposals, ~10 papers

Evaluation 1

Ratings and predictions

Ratings (1-100)

• Overall assessment: 40 CI: 20-60
  • Comment: See main review
• Advancing knowledge and practice: 30 CI: 20-60
  • Comment: The paper itself makes an important argument about resilient foods, but I don’t know if the additional element of AGI risk adds much to Denkenberger & Pearce (2016)
• Methods: Justification, reasonableness, validity, robustness: 50 CI: 40-60
  • Comment: Very major limitations around the survey method, and implementation of certain parts of the parameter sensitivity analysis. However many elements of a high standard
• Logic & communication: 60 CI: 40-75
  • Comment: Major limitations around the logic and communication of the theoretical model of cost-effectiveness used in the paper. Minor limitations of readability and reporting which could have been addressed before publication (such as reporting 95% CIs without medians, and not reporting overall cost and benefit estimates)
• Open, collaborative, replicable: 70 CI: 40-75
  • Comment: Provided models are shared with any reader who asks, I couldn’t ask for more here. Limitations of survey replicability (particularly E model) prevent perfect score
• Relevance to global priorities: 90 CI: 60-95
  • Comment: I’d be surprised if I ever read a paper with more relevance to global priorities, although as mentioned there are a few version of this argument circulating such as Denkenberger & Pearce (2016)

Journal predictions (1-5)

• What ‘quality journal’ do you expect this work will be published in? 2 CI: 1-2
• On a ‘scale of journals’, what tier journal should this be published in? 2 CI: 1-2

Written report

This is a very interesting paper on an important and neglected topic. I’d be surprised if I ever again read a paper with such potential importance to global priorities. The authors motivate the discussion well, and should be highly commended for their clear presentation of the structural features of their model, and the thoughtful nature in which uncertainty was addressed head-on in the paper.

Overall, I suspect the biggest contribution this paper will make is contextualising the existing work done by the authors on resilient food into the broader literature of long-termist interventions. This is a significant achievement, and the authors should feel justifiably proud of having accomplished it. However, the paper unfortunately has a number of structural and technical issues which should significantly reduce a reader’s confidence in the quantitative conclusions which aim to go beyond this contextualisation.

In general, there are three broad areas where I think there are material issues with the paper:

1. The theoretical motivation for their specific philosophy of cost-effectiveness, and specifically whether this philosophy is consistent throughout the essay
2. The appropriateness of the survey methods, in the sense of applying the results of a highly uncertain survey to an already uncertain model
3. Some specific concerns with parameterisation

None of these concerns touch upon what I see at the main point of the authors, which I take to be that ‘fragile’ food networks should be contextualised alongside other sources of existential risk. I think this point is solidly made, and important. However, they do suggest that significant additional work may be needed to properly prove the headline claim of the paper, which is that in addition to being a source of existential risk the cost-effectiveness of investing in resilient food is amongst the highest benefit-per-cost of any existential risk mitigation.

Structure of cost-effectiveness argument

One significant highlight of the paper is the great ambition it shows in resolving a largely intractable question. Unfortunately, I feel this ambition is also something of a weakness of the paper, since it ends up difficult to follow the logic of the argument throughout.

• Structurally, the most challenging element of this paper in terms of argumentative flow is the decision to make the comparator for cost-effectiveness analysis ‘AGI Catastrophe’ rather than ‘do nothing’. My understanding is that the authors make this decision to clearly highlight the importance of resilient food – noting that, “if resilient foods were more cost effective than AGI safety, they could be the highest priority [for the existential risk community]” (since the existential risk community currently spends a lot on AGI Risk mitigation). So roughly, they start with the assumption that AI Risk must be cost-effective, and argue that anything more cost-effective than this must therefore also be cost-effective. The logic is sound, but this decision causes a number of problems with interpretability, since it requires the authors to compare an already highly uncertain model of food resilience against a second highly uncertain model of AGI risk.
• The biggest issue with interpretability this causes is that I struggle to understand what features of the analysis are making resilient food appear cost-effective because of some feature of resilient food, and which are making resilient food appear cost-effective because of some feature of AI. The methods used by the authors mean that a mediocre case for resilient food could be made to look highly cost-effective with an exceptionally poor case for AI, since their central result is the multiplier of value on a marginally invested dollar for resilient food vs AI. This is important, because the authors’ argument is that resilient food should be funded because it is more effective than AI Risk management, but this is motivated by AI Risk proponents agreeing AI Risk is important – in scenarios where AI Risk is not worth investing in then this assumption is broken and cost effectiveness analysis against a ’do nothing’ alternative is required. For example, the authors do not investigate scenarios where the benefit of the intervention in the future is negative because “negative impacts would be possible for both resilient foods and AGI safety and there is no obvious reason why either would be more affected”. While this is potentially reasonable on a mathematical level, it does mean that it would be perfectly possible for resilient foods to be net harmful and the paper not correctly identify that funding them is a bad idea – simply because funding AI Risk reduction is an even worse idea, and this is the only given alternative. If the authors want to compare AGI risk mitigation and resilient foods against each other without a ‘do nothing’ common comparator (which I do not think is a good idea), they must at the very least do more to establish that the results of their AI Risk model map closely to the results which cause the AI Risk community to fund AI Risk mitigation so much. As this is not done in the paper, a major issue of interpretability is generated.
• A second issue this causes is that the authors must make an awkward ‘assumption of independence’ between nuclear risk, food security risk and AI risk. Although the authors identify this as a limitation of their modelling approach, the assumption does not need to be made if AI risk is not included as a comparator in the model. I don’t think this is a major limitation of the work, but an example of how the choice of comparator has an impact on structural features of the model beyond just the comparator.
• More generally, this causes the authors to have to write up their results in a non-natural fashion. As an example of the sort of issues this causes, conclusions are expressed in entirely non-natural units in places (“Ratio of resilient foods mean cost effectiveness to AGI safety mean cost effectiveness” given $100m spend), rather than units which would be more natural (“Cost-effectiveness of funding resilient food development”). I cannot find expressed anywhere in the paper a simple table with the average costs and benefits of the two interventions, although a reference is made to Denkenberger & Pearce (2016) where these values were presented for near-term investment in resilient food. This makes it extremely hard for a reader to draw sensible policy conclusions from the paper unless they are already an expert in AGI risk and so have an intuitive sense of what an intervention which is ‘3-6 times more cost-effective than AGI risk reduction’ looks like. The paper might be improved by the authors communicating summary statistics in a more straightforward fashion. For example, I have spent some time looking for the probability the model assigns to no nuclear war before the time horizon (and hence the probability that the money spent on resilient food is ‘wasted’ with respect to the 100% shortfall scenario) but can’t find this – that seems to be quite an important summary statistic but it has to be derived indirectly from the model.

Fundamentally, I don’t understand why both approaches were not compared to a common scenario of ‘do nothing’ (relative to what we are already doing). The authors’ decision to compare AGI Risk mitigation to resilient foods directly would only be appropriate if the authors expect that increasing funding for resilient food decreased funding for AI safety (that is to say, the authors are claiming that there is a fixed budget for AI-safety-and-food-resilience, and so funding for one must come at the expense of the other). This might be what the authors have in mind as a practical consequence of their argument, as there is an implication that funding for resilient foods might come from existing funding deployed to AGI Risk. But it is not logically necessary that this is the case, and so it creates great conceptual conclusion to include it in a cost-effectiveness framework that requires AI funding and resilient food funding to be strictly alternatives. To be clear, the ‘AI subunit’ is interesting and publishable in its own right, but in my opinion simply adds complexity and uncertainty to an already complex paper.

Continuing on from this point, I don’t understand the conceptual framework that has the authors consider the value of invested dollars in resilient food at the margin. The authors’ model of the value of an invested dollar is an assumption that it is distributed logarithmically. Since the entire premise of the paper hinges on the reasonability of this argument, it is very surprising there is no sensitivity analysis considering different distributions of the relationship between intervention funding and value. Nevertheless, I am also confused as to the model even on the terms the authors describe; the authors’ model appears to be that there is some sort of ‘invention’ step where the resilient food is created and discovered (this is mostly consistent with Denkenberger & Pearce (2016), and is the only interpretation consistent with the question asked in the survey). In which case, the marginal value of the first invested dollar is zero because the ’invention’ of the food is almost a discrete and binary step. The marginal value per dollar continues to be zero until the 86 millionth dollar, where the marginal value is the entire value of the resilient food in its entirety. There seems to be no reason to consider the marginal dollar value of investment when a structural assumption made by the authors is that there is a specific level of funding which entirely saturates the field, and this would make presenting results significantly more straightforward – it is highly nonstandard to use marginal dollars as the unit of cost in a cost-effectiveness analysis, and indeed is so nonstandard I’m not certain fundamental assumptions of cost-effectiveness analysis still hold. I can see why the authors have chosen to bite this bullet for AI risk given the existing literature on the cost of preventing AI Catastrophe, but there seems to be no reason for it when modelling resilient food and it departs sharply from the norm in cost-effectiveness analysis.

Finally, I don’t understand the structural assumptions motivating the cost-effectiveness of the 10% decline analysis. The authors claim that the mechanism by which resilient foods save lives in the 10% decline analysis is that “the prices [of non-resilient food] would go so high that those in poverty may not be able to afford food” with the implication that resilient foods would be affordable to those in poverty and hence prevent starvation. However, the economic logic of this statement is unclear. It necessitates that the production costs of resilient food is less than the production costs of substitute non-resilient food at the margin, which further implies that producers of resilient food can command supernormal profits during the crisis, which is to say the authors are arguing that resilient foods represent potentially billions of dollars of value to their inventor within the inventor’s lifetime. It is not clear to me why a market-based solution would not emerge for the ‘do nothing’ scenario, which would be a critical issue with the authors’ case since it would remove the assumption that ‘resilient food’ and ‘AGI risk’ are alternative uses of the same money in the 10% scenario, which is necessary for their analysis to function. The authors make the further assumption that preparation for the 100% decline scenario is highly correlated with preparation for the 10% decline scenario, which would mean that a market-based solution emerging prior to nuclear exchange would remove the assumption that ‘resilient food’ and ‘AGI risk’ are alternative uses of the same money in the 100% decline scenario. A supply and demand model might have been a more appropriate model for investigating this effect. Once again, I note that the supply and demand model alone would have been an interesting and publishable piece of work in its own right.

Overall, I think the paper would have benefitted from more attention being paid to the underlying theory of cost-effectiveness motivating the investigation. Decisions made in places seem to have multiplied uncertainty which could have been resolved with a more consistent approach to analysis. As I highlighted earlier, the issues only stem from the incredible ambition of the paper and the authors should be commended for managing to find a route to connect two separate microsimulations, an analysis of funding at the margin and a supply-and-demand model. Nevertheless, the combination of these three approaches weakens the ability to draw strong conclusions from each of these approaches individually.

Methods

With respect to methods, the authors use a Monte Carlo simulation with distributions drawn from a survey of field experts. The use of a Monte Carlo technique here is an appropriate choice given the significant level of uncertainty over parameters. The model appears appropriately described in the paper, and functions well (I have only checked the models in Guesstimate, as I could not make the secondary models in Analytica function). A particular highlight of the paper is the figures clearly laying out the logical interrelationship of elements of the model, which made it significantly easier to follow the flow of the argument. I note the authors use ‘probability more effective than’ as a key result, which I think is a natural unit when working in Guesstimate. This is entirely appropriate, but a known weakness of the approach is that it can bias in favour of poor interventions with high uncertainty. The authors could also have presented a SUCRA analysis which does not have this issue, but they may have considered and rejected this approach as unnecessary given the entirely one-sided nature of the results which a SUCRA would not have reversed.

The presentation of the sensitivity analysis as ‘number of parameters needed to flip’ is nonstandard, but a clever way to intuitively express the level of confidence the authors have in their conclusions. Although clever, I am uncertain if the approach is appropriately implemented; the authors limit themselves to the 95% CI for their definition of an ‘unfavourable’ parameter, and I think this approach hides massive structural uncertainty with the model. For example, in Table 5 the authors suggest their results would only change if the probability of nuclear war per year was 4.8x10^-5 (plus some other variables changing) rather than their estimated of 7x10^-3 (incidentally, I think the values for S model and E model are switched in Table 5 – the value for pr(nuclear war) in the table’s S model column corresponds to the probability given in the E model). But it is significantly overconfident to say that risk of nuclear war per year could not possibly be below 4.8x10^-5, so I think the authors overstate their certainty when they say “reverting [reversing?] the conclusion required simultaneously changing the 3-5 most important parameters to the pessimistic ends”; in fact it merely requires that the authors have not correctly identified the ‘pessimistic end’ of any one of the five parameters, which seems likely given the limitations in their data which I will discuss momentarily. I personally would have found one- and two-dimensional threshold analysis a more intuitive way to present the results, but I think the authors have a reasonable argument for their approach. As described earlier, I have some concerns that an appropriate amount of structural sensitivity analysis was undertaken, but the presentation of uncertainty analysis is appropriate in its own terms (if somewhat nonstandard).

Overall, I have no major concerns about the theory or application of the modelling approach. However, I have a number of concerns with the use of the survey instrument:

First, the authors could have done more to explain the level of uncertainty their survey instrument contains. They received eight responses, which is already a very low number of responses for a quantitative survey. In addition, two of the eight responses were from authors of the paper. The authors discuss ‘response bias’ and ‘demand characteristic bias’ which would not typically be applied to data generated by an approximately autoethnographic process – it is obvious that the authors of a survey instrument know what purpose the instrument is to be used for, and have incentives to make the survey generate novel and interesting findings. It might have been a good sensitivity analysis to exclude responses from the authors and other researchers associated with ALLFED since there is a clear conflict of interest that could bias results here.

Second, issues with survey data collection are compounded by the fact that some estimates which are given in the S Model are actually not elicited with the survey technique – they are instead cited to Denkenberger & Pearce (2016) and Denkenberger & Pearce (2017). This is described appropriately in the text, but not clearly marked in the summary Table 1 where I would expect to see it, and the limitation this presents is not described clearly. To be explicit, the limitation is that at least two key parameters in the model are based on a sample of the opinions of two of the eight survey respondents, rather than the full set of eight respondents. As an aside on presentation, the decision to present lower and upper credible intervals in Table 1 rather than median is non-standard for an economics paper, although perhaps this is a discipline-specific convention I am unaware of. Regardless, I’m not sure it is appropriate to present the lowest of eight survey responses as the ‘5th percentile’, as it is actually the 13th percentile and giving 95% confidence intervals implies a level of accuracy the survey instrument cannot reach. While I appreciate the 13th percentile of 8 responses will be the same as the 5th centile of 100 samples drawn from those responses, this is not going to be clear to a casual reader of the paper. ‘Median (range)’ might be a better presentation of the survey data in this table, with better clarity on where each estimate comes from. Alternatively, the authors could look at fitting a lognormal distribution to the survey results using e.g. method of moments, and then resample from the new distribution to create a genuine 95% CI. Regardless, given the low number of responses, it might have been appropriate simply to present all eight estimates for each relevant parameter in a table.

Third, the authors could have done more to make it clear that the ‘Expert Model’ was effectively just another survey with an n of 1. Professor Sandburg, who populated the Expert Model, is also an author on this paper and so it is unclear what if any validation of the Expert Model could reasonably have been undertaken – the E model is therefore likely to suffer from the same drawbacks as the S model. It is also unclear if Professor Sandburg knew the results of the S Model before parameterising his E Model – although this seems highly likely given that 25% of the survey’s respondents were Professor Sandburg’s co-authors. This could be a major source of bias, since presumably the authors would prefer the two models to agree and the expert parameterising the model is a co-author. I also think more work is needed to be done establishing the Expert’s credentials in the field of agricultural R&D (necessary for at least some of the parameter estimates); although I happily accept Professor Sandburg is a world expert on existential risk and a clear choice to act as the parameterising ‘expert’ for most parameters, I think there may have been alternative choices (such as agricultural economists) who may have been more obviously suited to giving some estimates. There is no methodological reason why one expert had to be selected to populate the whole table, and no defence given in the text for why one expert was selected - the paper is highly multidisciplinary and it would be surprising if any one individual had expert knowledge of every relevant element. Overall, this limitation makes me extremely hesitant to accept the authors’ argument that the fact that S model and E model are both robust means the conclusion is equally robust

Generally, I am sympathetic to the authors’ claim that there is unavoidable uncertainty in the investigation of the far future. However, the survey is a very major source of avoidable uncertainty, and it is not a reasonable decision of the authors to present the uncertainty due to their application of survey methods as the same kind of thing as uncertainty about the future potential of humanity. There are a number of steps the authors could have taken to improve the validity and reliability of their survey results, some of which would not even have required rerunning the survey (to be clear however, I think there is a good case for rerunning the survey to ensure a broader panel of responses). With the exception of the survey, however, methods were generally appropriate and valid.

Parameter estimates

Notwithstanding my concerns about the use of the survey instrument, I have some object level concerns with specific parameters described in the model.

• The discount rate for both costs and benefits appears to be zero, which is very nonstandard in economic evaluation. Although the authors make reference to “long termism, the view that the future should have a near zero discount rate”, the reference for this position leads to a claim that a zero rate of pure time preference is common, and a footnote observing that “the consensus against discounting future well-being is not universal”. To be clear, pure time preference is only one component of a well-constructed discount rate and therefore a discount rate should still be applied for costs, and probably for future benefits too. Even notwithstanding that I think this is an error of understanding, it is a limitation of the paper that discount rates were not explored, given they seem very likely to have a major impact on conclusions.
• A second concern I have relating to parameterisation is the conceptual model leading to the authors’ proposed costing for the intervention. The authors explain their conceptual model linking nuclear war risk to agricultural decline commendably clearly, and this expands on the already strong argument in Denkenberger & Pearce (2016). However, I am less clear on their conceptual model linking approximately $86m of research to the widescale post-nuclear deployment of resilient foods. The assumption seems to be (and I stress this is my assumption based on Denkenberger & Pearce (2016) – it would help if the authors could make it explicit) that $86m purchases the ‘invention’ of the resilient food, and once the food is ‘invented’ then it can be deployed when needed with only a little bit of ongoing training (covered by the $86m). This seems to me to be an optimistic assumption; there seems to be no cost associated with disseminating the knowledge, or any raw materials necessary to culture the resilient food. Moreover, the model seems to structurally assume that distribution chains survive the nuclear exchange with 100% certainty (or that the materials are disseminated to every household which would increase costs), and that an existing resilient food pipeline exists at the moment of nuclear exchange which can smoothly take over from the non-resilient food pipeline.

I have extremely serious reservations about these points. I think it is fair to say that an economics paper which projected benefits as far into the future as the authors do here without an exploration of discount rates would be automatically rejected by most editors, and it is not clear why the standard should be so different for existential risk analysis. A cost of $86m to mitigate approximately 40% of the impact of a full-scale nuclear war between the US and a peer country seems prima facie absurd, and the level of exploration of such an important parameter is simply not in line with best practice in a cost-effectiveness analysis (especially since this is the parameter on which we might expect the authors to be least expert). I wouldn’t want my reservations about these two points to detract from the very good and careful scholarship elsewhere in the paper, but neither do I want to give the impression that these are just minor technical details – these issues could potentially reverse the authors’ conclusions, and should have been substantially defended in the text.

Conclusions

Overall, this is a novel and insightful paper which is unfortunately burdened with some fairly serious conceptual issues. The authors should be commended for their clear-sighted contextualisation of resilient foods as an issue for discussion in existential risk, and for the scope of their ambition in modelling. Academia would be in a significantly better place if more authors tried to answer far-reaching questions with robust approaches, rather than making incremental contributions to unimportant topics.

Where the issues of the paper lie are structural weaknesses with the cost-effectiveness philosophy deployed, methodological weaknesses with the survey instrument and two potentially conclusion-reversing issues with parameterisation which should have been given substantially more discussion in the text. I am not convinced that the elements of the paper which are robust are sufficiently robust to overcome these weaknesses – my view is that it would be premature to reallocate funding from AI Risk reduction to resilient food on the basis of this paper alone. The most serious conceptual issue which I think needs to be resolved before this can happen is to demonstrate that ‘do nothing’ would be less cost-effective than investing $86m in resilient foods, given that the ‘do nothing’ approach would potentially include strong market dynamics leaning towards resilient foods. I agree with the authors that an agent-based model might be appropriate for this, although a conventional supply-and-demand model might be simpler.

I really hope the authors are interested in publishing follow-on work, looking at elements which I have highlighted in this review as being potentially misaligned to the paper that was actually published but which are nevertheless potentially important contributions to knowledge. In particular, the AI subunit is novel and important enough for its own publication.

Evaluator details

1. Name: Alex Bates
2. How long have you been in this field? In the field of cost-effectiveness analysis, 10 years. I wouldn’t consider myself to be in the field of x-risk
3. How many proposals and papers have you evaluated? I’ve lost count, but probably mid double figures - perhaps 50?

Hm. Sure a political-religious Christmas was in there somewhere? Still useful

Author Response

Reviewer #2 (Public Review):

Susswein et al. analyze a fine-scale, novel data stream of human mobility, openly available from Safegraph, based on the usage of mobile apps with GPS and sampled from over 45 million smartphone devices. They define a metric $\sigma_{it}$, properly normalized, that quantifies the propensity for visits to indoor locations relative to outdoor locations in a given county $i$ at week $t$. For each pair of counties $i$ and $j$, they compute the Pearson correlation coefficient $\rho_{ij}$ between the corresponding $\sigma$ metrics. This generates a correlation matrix that can be interpreted as the adjacency matrix of a network. They then perform community detection on this network/matrix, effectively clustering together time series that are correlated. This identifies three main clusters of counties, characterized geographically as either in the north of the country, in the south of the country, and possibly in tourism active areas. They then show, via a simple model, how including over-simplified models of seasonality may affect infectious disease models.

This work is very interesting for the infectious disease modeling community, as it addresses a complex problem introducing a new data stream.

This work builds on several strengths, among which:

It is the first analysis of the Safegraph dataset to capture seasonality in indoor behavior.

It provides a simple metric to quantify indoor activity, that thanks to the dataset can be computed with a high level of spatial detail.

It aims at characterizing clusters of counties with a similar pattern of indoor activity.

It aims at quantifying the impact of neglecting finer-scale patterns of seasonality, for example considering seasonality to be homogeneous at the US level.

We thank the reviewer for the positive review of our work.

At the same time, it presents several weaknesses that should be addressed to improve the methodology, its results, and the implication:

There is no quantitative comparison of the newly introduced metric for indoor activity with other proxies of seasonality (e.g. temperature or relative humidity). The (dis)similarity with other proxies may help in assessing the importance of this metric, showing why it can not be exchanged with other data sources (like temperature data) that are widely available and are not affected by sampling issues (more on that later).

We have now added supplementary figures (Figure S3) to illustrate how indoor activity seasonality compares with temperature and humidity. We have also added text to the Results and the Discussion to discuss this point.

A major flow of the analysis is to perform community detection on a network defined by the correlation between time series with an algorithm that is based on modularity optimization. As explained in Macmahon et al.[1], all modularity optimization methods rely on null assumptions that in the case of correlation between time series are violated. Therefore, there is a very strong potential bias in their results that is not accounted for. Possible solutions could be to proceed via the methodology presented in [1] or via a different type of algorithm (e.g. Infomap [2]). In both cases, as the network is thresholded (considering only a correlation larger than 0.9), a more quantitative assessment of the impact of the threshold value should be included.

References

[1] Mel MacMahon and Diego Garlaschelli Phys. Rev. X 5, 021006 (2015).

[2] Martin Rosvall and Carl T. Bergstrom PNAS 105, 1118 (2008).

We thank the reviewer for making this excellent point. We have now added Supplementary Figures S13 and S14. In Figure S13, we demonstrate the robustness of our clustering results with different correlation thresholds. (We have also corrected a typo in our original Methods section which mistakenly stated our correlation threshold as 0.9 rather than the 90th percentile which is what we used.) In Figure S14, we show the clustering results using a different clustering algorithm. In an effort to test a non-network-based clustering approach, we use a hierarchical clustering approach and find a consistent partition of the US to our main results.

It is not clear what is the added value of the data on indoor activity, as no fitting to real data is performed. Although this may be considered beyond the scope of this paper, I think it would be crucial to quantify how much a data-informed model would better describe real epidemic data (for example in the case of COVID-19). For now, only the impact of neglecting heterogeneity in indoor activity is shown, comparing a model with region-average parameters vs a model with county-level average parameters. Given that the dataset comes with potential bias in sampling (more on this later) it would be good to assess its goodness in predicting real epidemic spread. When showing results from different models, no visible errors are shown on the plot. How have the errors been estimated?

We appreciate this point by the reviewer, and agree that future work will have to consider how indoor activity seasonality affects our ability to capture observed transmission trends. However, such work would additionally need careful characterization of other seasonal factors hypothesized to drive transmission (including environmental and other behavioral factors), and is beyond the scope of our work. Instead, in Figure 4 we aim to (a) provide the infectious disease modeling community with empirically-inferred parameters for a simple sinusoidal model which is commonly used in infectious disease models to capture transmission seasonality; and (b) demonstrate the implications of ignoring geographic heterogeneity in transmission seasonality in theoretical models of disease dynamics, which are commonly used for scenario analysis and model-based intervention design. As we demonstrate, transmission seasonality described by such sinusoidal models, even when they are empirically characterized as in our case, can lead to meaningfully different epidemic dynamics when transmission seasonality varies from the assumptions.

Additionally, there is no uncertainty included in Figure 4B because transmission seasonality is either based on empirical data point per time step, or on the fitted sinusoidal model (where the estimated parameters have negligible standard errors).

The dataset is presented as representative of the US population. However, this has not been assessed over time. As adherence to social distancing is influenced by several socio-economic determinants the lack of representativity in certain strata of the population at a given time may introduce an important bias in the dataset. Although this is an inherent limitation of the dataset, it should be discussed in the paper more thoroughly.

We agree with the reviewer that this is a limitation. However, we do not have any way of assessing demographic representation in the dataset over time. We have instead included an additional sentence into the Discussion section acknowledging this point.

In conclusion, I think that the methodology should be revised to account for the fact that the analysis is performed on a correlation matrix. Capturing seasonal patterns of indoor activity can help in tackling the crucial problem of seasonality in human behavior. This could help in identifying effective strategies of disease containment able to curb disease spread at a lower societal cost than fully-fledged lockdowns.

We thank the reviewer again for their helpful suggestions.

!- explanation of : Atman -the thing that remains the same while everything else changes

Author Response

Reviewer #1 (Public Review):

In the current study, the authors reanalyze a prior dataset testing effects of D2 antagonism on choices in a delay discounting task. While the prior report using standard analysis, showed no effects, the current study used a DDM to examine more carefully possible effects on different subcomponents of the decision process. This approach revealed contrasting effects of D2 blockade on the effect of reward size differences and bias. Effects were uncorrelated, suggesting separate mechanisms perhaps. The authors speculate that these opposing effects explain the variability in effects across studies, since they mean that effects would depend on which of these factors is more important in a particular design. Overall the study is novel and well-executed, and the explanation offers interesting insight into neural processes.

We thank the reviewer for judging our study as interesting and well-executed.

Reviewer #2 (Public Review):

The authors aim to test the hypothesis that dopamine mediates the evaluation of temporal costs in intertemporal choice in humans, with a specific goal of synthesizing the competing accounts and previous results regarding whether dopamine increases or decreases evaluation of delays in comparing differently delayed future rewards. To do this, they computationally dissect the impact of the drug amisulpride, a D2R antagonist, using a variant of a sequential sampling model, the drift-diffusion model (DDM), that is well established in decision-making literature as a cognitive process model of choice. This model allows the dissociation of starting bias from the rate at which decision evidence is integrated ('drift'), which the authors map to different accounts of the role of dopamine: the temporal proximity of an outcome is proposed to impact bias, while the cost of a delay to impact the drift rate of evidence evaluation/accumulation. Consistent with previous results, and perhaps integrating conflicting findings, the authors find that d2R blockade impacts both bias and drift rate in a cohort of 50 participants, demonstrating dopaminergic action at this receptor is implicated in dissociable components of intertemporal choice, with D2R block reducing the bias towards sooner, more temporally proximate rewards as well as enhancing the contrast between reward magnitudes irrespective of delay, effectively diminishing the effect of delay in the drug condition. These effects are consistent across a small subset of alternative models, confirming the multiple cognitive mechanisms through which D2R block impacts intertemporal choice is a robust feature of decisions on this task.

Overall, this study is a detailed dissection of the specific effects of amisulpride on a type of future-oriented, hypothetical intertemporal choice, and provides consistent evidence integrating conflicting accounts that implicate dopaminergic signaling on evaluation of the cognitive costs, such as a delay, on choice. However the specificity of the empirical intervention and the task design limits the interpretation of the broader dopaminergic mechanisms at play in intertemporal choice, especially given the complexity of receptor specificity of this drug, dopamine precursor availability and individual differences and the specifics of the intertemporal choice in this task. As it stands, the results contribute an interesting, synthesized account of how D2R manipulation can impact evaluation of delays in multiple ways, that will likely be useful for motivating future studies and more detailed computational assessments of the cognitive process-level components of intertemporal choice more generally.

We thank the reviewer for the positive overall evaluation of our study. We revised the manuscript according to the reviewer’s comments, addressing also the receptor specificity of amisulpride and the specifics of the administered intertemporal choice task, which further improved the quality of the manuscript.

The focus of this study is important, and delineating the role of DA in intertemporal choice is of high relevance given DA disfunction is prevalent in many psychiatric disorders and a key target of pharmacological treatment. While the hypotheses of the current study are framed with respect to "costs", the task used by the authors reduces these to evaluation of a hypothetical delay, one which the participants do not necessarily experience in the context of the task. In some respects this is reasonable, given the prevalence of this task paradigm in testing temporal aspects of choice in humans in an economic sense. However, humans are also notoriously subject to framing effects and the impact of instructions in cognitive tasks like these, which can limit the generality of the conclusions, and in particular the specific ways in which a delay can be interpreted as costly (for eg cost as loss of potential earnings, cost as effortful waiting, cost as computational/simulation cost in future evaluation). Given the hypothesis recruits the idea of cost in assessing the role of dopamine, testing for generality in the effects of amisulpride in related but differently framed tasks seems critical for making this link in a general sense, and in connecting it to the previous studies in the literature the authors point to as demonstrating conflicting effects.

We agree that it is important to discuss whether our findings for delay costs can be generalized to other costs types as well, such as risk, social costs, effort, or opportunity costs. Based on a recent literature review (Soutschek, Jetter, & Tobler, 2022), we speculate that dopamine may moderate proximity effects also for risk and social costs but not for effortful rewards, though we emphasize that these hypotheses still require more direct empirical evidence. We also discuss the issue that delays can be perceived as costly in different ways. While in some tasks participants actually experience the waiting time until reward delivery, such that delayed rewards are associated with opportunity costs, in our current task paradigm delayed rewards were virtually free of opportunity costs as participants could engage in other reward-related behaviors during the waiting time. Previous studies suggest that lower tonic dopamine levels reduce the sensitivity to opportunity costs (Niv et al., 2007), which seems in line with our finding that amisulpride decreases the influence of delays on the starting bias parameter. Nevertheless, we emphasize that further evidence is needed to decide whether dopamine shows similar effects for experienced and non-experienced waiting costs. In the revised manuscript, we discuss the cost specificity of our findings on p.22:

“An important question refers to whether our findings for delay costs can be generalized to other types of costs as well, including risk, social costs (i.e., inequity), effort, and opportunity costs. In a recent review, we proposed that dopamine might also moderate proximity effects for reward options differing in risk and social costs, whereas the existing literature provides no evidence for a proximity advantage for effort-free over effortful rewards (Soutschek et al., 2022). However, these hypotheses need to be tested more explicitly by future investigations. Dopamine has also been ascribed a role for moderating opportunity costs, with lower tonic dopamine reducing the sensitivity to opportunity costs (Niv et al., 2007). While this appears consistent with our finding that amisulpride (under the assumption of postsynaptic effects) reduced the impact of delay on the starting bias, it is important to note that choosing delayed rewards did not involve any opportunity costs in our paradigm, given that participants could pursue other rewards during the waiting time. Thus, it needs to be clarified whether our findings for delayed rewards without experienced waiting time can be generalized to choice situations involving experienced opportunity costs.”

Further, while the study aims to test the actions of dopamine broadly, the empirical manipulation is limited to the action of amisulpride, a D2R anatgonist. There is little to no discussion of, or control for, the relationship between dopaminergic action at D2 receptors (the site of amisulpride effects) and wider mechanisms of dopaminergic action at other sites eg D1-like receptors, and the interplay between activation at these two receptor types alongside baseline levels of dopamine concentration. This is necessary for a comprehensive account of dopamine effects on intertemporal choice as the authors aim to test, as opposed to a specific test of the role of the D2 receptor, which is what the study achieves. On a related note, in some preparations at least, amisulpride also acts at some of the 5-HT receptors, raising the possibility of a non-dopaminergic mechanism by which this drug might impact intertemporal decisions. This possibility, while it would not be expected to act without dopaminergic effects as well, is consistent with established effects of serotonin on waiting behaviors and patience. Granted, the limits of pharmacology in humans does not necessarily mean this can be controlled for, it should be kept in mind with a systemic manipulation such as this.

We agree with the reviewer that it is important to distinguish between the contributions of D1 and D2 receptors to decision making, given that these receptor families are hypothesized to have dissociable functional roles. We therefore re-analyzed also data on the impact of a D1 agonist on intertemporal decision making (previous findings for this data set were published in Soutschek et al., 2020, Biological Psychiatry). This analysis provided no evidence for significant effects of D1R stimulation on parameters from a drift diffusion model. This suggests that D2R, rather than D1R, activation mediates the impact of proximity on intertemporal choices.

In the revised manuscript, we report the findings for the D1 agonist study on p.16:

“To assess the receptor specificity of our findings, we conducted the same analyses on the data from a study (published previously in Soutschek et al. (2020)) testing the impact of three doses of a D1 agonist (6 mg, 15 mg, 30 mg) relative to placebo on intertemporal choices (between-subject design). In the intertemporal choice task used in this experiment, the SS reward was always immediately available (delay = 0), contrary to the task in the D2 experiment where the delay of the SS reward varied from 0-30 days. Again, the data in the D1 experiment were best explained by DDM-1 (DICDDM-1 = 19,657) compared with all other DDMs (DICDDM-2 = 20,934; DICDDM-3 = 21,710; DICDDM-5 = 21,982; DICDDM-6 = 19,660; note that DDM-4 was identical with DDM-1 for the D1 agonist study because the delay of the SS reward was 0). Neither the best-fitting nor any other model yielded significant drug effects on any drift diffusion parameter (see Table 4 for the best-fitting model). Also model-free analyses conducted in the same way as for the D2 antagonist study revealed no significant drug effects (all HDI95% included zero). There was thus no evidence for any influence of D1R stimulation on intertemporal decisions.”

We discuss the specificity of D2 receptors for moderating the proximity bias on p.17: “This finding represents first evidence for the hypothesis that tonic dopamine moderates the impact of proximity (e.g., more concrete versus more abstract rewards) on cost-benefit decision making (Soutschek et al., 2022; Westbrook & Frank, 2018). Pharmacological manipulation of D1R activation, in contrast, showed no significant effects on the decision process. This provides evidence for the receptor specificity of dopamine’s role in intertemporal decision making (though as caveat it is worth keeping the differences between the tasks administered in the D1 and the D2 studies in mind).”

We also agree that amisulpride acts also on 5-HT7 receptors, such that it remains unclear whether also such effects contribute to the observed result pattern. We discuss this limitation in the revised manuscript on p.21:

“Lastly, while the actions of amisulpride on D2/D3 receptors are relatively selective, it also affects serotonergic 5-HT7 receptors (Abbas et al., 2009). Because serotonin was related to impulsive behavior (Mori, Tsutsui-Kimura, Mimura, & Tanaka, 2018), it is worth keeping in mind that amisulpride effects on serotonergic, in addition to dopaminergic, activity might contribute to the observed result pattern.”

Overall the modeling methods are robust and appropriate for the specific test of decision impacts of D2R blockade, and include several prima facie variable alternative models for comparison. Some caution is warranted, since there are not many trials per subject, and some trials are discarded as well as outliers, which raises the question of power. Given the models are fit hierarchically, which gives both group-level and individual-level parameter estimates, the elements are there to probe more deeply into individual differences, and to test how reliably this approach can dissociate the dual effects of bias and drift rate at the individual level, and perhaps correlate it with other informative subject measures of either dopamine activity/capacity or other dopamine-dependent behaviors. Alternative DDMs might also capture some of this individual variation, with meaningful differences potentially in model comparison at the individual level. It should be noted that the scope of these models do not exhaust the ways in which proximity (here, temporal) of rewards and contrast between choice options might be incorporated into a cognitive process model account of choice; all alternatives here rest on the same implicit 2-alternative forced choice assumption of the DDM, and the assumptions of this model are not here tested against other accounts of choice, for example the linear ballistic accumulator (LBA) and its derivatives. Further, the concept of proximity as a global feature of a trial (on average, how soon are these options overall?) is never tested on my read of the alternative models.

We thank the reviewer for these interesting suggestions. First, to explore whether measures of dopaminerigc activity correlate with individual differences in drug effects on DDM parameters, we now report correlations between DDM parameters and performance in the digit span backward task as proxy for dopamine synthesis capacity (Cools et al., 2008). None of these correlation analyses showed significant results. In the revised manuscript, we report these analyses on p.13:

“However, we observed no evidence that individual random coefficients for the drug effects on the drift rate or on the starting bias correlated with body weight, all r < 0.22, all p > 0.10. There were also no significant correlations between DDM parameters and performance in the digit span backward task as proxy for baseline dopamine synthesis capacity (Cools, Gibbs, Miyakawa, Jagust, & D'Esposito, 2008), all r < 0.17, all p > 0.22. There was thus no evidence that pharmacological effects on intertemporal choices depended on body weight as proxy of effective dose or working memory performance as proxy for baseline dopaminergic activity.”

Regarding model comparisons on the individual level, we note that the hierarchical Bayesian modelling approach allows (to the best of our knowledge) computing indices of model fit like DIC only on the group, not the individual level (while accounting for individual differences). However, we agree with the reviewer that theoretically different models might work best in different individuals (depending, for example, on the individual sensitivity to proximity). While such fine-grained model comparisons on the individual level are beyond the scope of the current study (and might not yield robust results given the limited number of trials for each participant), we now discuss this limitation in the revised manuscript (p.17-18):

“We note that the hierarchical modelling approach allowed us to compare models on the group level only, such that in some individuals behavior might better be explained by a different model than DDM-1. Such model comparisons on the individual level, however, were beyond the scope of the current study and might not yield robust results given the limited number of trials per individual.”

Likewise, linear ballistic accumulator (LBA) models represent a further class of process models with different assumptions on the mechanisms underlying the choice process than DDMs. In LBAs, evidence is accumulated separately for each choice alternative, whereas DDMs assume only one accumulation process which integrates attributes from two choice options, limiting the use of DDMs to two-alternative forced-choice scenarios. Nevertheless, proximity effects might be incorporated also in LBA models via modulating the starting point of the option-specific accumulators as a function of proximity. To the best of our knowledge, there is no built-in function in JAGS that allows estimating LBA models in a hierarchical Bayesian fashion (in contrast to, e.g., STAN), such that in the context of the current study it is difficult to directly compare our DDM-based approach with LBA models. It is importance to emphasize, however, that similar to other studies we do not make any claims about whether the choice process per se is best explained by DDMs or LBA models; instead, we focus on how rewards and delay costs affect different components of the decision process within a class of decision models. Nevertheless, we discuss such alternative modelling approaches in the revised manuscript on p.18:

“We also emphasize that alternative process models like the linear ballistic accumulator (LBA) model make different assumptions than DDMs, for example by positing the existence of separate option-specific accumulators rather than only one as assumed by DDMs. However, proximity effects as investigated in the current study might be incorporated in LBA models as well by varying the starting points of the accumulators as function of proximity.”

Lastly, we thank the reviewer for the interesting suggestion to assess whether the starting bias parameter is affected by the overall proximity of offers (sum of delays) instead of by the difference in proximity between the options. We ran a further DDM to test this hypothesis, but this model explained the data worse (DIC = 9,492) than the original DDM (DIC = 9,478). Nevertheless, also the overall proximity DDM yielded a significant amisulpride effect on the impact of reward magnitude on the drift rate, HDImean = 0.83, HDI95% = [0.04; 1.75], underlining the robustness of this effect. In the revised manuscript, we report this analysis on p.12:

“In a further model (DDM-4), we explored whether the starting bias is affected by the overall proximity of the options (sum of delays, Delaysum) rather than the difference in proximity (Delaydiff; see Table 3 for an overview over the parameters included in the various models). Importantly, our original DDM-1 (DIC = 9,478) explained the data better than DDM-2 (DIC = 9,481), DDM-3 (DIC = 10,224), or DDM-4 (DIC = 9,492). Nevertheless, amisulpride moderated the impact of Magnitudediff on the drift rate also in DDM-2, HDImean = 0.86, HDI95% = [0.18; 1.64], and DDM-4, HDImean = 0.83, HDI95% = [0.04; 1.75], and amisulpride also lowered the impact of Delaydiff on the starting bias in DDM-3, HDImean = -0.02, HDI95% = [-0.04; -0.001]. Thus, the dopaminergic effects on these subcomponents of the choice process are robust to the exact specification of the DDM.”

Reviewer #3 (Public Review):

Soutschek and Tobler provide an intriguing re-analysis of inter-temporal choice data on amisulpride versus placebo which provides evidence for an as-yet untested hypothesis that dopamine interacts with proximity to bias choices.

The modeling methods are sound with a robust and reasonably exhaustive set of models for comparison, with good posterior predictive checks at the single subject level, and decent evidence of parameter recoverability. Importantly, they show that while there is no main effect of drug on the proportion of larger, later (LL) versus smaller, sooner (SS) choices, this obscures conflicting-directional effects on drift rate versus starting point bias which are under-the-hood, yet anticipated by the hypothesis of interest.

We thank the reviewer for judging our findings as intriguing and the modelling approach as robust and convincing.

While I have no major concerns about methodology, I think the Authors should consider an alternative interpretation - albeit an interpretation which would actually support the hypothesis in question more directly than their current interpretation. Namely, the Authors should re-consider the possibility that amisulpride's effects are mediated primarily by acting at pre-synaptic receptors. If the D2R antagonist were to act pre-synaptically, it would drive more versus less post-synaptic dopamine signaling.

There are multiple reason for this inference. First, the Authors observe that the drug increases sensitivity to differences in the relative offer amounts (in terms of effects on the drift rate). With respect to the canonical model of dopamine signaling in the direct versus indirect pathway, greater post-synaptic signaling should amplify sensitivity to reward benefits - which is what the Authors observe.

Second, the Authors also observe an effect on the starting bias which may also be consistent with an increase in post-synaptic dopamine signaling. Note that according to the Westbrook & Frank hypothesis, a proximity bias in delay discounting should favor the SS over the LL reward, yet the Authors primarily observe a starting bias in the direction of the LL reward. This contradiction can be resolved with the ancillary assumption that, independent of any choice attribute, participants are on average predisposed to select the LL option. Indeed, the Authors observe a reliable non-zero intercept in their logistic regression model indicating that participants selected the LL more often, on average. As such, the estimated starting point may reflect a combination of a heightened predisposition to select the LL option, opposed by a proximity bias towards the sooner option. Perhaps the estimated DDM starting point is positive because the predisposition to select the LL option has a larger effect on choices than the proximity bias towards sooner rewards does in this data set. To the extent that amisulpride increases post-synaptic dopamine signaling (by antagonizing pre-synaptic D2Rs) it should amplify the proximity bias arising from the differences in delay, shifting the starting bias towards the SS option. Indeed, this is also what the Authors observe.

Note that it remains unclear why an increase in post-synaptic dopamine signaling would amplify one kind of proximity bias (towards sooner over later rewards) without amplifying the other (towards a predisposition to select the LL option). Perhaps the cognitive / psychological nature of the sooner bias is more amenable to interacting with dopamine signaling than the latter. Or maybe proximity bias effects are most sensitive to dopamine signaling when they are smaller, and the LL predisposition bias is already at ceiling in the context of this task. These assumptions would help explain why a potential increase in post-synaptic dopamine signaling both amplified the proximity effect of delay when it was smallest (when the differences in delay were smaller), and also failed to amplify the predisposition to select the LL option (which may already be maxed out). More importantly, the assumption that there are opposing proximity biases would also help explain why there is a negative effect of delay magnitude on the estimated starting point on placebo. Namely - as the delay gets larger, the psychological proximity of sooner over later rewards grows, counteracting the proximity bias arising from choice predisposition / repetition.

We thank the reviewer for suggesting this alternative interpretation of our data. We agree that the administered dose of 400 mg amisulpride can show both postsynaptic (reducing D2R activation) and presynaptic effects (enhancing D2R activation), which in many studies makes it difficult to decide whether the observed behavioral effects are caused by presynaptic or postsynaptic mechanisms.

The reviewer suggests that the observed stronger influence of reward magnitudes on drift rates under amisulpride compared with placebo speaks in favor of presynaptic effects, because according to theoretical accounts higher dopamine levels should increase reward seeking (e.g., Frank & O’Reilly, 2006). On the other hand, Figure 2C suggests that amisulpride (compared with placebo) increased the preference only for relatively high, above-average rewards. If the difference between reward magnitudes was below average, amisulpride reduced rather than increased the preference for the larger reward. In our view, this is consistent with the hypothesis that D2R activation implements a cost control, with higher D2R activation increasing the attractiveness of costly rewards and lower D2R activation reducing it. In other words, under low dopamine levels individuals should decide for the costlier reward only if the magnitude of the costlier reward is sufficiently large compared with the lower, less costly reward. In fact, this is exactly what we find in our data according to Figure 2C. In our view, the amisulpride effect on drift rates is thus compatible with both presynaptic and postsynaptic mechanisms of action, depending on the underlying conceptual account of dopamine, as we now discuss in the revised manuscript.

According to the reviewer, also the observed influence of amisulpride on the starting bias speaks in favor of increased rather than reduced dopamine levels. We agree with the reviewer that the result pattern for the starting bias is somewhat complex and seems to combine the effects of two different biases: a general tendency to choose LL over SS rewards (intercept of starting bias where the difference in delays is close to zero), and a shift towards the SS option under placebo if one options has a strong (temporal) proximity advantage over the other. Amisulpride shows opposite effects on the two different biases, as it shifts the intercept of the starting bias further away from the LL option but also reduces the proximity advantage of the SS over the LL reward for larger differences in delay. The reviewer writes that “To the extent that amisulpride increases post-synaptic dopamine signaling (by antagonizing pre-synaptic D2Rs) it should amplify the proximity bias arising from the differences in delay, shifting the starting bias towards the SS option. Indeed, this is also what the Authors observe.” In contrast to that statement, in our study amisulpride reduced rather than increased the starting bias arising from delay (as in Figure 2K the regression line is flatter under amisulpride compared with placebo, despite the differences regarding the intercept). We believe that the amisulpride effects on both the intercept and the delay-dependent slope can be explained via postsynaptic effects: First, the shift of the intercept of the starting bias (small differences in proximity) from the LL towards the SS option under amisulpride is consistent with the assumption that lower dopamine reduces the preference for larger reward (e.g., Beeler & Mourra, 2018; Salamone & Correa, 2012). Second, the finding that amisulpride weakens the proximity advantage of SS over LL rewards (delay-dependent slope) is consistent with the proximity account by Westbrook & Frank (2018) according to which lower tonic dopamine should reduce proximity effects. Thus, if we assume that the result pattern for the starting bias parameter is driven by dopaminergic effects on two separate decision biases (as suggested by the reviewer), we believe that both effects can better be explained by pharmacologically reduced rather than increased dopamine levels.

In the revised manuscript, we extensively discuss the question as to whether the observed drug effects are caused by postsynaptic versus presynaptic effects. We clarify that the amisulpride effect on drift rates seems consistent with both presynaptic and postsynaptic effects (depending on the underlying conceptual account). We moreover discuss that the starting bias effects may reflect the interaction between two different bias types, and the drug effects on both bias types can more easily be reconciled with postsynaptic than presynaptic effects. On balance, we believe that the observed effects are more likely to reflect lower as compared to higher dopamine levels, but the extended discussion of this issue gives all readers the opportunity to weigh the arguments for and against these alternatives. If the reviewer should not agree with some aspects of our argumentation as outlined above, we would of course be happy to modify the discussion according to the reviewer’s advice.

In the revised manuscript, we modified the discussion of presynaptic versus postsynaptic effects as follows (p.20-21):

“While higher doses of amisulpride (as administered in the current study) antagonize post-synaptic D2Rs, lower doses (50-300 mg) were found to primarily block pre-synaptic dopamine receptors (Schoemaker et al., 1997), which may result in amplified phasic dopamine release and thus increased sensitivity to benefits (Frank & O'Reilly, 2006). At first glance, the stronger influence of differences in reward magnitude on drift rates under amisulpride compared with placebo might therefore speak in favor of presynaptic (higher dopamine levels) rather than postsynaptic mechanisms of action in the current study. On the other hand, one could argue that amisulpride reduced the preference for the LL reward if the gain from the costlier LL option compared with the SS option was small (as suggested by Figure 2C), which is consistent with the cost control hypothesis of dopamine (Beeler & Mourra, 2018). The impact of amisulpride on the drift rate thus appears ambiguous regarding the question of pre- versus postsynaptic effects. The result pattern for the starting bias parameter, in turn, suggests the presence of two distinct response biases, reflected by the intercept and the delay-dependent slope of the bias parameter (see Figure 2K), which are both under dopaminergic control but in opposite directions. First, participants seem to have a general bias towards the LL option in the current task (intercept), which is reduced under amisulpride compared with placebo, consistent with the assumption that dopamine strengthens the preference for larger rewards (Beeler & Mourra, 2018; Salamone & Correa, 2012; Schultz, 2015). Second, amisulpride reduced the proximity advantage of SS over LL rewards with increasing differences in delay, as predicted by the proximity account of tonic dopamine (Westbrook & Frank, 2018). On balance, the current results thus appear more likely under the assumption of postsynaptic rather than presynaptic effects. Unfortunately, the lack of a significant amisulpride effect on decision times (which should be reduced or increased as consequence of presynaptic or postsynaptic effects, respectively) sheds no additional light on the issue.”

Regardless of the final interpretation, showing that pharmacological intervention into striatal dopamine signaling can simultaneously modify a starting point bias and drift rate (in opposite directions - thus having systematic effects on choice biases without altering the average proportion of LL choices) provides crucial first evidence for the hypothesis that dopamine and proximity interact to influence decision-making. These results thereby enrich our understanding of the neuromodulatory mechanisms influencing inter-temporal choice, and take an important step towards resolving prior contradictions in this literature. They also have implications for how striatal dopamine might impact decision-making in diverse domains of impulsivity beyond inter-temporal choice, ranging from cognitive neuroscience (e.g. in numerous cognitive control tasks) to psychiatry (treating diverse disorders of impulse control).

We thank the reviewer for highlighting the importance of the current findings for understanding dopamine’s role in decision making.

Reviewer #3 (Public Review):

A problem in synthetic ecology is that one can't brute-force complex community design because combinatorics make it basically impossible to screen all possible communities from a bank of possible species. Therefore, we need a way to predict phenomena in complex communities from phenomena in simple communities. This paper aims to improve this predictive ability by comparing a few different simple models applied to a large dataset obtained with the use of the author's "kchip" microfluidics device. The main question they ask is whether the effect of two species on a focal species is predicted from the mean, the sum, or the max of the effect of each single "affecting" species on the focal species. They find that the max effect is often the best predictor, in the sense of minimizing the difference between predicted effect and measured effect. They also measure single-species trait data for their library of strains, including resource niche and antibiotic resistance, and then find that Pearson correlations between distance calculations generated from these metrics and the effect of added species are weak and unpredictive. This work is largely well-done, timely and likely to be of high interest to the field, as predicting ecosystem traits from species traits is a major research aim.

My main criticism is that the main take-home from the paper (fig 3B)-that the strongest effect is the best predictor-is oversold. While it is true that, averaged over their six focal species, the "strongest effect" was the best overall predictor, when one looks at the species-specific data (S9), we see that it is not the best predictor for 1/3 of their focal species, and this fraction grows to 1/2 if one considers a difference in nRMSE of 0.01 to be negligible.

The same criticism applies to the result from figure 2-that pairs of affecting species have more negative effects than single species. Considered across all focal species this is true (though minor in effect size, Fig 2A). But there is only a significant effect within two individual species. Again, this points to the effects being focal-species-specific, and perhaps not as generalizable as is currently being claimed.

Another thing that points to a focal-species-specific response is Fig 2D, which shows the distributions of responses of each focal species to pairs. Two of these distributions are unimodal, one appears bimodal, and three appear tri-modal. This suggests to me that the focal species respond in categorically different ways to species addition.

These differences occur even though the focal bacteria are all from the same family. This suggests to me that the generalizability may be even less when a more phylogenetically dispersed set of focal species are used.

Considering these points together, I argue that the conclusion should be shifted from "strongest effect is the best" to "in 3 of our focal species, strongest effect was the best, but this was not universal, and with only 6 focal species, we can't know if it will always be the best across a set of focal species".

My second main criticism is that it is hard to understand exactly how the trait data were used to predict effects. It seems like it was just pearson correlation coefficients between interspecies niche distances (or antibiotic distances) and the effect. I'm not very surprised these correlations were unpredictive, because the underlying measurements don't seem to be relevant to the environment tested. What if, rather than using niche data across 20 nutrients, only the growth data on glucose (the carbon source in the experiments) was used? I understand that in a field experiment, for example, one might not know what resources are available, and so measuring niche across 20 resources may be the best thing to do. Here though it seems imperative to test using the most relevant data.

Additionally and relatedly, it would be valuable to show the scatterplots leading to the conclusion that trait data were uninformative. Pearson's r only works on an assumption of linearity. But there could be strong relationships between the trait data and effect that are monotonic but not linear, or even that are non-monotonic yet still strong (e.g. U-shaped). For the first case, I recommend switching to Spearman's rho over Pearson's r, because it only assumes monotonicity, not linearity. If there are observable relationships that are not monotonic, a different test should be used.

In general, I think the analyses using the trait data were too simplistic to conclude that the trait data are not predictive.

Author Response

Reviewer #1 (Public Review):

This paper shows that nuclear pore complex components are required for Kras/p53 driven liver tumors in zebrafish. The authors previously found that nonsense mutation in ahctf1 disrupted nuclear pore formation and caused cell death in highly proliferative cells in vivo. In the absence of this gene, there are multiple mitotic functions involving the nuclear pore that are defective, leading to p53 dependent cell death. Heterozygous fish are viable but have reduced kras/p53 liver tumor growth, and this is associated with multiple nuclear and mitotic defects that lead to cancer cell death/lack of growth. This therapeutic window suggests targetability of this pathway in cancer. I think the data are robust, rigorous, and clearly presented. I believe this in vivo work will encourage therapeutic targeting of NPCs in cancer.

We are pleased that this reviewer believes that our data are robust, rigorous, and clearly presented and that our in vivo work will encourage therapeutic targeting of NPCs in cancer.

Reviewer #2 (Public Review):

Overall this is a very interesting and important paper that demonstrates a novel synthetic interaction between nucleoporin inhibition and oncogene-driven hyperproliferation. This work is especially significant because of the paucity of effective treatments for hepatocellular carcinoma (HCC). The authors' demonstration that the Nup inhibitor Selinexor decreases larval liver size in KRAS-overexpressing zebrafish but does not cause toxicity in wild-type animals lays the groundwork for exploiting this class of drugs in HCC treatment. This paper represents an elegant demonstration of the utility of zebrafish models in cancer studies. The relevance of this work to human cancer is supported by the authors' studies using TCGA data, wherein they demonstrate that decreased NUP expression is associated with increased survival in HCC.

Other major strengths of the paper include beautiful pictures demonstrating that ahctf1+/- decreases the density and volume of nuclear pores in TO(kras) larvae and increases the rate of multipolar spindle formation, misaligned chromosomes, and anaphase bridges. The experiments are very well-controlled, including detailed analysis of the effects of ahctf1 heterozygosity and Selinexor on wild-type animals. The inclusion of distinct methods for disruption nucleoporins (ranbp2 heterozygosity and drug treatment) bolsters the authors' conclusion that this represents a viable drug target in HCC.

My major concerns are as follows:

1) The authors state that "the beneficial effect of ahctf1 heterozygosity to reduce tumour burden persists in the absence of functional Tp53, due to compensatory increases in the levels of tp63 and tp73". However, tp63 and tp73 appear similarly upregulated in ahctf1 heterozygotes regardless of tp53 status. The authors do not provide enough evidence that tp63 and tp73 are compensating for tp53 loss. An alternative possibility based on the data presented is that the effects of ahctf1+/- are independent of tp53 family members, and the effects on apoptosis go through a different pathway.

We agree with this reviewer that we did not provide enough evidence that tp63 and tp73 are compensating for tp53 loss. Accordingly, we have addressed this issue comprehensively.

2) The authors state in multiple locations that nucleoporin inhibition decreases tumor burden. In my opinion, this is not strictly correct. The TO(kras) model clearly results in HCC in adults, but it's a little unclear whether the larval liver overgrowth is truly HCC or not based on the original paper by Nguyen et al. (2012 Dis Model Mech).

We agree with these comments and accordingly, we performed several new experiments in adult fish.

Reviewer #3 (Public Review):

The nuclear transport machinery is aberrantly regulated in many cancers in a context-dependent fashion, and mounting evidence with cultured cell and animal models indicates that reducing the activity or expression of certain nuclear transport proteins can selectively kill cancer cells while sparing nontransformed cells. Here the authors further explore this concept using a zebrafish model for hepatocellular carcinoma (HCC) induced by liver-specific transgenic expression of oncogenic krasG12V. The transgene causes greatly increased liver size by day 7 in larvae, associated with a gene expression profile that resembles early-stage human HCC. This study focuses on Ahctf1, a nuclear pore complex (NPC) protein known to be essential for postmitotic NPC assembly. Using the krasG12V background, the authors analyze animals that are heterozygous for a recessive mutation in the ahctf1 gene that leads to ~50% reduction in ahctf1 mRNA (and likely the encoded protein). The authors show that the ~4-fold increase in liver volume of krasG12V animals is reduced by ~1/3 in the ahctf1 heterozygous mutants. This is associated with increased apoptosis, decreased DNA replication, up-regulation of pro-apoptotic and cdk-inhibitor genes, and down-regulation of anti-apoptotic gene. These effects found to be substantially Tp53-dependent. Consistent with previous Ahctf1 depletion studies, hepatocytes of ahctf1 heterozygotes show decreased NPC density at the nuclear surface, elevated levels of aberrant mitoses and increased DNA damage/double stranded breaks. Finally, the authors show that combining the achtf1 heterozygous mutant with a heterozygous mutation in another NPC protein- RanBP2- or treating animals with a chemical inhibitor of exportin-1 (Selinexor) can further reduce liver volume. Overall they suggest that combinatorial targeting of the nuclear transport machinery can provide a therapeutic approach for targeting HCC.

This is an interesting study that bolsters the notion that reduction in the levels of discrete nucleoporins (and/or inhibiting specific nuclear transport pathways) can result in cancer cell-selective killing. Moreover, the work extends previous studies involving cultured cell and mouse xenografts to a new cancer model (HCC) and nucleoporin (Ahctf1). Whereas the authors describe multiple aberrant cellular phenotypes associated with the dosage reduction in ahctf1, the exact causes for reduction in liver size in the krasG12V model remain unclear. Although it would be desirable to parse effects of Ahctf1 related to NPC number, aberrant mitoses, licensing of DNA replication and chromatin regulation, this is a tall order at present, given the limited understanding of Ahctf1. However, useful insight on these and related questions could be gained with further analysis of the system as outlined below.

We are pleased this reviewer thinks this is an interesting study that bolsters the notion that reduction in the levels of discrete nucleoporins (and/or inhibiting specific nuclear transport pathways) can result in cancer cell-selective killing. This reviewer also suggests that useful insight on these and related questions could be gained with further analysis of the system as outlined below:

1) In the krasG12V model, it would be helpful to distinguish the contribution of increased cell death vs decreased cell proliferation to the change in liver size seen with heterozygous ahctf1. Is this predominantly due to decreased proliferation?

We think this question is difficult to address, because the relative contributions of the two processes may vary with time. Our data show definitively that by 7 dpf, the impact of ahctf1 heterozygous mutation has disrupted multiple cellular processes, leading to a 40% increase in the number of hepatocytes expressing Annexin 5 (dying cells), and a 40% decrease in the number of hepatocytes incorporating EdU over a 2 h incubation (fewer cells in S-phase). Both responses are likely to contribute to the reduction in liver volume observed in response to ahctf1 heterozygosity. It is worth stating that in our experiments, we captured snapshots of apoptosis and DNA replication in the livers of larvae at 7 days post-fertilisation after 5d of dox treatment/KrasG12V expression. To answer the Reviewer’s question properly, we would need to monitor the behaviour of individual cells over time. If such experiments were technically possible, we think that some cells that undergo growth arrest in response to dox treatment might ultimately succumb to apoptosis (unless dox treatment is withdrawn) while other cells might enter into a state of prolonged senescence. However, given the technical challenges, we did not attempt to test this in the current manuscript.

2) It would be good to know whether the heterozygous ahctf1 state blunts the overall level of Ras activity in krasG12V animals.

We have addressed this interesting question thoroughly in new Fig. 1g, h. To do this, we used a commercial RAS-RBD pulldown kit followed by western blot analysis to determine the levels of activated GTP-bound Kras protein. Our results demonstrate that the levels of GTP-bound Kras protein, expressed as a proportion of total Kras protein, do not change in response to ahctf1 heterozygosity. We conclude from these data that the potentially therapeutic value of reduced ahctf1 expression in a cancer setting is not caused by inhibiting Kras activity.

3) Notwithstanding the analysis of Tp53 target genes presented in this study, it would be helpful to see detailed transcriptional profiling of hepatocytes in the krasG12V model with the heterozygous ahctf1 mutation, and to assess the effects of Selinexor. GSEA type analysis offers a way to start untangling the effects of these pathways. Moreover this analysis could provide insight on the relevance of this model to human HCC.

We used RNAseq to address the relevance of our larval model to human HCC. Specifically, we performed differential gene expression analysis to identify up- and downregulated genes in cohorts of ahctf1+/+ (WT) larvae versus dox-treated ahctf1+/+(WT);krasG12V larvae. We used gene set enrichment analysis to compare these differentially regulated transcripts with the gene expression signature of 369 patient samples in the Liver hepatocellular carcinoma (LIHC) dataset versus healthy liver samples in the TCGA. These analyses revealed a significant association between the patterns of gene expression in our larval model of zebrafish HCC and those of human HCC (Fig. 1-figure supplement 1c, d).

The genetic experiments we report in Figures 4, 5, 6 show that WT Tp53 is required for the reductions in liver enlargement (Fig. 4), apoptosis (Fig. 5) and DNA replication (Fig. 6) that occurs in response to ahctf1 heterozygosity in dox-treated krasG12V larvae. We also used RT-qPCR to show that a Tp53-mediated transcriptional program was activated in these ahctf1 heterozygous livers (Fig. 5). Similarly, in adult livers, ahctf1 heterozygosity triggered the upregulation of Tp53 target genes, including pro-apoptotic genes (pmaip1, bbc3, bim and bax) and cell cycle arrest genes (cdkn1a and ccng1) (new Fig. 6-figure supplement 1). These results show that to obtain the full potential of ahctf1 heterozygosity in reducing growth and survival of KrasG12V-expressing hyperplastic hepatocytes requires activation of WT Tp53. This is an important conclusion from our paper that is likely to be relevant in a clinical setting, for instance in patient selection, if ELYS inhibitors are developed for the treatment of HCC in which the KRAS/MAPK pathway is activated.

Also, one reviewer mentions performing genome-wide transcriptional profiling of hepatocytes in the krasG12V model in response to ahctf1 heterozygosity and the presence and absence of Selinexor treatment. While these are potentially interesting experiments, they are substantial in nature and not crucial for the main messages of our paper. Therefore, we respectively contend that they are beyond the scope of the current manuscript.

4) Functions of Achtf1 in regard to chromatin regulation could be compromised in this model. Scholz et al (Nat Gen 2019) report that Ahctf1 is involved in increasing Myc expression via gene gating mechanism. It would be good to know what the effects are in this system.

The Scholz, 2019 and Gondor, 2022 papers from the same group, are very interesting in that they demonstrate a novel role for the ELYS protein in addition to the ones we pursued in our paper. The authors showed that in HCT116 cells, a human colorectal cancer cell line in which proliferation is driven by aberrant WNT/CTNNB1 signalling, the longevity of nascent MYC mRNA was increased by accelerating its movement from the nucleus to the cytoplasm, thereby preventing its degradation by nuclear surveillance mechanisms. The authors showed that siRNA knockdown of AHCTF1 in HCT-116 cells reduced the rate of nuclear export of MYC transcripts without changing the transcriptional rate of the MYC gene. They proposed a mechanism that depended on the formation of a complex chromatin architecture comprising transcriptionally active MYC and CCAT1 alleles plus proteins including β-Catenin, CTCF and ELYS. Together these interacting components guided nascent MYC mRNA molecules to nuclear pores, enhanced their export to the cytoplasm to be translated, resulting in activation of a MYC transcriptional program that induced expression of pro-proliferation genes.

In theory, this role of ELYS in protecting MYC from nuclear degradation might extrapolate to other cancer settings where MYC expression is elevated. While interplay between MYC and mutant KRAS to enhance cancer growth has been previously reported, to date, most emphasis on this interaction has focused on the role of mutant KRAS in increasing the stability of the MYC protein, for example via RAS effector protein kinases (ERK1/2 and ERK5) that stabilise MYC by phosphorylation at S62 (Farrell and Sears, 2014: https://doi.org/10.1101/cshperspect.a014365) (Vaseva and Blake 2018: DOI:https://doi.org/10.1016/j.ccell.2018.10.001). While we appreciate the novelty of the recent papers, the current findings are limited to -Catenin activated HCT-116 cells and may not be relevant to our zebrafish model of mutant Kras-driven HCC. Accordingly, we have not allocated a high priority to following this up in our current manuscript.

6) The synthetic lethality argument pressed in this manuscript seems exaggerated. Standard anti-cancer treatments typically target several cellular pathways, and nucleoporins directly affect a multiplicity of pathways besides nuclear transport.

While we do not disagree that standard anti-cancer treatments may target several cellular pathways, we believe our data are consistent with the accepted definition of a synthetic lethal interaction whereby single mutations in two separate genes (kras and ahctf1) cooperate to cause cell death, whereas cells harbouring just one of these mutations are spared.

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Reviewer #1 (Evidence, reproducibility and clarity):

The manuscript reports effects on brood size, lifespan and healthspan upon manipulation of C. elegans genes encoding RagA, TOR and Pol III orthologs, as well as other well-characterized lifespan-affecting genes. The results point to complex relationships among TOR and Pol III that are not fully resolved, suggest a role for rpc-1 Pol III that is additive with well-characterized lifespan pathways, indicate a late-life requirement for rpc-1 Pol III to limit lifespan, and, contrary to a previous publication, suggest a muscle requirement for rpc-1 Pol III for lifespan limitation.

Major comments regarding key conclusions:

The work demonstrates that brood size is reduced upon rpc-1 Pol III RNAi feeding from the L4 stage. However, no further analysis is provided to show how later aspects of reproduction impair brood. Minimally, ruling out effects on spermatogenesis would be important since sperm number limits self-fertile brood size. It is also unclear from the methods whether the brood size results include embryonic lethality (post-reproduction). Internal hatching, if it occurred, could also affect interpretation of the results. A change in the reproductive period should be noted if it occurred.

The reviewer is correct that it is important to address the role of Pol III more thoroughly in relation to reproduction.

• The brood size experiments we present simply record the number of hatched progeny. To develop this analysis further we will present the age-specific fecundity data that we generated whilst doing these assays to demonstrate the impact of Pol III on the reproductive period. In addition, we will quantify and present data on the total brood size (dead eggs and hatched progeny) to address whether Pol III also impact embryonic development.
• At 25oC (the temperature that we did these experiments) very few animals suffered internal hatching and those that did were taken out of the analysis – therefore this is unlikely to skew the results.
• The question as to whether Pol III limits egg or sperm function (or later developmental roles) is also interesting and is not yet addressed. To examine this we will: Quantify brood size (dead eggs and hatched progeny) in elegans +/- Pol III RNAi that have been exposed to males during the reproductive period compared to those that reproduce solely as hermaphrodites.

The authors claim that, similar to the relationship previously concluded from aging studies, rpc-1 acts downstream of TORC1. However, this claim is not well supported. In an effort to circumvent early lethality caused by loss of let-363 ("CeTOR"), they use a mutation in raga-1 RagA and demonstrate a further reduction in brood with rpc-1 RNAi. If raga-1(ok386) were a null this result would demonstrate a relationship that is at least partially parallel, not linear. By contrast, double RNAi with let-363 was "non-additive", suggesting a more linear relationship. However, interpretation of these experiments requires (1) that the raga-1 mutation is null and affects only TORC1 signaling, (2) evidence that the double RNAi worked well (e.g., qPCR; see Ahringer et al. 2006 review regarding issues with multi-RNAi), and (3) failure to consider alternative effects of loss of let-363 (e.g., TORC2). Negative results with RNAi are particularly problematic in the absence of convincing evidence that the RNAi worked well. Moreover, results in Figure 1G are difficult to interpret since the initial values are low. Here and elsewhere the genetics descriptions are unconventional, hampering interpretation. For example, what is meant by a mutation being "incomplete"? That it acts as a hypomorph?

We understand the concerns of the reviewer:

• The raga mutant strain that we use is raga-1 (ok386.) This allele harbours a 1242 bp deletion at the raga-1 locus that removes almost the entire coding region of the gene. Details on this allele can be found on Wormbase, and we will reference this in the methods. https://wormbase.org/species/c_elegans/variation/WBVar00091681#02-456-10

For reference, this has been used in several other studies, e.g. doi.org/10.7554/eLife.49158

• We agree that double RNAi can be challenging. Appropriate controls were used here e.g. each RNAi diluted 50:50 with control RNAi in the single treatments and phenotypes were observed in each case (either brood size or lifespan). However, to address the precise knockdown of rpc-1 and let-363 obtained with RNAi we will perform qPCR in response to single and double RNAi treatment (both in WT and raga-1 mutant elegans).
• In addition, we will attempt to measure S6Kinase phosphorylation, a downstream readout of TORC1 signalling in response to raga-1 mutation or let-363 RNAi treatment with and without rpc-1 A phosphor S6 Kinase antibody is commercially available and has been used successfully in C. elegans - doi.org/10.7554/eLife.31268
• Our apologies that the nomenclature was confusing. The CeTOR RNAi nomenclature was ’borrowed’ from other papers describing this tool e.g. org/10.7554/eLife.31268 and doi: 10.1371/journal.pgen.1000972. Here, to make our work clearer, we will change ceTOR to let-363 TOR RNAi and raga-1 to raga-1 RagA in the manuscript – as suggested by the reviewer (see below). The description of ‘incomplete’ mutations will also be amended, and informed by our proposed qPCR analysis.

Another claim is that rpc-1 Pol III limits adult lifespan downstream of TOR. These results are not convincing. The two treatments (raga-1 mutation as "embryonic" and L4 stage "CeTOR" let-363 RNAi as late) are not directly comparable for reasons noted above, and the double RNAi problem hampers interpretation.

Our lifespan data points out that the longevity increase upon Pol III knockdown is additive with TOR/let-363, suggesting a mechanism independent of TOR. Indeed, due to lack of ideal reagents, we were forced to try the double RNAi knockdown approach for TOR/let-363 and Pol III/ rpc-1. To make the data interpretation easier, and rule out the possibility of confounding background RNAi to the maximum possible extent, we have included appropriate RNAi controls. Wherever double RNAi has been used, the effect on the phenotype by 50% dilution of target RNAi with empty-vector control, has also been shown independently and used for the statistical comparison with combinatorial RNAi. Our results have shown that diluting let-363 RNAi and rpc-1 RNAi both to 50%, is enough to impart lifespan increase when initiated from L4 stage.

The nomenclature might be easier to follow if the authors state the actual C. elegans genes manipulated (e.g., let-363 TOR versus raga-1 RagA) rather than using "CeTOR" as a catch-all since these genes are not identical in action.

Thank you for this suggestion. We will implement this in the manuscript where appropriate.

Based on genetic interactions (rsks-1, ife-2, ppp-1, daf-2 and germline loss) they show that rpc-1 RNAi further extends the long lifespan conferred by each of the mutant alleles tested, as well as germline loss induced by two different mutant conditions. These results, though negative, are important. The statement that rpc-1 does not affect global protein synthesis is somewhat overstated without additional experimental support.

We thank the reviewer for supporting our inclusion of ‘negative data’. We agree that our statement relating to protein synthesis is overstated given the data presented. We will soften this to: “rpc-1 does not seem to affect the lifespan incurred by reducing global protein synthesis, although this does not rule out the possibility that Pol III affect protein synthesis by other mechanisms”.

Extending and challenging their own previous work showing an intestinal focus of activity for rpc-1 in limiting longevity (Filer et al., 2017), and noting that RPC-1::GFP detection can be knocked down by RNAi in several tissues, they use a tissue restricted rde-1 expression approach (or sid-1 for neurons) to test the contribution of intestine, hypodermis, neurons, muscle and germline. This new analysis points to a role for the muscle. This result is intriguing and warrants further experiments. To shore up tissue-specific claims the authors could consider (1) additional drivers for intestine and muscle rde-1 in the RNAi experiments, or, ideally, a different approach such as tissue-specific protein degradation (again with multiple drivers), (2) a sufficiency experiment for muscle (wild-type muscle expression in the mutant to demonstrate reversal of the phenotype, or rescue of RNAi defects with an RNAi-insensitive reagent expressed in muscle).

Thank for you appreciating the work we have done here and suggesting further experiments. To take your points one at a time: (1) We have already used the most robust tissue-specific alleles generated and reported in the C. elegans literature so far. It would be a significant amount of work to generate new rde-1 driven tissue specific alleles to double check the Pol III levels/ rpc-1 knockdown response in certain tissues, and we feel this is beyond the scope of this project. Suggestion (2) is interesting and would require us to generate a muscle specific rpc-1 strain. However, there are issues with this approach. Firstly, it would require that we have a rpc-1 mutant to rescue – which we don’t as it is embryonically lethal and secondly it would not be possible to do this experiment using RNAi as the RNAi would then knock down the muscle construct.

The possible explanation for the differences in rde-1 results from the previous work should not be buried in the legends of Figure 3 and Figure S3. Perhaps this leaky background hypothesis should be directly tested (e.g., using the RPC-1::GFP to examine whether residual expression exists in ne219 but not in ne300)? In any case, legend to Figure S3 needs editing: The ne219 background is not itself "intestine-specific", as implied, and the last sentence of Figure S3 legend should be "Thus, the rde-1(ne219)...", right?

The differences between the different tissue-specific strains is interesting. On reflection we agree with the reviewer that it should be included in the main text. We will describe the differences between the two rde-1 alleles ne219 and ne300 in the appropriate section in the manuscript and state our results.

Finally, they show that late-adult rpc-1 RNAi extends lifespan over control RNAi and that, by several movement assays, healthspan is improved upon L4 rpc-1 RNAi, even when RNAi is active in muscle (based on WM118).<br /> The most significant new results are that rpc-1(RNAi) affects brood size, can extend lifespan (though modestly) after day 5 of adulthood, and that muscle may be involved rather than intestine.

Additional comments:

Text throughout should clarify TOR vs presumed TORC1. Methods are insufficient. Important aspects of the lifespan methods and raw data are missing - e.g. exact numbers of worms censored. Exact information regarding statistical analysis is lacking (e.g., which tests, corrections for multiple testing). References should be given for all strains. For the rde-1 strains, it would be helpful to include, in addition to the transgene alleles, the actual promoters used to claim tissue specificity. Note, worms do not have "skeletal" muscle, as implied in the discussion. Figure 5 was not helpful for this reviewer. Figure legend to S3A is confusing: the intestinal signal appears stronger or at least equal, not weaker, in the rpc-1 RNAi background. Were these images collected using the exact same exposure settings?

To address this we will:

• Standardise genetic notation throughout the manuscript (see specific comments above)
• Provide more detail on the transgenic alleles used e.g. promoters driving rde-1.
• The majority of strains were obtained from the CGC but wherever appropriate we will also supply a reference.
• Expand and revise Material and Methods section to appropriately describe all the statistical analyses performed.
• Revise lifespan methods to include censoring detail and lifespan Tables to include information on censored animals.
• Remove the reference to ‘skeletal muscle’ and replace with ‘body wall muscle’.
• Once we have generated new data on the specific knockdowns and downstream targets achieved with let-363 TOR RNAi and raga-1 RagA mutation, as well as on the brood size/dead eggs effects, we will incorporate this information into Fig. 5A for better clarity and readability.
• We can see on reflection that Figure S3A is confusing, mainly due to the gut autofluorescence in both the control and rpc-1 RNAi conditions. We will amend this figure to make this clear and include a selection of close up images of each tissue to make it easier to see the tissue specific knockdown by RNAi.

Reviewer #1 (Significance):

See above. Study will be of interest to aging community.

Reviewer #2 (Evidence, reproducibility and clarity):

The study by Malik and Silva et al describes results of the study investigating the role of RNA Polymerase III in regulating fecundity and lifespan in C. elegans. The authors show that knockdown of Pol III, similar to mTOR suppression, is detrimental for reproduction. Likewise, suppression of either Pol III or mTOR in adult animals extends lifespan via apparently the same pathway. In contrast, Pol III knockdown has an additive effect on lifespan in combination with other established genetic lifespan-extending approaches suggesting that they are working via different mechanisms. Furthermore, using the tissue-specific knockdown of Pol III the authors found that suppression Pol III expression is the muscle, but not other major worm tissues, is sufficient for its lifespan extending effect. Finally, the lifespan extension is also observed when Pol III knockdown is initiated late in adulthood. The overall conclusion is that suppression of Pol III expression late in animal life, particularly in the muscle, is a potential strategy to extend life- and health-span. Overall, the study is well-designed, the tools and results are robust and analysed appropriately. The data presentation is excellent, and the manuscript is clearly written. Addressing the points below will help to improve the clarity further.

We thank the reviewer for their very positive response to our study and are pleased that they found the data convincing. We are extremely pleased that the reviewer agrees with the design and tools used in this study. We can address all of the review’s comments – as discussed below.

Major:

Significant amount of GFP signal is still present in RNAi treated animals, what is the tissue that maintains particularly high levels of expression (Fig. 3A) and how does it affect the conclusions? What is the level of Pol III reduction in different tissues? Could different efficiency of knockdown explain the tissue-specific effect of Pol III downregulation on lifespan? It would be important to show (and, if possible, to quantify) the knockdown efficiency in different tissues using the available reporter

• This experiment had originally been done to test the efficiency of the RNAi, particularly in tissues where rpc-1 RNAi did not impact lifespan. The reviewer is right though, and this information could be analysed further to enhance our study. Figure 3A shows C. elegans expressing the rpc-1::3xflag::gfp reporter. This was used to a) determine the expression pattern of RPC-1 and b) determine the effect of rpc-1 RNAi on this. We noted that RPC-1::GFP is expressed a wide number of tissues and when the reporter strain is treated with rpc-1 RNAi, it is decreased in all tissues. The ‘green’ observed in the RNAi treatment is unfortunately attributable to autofluorescence generated by lysozymes in the C. elegans intestine and masks some of the effects we saw by eye.
• To establish the tissue-specific efficiency of Pol III knockdown and also address the confounding issue of the autofluorescence we will now use a combination of quantitative and qualitative fluorescent microscopy to measure the percentage RPC-1::GFP knockdown in each tissue relevant to this study.

Minor:<br /> Fig. S3B is not cited in the text and the legend for the figure is somewhat confusing, potentially containing errors, this needs to be clarified.

We thank the reviewers for pointing this out. The legend for this figure will be re-written as a result of the analysis described above and we will cite it in the main text.

Reviewer #2 (Significance):

This is the first thorough study of Pol III knockdown as a lifespan extending strategy in C. elegans. In addition to the different laboratory model (previous study of Pol III in ageing primarily focused on Drosophila), this manuscript also offers several novel insights into consequences of Pol III perturbation at phenotypic, as well as mechanistic level in terms of interaction with other longevity pathways. The study will be of interest to those interested in processes underlying longevity and ageing. Considering that this topic is currently in fashion the publication will probably attract attention of not only specialist but also general public.

We are extremely pleased that the reviewer shares our enthusiasm for this study and that they find the experimental evidence compelling.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary: The paper by Yasir Malik et al investigates the genetic interrelationship between TOR signalling and Pol III expression regarding fecundity and longevity in C. elegans. Based on a previous study that defined a role of Pol III downstream of TOR in longevity across various species, this study looks particularly at the relative timing and tissue requirements for TOR and Pol III inhibition in longevity. Data indicate that Pol III acts downstream of TOR in regulating fecundity while there are additive effects regarding survival. The Pol III effect on longevity is based on its role in the muscle. Finally, health-span parameters mirror the survival data.

Major comments: This is a nice study the relies on genetic interaction to ask how TOR and Pol III interact. I find the observation that Pol III inhibition extends survival when initiated at day 5 of adulthood very exciting. In general, the study would benefit from additional data that back up the genetic observations._We thank the reviewer for appreciating the study and the novel insights it provides about the TOR-Pol III inter-relationship. We can address reviewer’s comments with the a few, limited experiments. Discussed below.

In Fig. 1, experiments are done to inhibit TOR to varying degrees in order to perform epistasis experiment. Of course these are difficult to interpret without the use of full KOs/loss of function. So while this is a good solution, it would be important to quantify the level to which TOR signalling is inhibited, optimally with biochemical experiments. We fully appreciate the reviewer’s point. A similar concern was raised by reviewer 1. We propose to address this in two ways: 1) by quantifying mRNA levels by qPCR of let-363 in response to either let-363 TOR RNAi; and 2) by determining the extend of TORC1 activity by using a biochemical readout of the pathway’s activity – S6 Kinase phosphorylation using Western blotting as described here: doi.org/10.7554/eLife.31268 2. General brood size is very low in the WT worms. Normally, one would expect 250-300 offspring per adult worm. It would be helpful if the authors could address this.

Indeed, as pointed out by the reviewer, the WT worms have a brood size of 250-300 eggs when kept at 20oC. but C. elegans exhibit different brood sizes dependent on temperature and these decline in size with increasing temperature. The experiments shown here were carried out at 25oC, where C. elegans produce less offspring. Our observation is in agreement with other studies of similar nature e.g. doi:10.1371/journal.pone.0112377 and doi.org/10.1371/journal.pone.0145925

1. Why were lifespan assays performed at 25C? The standard temperature for the worm is 20C and here I think this is very relevant as the TOR pathway is responsive to suboptimal conditions. I wonder if the results are also true for lower temperatures.

The reviewer raises an interesting point. This study follows from the previous study of Filer et al., Nature 2017 which demonstrated the role of Pol III in ageing. During this study we found and reported that there was a high proportion of intestinal bursting when lifespans were carried out at 20oC, which was ameliorated by carrying out the experiments at 25oC. This was quantified in the original manuscript. To maintain consistency, we continued carrying out Pol III lifespans at this slightly higher temperature. Due to this limitation it is not possible to test the impact of TOR signalling on Pol III at lower temperatures.

Minor comments: 1. It would help to better delineate the rationale for the experiments in Fig. S1. Experiments here are aimed to find mediators of TOR effects distinct from Pol III. Such distinct mediators would be additive to Pol III (as is the case in the figure) and downstream of TOR.

Interpreting epistasis analysis is challenging. We were looking for interactors of Pol III using this targeted genetic approach and working on the premise that if two genes interacted then their effects would be non-additive. However, the reviewer is correct that if two genes are doing the same thing independently then their effects may be additive. Although our data does not suggest these mediators interacting with Pol III in the same pathway, it does not rule out the other possibility. When we re-work the manuscript we will explain our rational more clearly and outline the two scenarios.

Reviewer #3 (Significance):

Strengths: The study advances our knowledge regarding the timing of the Pol III targeting intervention for survival effects.<br /> Limitations: The study relies only on genetic data and not all of it is conclusive.

This study will be interesting for the geroscience community with an eye on TOR inhibition and is relevant to worm biology. I work with C. elegans as a genetic model and I am interested in protein homeostasis, metabolism, health, and longevity.

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Reply to the reviewers

Manuscript number: RC-2022-01480

Corresponding author(s): Ananda, Sarkar

1. General Statements

We are thankful to Review commons platform that helped our manuscript critically reviewed with very constructive and valuable feedback. This gave us the opportunity to do the experiments accordingly and significantly improve the manuscript. We are hopeful that this platform will help our manuscript get published in a journal of repute.

2. Point-by-point description of the revisions

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

The manuscript entitled "LDL1 and LDL2 histone demethylases interact with FVE to regulate flowering in Arabidopsis" characterized that LDL1 regulates flowering by binding on the chromatin of MAF4 and MAF5 to repress their expression. Further the authors proposed LDL1/LDL2-FVE model. Here are some comments for this manuscript.

Major problems: 1. This experiment is still not testing or showing/concluding that the whole complex forms on the MAF4 and MAF5

Response: We understand reviewer’s concern regarding the complex. Previously FVE was shown to be a part of co-repressor complex including HDA6, HDA5 and FLD to regulate the expression of FLC and its clade members during floral transition1-3 We showed that LDL1 binds directly to the chromatin of MAF4 and MAF5 to suppress their expression (Figure 1 and 2). Furthermore, we discovered that LDL1 and LDL2 interact with FVE to influence floral transition (Figure 8 and 9). Hung et al., 2018 reported the interaction of LDL1 and LDL2 with HDA6 to regulate circadian rhythm4 and we found that the expression of MAF4 and MAF5 was upregulated in ldl1ldl2hda6 than ldl1ldl2 (Figure 5C and 5D). Therefore, our experimental data, together with previously reported data makes it evident that LDL1 and LDL2 are a part of co-repressor complex through their interaction with FVE and HDA6, which we concluded here. We agree with the reviewer that an additional experiment, such as complex pull-down, will be helpful, but in our opinion, it will only provide additional confirmatory evidence.

2.It is not shown LDL1/LDL2 repress MAF4 and MAF5 by removing H3K4me2 activity. It would be useful to test whether the methylation level of MAF4 and MAF5 has been altered in ldl1/ldl2 mutant

Response: We found altered methylation level in MAF4 and MAF5 chromatin during floral transition in ldl1 and ldl1ldl2 mutants (Figure 6 and 7). We observed that the absence of LDL1, or both LDL1 and LDL2 disturbs the shift in H3K4 methylation status on MAF4 and MAF5 during floral transition and ends up in a more active (enriched in H3K4me3 marks) chromatin state at 19 days. This result, taken together with the increased MAF4 and MAF5 expression in ldl1 and ldl1ldl2 double mutants (Figure 5C and 5D) indicates that LDL1/LDL2 repress MAF4 and MAF5 by altering H3K4 methylation.

3.I suggest that further research is required to provide conclusive evidence concerning the physiology function of LDL1/LDL2-FVE. Such as the expression pattern of LDL1/LDL2, the methylation level of MAF4 and MAF5 before or after floral transition

Response: Taking this suggestion into account, we performed quantification of rosette leaves and flowering time of fvec, ldlfvec and ldl2fvec along with WT, ldl1 and ldl2 (Figure 9). We also observed decreased expression of floral activator genes, FT and SOC1 (targets of MAF4 and MAF5) in fvec, ldlfvec and ldl2fvec in comparison to the WT (Supplementary Figure 10C), which corresponds to their late flowering phenotype.

To understand the role of LDL1and LDL2 during floral transition, we first analyzed the expression of LDL1 and LDL2 during floral transition (Supplementary Figure 8). We observed that the expression of LDL1 and LDL2 expression peaks at 16 days and gets stabilized till 19 days. Then we checked the enrichment of H3K4me1, H3K4me2 and H3K4me3 on MAF4 and MAF5 chromatin in ldl1 and ldl1ldl2 plants with respect to the WT at 16 days (before floral transition) and 19 days (after floral transition). We found an increase in the conversion of H3K4me1 to H3K4me3, when LDL1 and LDL2 were not present (Figure 6 and 7).

Reviewer #1 (Significance (Required)):

The manuscript provide some evidences how LDL1 involve in flowering through epigenetic regulation.

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

Mahima and colleagues investigated LDL1/LDL2-MAF4/MAF5 in Arabidopsis flowering time control. The manuscript contains some interesting observations. To my point of view, however, the data need to be consolidated to support conclusions drawn in the manuscript.

• Title: it does not correctly reflect the manuscript content. Data in relation with FVE were limited to Fig 6, where the data themselves appear preliminary.

Response: We agree with the reviewers that our title didn’t reflect the manuscript content precisely and are happy to take this criticism into consideration. We have revised the title to, “LDL1 and LDL2 affect the dynamics of H3K4 methylation on the chromatin of MAF4 and MAF5 to allow floral transition in Arabidopsis”. Additionally, have provided the quantification data for fvec, ldlfvec and ldl2fvec with respect to WT, ldl1 and ldl2 plants (Figure 9)

• Abstract: most conclusions are over-stated. The current data shown in the manuscript cannot support such strong conclusions.

Response: We have rigorously revised the abstract and toned down the overstated conclusions

• Introduction: It is necessary to make clear that the role of the LDL1 and LDL2 genes in flowering time control had been well established in previous studies, including their repression of transcription of FLC, MAF4 and MAF5 (Berr et al., 2015, Plant J 81:316).

Response: We have revised the introduction to include the previously known roles of LDL1 and LDL2 in regulating flowering time.

• Results:

Regarding LDL1-overexpression lines, 'Relative expression' in Supplementary Fig 2B referred to normalization to WT? The phenotype of plants needs to be shown.

Response: Yes, the level of upregulation of LDL1 expression in different T1 plants (after selection from Hygromycin) was calculated with respect to the WT.

Regarding flowering time, have the observation and measures been performed in the same experiments for the ldl1, ldl1 flc, ldl1 maf4 and ldl1 maf5 mutants (Fig 3 and Supplementary Fig 1)? The late-flowering phenotype of ldl1 shown in Fig 3D-F is much severe than the same mutant shown in the other Figs, any explanation? What's the interpretation that ldl1 is epistatic to flc, maf4 and maf5?

Response: We agree with the reviewer’s observation which is correct. The following quantifications were taken at various points during the study:

flc, ldl1, and ldlflc (Supplementary Figure 1)

WT, ldl1, and ldl1maf4 (Figure 3A, 3B and 3C)

WT, ldl1, and ldl1maf5 (Figure 3D, 3E and 3F)

The rosette leaf numbers and flowering time of the plants in Figure 3D-3F are more severe than the others because seeds were directly sprinkled onto the soil in this phenotyping, whereas in previous phenotypings, plants were grown on 1/2MS plates before being transferred to soil. However, all the components of a single experiment were grown in the same condition. We appreciate your observation, the present data does suggest ldl1 being epistatic to flc, maf4 and maf5.

The in vitro test of LDL1 for its enzyme activity (Fig 4) appears preliminary and fragmented. The quantification data in Fig 4C-D need repeats. Have other histone methylation types (e.g. H3K4me3, H3K27me3, H3K36me3) been tested? The only two types (H3K4me2 and H3K9me2) shown are both down-regulated by LDL1-GST. Can H3K9 demethylation also play a role in flowering time control? In any case, the current in vitro data only are not sufficient to draw the strong conclusions as those appeared in the manuscripts.

Response: Before concluding that LDL1 has H3Kme2 and H3K9me2 demethylase activity, we confirmed it several times__. __Please refer to the PDF file for “response to reviewers” for supporting data.

We analyzed the western band intensity by calculating the area under the curve with imageJ software, which varies between experiments depending on the band intensities, therefore, rather than plotting absolute values of band intensity, we plotted the ratio of LDL1-GST/GST from three independent experiments in Figure 4B. We did perform a preliminary experiment to see if LDL1 has demethylation activity against different methylation marks, such as H3k4me1, me3, H3K9me1, and me3 (1=GST, 2=LDL1-GST), but there was no significant change in the methylation marks in the presence of LDL1. Please refer to the PDF file for “response to reviewers” for supporting data.

H3K9 is a repressive chromatin mark, and its removal would suggest gene activation. Upregulation of FLC, MAF4, and MAF5 in ldl1 and ldl2 mutant suggests LDL1 and LDL2 removes H3k4me2 methylation marks during flowering. However, JMJ28, Jumonji C (JmjC) domain-containing histone demethylase have been shown to positively regulate flowering by removing repressive H3K9me2 marks from the chromatin marks from the chromatin of CONSTANS (CO)5.

In the manuscript, it is saying that LDL1 binds on the chromatin of MAF4 and MAF5. However, I cannot find any data shown to support this conclusion.

Response: We would like to refer to Figure 2A and B where we have provided this information.

Protein-protein interactions, e.g. LDL1/LDL2-FVE in Fig 6A and LDL1-LDL2 and LDL1-HDA5 in Supplementary Fig 5, are examined in yeast two-hybrid assay. Other independent assays would be required.

Response: We have confirmed the interaction of LDL1 and LDL2 with FVE using co-immunoprecipitation assay (Figure 8B). Since Co-IP is a confirmatory experiment, we have done it for positive interactions found through Y2H only. Moreover, in the current manuscript our focus has not been on HDA5, so we didn’t proceed with further experiments.

The study of genetic interaction between fve and ldl1/ldl2 (Fig 6B-D) looks very preliminary. It is unclear how ldl1 fve and ldl2 fve were obtained: by crosses or by CRISPR-Cas9 using ldl1 and ldl2? The phenotypes need more investigations and some molecular data regarding flowering regulatory genes (e.g. MAF4/5) are necessary. In any case, the current title and the related conclusions drawn in the manuscript are over-stated.

Response: We performed the quantification of the genetic interaction between fve and ldl1/ldl2. The binary vector pHSE401-FVE was transformed in ldl1 and ldl2 to produce ldl1fvec and ldl2fvec, respectively. We previously mentioned it in the material methods, but we have now updated it in the results section to avoid confusion.

Following the suggestions, we have scored the phenotype (Figure 9) and checked the expression of flowering regulatory genes (Supplementary Figure 10C).

Fig 7 showed data about MAF5-FLC, MAF5-SVP and MAF5-MAF5 interactions in yeast two-hybrid and about transcriptional repressor activity assay in tobacco leaves using the LUC-reporter. Again, the data need to be confirmed and reproducibility of experiments need to be shown. In addition to proFT:LUC, it is also necessary to have an internal normalization reference construct. Anyway, currently it is far away to allow a strong conclusion such as drawn in the manuscript that MAF5 interacts with FLC and SVP and repress FT to delay floral transition. Response: We have confirmed the interaction of MAF5-FLC, MAF5-SVP and MAF5-MAF5 using co-immunoprecipitation (Figure 10B). We quantified the firefly luciferase activity under proFT using renilla luciferase under pro35s as an internal control and the ratio of LUC/REN represented the promoter activity of FT promoter (Figure 10C).

Reviewer #2 (Significance (Required)):

Topic is interesting, but data are poor to support the conculsions drawn.

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

LDL1 and LDL2 histone demethylases interact with FVE to regulate flowering in Arabidopsis Summary This work study the role on flowering time of LDL1 and LDL2, two Arabidopsis homologs of the histone demethylase LSD1. Although this phenotype was previously described, the authors explore if LDL1 and LDL2 regulate other genes in addition to the floral repressor FLC. In fact, mRNA expression experiments and genetic analyse suggest that LDL1 modules flowering regulating the expression of MAF4 and MAF5, two FLC-like genes that has been less characterized. The also provide some in vitro biochemical evidence of the demethylase activity of LDL1 protein and yeast-two-hybrid data showing the interaction with FVE, another chromatin regulator involved in flowering time.

Major comments 1. Lines 116-117. Please rephrase these lines and remove panels C, D and E from figure 1 (these could be supplementary material). The flowering time phenotype of MAF4 and MAF5 in Col background is very well documented and was described before, see Gu et al Nat. Comm., 2013 (10.1038/ncomms2947) and Kim et al. Plant Cell, 2013 (10.1105/tpc.112.104760)

Response: As per the suggestion, we have modified the discussion and moved the panels 1C, 1D and 1E to the supplementary.

Lines 128-130 and Fig Sup3. The proLDL1:LDL1-GUS cannot be described as fully functional because its flowering time and LDL1 mRNA expression levels has not been compared to the wild-type plant. The line flowers earlier that the ldl1 mutant but it may only partially complement the flowering phenotype.

Response: We have provided additional experiment that the transgene is functional in proLDL1:LDL1-GUS (ldl1) with respect to the WT plants (Supplementary Figure 5A).

Line 135 and Figure 2. How the Chip data was normalized? What are you comparting in your statistical significance tests? Only two regions of each gene were analysed; to assess the binding of LDL1 to MAF4 and MAF5 loci more regions must be analysed.

Response: Normalization of the ChIP data and significance of enrichment of LDL1 was calculated with respect to the fold enrichment in the empty vector control (EV (ldl1)) plants. We only examined the promoter and exon1 of MAF4 and MAF5 for LDL1 enrichment because Hung et al,2019's6 study demonstrated that LDL1 is enriched on the promoter and exon1 of the downstream protein coding genes. However, to check for methylation marks during flowering, we have employed different primer sets on various positions between the promoter and exon1 on MAF4 and MAF5 chromatin.

Figures 6C and 6D. The genetic analysis of ldl mutant with fve-c line is prelaminar and incomplete. The epistasis cannot be evaluated as no quantitative flowering time data is provided. A questionable picture of one lonely plant cannot sustain the conclusions of lines 207-208.

Response: We have modified the picture and quantified the flowering time data to show genetic interaction of ldl1 and ldl2 with fvec mutant plants (Figure 9).

METODS. Please clarify the used mutant alleles for LDL1 LDL2, MAF4, MAF5 and FLC; if they has been previously described; if they are full knock-outs; and, consequently, use the appropriated allele name across the manuscript.

Response: As per the suggestion, we have clarified the different mutant alleles used in the study.

Minor points: 6. I think the title does not describe the work - the interaction with FVE is very relevant but it is not the central theme of the article.

Response: We have changed the title of the study to “LDL1 and LDL2 affect the dynamics of H3K4 methylation on the chromatin of MAF4 and MAF5 to allow floral transition in Arabidopsis”.

It would be very informative to have short-day flowering tome data of the genetic combinations of ldl mutants with flc, maf4 and maf5 mutations.

Response: We absolutely agree that elaborate SD experiment may open interesting avenue for LDL1 mediated regulation of flowering, which might be good for future studies. However, ldl1ldl2 shows late flowering, while maf4 and maf5 exhibit the early flowering phenotype irrespective of the day length7,8.

I found the Discussion section rather too long.

Response: We have shortened the discussion to make it more focused.

Reviewer #3 (Significance (Required)):

Although it is clear that LDL proteins regulate MAF4 and MAF 5. I found that the manuscript lacks of a general overview of flowering time regulation. At the end, it is not clear how LDL proteins regulate flowering time because they regulate FLC, FWA, MAF4 and MAF5: What is more important? Which is the main role of each protein? Are they reductant or do they have specialized functions? In a nut shell, this study is an interesting piece of work for the flowering time field: However, in my opinion, some of the presented data are redundant with previous works and the manuscript may not be relevant for a general audience.

1. Yu, C.-W. et al. HISTONE DEACETYLASE6 Interacts with FLOWERING LOCUS D and Regulates Flowering in Arabidopsis. Plant Physiology 156, 173-184 (2011).
2. Luo, M. et al. Regulation of flowering time by the histone deacetylase HDA 5 in A rabidopsis. The Plant Journal 82, 925-936 (2015).
3. Yu, C.-W., Chang, K.-Y. & Wu, K. Genome-wide analysis of gene regulatory networks of the FVE-HDA6-FLD complex in Arabidopsis. Frontiers in plant science 7, 555 (2016).
4. Hung, F.-Y. et al. The Arabidopsis LDL1/2-HDA6 histone modification complex is functionally associated with CCA1/LHY in regulation of circadian clock genes. Nucleic acids research 46, 10669-10681 (2018).
5. Hung, F.-Y. et al. The Arabidopsis histone demethylase JMJ28 regulates CONSTANS by interacting with FBH transcription factors. The Plant Cell 33, 1196-1211 (2021).
6. Hung, F.-Y. et al. The expression of long non-coding RNAs is associated with H3Ac and H3K4me2 changes regulated by the HDA6-LDL1/2 histone modification complex in Arabidopsis. NAR Genomics and Bioinformatics 2 (2020). 7 Berr, A. et al. The trx G family histone methyltransferase SET DOMAIN GROUP 26 promotes flowering via a distinctive genetic pathway. The Plant Journal 81, 316-328 (2015).

8 Kim, D.-H. and Sibum, S. Coordination of the vernalization response through a VIN3 and

        FLC gene family regulatory network in Arabidopsis. *The Plant Cell *__25, __454-469 (2013)

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Reply to the reviewers

We are grateful to the reviewers for their efforts in critically reading our work. Their meaningful input led us to make the revisions detailed below in our “point-by-point” answers to the reviewer’s comments. The insightful comments have helped us significantly improve the manuscript, allowing us to more accurately quantify and convey our data – we are thankful for that.

Reviewer #1

1. The Figure 1 legend indicates that the BirA tagged strains are mated with ~6000 AviTag yeast strains but results in Figure 2 pie chart account for 4812 total readouts. Presumably 1000 or more strains could not mate or did not produce viable diploids with the BirA tagged strains? It would be helpful to explain this differential. We thank Reviewer #1 for pointing out this gap which occurred exactly as they have interpreted. We have now corrected the figure legend to say exactly how many strains were in the library (5330) and have clearly stated the attrition of strains.

If possible, suggest including more of the raw data (in supplementary) that supports the pie chart in Figure 2. Table S1 shows the 111 proteins that display preference for Ssh1 (out of 586 total interactors?) and the fold change (in rank order) for interaction preference. At a minimum, similar data on Sec61 preference and the list of positive interactors should be included. There may also be useful information in the relative biotinylation signal for each BirA and AviTag combination when significantly above background. This is presumably a readout of AviTag protein abundance, dwell time and orientation to BirA activity. The data could be useful to other investigators.

This is a very good suggestion. We have now added a supplementary table (Supplementary Table S2) with the interaction results for proteins that preferred Sec61 and proteins that did not show any preference.

The authors might want to be more cautious in interpreting impact of the UPR on ssh1 phenotypes in the results and discussion. The Wilkinson et al 2002 paper referenced used very different conditions to detect UPR in ssh1 deletions strains. Jonikas et al 2009 does not detect a chronic UPR in ssh1 deletion cells and the conditions used in the current study seem more similar to the 2009 report. It seems more likely that deficits in translocating/localizing specific proteins causes the observed phenotypes instead of chronic UPR due to reduced ER levels of PDI.

*We agree that as result of the different conditions it is difficult to compare our data to the Wilkinson et al 2002 paper. We have therefore adjusted the text to remove this interpretation. *

Reviewer #2

1. Why was BirA used to study transient interactions? Biotinylation through BirA is slow (that is why it takes several hours to label proximity proteins) and thus it may not be suitable for capturing transient interactions. Instead, TurboID would be more suitable as the biotinylation reaction is faster than BirA. A reasonable explanation using BirA is required. We thank the reviewer for this comment which indeed also reflects our “process” of thinking. Originally, we did try to use TurboID to identify potential cargo proteins. We now have a very robust methodology to look at protein substrates by TurboID (see: https://www.biorxiv.org/content/10.1101/2022.04.27.489741v1) and so this would have obviously been the easier and faster method. However using this approach we mainly observed ribosome subunits and cytosolic proteins for Sec61 and very few, mostly cytosolic, proteins for Ssh1. Our interpretation of this is that since all biotinylation of TurboID strains occurs in parallel there is “competition” from the highly abundant and strong interactors and this does not leave a possibility to detect the low-abundance and even more transient interactions that we would like to measure. It seems that although birA/AviTag are much slower, the specificity and singular ligation site that should be exposed also in co-translational-translocation events, are more suitable for this specific experimental setup. We have now explained this also in the text.

One key question is whether biotinylated proteins identified by this method are substrates or proteins just proximal to Sec61 or Ssh1 due to close cellular localization (e.g. ER membrane) or same protein complex members. An experiment or analysis would be required to confirm that the proteins they identified are indeed potential substrates.

*This is indeed an extremely important point and we have now carefully addressed it in the text. We are certain that the reviewer is right and that many of the biotinylated proteins are same complex members and cytosolic components that happen to be in proximity (maybe regulators?) just as the reviewer suggested. We now clearly write this in the results section. This is why we focused on signal peptide containing proteins. These proteins CAN NOT be complex members nor biotinylated simply due to proximal location on the ER membrane. This is since they reside inside the lumen of the ER if they are soluble or are inserted (if they contain also a transmembrane domain) with their tagged N’ facing the lumen of the ER (So called Type I proteins). The only way such proteins could be biotinylated by the slow BirA on the cytosolic surface is if they passed through the pore of the translocon. *

Along the same line, if proteins identified by this approach are bona fide substrates of Sec61 and Ssh1, proteins having signal peptides should be enriched in the candidate list of substrates. However, it does not look like that according to Figure 2A where the secretome proteins/total proteins ratio appears to be similar among the 4 categories (e.g., Ssh1 preferring, No preference, and Not interacting or excluded). The authors should comment on this.

*We thank Reviewer #2 for highlighting this point that was not clear from our text and figures. There is definitely an enrichment of Signal Peptide (SP) containing proteins amongst the proteins that we think are bona fide substrates however this was not visualized clearly. To highlight this point we have modified Figure 2 and added a bar graph showing the distribution of SP and TMD proteins within the potential secretome. This graph now highlights the enrichment of SP containing proteins in the groups of proteins that preferred Sec61 or Ssh1 in comparison to the group that did not show a preference. *

*We also now add a citation from a new manuscript from the Hegde lab that suggests that indeed soluble SP containing proteins are the key clients for the translocon pore (https://pubmed.ncbi.nlm.nih.gov/36261528/). We have also added a section to the discussion as to why we do not see differential enrichment of SRP or its receptor on either pore although in the past this was suggested to be the key difference between the two translocons. *

Figures 1-2: They should comment on the reproducibility of the method. How many independent experiments were performed? If performed, how was reproducibility of results?

Thank you for highlighting that this was not clarified enough – we have now extended the materials and methods section to make all of the above issues clear and apparent. In short, we performed 3 biological repetitions for each experiment and for each biological repeat we performed 3 technical repeats making our results altogether rely on 9 repeats. We then excluded proteins in two cases

1. If strains were missing in either of the collections (so there was no complete set to compare them) – this caused us to drop 661 strains.
2. In cases where the proteins were expressed at very low levels of extracted poorly in our assay – we defined this as the signal being ten standard deviations (or more) lower than the rest of the signals on the same membrane – this caused us to lose an additional 93 strains. Importantly, the SD between all 9 repeats never rose above 3 (see graph below showing al strains arranged by order in library and the SD between all 9 repeats) and also now stated clearly in the text) hence we think that our method is highly reproducible

Figure 3: It is important to know the overlap of proteins commonly identified in both the interaction screening and protein localization assay. A Venn diagram that compares results between the two high-throughput assays would be useful.

*We have indeed considered making this Venn diagram (See below). However, since the connection between the screens is not direct due to the fact that the protein localization is downstream to translocation events or maybe completely independent of it, we found that the number of specific proteins that are in both screens is low. However, there is a much larger overlap in joining processes and functions, therefore we decide to make the grouping showed in Figure 4B. We would prefer not to show this figure in the manuscript however we leave this to editorial decision. *

Figure 4A (GO term): The authors mentioned that " the most consistent and repeating GO term group was those related to budding and polarity process. These include: "Establishment or maintenance of cell polarity"; "Development process involved in reproduction"; "Bipolar cellular bud site selection"; "Cell budding" and "Structural constituent of cell wall". Are protein sets in these functional categories similar or different? I am asking because GO enrichment analysis often provides apparently different functional categories but similar protein sets are included.

Indeed, this reviewer is totally correct and this is also the case here to some extent. There is some level of overlap between the GO terms. However, in our case this overlap is quite small: Out of the 77 genes that have one of those GO terms assigned only 2 have all 4, 9 have 3 and 4 have 2 of the GO terms therefore we believe that in this case this issue with GO terms hierarchy and assignment is not redundant. We are happy to highlight this in the figure or text if this is deemed to be important.

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Reply to the reviewers

1. General Statements

        We greatly appreciate the valuable comments from the referees, which have generally been very positive and constructive. The three referees have emphasized the significance of our study that opens a new direction of research regarding the role of RNA modification in viral defense. In addition, the reviewers confirm our view that the audience of our work would be broad.

        The major concerns of the reviewers are limited to four main points:

1. i) to be clearer in our description on the effect of the m6A-YTHDF axis on the viral infectivity and avoid making assumptions on effects on replication (ref. #1 and #3);

2. ii) reviewer 1 finds that the title and conclusion of this manuscript defining YTHDF proteins (ECTs) as "direct effectors of antiviral immunity" is misleading. Nonetheless, as detailed below, Reviewer 1 confuses mere knowledge of effects of m6A with those conferred by YTHDF proteins binding to m6A, and indeed overlooks nearly all evidence presented in the paper for how m6A in AMV confers antiviral resistance (i.e. mechanistic insight); iii) the discussion on the relative importance of antiviral RNA silencing and m6A-YTHDF against AMV;

3. iv) to establish more clearly whether the phase separating capability of IDRs in the reading proteins correlates with the antiviral activity (reviewer 2). We have already completed substantial experimental work to address several of these points. Nonetheless, we find it prudent to ask for an extension of the revision time beyond four weeks to allow for repeats of a few of the infection experiments in question. In the following section, we specify a plan of action for the revisions.

2. Description of the planned revisions

• *Regarding the four major concerns raised by the reviewers, we will experimentally address the last two, whereas we think the first two do not need any further experimental work, as explained in section 4. Thus, the working plan for points #3 and #4 will be as follows:

iii) the discussion on the relative importance of antiviral RNA silencing and m6A-YTHDF against AMV and related viruses

As we mention in the manuscript (discussion, first chapter), AMV *“is one of only very few studied plant RNA viruses for which no anti-RNAi effector has been identified. In addition, prunus necrotic ringspot virus (PNRSV), a virus genetically and functionally closely related to AMV (Pallas et al, 2013), does not induce easily detectable siRNAs, unlike nearly all other studied plant RNA viruses (Herranz et al, 2015)”. *

Thus, we do not come up with a strong judgment on whether RNAi is more or less important than m6A-YTHDFs for AMV resistance.

In any case, although these indirect observations seem to be quite solid, we agree with the reviewer that conclusive evidence to discard RNAi as a defense layer against AMV, at least at the time where ECTs are acting, is lacking. Thus, we plan to evaluate how the absence of the main components of the RNAi machinery affects AMV infection and if this ‘universal’ defense layer interferes/overlaps with the ECTs antiviral defense observed here. Realistically, this will take us 8-10 weeks. The experiments within this topic are based on established and published methods and thus, on solid experience. We do not expect any fallback solution and the results will be conclusive in this sense. We also note that the very time-consuming part of constructing mutants defective in both RNAi and m6A-ECT components (in this case, ect2/ect3/rdr6), as well as a first round of infection assays has already been completed at this point

iv) To establish more clearly whether the phase separating capability of IDRs in the reading proteins correlates with the antiviral activity (Reviewer 2).

We agree with Reviewer 2 that this is an interesting and important question. Hence, we have teamed up with the group of Prof. Kresten Lindorff-Larsen, expert in molecular simulations of protein folding and interaction. The Lindorff-Larsen group has recently published a powerful computational approach to simulate phase separation behavior of intrinsically disordered proteins (IDPs) or regions of proteins (IDRs) (Tesei et al., 2021, Accurate model of liquid-liquid phase behavior of intrinsically disordered proteins from optimization of single-chain properties, PNAS 118, (44) e2111696118). Applying this simulation method to the Arabidopsis ECT proteins establishes two facts that we will incorporate into a revised version:

• The IDR of ECT2 shows marked phase separation propensity, in agreement with the experimental evidence published in Arribas-Hernández et al., 2018, Plant Cell.
• The deletion mutant of ECT2 (ΔN5) with defective antiviral activity, yet unaffected ability to accelerate growth of leaf primordia shows markedly reduced phase separation propensity driven, in the main, by the many tyrosine residues in the region deleted in the mutant. These results suggest that phase separation capability indeed correlates with antiviral activity.

Since not only ECT2, but also ECT3, ECT5 and, to some extent, ECT4, participate in AMV resistance, we plan further simulation work on these proteins during the first two weeks of January 2023 before submission of a revised version of the manuscript.

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

• • All the minor concerns raised by the three reviewers have been addressed and we have incorporated all of their suggestions in this intermediate version.

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

• *As previously mentioned, we believe that points 1 and 2 do not require an experimental approach to be addressed for the following reasons:

i) to be clearer in our description on the effect of the m6A-YTHDF axis on the viral infectivity and avoid making assumptions on effects on replication (ref. #1 and #3)

        We agree with the reviewer that the term 'inhibition of viral replication' was not very appropriate because the idea that was intended to be conveyed was that of viral accumulation.        Hence, we will change this use of language, and we thank the reviewer for pointing out this inaccurate description.

When it comes to differences between effects on infection in inoculated and non-inoculated leaves, there may be a slight misunderstanding, perhaps because we were not clear enough in our originally submitted version. In reality, there are some differences even in inoculated leaves between wild type and ect mutants, especially in the triple mutant, but the slightly higher accumulation in ect mutants is not clearly observed in every experiment and hence, does not always rise to the level of significance. Although it is possible that, at local level, ALKBH9B-mediated m6A would have other ECTs-independent effects, similar to what has been described for some animal viruses (Baquero-Pérez et al., 2021. Viruses), we think that the most likely explanation for this phenomenon is a combination of infection titers and ECT redundancy.

The suggestion to use protoplasts is very accurate, but it would not resolve any doubt in this scenario, because ECTs are mainly expressed in mitotically active cells (Arribas-Hernández et al, 2020, 2018) and, since mature tissues make up the better part of the leaves used to isolate protoplasts, only few of the isolated cells would be useful. In addition, we previously showed that AMV accumulation is reduced in alkbh9b protoplasts compared to WT (Martínez-Pérez et al., 2021. Front. Microbiol.), which suggests that m6A levels of vRNAs are critical for the first stages of the infection, but in that case no problems with the expression pattern of the demethylase were expected.

ii) The title and conclusion of this manuscript defined YTHDF proteins (ECTs) as "direct effectors of antiviral immunity", which is misleading. Effector molecules of an antiviral immunity cannot be identified when the effector mechanism is unknown;

In this regard, we have a very different vision from the one the reviewer proposes. We believe that it is not correct to say that the effector molecules of an antiviral immunity cannot be identified until its mechanism is demonstrated. In fact, RNA silencing effectors were discovered long before their mechanism was elucidated in detail. One molecular interpretation of the Flor’s seminal gene-for-gene model, in terms of receptor/effector recognition, is that specific interaction between the receptor and its recognized (cognate) effector protein triggers resistance.

Furthermore, we strongly believe that we provide enough arguments to propose a model, although, as we comment in the end of the discussion, “we view this model as a conceptual framework of value in the design of future experiments to test its validity”. The reasoning that we show here is the following:

1. The m6A binding proteins are necessary for the antiviral response.
2. At least ECT2 recognizes AMV RNAs in vivo and that its m6A-binding capacity is necessary to play a role in AMV infection.
3. Simply losing methylase activity – with the same developmental defects as ect2/3/ – does not lead to the same degree of loss of resistance, and you can affect AMV resistance without affecting developmental functions of ECT2. Altogether, these observations justify the proposal that m6A exerts antiviral effects by acting as binding sites of ECT proteins in viral RNA, which we consider a clear mechanistic advance.

Bearing in mind that m6A-modified vRNAs might concentrate in replication complexes and that MeRIP-seq methodology to map m6A revealed site multiplicity in the genome of some RNA viruses (Gokhale et al., 2016. Cell Host&Microb; Martínez-Pérez et al., 2017; Lichinchi et al., 2016. Nat Microbiol; Lichinchi et al., 2016. Cell Host&Microb; Marquez-Molins et al, 2022), our results recalled the previously proposed model in which m6A sites multiplicity causes the phase separation of these RNAs through the interaction of the IDRs of the YTH proteins (Ries et al, 2019; Fu & Zhuang, 2020; Gao et al, 2019). Now, with the new simulations of phase separation behavior, although still a model that requires further experimental tests, we have better evidence to support the model that it is related to LLPS of ECT-bound viral RNA. Therefore, we firmly believe that our title conceptually reflects the basic concepts of resistance induction in virus-plant interactions.

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Reviewer 1

Although this is an interesting, and generally well-performed study, it is primarily observational and there are few mechanistic insights provided into how MUC13 modulates barrier function. The authors propose a presumably direct interaction between MUC13 and PKC, which apparently sequesters PKC, preventing this kinase from triggering PKC-dependent increases in TJ barrier function; however, there is no evidence that a MUC13-PKC interaction occurs, that MUC13 is phosphorylated by PKC, or that phosphorylation of MUC13 has any impact on its function or overall barrier function. Thus, the hypothesis is not directly tested and all observations in this manuscript are generally correlative in nature.

While the MUC13 cytoplasmic tail contains a putative PKC-binding motif, we indeed do not show a direct interaction between MUC13 and a member of the PKC family in this manuscript. Unfortunately, we have so far not been able to successfully perform (co-)immunoprecipitation of MUC13 with our current anti-MUC13 antibodies.

To provide more insights into the possible MUC13-PKC interaction, we plan to perform several experiments.

• First, we will determine the expression levels of the different PKC isotypes (PKC alpha, beta, gamma, delta, epsilon, and zeta) in the HRT18 cell lines by western blot.
• Next, we will determine the localization of the relevant PKC isoforms and MUC13 by immunofluorescence microscopy. We are curious to see if we can find a colocalization between MUC13 and a PKC member on the lateral or apical membrane. If we can demonstrate a colocalization, we could follow up with a proximity ligation assay, but this would require the MUC13 antibody directed against the cytoplasmic tail (which only detects the lateral population) and might therefore be challenging.
• Furthermore, since PKC delta protein levels were upregulated in the total lysate of ∆MUC13 cells, we will test a PKC delta-specific inhibitor in the TEER assay.

  Consider quantifying all blots (Fig. 5C, Fig. 6B).

As suggested, we will quantify both blots.

Consider using dot-plots for all quantified data.

The graphs will be altered to include individual measurement points.

Reviewer 2

Fig2E showed two bands with different size in the two MUC13 WT control cell lines. They hypothesized that this could be the consequences of glycosylation different patterns. A sample with untransfected HRT18 might be included in the western blot panel. Additionally, what is the 100kDa band?

Mucin blots are notoriously difficult and these MUC13 blots are the result of a lot of trial and error. We repeated the Western Blot with original HRT18 cells, HRT18 original cell line, as well as the two CRISPR control cells used in the study (WT 1 and WT 2) and one of the full-length MUC13 knockout cells. The higher band was absent from the MUC13 knockout cells, but a small shift in the MUC13 band size can be noted in the WT 1 cells compared to the original and the WT 2 cell lines, possibly indicating a change in the glycosylation pattern. The 100 kDa band remains detectable in all cell lines including the ∆MUC13 cell line, therefore we consider this to be an aspecific background band of the MUC13 antibody. We will add a more extensive Western Blot analysis to the manuscript.

Did the transfection of the inducible GFP-MUC13 plasmid induce any decrease of Claudin1/3/4 in HRT18 or Caco2 cells? Same question regarding PKCdelta.

These are indeed interesting questions. We will perform these experiments with our MUC13-overexpression HRT18 cells.

Reviewer 3

Moreover, the authors should determine if MUC13∆CT localize to TJs, as suggested by the working model in Figure 7C. The subcellular localization of MUC3∆CT could give critical clues for its function, but Figure 2G fails to provide any information and the authors do not present any additional data concerning the localization of MUC13∆CT. Detection of MUC13 in membrane fractions of WT, MUC13∆CT and cells lacking the mucin domain could be a feasible strategy forward.

We will perform additional immunofluorescence experiments to determine the subcellular localization of MUC13-∆CT more accurately. However, detection of the extracellular domain by western blot, as suggested, is not possible due to the incompatibility of the extracellular MUC13-directed hybridoma antibody with the western blot technique. We currently do not have a suitable antibody that recognizes the ED and can be used for western blot.

The authors introduce an inducible MUC13-GFP fusion protein into WT and ∆MUC13 cells and show that it reverses the enhanced TEER upon MUC13 deletion. Unfortunately, the "Materials and Methods" section lacks adequate information on how this fusion protein was designed. Critical questions are the position of the GFP tag within MUC13, whether the fusion protein is correctly processed in HRT18 cells, and if it localizes to the apical or apico-lateral membrane domains? Figure 2H is of low magnification and fails to provide information on the subcellular localization of the MUC13-GFP fusion protein.

The materials and methods section will be adjusted to describe all the design details of the fusion protein. The GFP tag was added to the MUC13 C-terminus with a GGGS linker sequence in between. Processing of the fusion protein seems correct as we observed MUC13-GFP localization to both lateral and apical membranes and no access intracellular build up. As suggested by the reviewer, we will add more detailed immunofluorescence pictures to the manuscript.

Figures 6B-C suggest that PKCdelta levels increase in ∆MUC13 cells, which correlates with higher enrichment of Claudins in membrane fractions. The authors then inhibited PKCdelta and observed reduced recruitment of Claudins to membrane fractions. Since the family of Claudins are differentially regulated by phosphorylation (PMID: 29186552), the authors should investigate the TEER phenotype of WT, ∆MUC13 and MUC13∆CT upon PKC inhibition.

We must clarify that figures 6C-D are done using the PKC inhibitor targeting all conventional PKCs (alpha, beta, gamma) as well as delta (https://www.tocris.com/products/gf-109203x_0741). We recently obtained a PKCdelta-specific inhibitor which we will test in the TEER build-up experiments.

Moreover, the authors predict phosphorylation sites in MUC13CT and suggest a link between PKC and MUC13 (Figure. 6A), however no evidence is presented to support this hypothesis. The authors should either determine if PKC phosphorylates MUC13 and if this modification has implication on MUC13 localization and TJ function, or remove statements regarding MUC13 phosphorylation. The data provided suggest that PKC regulates TJ proteins independent of MUC13.

We will adjust the manuscript to put less emphasis on the putative PKC motifs in the MUC13 cytoplasmic tail. For further details on how we will proceed regarding the possible MUC13-PKC interaction see question 1 from reviewer #1.

Figure 5C. Quantification of at least 3 independent experiments is required.

These data will be added to the manuscript.

Figure 6B. Quantification of at least 3 independent experiments is required.

These data will be added to the manuscript.

Reviewer 4

OPTIONAL: MUC13 is expressed both, in the basolateral membranes and in the apical membrane of intestinal epithelial cells (IECs). Does the authors check the relevance of MUC13 in the formation of microvilli in IECs? Are microvilli different (microvilli staining, number of positive cells to microvilli, length, width or distribution of microvilli) in ΔMUC13 and in MUC13-ΔCT? How the glycocalyx looks like in these cells genetically modified for MUC13?

HRT18 cells do not seem to develop microvilli. However, we plan to stain these cells with a microvilli-specific antibody (ACTUB). The HRT18 cells express mostly MUC13 and relatively low levels of the larger TM mucin MUC1. To study changes in the glycocalyx, we will stain using a MAL-II antibody which targets α-2,3 sialic acids, which are abundantly present in mucins. In this way, we will determine any big changes in the total glycocalyx that may occur in response to the removal of MUC13.

In the figure 1D would be nice to represent the co-localization of MUC13 together with occluding in a graph in each Z-stack so you can visualize in which part of the cell is maximum colocalization of these both components.

These data will be provided.

In the figure 1E, would be great to compare between the two different MUC13 antibodies the apical fraction stained in HRT18 and Caco-2. Specially in the HRT18 cell line since the first antibody did not label apical MUC13 expression meanwhile the second antibody detects the apical expression in these cells. How much lateral lateral stain the C terminal antibody compare with the extracellular antibody for MUC13 and how much stain apically the C terminal antibody compare with the extracellular antibody? Would be nice to see some comparative results using the intensity by Z-stack and plotting in a graph.

This is a good suggestion as it is quite intriguing that both MUC13 antibodies seem to target (partially) different MUC13 populations. We will perform co-staining with both MUC13 antibodies to provide information on which MUC13 populations are detected by each antibody (apical vs lateral membrane).

Manuscript would be improved if in the figure 2H to compare within the same cell line the number of MUC13 positive cells in the WT, number of MUC13 positive cells in WT+pMUC13 and the number of MUC13 positive cells in the ΔMUC13+pMUC13

We will quantify the percentage of MUC13-GFP positive cells in both the WT and ΔMUC13 backgrounds by either microscopy or flow cytometry.

In figure 5C would be helpful to plot in a graph the normalized expression of each TJ protein and compare between the different cells used (WT, ΔMUC13 and MUC13-ΔCT) as you did in figure 5A

We will provide the quantification data of three independent experiments.

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

Reviewer 1

In addition, this model does not explain why all kinase inhibitors tested reverse the increase in TER observed in deltaMUC13 cell lines. Does this reflect the lack of inhibitor specificity or the likelihood that many kinases are involved?

As stated in the manuscript, we think that MLCK, ROCK, and PKC are all essential for TER buildup in the ∆MUC13 cells. Because the roles of MLCK and ROCK are well established, we choose to follow up on the PKC results. We adjusted the text to clarify this point.

The authors do observe that there is an increase in expression of several tight junction-associated proteins, including the claudins, in deltaMUC13 cells. Affected CLDNs include 1, 2, 3, 4, 7, 12. (1) While it appears the authors are arguing that this increased claudin expression results in increased barrier function, they do not sufficiently highlight the well-known role that CLDN2 has in cation transport, and both CLDN-4 and -7 have also been implicated in paracellular ion flux (although this is apparently cell-type specific). These observations would seem to argue against a simple correlation between claudin expression and tight junction barrier function.

The reviewer is right about the different functions of claudins. Claudin-2, -4 and -7 have (potentially) pore-forming properties, while the other claudins restrict paracellular passage. It has been previously demonstrated that the magnitude of paracellular ion and water flux is reflected by the specific repertoire of claudin family members (Shashikanth et al., 2022). In this paper, overexpression of claudin-4 was shown to mobilize and affect polymeric strands of claudin-2, thus blocking its channel activity. Our mass spectrometry data demonstrated a striking increase in claudin-1, -2, -3, -4, -7, and -12 in the MUC13 knockout membranes compared to WT. We hypothesize that the claudin repertoire in the MUC13 knockout cells leads to a more restricted paracellular route (as observed in the TEER and tracer experiments). The pore-forming claudins may be subject to “interclaudin interference” therefore leading to restriction of the total paracellular ion and water flux. We have adjusted the text of the manuscript to clarify this point.

We attempted to investigate claudin-2 expression levels in isolated membranes by Western Blot but were unsuccessful as the antibody did not detect any protein while claudins-1 and -4 could be detected with the same method.

Furthermore, the authors should note the disconnect between paracellular ion flux mediated by claudins and the flux of markers such as dextrans and lucifer yellow, which can be dissociated from claudin function.

We acknowledge that the flux of larger particles (the leak pathway) is not regulated by claudins (which regulates the pore pathway). We aimed to assess both the pore and the leak paracellular pathways, by using different techniques including TEER, small solutes (Lucifer Yellow CH), and larger molecules (4 and 70 kDa FITC-Dextrans). HRT18 wild type cells are already very restrictive to the pass of larger molecules (FITC-Dextrans) but are more permeable to smaller solutes such as Lucifer Yellow (400 Da). We observed that removal of the MUC13 cytoplasmic tail did not affect the TEER, but reduced the paracellular passage of Lucifer Yellow, demonstrating that manipulation of MUC13 can affect both the pore and leak pathways. We adjusted to text to include this point.

The increased expression of claudins in the nominally tail-minus MUC13 without a corresponding change in TER would again seem to argue against a simple correlation;

MUC13-dCT cells showed consistently increased levels of claudins-1 and -2, but not the other claudins. This claudin repertoire (with high claudins-1 and -2, but lower claudin-3, -4, -7, and -12) is apparently not enough to increase TEER. We think that this again reflects the importance of the total claudin composition for the control of the paracellular pathway.

Watch the use of decimal points instead of commas (lines 253 and 256).

Corrected.

Line 543: MilliQ is not a washing agent (or is it?). (Line 535) We use MilliQ as a final step before mounting the glass slides to remove any possible salt deposition that would affect the visualization by microscopy.

We have specified this in the text.

Line 553: TER is the product of total resistance times the area. The units are ohms times area.

Indeed, we have changed this mistake (line 545).

Line 630: Please provide the transfer conditions (voltage, amp, watts?) and transfer buffer when describing the Western blot protocol.

For immunoblotting of MUC13, protein lysates were transferred to 0.2 µm PVDF membranes using the Trans-Blot Turbo Transfer system (Biorad). The transfer was run using the protocol (High MW) which consisted in running for 10 min at 25 volts (V) and 1,3 amperes (A). These experimental data were added to the manuscript.

Reviewer 2

My main concern about this manuscript is that the authors analyzed MUC13 role in intestinal homeostasis and function using colorectal cancer cells. As helpful as cancer cells are, we should always be cautious about extrapolating roles in normal intestinal epithelium or IBD pathology. Obviously, these finding are also interesting in a cancer context. Using GEPIA (http://gepia.cancer-pku.cn/), I observed that MUC13 is overexpressed in colorectal cancer COAD-TCGA dataset (compared to normal colon from GTEX). Similar results were obtained previously by Gupta et al. (ref #10). I am aware that this would be difficult to confirm the main findings in a non-cancerous intestinal cell line but this limit (normal intestine using cancer cells) should be at least discussed in the manuscript.

We appreciate the reviewers’ comments and are aware of the downsides of using cancer-derived cell lines. We have performed the GEPIA analysis ourselves and have an ongoing project about the possible role of MUC13 in colorectal cancer progression. In a separate project, we are collaborating with the Gaultier Laboratory at the University of Virginia which has generated a MUC13 knockout mouse. This model will allow us to study the role of MUC13 in non-cancerous tissue. We recently received intestinal biopsies from these mice which will be stained with MUC13 and claudin antibodies to determine localization in healthy tissue. These experiments will reveal if MUC13 colocalizes with claudin on the lateral membrane in the healthy mouse intestinal tract. In future experiments, we will also address MUC13 localization and function in human intestinal organoids. We have adjusted the discussion to refer to the limitations of using cancer cell lines.

Massey et al (Micro 2021, PMC7014956) previously showed that MUC13 overexpression increased rigidity in PDAC cells and discussed involvement MUC13 link with EMT. MUC13-Her2 interaction was also associated with decrease of E-cadherin suggesting an EMT phenotype. This should be included in the discussion section.

The discussion has been adjusted to include the link with EMT.

The authors performed mass spectrometry analysis. Results are deposited on ProteomeXchange but are not yet publicly released. Among the 1189 membrane protein identified. Did the authors observed alteration of EMT proteins? (decrease of vimentin for example). In the discussion section (lane 347), the authors mentioned the relationship between other membrane bound mucins such as MUC1, MUC4, MUC16 or MUC17 and AJ/TJproteins. Did the authors observed any alteration of these mucin in the mass spectrometry data?

The mass spec analysis was performed on membrane fractions, therefore our dataset will not contain true cytosolic proteins. One of the key EMT proteins, Vimentin, is a cytosolic protein, and indeed it was not found in our dataset. Other EMT-related proteins are shown in the following table. TGF beta 1 was slightly decreased, while E-cadherin and Integrin beta 6 were slightly increased in the ∆MUC13 cells compared to WT cells.

Gene Name

Mean WT

Mean ∆MUC13

Mean MUC13-∆CT

TGFBI (TGB beta 1)

20,54

16,48

18,83

CDH1 (E-cadherin)

22,69

24,57

24,24

ITGB6 (Integrin beta 6)

18,86

21,74

19,19

Vimentin - Cytosolic

-

-

-

CDH2 (Cadherin-2, N-cadherin)

-

-

-

Mucins are large proteins comprised of densely O-glycosylated mucin domains, which makes them extremely challenging to study by mass spectrometry (MS) (Rangel-Angarita et al., 2021). We did not specifically employ mucin-directed technologies in this dataset, thus making the detection of mucins hard. No mucins other than MUC13 were detected. For MUC13, two peptides corresponding to the EGF-like domains in the extracellular domain, a region that is less densely glycosylated. We added a sentence to the description of the mass spec results to include the EMT proteins and other mucins.

Minor points:

Lane 126: HRT18 and Caco2 colon cancer cells instead of intestinal epithelial cells

Corrected.

Lane 181 and lane 514: add "full length" MUC13 DNA sequence

Corrected.

Lane 234: TEER was measured every 12h. How the authors did observed the largest increase at 42h? Was it 48h? Please clarify.

We aimed at measuring every 12 h, however the exact measurements were done at 18h, 24h, and 42 h post-infection. We have corrected this in the manuscript.

Reviewer 3

Line 43 and 46. "Enterocytes" should be replaced with "intestinal epithelial cells", since enterocytes are themselves a distinct subpopulation of IECs.

We have changed it in the manuscript.

Lines 58-60. References in support of the statements should be added.

We added a reference to this sentence.

Lines 188-190. Authors comment on "roundness" of different cell lines. If the parameter is critical for the manuscript, the authors should quantify this phenotype.

The parameter is not critical for the manuscript. We removed the sentence.

Figure 3A. Staining of cell lines should include panels showing localization of MUC13.

Co-staining of MUC13 with occludin in HRT18 cell lines can be found in figure 1D, and MUC13 with E-cadherin in supplementary figure 1.

Lines 323-327 and 390-392. Sentences on these lines contradict each other. The sentences should describe/discuss quantified data presented in Figure 6D.

The reviewer is right that we should be discussing the quantified data in 6D. We adjusted the sentence in line 323-327.

Proteomic data sets should be made publicly available on data depositories.

All proteomics raw data were deposited to the ProteomeXchange Consortium with the dataset identifier PXD029606.

Reviewer 4

OPTIONAL: In the figure 2E, is the extracellular antibody still detecting the MUC13-ΔCT?

No, unfortunately the antibody directed against the MUC13 ED is not compatible with western blot.

In the figure 2G, would be nice to comment possible reasons why the deletion in the first cell line of the MUC13-CT you can still detect with the extracellular antibody some lateral expression of MUC13 meanwhile in the second cell line, the same deletion (MUC13-CT) you cannot see any lateral MUC13 staining with the extracellular antibody.

Yes, this is indeed a puzzling finding, especially because the CRISPR deletion is the same in both cell lines. We will add a sentence about possible reduced stability of the MUC13 without CT domain that leads to a different outcome in both cell lines.

It would be nice that the results from Figure 3H are better explained since it is difficult to follow.

We adjusted the text to explain the experiment in more detail.

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

Reviewer 1

The authors may be overly reliant on TER measurements. Epithelial cells have two parallel resistive pathways: transcellular and paracellular. TER measure the contribution of both. Thus, an increase in TER could result from a decrease in transcellular ion transport. The authors need to measure transcellular ion flow or selectively measure the junctional resistance in a select set of experiments to rule this possibility out.

The reviewer is right that TEER is a sum of the resistance of the transcellular and paracellular pathways. However, due to the high resistance of cell membranes, the current predominantly travels via the paracellular route (Elbrecht et al., 2016). For this reason, TEER measurements are widely accepted techniques for the assessment of ions passage through the paracellular pathway (Shen et al., 2011).

Reviewer 3

Figure 1C. Caco2 and HRT18 cells exhibit distinct MUC13 expression patterns when probed with an antibody against the MUC13 CT; MUC13 localizes almost exclusively to lateral cell junction in HRT18 cells, while a higher portion of MUC13 is present on the apical surface of Caco2 cells. This observation has two possible explanations: 1) the two cell lines express distinct forms of MUC13, or 2) the two cell lines carry distinct machineries for anchoring MUC13 to apical versus apico-lateral membranes. Thus, The authors should take the opportunity to determine the impact of MUC13 deletion on TEER and TJ function in Caco2 cells. Proteomic analysis and functional assays in Caco2 cells may provide more a general mechanism for how MUC13 regulates TJ proteins.

Yes, this would be a great line of investigation. However, we aimed to knockout MUC13 in Caco-2 cell lines (with the same CRISPR/Cas9 protocol as the HRT18 cells) but were unable to obtain Caco-2 knockout clones. We think this might be a consequence of the poor capability of Caco-2 cells to grow as single colonies (a required step in the protocol). Another option is Caco-2 MUC13 knockout cells have reduced viability.

The authors generate cell lines that either lack MUC13 or express MUC13 lacking the cytoplasmic domain. Loss of MUC13 cells resulted in enhanced TEER and increased recruitment of TJ proteins to membrane fractions. MUC13∆CT cells show moderate recruitment of TJ proteins to membranes and no increase in TEER but inhibit paracellular diffusion of Luciferase Yellow across monolayers. Figure 3A suggests that Occludin redistributes to tricellular junctions in ∆MUC13 cells, whereas it is found more laterally in WT and MUC13∆CT cells. These finding suggest that full-length MUC13 interferes with TJ protein complexes. However the impact of the extracellular and intracellular (CT) domains is not fully elucidated. Does the O-glycosylated mucin domain interfere with the extracellular domains Occludin and Claudins? The authors should clarify the contribution of the mucin domain to the observed phenotype, for example by performing the described experiments in a cell line expressing MUC13 lacking the mucin domain.

Mucins are type I membrane proteins with the N-terminal part of the protein on the extracellular site. Therefore, a CRISPR method to specifically remove the glycosylated domain but leave the remainder of the protein in frame is challenging. An additional difficulty is that the ED contains a lot of repeats, complicating the design of specific guide RNAs. To specifically address the contribution of the glycosylated domain, we could complement the MUC13 knockout cell with a construct lacking the ED. However, this would not be comparable to the endogenous MUC13∆CT cell line presented in this manuscript. In future studies, we will strive to address the functions of the different MUC13 domains in more detail.

Figure 5A. Turnover of TJ proteins in membrane fractions occurs faster than over a period of 1-3 days (PMID: 18474622). The authors should determine TJ protein turnover over a period of minutes and hours.

We acknowledge the findings in this interesting paper concerning the continuous remodeling of tight junctions. However, the readout of our biotinylation assay is degradation and the timeframe of degradation turns out to be days and not hours. Within this timeframe remodeling is taking place but it cannot be captured in the total lysate.

Reviewer 4

OPTIONAL: The authors show that the probiotic Lactobacillus plantarum increase epithelial barrier independently of MUC13. Have the authors considered to use other probiotics as Lactobacillus paracasei (10.3389/fcimb.2015.00026), Akkermansia muciniphila (10.1038/emm.2017.282) or some metabolic products from intestinal microbiota as short-chain fatty acids (SCFAs) (10.3389/fphys.2021.650313) to check what is the role of MUC13 and if it is related with other microbe or microbiota metabolite?

Thank you for the suggestion. We have an ongoing project in which we investigate the impact of different probiotic bacteria and plan to investigate whether they have an impact on the epithelial barrier function in a MUC13-dependent manner. This study will lead to a separate publication.

OPTIONAL: The authors successfully delete MUC13 in IECs, both, full length and the cytosolic tail. Have the authors considered targeting the deletion of the PTS domain in MUC13? Could affect that something different from paracellular trafficking as the extracellular detection of microbes and microbial products?

Removal of a domain in the extracellular domain of MUC13 with CRISPR is challenging because mucins are type I membrane proteins, the repeats and possible frameshift, as described above.

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Reply to the reviewers

Official Revision Plan Document:

Manuscript number: #RC-2022-01681

Corresponding author(s): Nicholas, Leigh

1. General Statements

We sincerely appreciate these positive and helpful reviews. We are grateful for the constructive comments and we outline our responses below. Addressing these comments will further broaden the impact of the work and increase the power, reliability, and application of single cell approaches while decreasing the cost and labor intensive collection steps.

As single cell sequencing approaches have entered the mainstream, we are still finding flaws and artifacts from these methods. A major limitation of widely used collection approaches is a difficulty in obtaining biological replicates, which are required to generate robust sequencing datasets. In general, a lack of biological replicates has been a major oversight in the vast majority of single cell studies, and any technique that can facilitate biological replicate collection should be widely applied. The elegance of SNP-based demultiplexing lies in the fact that it can be applied regardless of any external label, applied to previously collected data, and the data are already collected for every sample sequenced. We were pleased to have the reviewers agree and identify the many conceptual advances in this manuscript, with one major critique being noted by one reviewer as a lack of novelty.

Regarding the lack of novelty, we appreciate that SNP-based demultiplexing was not developed as a method within this manuscript, but disagree that a broad benchmarking and validation study that opens the doors to the use of SNP-based demuxing in any species with sufficient between animal genetic heterogeneity lacks novelty. To address this concern, we will now further emphasize the drawbacks and artifacts that can arise in the currently common practice of pooling samples and choosing not to demultiplex, while improving our explanation of our discoveries in this manuscript. The lack of biological replicates in single cell sequencing studies is rampant and needs to be addressed with approaches such as those demonstrated here. We also want to emphasize the importance of validating and benchmarking bioinformatic approaches with orthogonal, priorly established approaches (eg. wet-lab based methods), which had previously not been conducted for SNP-based demultiplexing, outside of human samples. The inbred nature of common lab animals and broad range in quality and availability of genomic resources make this a major step forward in bringing SNP-demultiplexing to all labs. We believe that our paper broadly extends, benchmarks and most importantly validates the advantages and limitations of SNP-based demuxing across various species.

2. Description of the planned revisions

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

“Cardiello et al tested if souporcell (https://pubmed.ncbi.nlm.nih.gov/32366989/) can be used to demultiplex samples for some model organisms, based on identified SNPs. For this, they used synthetic multiplexed data, publicly available datasets and some new datasets, spanning samples from five model organisms. Their analysis indicates that souporcell could be used to

demultiplex scRNA-seq experiments for multiple species, which offers a cost-beneficent approach.

The manuscript reads well and shows this approach can work for different model organisms. However, unfortunately, I am confused about the amount of novelty in this manuscript. The method, souporcell, is already published. The authors indicate souporcell is not validated in non-human samples, but the original paper states that their method works with malaria parasite data (Fig 3b, FigS4). Adapting and using an available tool for different model organisms is good and groups working on different model organisms may find this manuscript useful, but the same could be said for the original article. Due to these reasons, I am not sure whether this manuscript has novelty sufficient for publication.”

__Our response: __We appreciate this constructive criticism that helped us realize that our novelty was not clearly stated in the first version of the manuscript. We need to improve our Introduction and our verbiage as to what has been previously performed and how this current manuscript provides novel insight into multiple previously unanswered questions which broadly extend the utility of SNP-based demultiplexing. To address this comment, we will revamp our Introduction, Results, and Discussion to more clearly highlight the novelty of this work.

Planned revisions:

Defining “validation”. We define validation as establishing the accuracy or validity of a method. Therefore, validation of SNP-based demultiplexing for use in non-human species requires comparison to an already proven, orthogonal method, such as a wet-lab based demultiplexing approach. The souporcell paper does not validate (i.e., confirm with an orthogonal wet-lab method) the results from souporcell in any species but humans. This lack of validation for SNP-based demultiplexing in samples from non-human species made it unclear how and if these approaches would work in other species. Human samples are expected to perform exceptionally well in this approach due to their extremely high genetic diversity and wealth of available genomic resources. Thus, while it was exciting that the original souporcell authors chose to try applying their algorithm to a non-human (e.g., malarial parasite) dataset, the paper left many unanswered questions about potential uses and accuracy. In addition to validating the accuracy of souporcell results in many species, we demonstrated that souporcell shows a relatively poor ability to call doublets in many non-human vertebrates. In addition to highlighting a novel drawback of the method, this demonstrates the need to validate the accuracy of different aspects of tools like souporcell when applied to new systems rather than use souporcell or other SNP-demuxers prior to validation. Highlighting other novel findings in this work: For instance, our assessment of which genomic resources are required for using SNP-based demultiplexing in different species, whether this could be applied to lab animals likely to be inbred to various degrees (and to address other reviewers comments, the inbred level permitted), assessment of the accuracy of SNP-demultiplexing in species with alignment references of varying qualities (i.e., only de novo transcriptome) and genomes of varying sizes (up to 30Gb, 10 times larger that of human, which can be extremely computational intensive), and the exploration of pooling and demultiplexing of multiple species in a single library. Making clear how we made the necessary adjustments to the original souporcell pipeline to successfully apply it to datasets with various resources available in these species.

(Reviewer #1): I also wrote down two minor points below:

“1- Doublets assigned by souporcell compared to the fluor-based assignment look random. In Fig 2 doublet recovery rate looks smaller, and in fig 3 doublet rate prediction looks more random. This is a bit confusing. Is there any explanation for this?”

__Our response: __We agree and thus noted in the manuscript that the detection of doublets in these datasets by Souporcell are not very reliable.

Planned revisions:

We will expand our Discussion to include brief hypotheses for factors that likely contributed to poor doublet detection by souporcell in these analyses. In the Discussion we will clearly suggest complementary approaches for improving the detection/removal of doublets in pooled scRNA-seq experiments through applying external gene expression-based doublet detection programs. We will also attempt to use these programs on at least one of our datasets to see how well independant doublet detection methods complement souporcell on pooled datasets. A full benchmarking of these doublet detection methods already exists and will be referenced in our Discussion.

Reviewer #1: “2- The authors discussed the immune system cells might show some variability in their discussion (referring to fig 3), but this is not clearly shown in the figures as data. Having a percentage bar graph could make it clearer for the readers.”

__Our response: __This is a valid point that we plan to address with the addition of a new figure as well as some clarifications in the text.

Planned revisions:

We will make a supplemental figure for Figure 3 in which we clearly demonstrate animal to animal variability. (bar plot of absolute cell numbers present from each individual animal present in each cell cluster as requested). In the new supplemental figure we will also include a new UMAP plot of fluorescently assigned cell identities belonging only to one of the three animals, which makes it easier to visualize the difference in numbers of cells from each animal present in each individual cell cluster. We will also cite papers that have already demonstrated the phenomena of animal to animal variability in scRNA-seq datasets. We will further emphasize that even in the absence of animal-to-animal variability in co-clustering, that demultiplexing pooled datasets is important because differential expression analysis is greatly enhanced with biological replicates.

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

Major comments:

“1. SNP-based demultiplexing performed well on some species, such as zebrafish and Africa green monkey, from which over 90% of the cells analyzed were correctly identified. However, this accuracy decreases in Pleurodeles samples when a common SNPs VCF file is absent (Fig.3). It showed that cell identity can be more precisely defined with the increase of average read depth (Fig 3B). So, I am wondering whether the mis-defined cells shown in Fig. 3E, actually are cells with lower reads. It is better if the authors can test such a correlation between the cell identity and the depth of reads using the data from Fig. 3E.”

__Our response: __We are thankful to reviewer #2 for raising such a great point. We do see the accuracy of the benchmarking results for this experiment increase with increasing sequence depth/cell quality. However, the reasons for this are potentially more complex than just higher accuracy of souporcell in higher quality cells: The fluorescent-based demultiplexing that is being used for “ground truth” in benchmarking souporcell for this figure is more accurate in cells with higher read depth because more fluorescent gene reads are likely to be captured. Therefore analyzing the accuracy of souporcell relative to fluorescent-based demultiplexing over varying read depths can be confusing because it is possible that both methods improve in accuracy with higher read depth. Figure 3B attempts to illustrate this concept, and to demonstrate why we chose to benchmark only the cells with sufficient read depth (read depth between 5K, and 40K, and >1 fluorescent gene read per cell). We plan to complement our manuscript with additional figures and text that will make this clearer.

Planned revisions:

We will produce a plot similar to Figure 3B, but with a Y axis that is the percent agreement between the two methods. For Figure 4 we will also make a plot showing percent agreement between demux methods versus read depth. This plot will be a useful comparison to investigate whether scRNA read depth is directly affecting the quality of souporcell’s SNP-based demux results. Plotting this comparison for a dataset in which Cellplex/Cell hashing is the benchmarking demux method is a more fair test of the effect of sequencing depth on the souporcell demux results because cellplex results rely on reads from the cellplex library, which are an independent sequencing library from the scRNA reads. We will investigate whether the use of a common VCF file or lack thereof affects souporcell accuracy. To test this, we will try repeating souporcell demux of one dataset with and without a common VCF file input to see if the VCF file inclusion affects the accuracy of souporcell results.

Reviewer #2:

“2. Please discuss limitations of this approach in the manuscript. (1) To which extent, when SNPs are roughly present in the individuals of same species, SNP-based demultiplexing can be applied, e.g., individuals from an inbred strain (c57bl6 mice) would not work.(2) The authors experimentally tested two newt species using SNP-based demultiplexing. When multiple species are experimentally applied, may the cell/nuclei size variation cause problem?”

__Our response: __We agree with Reviewer 2 that this paper brings up many technical questions about the limits to which SNP-based demultiplexing will succeed. These limitations should be addressed more thoroughly in our Discussion section.

Planned revisions:

We will expand our Discussion to more fully discuss the predicted limits for SNP-based demuxing for separating pooled cells from genetically similar individuals. We referenced the single paper previously published which reported that Freemuxlet, a similar approach to souporcell, did not succeed when applied to cells pooled from multiple animals within an inbred mouse strain, but did succeed across mouse strains (though without any validation of results). We will expand this Discussion to address the expected effects of genetic diversity on the success of SNP-based demultiplexing methods. We will also note in this expanded Discussion that SNP-based demuxing worked in this paper on siblings (some of the xenopus, some of the zebrafish), and other SNP-based demuxers have been used successfully for demuxing cells from closely related individuals including human siblings (scSplit) and human maternal/fetal pairs (souporcell). We will expand our Discussion to address the potential drawbacks of pooling cells from different species or tissue types including the possibility of a bias in scRNA-seq sample preparation methods. We expect that variations in cell or nuclei sizes between species could cause biases in cell capture depending on the scRNA-seq library preparation method, especially with microfluidic based scRNA-seq preparation methods. We will search for a dataset that would allow for synthetic pooling of inbred mouse data and, if available, put this through our synthetic pooling and demuxing pipeline. While other papers have reported this does not work with other SNP demux tools, and on comments on the souporcell github (https://github.com/wheaton5/souporcell/issues/154) it does not seem to be working, we feel this would be a nice test/reference for showing the limitations for SNP-based demuxing in highly genetically similar individuals.

(Reviewer #2)* *

“3. What is the upper limit number of samples when using this model. Please make some estimation or discussion about it.”

__Our response: __We think this is a pressing question for the future of SNP-based demuxing and deserves further discussion in this manuscript. This is directly addressed by the authors of souporcell in a github thread with regard to human samples (worked on 21 human samples, may work in up to 40). At this point, we have no reason to believe that the limit on sample numbers should be different in other species.

Planned revisions:

We will include discussion about potential limits for the maximum number of samples that can be pooled and demuxed using this approach. As discussed below in response to reviewer 3, we will quantify the genetic differences in pooled datasets in this manuscript in order to give readers an improved prediction of how well SNP-based demuxers are likely to work on their animals of interest. We will look for previously published pooled dataset from zebrafish that includes multiple dozens of samples and attempt to SNP-demultiplex this pool. While we will be unable to validate the accuracy, given how well SNP-based demuxing has performed we can at least determine if cell origins are assigned.

Reviewer #2: Minor comments:

“1. Please add an algorithm principle of this model.”

__Our response: __Thanks for the suggestion, we will do so.

Planned revision:

We will direct readers to the algorithm principle of souporcell in the original paper and include a flowchart of our workflow for running souporcell piece by piece as we have done in the manuscript. As mentioned above, we will make clear how we made the necessary adjustments to the original souporcell pipeline to successfully apply it to datasets with various resources available in these species.

Reviewer #2:

“2. Give a clear definition of doublets including the ground truth and Souporcell result.”

__Our response: __We appreciate this recommendation. For the purposes of this paper our definition of a ‘doublet’ is a dataset represented by a single cell barcode that actually contains more than one cell. However, true doublets can be identified with absolute certainty only in our synthetically pooled datasets, because no demultiplexing approach used for benchmarking is 100% accurate. Therefore, ‘true doublet’ will refer to known doublets based on synthetically pooled dataset ground truths. Further, for our experimental datasets we will also use ‘confirmed doublet’ to refer to cells that were called doublets by both the ground truth and souporcell. And we will use ‘contested doublet’ to refer to cells in which the experimentally derived ground truth and souporcell result disagree about a potential doublet.

Planned revision:

We will insert a clear definition of doublets used in this paper as described above, including the complexity in identifying which doublets are real given the relationship between ground truth and the souporcell results for each experiment.

Reviewer #2:

“3. Authors should indicate the time cost of running one round of such analysis, the minimal computational requirements?”

__Our response: __This is an important point and will be helpful to readers.

Planned revision:

We will add to the manuscript information on the required time, RAM consumption, and computational requirements for running various setups for souporcell.

Reviewer #3: Major comments:

“The manuscript makes a convincing case for the ability of a preexisting SNP-based demultiplexing tool, called souporcell, to demultiplex pooled samples. The study uses three methods for validation: 1. In silico data pooling; 2. Pooling of transgenic lines; 3. Pooling of cells tagged with CMOs (10x genomics). The results are consistent across experiments.

The authors propose that souporcell is a solution for demultiplexing pooled samples whenever sample tagging methods are not feasible. Although the authors test this approach in several species and conditions, the validation does not cover all possible cases and situations, obviously. Indeed, the authors recommend potential users to run pilot validation experiments with a secondary demultiplexing methods.

However, the manuscript would become more useful if the following points are addressed:

First, what is the genetic relatedness of the individuals pooled in the experiments? What is the SNP frequency in the samples analyzed, and how does that compare to SNP frequency in mouse strains? (The number of SNPs in the VCF is reported in a supplementary table but not discussed in the main text). This point is extremely important: as the authors mention, it is not possible to demultiplex samples from the same mouse strain. Inbreeding is relatively common in laboratory species, even unconventional ones; therefore, information on genetic relatedness and SNP rate would help readers assess whether SNP-based demultiplexing has a good chance to work in their systems. Addressing this point does not require any additional experiments, and computing from the single-cell reads how many SNPs distinguish the individuals pooled here should be straightforward.”

__Our response: __We appreciate the comments raised by reviewer #3.These are valuable critiques and will greatly improve the manuscript.

Planned revisions:

We will expand our Discussion with a paragraph on the limits for genetic differences required for SNP-based demuxing to work, as mentioned in response to Reviewer 2. This will include references to Table 1 values on SNP numbers utilized in each analysis, and hypotheses on the absolute limits for genetic relatedness. We will expand Table 1B to include green monkey. As mentioned in response to Reviewer 2, if previously published data we will also try applying souporcell to data from an inbred mouse line to test run an extreme case of applying SNP-based demuxing to data from very inbred animals. We will more clearly annotate the known relationship between individuals in our experiments, and will discuss this within our Discussion. We will contact the zebrafish and axolotl authors and ask if these animals were siblings. We will identify and apply a method for quantifying the genetic relationship between individuals in each scRNA-seq experiment in this study, to enable us to provide readers with a quantitative measure of genetic diversity present in each experiment. This analysis should shed some light on the requirements for genetic variability in order for SNP-based demultiplexers to succeed.

Reviewer #3:____

“Moreover, the relatively limited number of samples pooled does not validate the use of souporcell with a larger number of samples. For example: in developmental studies, often dozens of embryos are collected and pooled. What are the potential caveats of using souporcell for demultiplexing larger number of samples? The Discussion would be a good place to warn potential users of the limitations of the approach.”

__Our response: __We agree this could still be a limitation, and for developmental studies with multiple dozens of samples, further exploration of optimal demultiplexing methods or the combination of computational and wet-lab based demux methods may be required.

Planned revision:

We will expand our Discussion on predicted limits for SNP-based demuxing of high sample pools, as discussed in response to Reviewer 2. We agree that developmental projects often involve pooling large numbers of samples, so it is worth clearly outlining the benefits and risks of planning to use SNP-based demultiplexing on such high sample pools, and to outline the limits as discussed by the developer of souporcell. As stated above, we will work to identify a previously published pooled zebrafish dataset with multiple dozens of samples and run souporcell on it. While this will not provide any validation it will at the least determine if we are able to assign cell origins, which have thus far been very reliable when assignments have been made.

Reviewer #3: Minor comments:

“- is the accuracy of doublet detection rate a function of number of samples? This can be tested by repeating the monkey in silico experiment with three individuals.”

__Our response: __This is a good question. We do not thing that the number of samples substantially affects the accuracy of doublet detection by souporcell, but we will test this.

Planned revision:

As suggested, we will repeat the monkey analysis with 3 samples to see how this changes doublet detection. Overall, due to the low quality of doublet detection by souporcell found in this manuscript, we will expand our Discussion of doublet detection to propose some potentially useful recommendations for making conservative doublet calls with souporcell external programs (addressed above in response to Reviewer 2. We expect that the more substantial filtering of the monkey datasets relative to the zebrafish dataset prior to pooling contributed to this question. To make these differences more obvious we will more deliberately emphasize the differences in dataset filtering for each experiment.

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

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

From Reviewer 1:

“More generally, showing more direct evidence for the variability of different cell types (not just the immune system) could be informative for scRNA-seq users.”

__Our response: __We do not plan to conduct extensive analyses of other published single cell datasets to provide a further reason for why it is important to have biological replicates for single cell experiments. When building this manuscript, we chose not to pursue the option of publishing an analysis of published single cell datasets in which we could identify artifactual results and animal to animal variability, because we worried that this would be harmful to future open science efforts, and therefore, counterproductive. Further, past papers have already demonstrated the issue of batch effects and animal to animal variability in scRNA-seq datasets, and the requirement for biological replicates to facilitate differential expression analysis. As mentioned above, we will do a better job citing the papers that address these points.

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 manuscript "An Sfi1-like centrin interacting centriolar plaque protein affects nuclear microtubule homeostasis" by Wenz and co-authors describes the detection and analysis of the Sfi1-like protein in apicomplexan parasite Plasmodium falciparum. The authors examined the protein localization and function in asexual stages during parasite replication in the red blood cells. The authors detected PfSlp in the PfCentrin1 pulldown, created PfSlp conditional knockdown strain, and evaluated growth and morphological deficiencies associated with the PfSlp deficiency. The study's primary finding is that PfSlp inhibits the extension of nuclear MTs.

Major comments

The key conclusion is appropriate but is poorly supported by experimental evidence. The transitional, experiment-to-experiment conclusions are preliminary and may require additional experiments. The authors did not present a convincing model of the PfSlp1 function in mitosis.

We appreciate the reviewer’s evaluation that our key conclusions are appropriate, but also have taken some of the valid comments below into account and added some conclusive experimental data and partly modified the choice of words when interpreting the data. We are now fully convinced that our conclusions are appropriate and supported by experimental evidence. To understand the function of PfSlp, which was described for the first time in this study, precisely will require a more detailed model of the still very much understudied malaria parasite centrosome and will be the subject of future inquiries.

If PfSlp inhibits the MT polymerization, then the PfSlp reduction should lead to an extension of the bipolar spindle, which is partly supported by longer MTs in the hemispindles. How is the excess of the nuclear MTs prevent the spindle resolution in anaphase?

Intranuclear hemispindle microtubules are indeed elongated. Increased microtubule polymerization does not necessary lead to an increased spindle length but could just as well promote the nucleation of multiple short microtubules or increase overlap between antiparallel microtubules. We, however, want to emphasize that our key conclusion is that PfSlp is implicated in the regulation of nuclear tubulin levels, rather than “inhibits extension of nuclear MT”. In our view this is an important distinction since microtubule misorganization is merely a consequence of changing nuclear tubulin levels. At no point we want to suggest that PfSlp somehow directly inhibits polymerization of microtubules and therefore did not provide any specific evidence. The fact that PfSlp and microtubules are in different compartments underlines this. Yet, we have noted that our abstract uses the word polymerization. Although we mention that it occurs as a consequence of increased tubulin concentration, which thermodynamically favors microtubule polymerization, we acknowledge that this could be misleading and removed this term (line 30). Concerning how the excess nuclear MTs prevent anaphase spindle resolution we propose several explanations in the discussion (lines 381ff). All line numbers refer to document with “tracked changes”.

Fig 4C misrepresents mitotic phases: bipolar spindle should be broken into two in anaphase, while the drawing shows one elongated spindle connecting two poles.

Indeed, we frequently observed, anaphase spindles being “split” ourselves (Simon et al. LSA, 2021, Fig. 2A). Although sometimes we would see one elongated spindle and sometimes more than two as in Liffner et al. 2021 Fig. 3A. For simplicity we only drew one elongated interpolar microtubule bundle but have now corrected this for more accurate representation.

The authors should correct the use of terminology. Throughout the manuscripts, the parasite division stages are called life stages. Life stages are merozoites, gametocytes, ookinetes, sporozoites, etc. The division stages apply to a single life stage and, in the case of schizogony, are rings, trophozoites, and schizonts.

We once falsely referred to life cycle in line 182 when we should have referred to the intraerythrocytic development cycle. The paragraph using the incorrect wording was removed in the revision.

Please, note that schizogony does not follow the ring and trophozoite stages (line 119); it includes them as the distinctive morphological stages of one round of schizogony. The cell cycle terminology is incorrectly applied.

We have the impression that the usage of the term schizogony is rather “fluid” in that it is occasionally also employed to just the describe the phase where DNA replication, nuclear division, and cytokinesis occur (hence schizont stage), but we clearly note the more canonical use as equivalent of the asexual intraerythrocytic development cycle as whole. We modified the terminology accordingly (e.g. by employing “schizont stage”) lines 43, 142, 184, 238, 265.

What is the "mitotic spindle stage," "mitotic spindle nuclei, "or "mitotic spindle duration" (Fig. 4B)?

It has now been conclusively demonstrated that nuclei go through independent nuclear cycles with different morphological stages (Simon et al. 2021 LSA, Klaus et al. 2022 Sci Advances). Hence, we use the term “mitotic spindle stage” to contrast it with the “hemispindle stage”, which can be morphologically distinguished using microtubules as a marker and occurs just prior to S-Phase. Consequently, “mitotic spindle nuclei” are nuclei in the “mitotic spindle stage”. “mitotic spindle duration” designates the time nuclei spend in that stage i.e. from hemispindle collapse until anaphase spindle elongation. We have adjusted and more accurately defined the terminology throughout the text and complemented Fig. 1A for clarity.

Minor comments

The PfSlp knockdown is inefficient: the 55% reduction at the RNA level translates into a minor change at the protein level (Fig.2 and S4). The evaluation of the protein changes should be done by western blot analysis with appropriate controls. The intensity of the IFA signal (used in the study) changes depending on the focal plane, as seen in Fig 1D.

Due to the exceptionally big size of PfSlp of around 407 kDa and the low expression levels western blot analysis was not feasible in our hands. For quantification of the IFA signal we used image projections and background subtraction to integrate the signal of the full z-stack containing the entire cell and our measurement was therefore independent of the focal plane. We have now described this a bit more thoroughly in the methods section (lines 620ff). The change in signal as measured by IFA is still clearly significant and shows a reduction of about 45%, which is coherent with the reduction of 55% found by RNA analysis and ultimately results in a specific phenotype.

Growth defects of the PfSlp KD: It is unclear what causes the reduced parasitemia of the GlcN untreated Slp parasites (Fig. 2C and D).

A likely explanation is that the C-terminal tagging of PfSlp already slightly impairs the function of the protein causing a mild growth phenotype that is not observed in wild type although it is not statistically significant (Fig. 2C). Importantly, the reproduced analysis of parasite growth, shown as multiplication rate in Fig. 2C (and growth curve in Fig. S6) now more clearly demonstrates that when normalizing for GlcN treatment and GFP-glms tagging (“3D7 corr.”) the growth defect is still significant and can therefore be attributed to Slp KD and not to tagging or GlcN treatment addition, which on their own do not cause a significant phenotype.

To conclude that the kinetics of DNA replication is affected, the authors will need to perform the real-time measurements of DNA replication forks.

We thank the reviewer for pointing this out and removed the term “kinetics” (line 182, 269).

The presented data supports that fewer S/M rounds were performed by PfSlp lacking parasites but gives no way to determine whether the S or the M phase was affected.

We thank the reviewer for this valuable comment. Our data so far showed that the very first spindle extension, and therefore M-Phase, is clearly affected (Fig. 4A-B). If the first division fails all subsequent S phases and M phases might be affected at the population level. To test whether S-phase is affected we now acquired time lapse imaging of single cells labeled with the quantitative DNA dye 5-SiR-Hoechst and saw no difference in DNA signal increase for PfSlp KD parasites, while nuclear number was reduced, showing directly that M phase rather than S-Phase is affected (Fig. 4C, lines 280ff).

DNA quantification graph (Fig. 2D) is confusing and does not correlate with the quantification of merozoites (Fig. 2E). Why is the DNA intensity of Slp- parasites lower than the DNA intensity of the Slp+ parasites, even though Slp deficient line produces less progeny? Is it possible that you missed the actual peak of DNA replication? Authors may consider more tight time courses with a few additional time points.

This is a good point. We have repeated this experiment with longer sampling time and shorter intervals. We now plot the fraction of cells with DNA content above 2N (also to exclude double infections and cells that arrest prior to the schizont stage) as a measure to see how many cells are replicating (Fig. 2D, lines 175ff). Although the replication peak was, as observed before, shifted by GlcN treatment we found no significant differences in height. Although the lack of PfSlp tagging and GlcN treatment in the 3D7- control might favor the slightly more productive replication. We complement this analysis by plotting the average DNA fluorescence intensity over time (Fig. S7A) and the area under the curve (see below), as an approximation of “total replication activity” and still found no significant differences (Fig. S7B). The fact that the DNA fluorescence intensity peak does not correlate with the slightly reduced merozoite number observed in Fig. 2E is not very surprising as the fixed time point sampling for DNA quantification can’t differentiate between cells slowing or even halting progression and thereby confounding the averages. This limitation of single timepoint population analysis specifically highlight the importance of our time resolved single cell analysis presented later in Fig. 4, which clarifies the phenotype. Further, merozoite number counting does not give any insight about ploidy of the individual merozoites. Considering the significant nuclear division defect we also show in Fig. 4 it is plausible that some merozoites in the Slp KD could be polyploid, while globally replication is not strongly affected.

Given the main claim, the study lacks the spatial-temporal analysis of tubulin described only in words. The tubulin quantifications by WB (Fig. S6) are not convincing, as well as the resulting conclusion of the cell cycle retardation.

We are not completely sure what the reviewer is indicating by a lack of spatial-temporal analysis of tubulin given that we show time-resolved imaging data of tubulin organization in dividing cells and quantify intranuclear tubulin levels. Those data (particularly Fig. 4A) clearly show a retardation in the mitotic spindle stage. We, however, acknowledge that the data on tubulin quantification via western blot could, as Reviewer 2 also points out, be improved through the addition of biological replicates. We have repeated those experiments twice and can now confirm by statistical analysis that total tubulin, aldolase, and centrin protein levels are not affected by Slp KD at 24, 30, and 36 hpi (Fig. 3E, Fig. S8, lines 232ff). This indicates that the increase in intranuclear tubulin is not a consequence of globally increased tubulin expression.

It is unclear how the authors arrived at the conclusion that the mitotic spindle is deficient in PfSlp KD parasites. Fig. 3C does not show visible differences in GlcN treated and untreated parasites.

PfSlp KD parasites show unusual microtubule protrusions branching of the main microtubule mass, which have never been observed in wild type parasites. This should have been indicated more clearly by adding an arrow in Fig. 3C. We further think our observation that the tubulin content in mitotic spindles is almost three times higher on average than in wild type spindles (Fig. 3D) and that those spindles do not properly extend (Fig. 4A-B) justifies this claim.

How many nuclei are in the cells shown in figure 4 and supplemental movies? It seems as if GlcN treated Slp parasites form one long spindle.

In a previous study (Simon et al. 2021, LSA, Fig. 1B) we have demonstrated that the number of distinct microtubule foci, i.e. mitotic spindles, observed in cells corresponds directly to the number of nuclei. Hence we can assume that prior to successful spindle extension in the PfSlpKD there is one nucleus or two nuclear masses that are in the process of separation. We now added some new time-lapse microscopy data of DNA- and tubulin-stained parasites that confirms that arrested Slp KD parasites fail to properly divide their nuclei (Fig. 4C, Mov. S4-5) and confirms our previously published findings about nuclear number.

A majority of PfSlpKD parasites indeed seem to form one long spindle. However, this “long spindle” appears only after a significant time delay during which wild type parasites already have undergone multiple nuclear divisions and could be a downstream effect of this retardation through e.g. increase of total tubulin levels over time (Fig. 3E).

The conclusion of anaphase block is unsupported: the authors need to demonstrate the accumulation of the metaphase nuclei with a bipolar spindle.

Anaphase describes the phase of chromosome segregation and includes the full extension of the spindle, as discussed above, both of which fails in more than half of the PfSlpKD parasites (Fig. 4A, Mov. S3, S5) and is therefore interpreted as “failure to properly progress through anaphase” for the first time in the discussion (line 381). We currently can’t think about a more direct way to demonstrate this than by time lapse imaging of the very first mitosis in individual parasites. Any analysis of populations at later time point or using fixed cells will be skewed by the phenotype occurring in the very early stages of nuclear division.

Reviewer #1 (Significance (Required)):

The eukaryotic centrosome is a microtubule organizing center that guides the segregation of duplicated chromosomes. Despite being an essential regulator of the parasite division, the apicomplexan centrosome remains poorly understood. Recent studies in Toxoplasma gondii (Suvorova et al., 2015) and Plasmodium species (Simon et al., 2021) demonstrated high diversity of the centrosome organization making the studies of microtubule organizing centers in apicomplexans, particularly challenging. Examining the protein composition is one of the ways to uncover organelle function. The current study would help to understand the evolution of the MTOC and mechanisms of cell division in understudied eukaryotic models.

The focus of my research is the apicomplexan cell cycle. I previously showed the bipartite organization of the Toxoplasma centrosome and identified and characterized several centrosomal constituents, including centrin partner Sfi1. Our most recent study presented evidence of the functional spindle assembly checkpoint in Toxoplasma tachyzoites.

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

Summary:

Plasmodium falciparum parasites undergo several rounds of asynchronous nuclear divisions to produce daughter cells. This process is controlled by the centriolar plaque, a non-canonical centrosome that functions to organize intranuclear spindle microtubules. The organization and composition of this microtubule organizing center is not well understood. Here, Wenz et al. identify a novel centrin-interacting protein, PfSlp, that, following knockdown, leads to fewer daughter cells and aberrant intranuclear microtubule homeostasis and organization.

Wenz et al. identify PfSlp via co-immunoprecipitation of P. falciparum 3D7 strain with an episomally expressed PfCen1-GFP, noting PfSlp as a gene of interest based on the presence of several centrin-binding motifs. The authors go forward to generate a transgenic 3D7 strain, equipping PfSlp with GFP and glmS ribozyme, to localize and evaluate the function of PfSlp in asexual blood stage parasites. PfSlp appears to, using immunofluorescence and STED microscopy, localize to the outer centriolar plaque in schizonts, based on its colocalization with PfCen3. The authors show, utilizing the inducible glmS ribozyme knockdown system, that PfSlp is required for proper parasite growth, noting a defect following addition of GlcN. This defect is noted to cause a delay in the initiation of nuclear division, or schizogony. Analysis of intranuclear microtubule dynamics reveal abnormal microtubule organization, specifically an increase in nuclear microtubule abundance and length following PfSlp knockdown. Together, these findings characterize the role of a novel protein, PfSlp, that contributes to nuclear tubulin homeostasis and organization during schizogony.

Major comments:

The major claims made by Wenz et al. are largely convincing with the data provided.

1. One area that requires additional attention is the following: Wenz et al. claim PfSlp and centrin to be interacting partners based on 1) co-immunoprecipitation (without prior protein crosslinking), 2) the presence of centrin-binding motifs in PfSlp and 3) colocalization of PfSlp and PfCen3. This interaction is not interrogated fully and claims specific to this point need to be clarified and described as preliminary. As it is written, Wenz et al. claim PfSlp is required for centrin recruitment to the centriolar plaque but this is not investigated fully. The data show lower levels of endogenous centrin at the centriolar plaque in PfSlp knockdown parasites but centrin protein levels are similar in wildtype and knockdown PfSlp parasites. As is, the phenotype attributed to PfSlp knockdown could be attributed to PfSlp or aberrant centrin recruitment to the centriolar plaque. Experiments manipulating PfSlp centrin-binding motifs would strengthen these claims and elucidate the role of PfSlp apart from centrin. If not included, less emphasis should be placed here.

We agree with the reviewer that additional evidence to demonstrate the direct interaction between PfSlp and centrin would be adequate. Due to the presence of multiple widely spaced centrin binding motifs in PfSlp, which would require multiple highly challenging rounds of genome editing to be modified, we have opted for reciprocal co-IP using PfSlp-GFP (line 139, Fig. S3, see below). The exceptionally large size of PfSlp of 407 kDa and low expression prevented us from detecting it directly on the western blot, but we found a clear centrin band in the Slp IP that was absent in the control.

We have also further qualified our formulation about centrin recruitment depending on PfSlp (lines 138, 146). Finally, we agree that there are many factors downstream of PfSlp that can contribute to the observed phenotype, which might include centrins and will be subject of future investigations.

The 3.5 mM glucosamine has some toxicity in the parental 3D7. Is it possible to use a lower concentration so the growth of 3D7 is unaffected but the grow of the Slp-GFP GlmS parasites is still reduced?

We acknowledge that the used Glucosamine concentration is on the higher end of the classically used range. The slight toxicity of Glucosamine is dose-dependent and only vanishes at submillimolar concentrations. During initial experiments we have found to generate a robust phenotype with 3.5 mM and decided to carry out all experiments at this concentration. We think that the added effect of PfSlpKD over GlcN treatment alone is sufficiently show as e.g. the merozoite number phenotype (Fig. 2E) and the mitotic delay (Fig. 4B) only occurs in Slp+ parasites.

Fig 3E - the quantification of tubulin levels requires biological replicates to have means and error bars.

We fully agree with reviewer 2 (and reviewer 1 who commented along the same lines) and now generated two more biological replicates that allow us to confirm by statistical analysis that total tubulin, aldolase, and centrin protein levels are not affected by Slp KD at 24, 30, and 36 hpi (Fig. 3E, Fig. S8, lines 235ff).

The use of "centrin" is somewhat imprecise throughout. The authors should specific which centrin (PfCentrin1 or PfCentrin3 or others) they are referring to each time in the text.

Thank you for requesting this clarification. We have used “centrin” on purpose but have failed to properly explain our terminology in the text. For the detection of endogenous centrin we use a polyclonal antibody raised against PfCentrin3 (Simon et al. 2021). Due to the very high sequence identity between PfCentrin1-4 we can’t exclude cross-reactivity of any polyclonal antibody. Throughout the field so far polyclonal antibodies raised against Chlamydomonas centrin and Toxoplasma centrin 1 have been successfully used to label centrin pool at the centriolar plaque. Since we can’t distinguish with certainty which of the centrins (PfCen1-4) is targeted we chose the general description “centrin”. We were however able to show that all four centrins (PfCen1-4) colocalize at the centriolar plaque (Voss et al. biorxiv, /10.1101/2022.07.26.501452) and that Plasmodium centrins interact with each other was demonstrated previously (Roques et al. 2019) while the interaction between PfCen1 and PfCen3 was shown in this study. Therefore, this will not limit our conclusions. We now explain this better in the text (lines 132ff) and adjusted the labeling in Fig. 1E.

The mention of the cell cycle checkpoint is an interesting and appropriate point in the discussion. However, the discussion of it in the last sentence of the introduction is less appropriate. It should be removed from line 92-93.

We are excited by the prospects of this study to finally be able to investigate the presence of checkpoint induced delays using time-lapse microscopy, but absolutely agree with the reviewer and have removed the statement in the introduction.

Minor comments:

1. Line 50 - "are remaining unclear" should "remain unclear"

Has been corrected.

Line 65 - "players" is quite informal. A better word should be selected.

Was replaced with “factors”.

Line 223 - "were" should be "where"

Has been corrected.

The delay in schizogony which is observed following addition of GlcN (Figure S5) may be made more convincing if the experiment is performed hours post invasion rather than hours post treatment. The synchronization of the parasites is in question as it is described in the methods.

We have included this data from our initial exploratory analyses and since it was not central to our argumentation, we choose to add it as supplemental figure. After producing further data, we came to realize that the classical morphological characterization using Giemsa-staining partly mispresents the relevant transition from the pre-mitotic to mitotic stages as the onset of first spindle formation and DNA replication can’t be detected. Previous studies have also indicated that parasites which were drug arrested at the trophozoite to schizont transition were morphologically similar to mid- to late schizonts (Naughton and Bell, 2007). In a context that investigates nuclear division phenotypes we feel that this analysis might rather be misleading and that the provided growth assays, DNA replication quantification, and time lapse movies are significantly more informative. Therefore, we have decided to remove the figure altogether. However, we have moved Fig. S7 to Fig. 4 to show the results of the 3D7+GlcN movie quantification in the context of the Slp+/-GlcN results.

In general, data presentation is clear and readable. The growth defect observed following GlcN treatment (Figure 2C) could be made more clear with data normalization to emphasize that which can be attributed to PfSlp knockdown and not GlcN.

This is a good suggestion and we have reproduced the initial dataset (Fig. 2C, Fig. S6, see below) and normalized the 3D7 multiplication rate, which shows the effect more directly than the growth curves displayed before, for Slp-tagging and GlcN treatment (“3D7 corr.”). We still found Slp +GlcN to be the only condition to have a significant reduction in multiplication rate in the first cycle after treatment (24-72hpi) with respect to 3D7 control as well as the normalized 3D7 value (“3D7 corr”).

Line 276 - Why is nuclear tubulin homeostasis more relevant for closed mitosis? This is difficult to understand. It should be phrased differently or provided with additional explanation.

We thank the reviewer for the comment and agree that this is poorly formulated. We were meaning to express that in e.g. mammalian organisms the nuclear envelope gets disassembled during mitosis and thereby removes the need to regulate import of tubulin into the nucleus for spindle assembly. This is a self-evident statement and has been removed for clarity.

Line 316 - "were" should be "was"

Has been corrected.

The identity, source, and dilution for each antibody must be reported for each use in the methods.

We noticed that we had not fully referenced Table S3, where we listed all used antibodies and dilutions, which we have now done throughout the methods section.

Reviewer #2 (Significance (Required)):

The mechanisms by which intranuclear microtubule dynamics are regulated by Plasmodium falciparum parasites are not well understood. Furthermore, the proteins that are present near the centriolar plaque remain mostly unknown. Understanding the role of the Plasmodium centriolar plaque and its members is critical to describing these dynamics and contributes to our growing understanding of schizogony, an atypical mode of cell division mode with several rounds of nuclear division lacking cytokinesis. Therefore, the identification and initial characterization of PfSlp1 is useful for malaria parasite cell division community.

__

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

The work by Wenz and Simon approaches the function of a novel component of the malaria parasite centriolar plaque, a structure whose complexity has begun to be unraveled only recently__, greatly by the same group. __The authors identify a homolog of Sfi1, a centrin binding protein highly conserved in eukaryotes. Sfi1 homologues usually co-localize with centrioles.

As a tool to characterize its function, the authors uses a conditional knock down strategy, based on GlcN addition, to downregulate PfSfi1-like protein (PfSlp). The authors analyze the impact of pfSlp downregulation on cell division progression, and go on detailly characterizing the progression of mitotic nuclear division. In sum the study finds that expression of Slp1 is required for proper progression of cell division in Plasmodium parasites.

The study is well conducted, and the manuscript clearly written. In general terms I found the data shown to support the author's claims. However, I do have a few points of concern to raise, particularly pertaining overinterpretation of the data, and points that need clarification before the manuscript is fit for publication. In particular the authors should explain more clearly how the data based on fluorescence intensity quantifications was acquired and processed, and how this information is intertwined with the expected kinetics of structures measured, along the cell cycle.

We appreciate the positive feedback and the constructive comments made by the reviewer and now adapted our interpretation of the data or provide additional experimental data to strengthen our argumentation as outlined below. Further we have added some detail to the description of our experimental approaches in the methods section.

I outline below major and minor points that require attention,

Major Points

The manuscript stems off the premise that PfSlp interacts with PfCen1. Despite the fact that Sfi1 is a known interactor of centrin, that the identified protein in Plasmodium has centrin binding motifs, and these proteins co-localize, the support for the direct interaction between the two proteins is based solely on the IP/MS result. No reciprocal IP results are shown.

We thank the reviewer for the suggestion and have now added the reciprocal co-IP, which shows a specific interaction between PfSlp and centrin without need for cross-linking (Fig. S3, see also reply to comment 1 by reviewer 2).

Line 118 specifies that co-localization of Slp-GFP with centrin "corroborates their direct interaction." Co-localization most certainly does not show direct interaction. In addition, Figure 1D shows co-localization with Cen3, not with Cen1, which was the only protein shown to have a physical interaction with Slp via immunoprecipitation. Hence, the claim is unplaced and this section should be reworded for clarity.

The reviewer is correct to point out that co-localization even at STED nanoscale resolution does not demonstrate interaction. We have reworded this statement. Cen3 was the only other specific protein found in the Cen1 immunoprecipitation (Table S1) and the interaction between the four centrins Cen1-4 was shown in an earlier study in P. berghei (Rogues et al. 2019). However, as the Reviewer 2 also indicated, we did not clearly communicate what the targets of our centrin antibody are. We, indeed used an antibody raised against PfCen3. Due to the very high sequence identity between centrins it is, however, unrealistic to exclude cross-reactivity between centrins for a polyclonal antibody (as explained in more detail in our response to Reviewer 2). We have added an explanatory statement in the main text (lines 132ff). Our recent finding that GFP-tagged PfCen1-4 all colocalize at the same position in the centriolar plaque (Voss et al. biorxiv, /10.1101/2022.07.26.501452) and our previously published study of the centriolar plaque (Simon et al. 2021) gives us additional confidence that the antibody specifically labels the compartment of interest.

I was surprised to see how little recovery of PfCen1-GFP the authors obtained from their IP experiments. Whilst I understand that a western blot is not quantitative, I wonder, were the amounts of protein loaded onto each lane normalized for comparative purposes in any way? Please comment on this at least in the figure legend so the reader can gage whether the little PfCen1-GFP recovery was a consequence of the IP experiment, or whether the WB is not representative of the actual IP results but rather show a fraction of the recovered material.

We did not determine the total protein concentration (by e.g. Bradford assay) and therefore did not normalize for protein amounts per lane. Instead, we determined the number of infected red blood cells per ml before Saponin-lysis of the red blood cells and loaded protein lysate equivalent to 1 x 107 cells per lane. We now explain this more clearly in the legend for Fig. S1. During the IP, much of the total protein amount might got lost during the washing steps, which might explain the weak Centrin1-GFP band and the absence of a protein signal in the eluate lane by Ponceau staining (neither a signal for Centrin1-GFP nor unspecific protein signal in the Ponceau). We would conclude that the WB, or at least the lane with the eluate, shows a fraction of the recovered material.

If the WB is indeed representative of the actual PfCen1-GFP recovery rates, I suggest you discuss the possible outcomes of having pulled down so little from the total cell lysate - could it be that the recovered proteins are representative of interactions happening only for a subset of soluble PfCen1 molecules? Can the little protein recovery be explained by Cen1 interactions with insoluble cell components such as the cytoskeleton?

As described above, the eluate lane does likely not represent the actual amount of Cen1-GFP that was pulled down and therefore the WB is not representative of the PfCentrin1-GFP recovery rates. Based on our previous studies we are not aware of any cellular PfCen1 pool beside the cytoplasm and the centriolar plaque. Although they might be below the detection limit. The reviewer raises an interesting hypothesis but we don’t have sufficient data to assume an association with the cytoskeleton and verifying this would require extended further studies.

Were other IP conditions tested? Were the same results obtained?

We carried out three PfCen1-GFP IPs. Once without cross-linking as shown in the study and twice with cross-linking. The two IPs with crosslinking had different amounts of targets identified (24 vs 162). While we did not detect PfSlp in the one with the low number of peptides we detected PfSlp in the second IP. In both IPs we additionally detected PfCen2 and PfCen3.

Do you get the same interactors if the IP is done using anti-Centrin instead of anti-GFP?

We did not test an anti-Centrin antibody for IPs as the protocol from the Brochet group was optimized for the highly specific bead-coupled anti-GFP antibody.

Please define how you identified "specific hits." This is, please describe your criteria for determining "specificity." Was it an all or nothing selection approach? Are Cen1, Cen3 and PfSlp significantly enriched? And if so, how did you define "enriched for" in the context of your experiment?

We thank the reviewer for given us the chance to clarify our candidate selection. We specifically selected the Cen1-GFP IP targets without cross-linking since it produced a short list of hits detected by mass spectrometry. We used an all or nothing approach in that we subtracted from that list any protein that was ever identified in a GFP control IP analysis by the Brochet lab using the same protocol (Balestra et al. 2021). This left only three proteins Cen1, Cen3, and Slp, as our “specific” hits. We have modified the text to explain our selection criteria more explicitly (lines 112ff) while avoid using the term “enrichment” since this is an all or nothing selection.

I'm not at all suggesting here that you repeat this experiment. I understand that the focus of the manuscript is the description of PfSlp, and this stands regardless of the IP results. However, I suggest you include a lengthier discussion of the results shown in SFig1 and Fig1, and the limitations of the approach.

We appreciate the assessment by the reviewer that the focus of the manuscript is otherwise and acknowledge that this is not an extensive analysis of PfCen1 interaction partners. We have, as requested, added a comment addressing this limitation in the discussion (lines 331ff).

Line 123 mentions that Cen3 and Slp1 are recruited together only because they co-localize in most cells showcasing hemi-spindles. Please simply keep "simultaneously" here, as this is the only thing you can conclude from your quantification data. Being recruited "together" implicitly means by "the same mechanism", which is not shown by your data.

We agree that simultaneously is more accurate and we have modified the text (line 146).

Please specify which statistical test was used for determining significance in Figure S4, and what *** refers to in this case. It is hard to judge really how different these data sets are in light of the overlapping error bars. Also, what is quantified here? Integrated density from an immunofluorescence assay? How are the data normalized to be comparable? How many replicates did you quantify? Or are the data shown representative of a single experiment? I could not find these details in the M&M section or the figure legend.

We have revisited all figure legends and consistently defining the p-value and number of replicates (usually N=3) and briefly explain the measurement. Further we have extended the methods section to make our image quantification approach clearer.

Also, on the interpretation of these data; If Slp1 causes a delay in cell cycle progression, and taking into account that the fluorescence intensity of Slp1 varies along the cell cycle, with Slp1 intensity increasing as cell cycle progresses from the ring stages onwards, are these comparable measurements? In other words, are you selecting the same stages whereby the same Slp1 intensities at the centriolar plaque would be expected?

If I understand correctly these measurements are carried out at 55hs post GlcN addition (when the growth phenotype starts evidencing itself?). At this time point, the relative abundance of ring and trophozoite stages (stages at which Slp1 is not expected to be detectable at the CP) is considerable higher than that of the control condition, hence a reduction in Slp1 is expected, and a mechanistic claim about recruitment or stability would be incorrect. Please clarify.

As the reviewer correctly points out it is important to normalize for the stages when quantifying the PfSlp intensities. To achieve this, we only selected schizont stage parasites with a similar distribution of cells containing 3-10 nuclei between the conditions to ensure we are looking at comparable stages. We then quantified the integrated density at each individual centriolar plaque, designated by the presence of a centrin signal. Outside of centriolar plaques no PfSlp signal can be detected. As for ring and trophozoites stages, they do not have a discernable centriolar plaque, or at least not with the markers available in the field, and likely do not express PfSlp based on published transcriptomics data (Plasmodb.org). We have revisited the text to make our quantification strategy clearer (line 170, 621ff).

To understand the relative contribution of Slp1 to the growth delay phenotype, please include 3D7+GlcN control in the quantification of stages shown in Fig. S5. Please check how the data shown in Fig S5 was normalized; the 49 and 73hs bars in the -GlcN condition exceed 100%.

As indicated in our reply to Reviewer 2 we only included this data from our initial exploratory analyses and since it was not central to our argumentation, we chose to add it as supplemental figure. After producing further data, we came to realize that the classical morphological characterization using Giemsa-staining partly mispresents the relevant transition from the pre-mitotic to mitotic stages as the onset of first spindle formation and DNA replication can’t be detected. Previous studies have also indicated that parasites which were drug-arrested at the trophozoite to schizont transition were morphologically similar to mid- to late schizonts (Naughton and Bell, 2007). In a context that investigates nuclear division phenotypes we feel that this analysis might rather be misleading and that the provided growth assays, DNA replication quantification, and time lapse movies are significantly more informative. Therefore, we have decided to remove the figure altogether. However, we have moved Fig. S7 to Fig. 4 to show the results of the 3D7+GlcN movie quantification in the context of the Slp+/-GlcN results.

What is "centrin signal" shown in Figure 2B? Centrin1? Centrin 3? Please clarify which centrin protein you are referring to throughout the manuscript, or provide evidence that they could be interchangeably used for localization and intensity measurement experiments.

We thank the reviewer for pointing out this vagueness. As explained above in the second major point and in the reply to reviewer 2 we use the term “centrin” to emphasize that we cannot be certain to which degree PfCen1,2,3 or 4 contribute to the signal. Our recent preprint (Voß et al. 2022) and Roques et al. 2019 and Simon et al. 2021 however suggest that all centrins co-localize and interact at the outer centriolar plaque. As mentioned we now discuss this in the text (lines 130ff).

Line 149 outlines that Slp1 and centrin intensities are simultaneously reduced, and that this fact alone "affirms" they are part of one complex, and that this implies that Spl1 is somehow involved in centrin recruitment. This claim is not supported by the data shown. There are multiple possible explanations as to how the intensities of both proteins could simultaneously decrease without them conforming the same structure, the same complex or even directly interacting. For example, if the centriolar plaque homeostasis is altered, or the "intensities" are simultaneously dependent on cell cycle progression, they will both be affected without necessarily ever interacting. In fact, if the centrin intensity monitored is that of Cen3, a direct interaction between Slp1 and Cen3 is not demonstrated at any time. At best, the authors could argue that both proteins are directly interacting with Cen1. Again, even this is no definitive proof that they form the same complex.

The reviewer is correct to point out that there are multiple explanations for the decrease of centrin and Slp signal and we have phrased some of the relevant statements more carefully (lines 138, 146, 172). We, however, think that our new reciprocal co-IP data (Fig. S3) in combination with the already provided evidence now significantly strengthens our claim about the interaction between centrin and Slp.

Measurements of DNA content, shown in Figure 2D, show that +GlcN Slp1 knockdown parasites exhibited reduced DNA amounts at 42hs post induction. These results are interpreted as "defects in nuclear division," however, 1. Nuclear division is not analyzed directly, but rather approximated by measuring DNA content. 2. Even in the presence of perfectly normal nuclear division, the DNA content reduction for these parasites at this time point is expected, as cell cycle progression is affected.

Line 160 states that a reduction in merozoite number corroborates a defect in nuclear division. However, the data shown only quantifies merozoites per schizont. As mentioned above, nuclear division is not directly assayed.

We thank the reviewer for emphasizing this important distinction (alongside Reviewer 1). Making the conclusion about nuclear division based on the reduced number of merozoites was premature and we now phrased this more carefully (line 198). Even our data showing inhibition of spindle extension (Fig. 4A-B), although being a strong indicator, do not strictly speaking observe nuclear division. Hence, we have added time-lapse imaging data of nuclear number in KD vs control conditions using the quantitative live cell DNA dye 5-SiR-Hoechst (Fig. 4C. Mov. 4-5). These data now clearly show that the nuclear division or M-phase is affected, while the increase of DNA signal, which represents replication, is not distinguishable from the control. This confirms that nuclear division is the initial and relevant phenotype.

What the nuclear division defects observed are is unclear. Is there fusion, fission? loss of nuclear content? defects in mitosis completion? defects in DNA replication? A reduction in merozoites per schizont, with a concomitant reduction in overall DNA levels could also be explained by a general arrest in the final stages of division. Do other processes linked to nuclear division progress normally? For example, is there daughter cell formation during schizogony without the expected accompanying nuclear division? Are daughters forming in the correct number and position? Are there more daughter cells than nuclei? Or are parasites dying before completing schizogony and producing merozoites? These possibilities need to be carefully teased out before a nuclear division defect can be assigned as the sole causing factor of the division phenotypes observed.

These are all very pertinent questions some of which go beyond the scope of this very first characterization of PfSlp function but we are keen to include those in our future analysis. Some of them we can answer while I will try to offer an interpretation for the remaining ones:

It isn’t fully clear to us what is meant by “Is there fusion, fission”. We will assume that the reviewer refers to the process of karyofission where the nuclear membrane is constricted and fused between the segregating chromatin masses. The field is still lacking a nuclear membrane marker, which makes a direct analysis of this question difficult. Under normal circumstances it has been demonstrated that mitosis is fully closed and the nuclei are completely surrounded by membrane right after division (Klaus et al. 2021). To maybe clarify further we use the term nuclear division to designate the formation of two physically distinct nuclei from one progenitor. We can’t and don’t comment on the integrity of the nuclear membrane and if we had to speculate, it is probably not affected.

Our new data on DNA dynamics (Fig. 4C) shows a delay in nuclear division while DNA replication seems unaffected in the early division stages. The failure to complete mitosis is also shown by the lack of proper spindle extension. It is possible that PfSlp KD affects final stages of division, but since we treat parasites at ring stages and detect a strong phenotype already at the very first division which occurs only a couple of hours after centrin/Slp recruitment one must assume that this is the defining phenotype, which likely has repercussion on later rounds of division. This makes it virtually impossible to clearly define late phenotypes. We actually have to assume that parasites that proceed to later stages of division do so because PfSlp KD was less efficient.

Our data directly shows that more than half of our PfSlp KD parasites “fail to properly divide their nucleus” in the first round of mitosis and therefore can’t construe any other way than to designate this as a “nuclear division phenotype”. We purposefully don’t comment on potential later phenotypes and an impact on cytokinesis (budding) but look forward to investigating this in the future.

Minor Points

• Line 49: consider "...mechanisms remain unclear" instead of "... mechanisms are remaining unclear"

We have corrected this sentence as suggested.

• Readers not familiar with Plasmodium cell division would benefit from having the different stages shown schematically in Figure 1A labeled (ring, merozoite, trophozoite, etc.)

Good suggestion. We have expanded the labeling in Fig. 1A, but still choose to focus on the division stage, which is relevant for the presented data.

• Figure 1 legend: Please specify that "centrin" staining is approximated by centrin 3 specifically. Figure 1E is missing a legend in Figure 1's legend.

Thank you for pointing this out. We have expanded the figure legend accordingly.

• To ease the reader's interpretation of the data, please consider using a different color for 3D7 +GlcN in the plots shown in Figure 2. It is difficult to distinguish the light magenta from the red color at first glance, especially when the lines are partially overlapping.

We explored many different color combinations and consulted with several colleagues and concluded that the chosen color combination is most suitable to convey the logic of the strains (while accounting for green-red blindness).

• Please clarify how long after GlcN addition are phenotypes assessed - ex. Microtubule cumulative length measurements shown in Figure 3.

We mentioned in the previous Fig. 2 that we add GlcN at the ring stage preceding the schizont stage we analyze but failed to specify that we consistently do so for all experiments. We have added more information in the results (line 221) and to the methods section in more detail.

• For Figure 3C please provide a separate image for the Slp channel alone. The overlay of the green centrin signal and the magenta from the tubulin staining render a yellow signal. It is difficult to appreciate the level of Slp knockdown in these cells. Moreover, in the inset, the label "zoom in" is on top of the centrin signal in green, precluding the proper assessment/observation of any yellow signal left over.

Thank you for this remark. We have removed the centrin signal, which is clearly shown in the main panel, from the zoom ins to render the residual PfSlp signal clearly visible.

• When describing Sf1 in T. gondii, please also cite PMID: 36009009 PMCID: PMC9406199 DOI: 10.3390/biom12081115

When submitting our manuscript this study was not yet published, but we are happy to now include it in the introduction (line 92).

The notion of "checkpoint" is mentioned in the introduction and revisited in the discussion. This is a topic under current discussion/evaluation in the field. As mentioned by the authors, demonstration of a checkpoint implies demonstrating reversibility of the putative checkpoint. Though the authors do not make claims about Slp1 or the phenotypes observed activating a specific checkpoint, the manuscript could be further strengthened if the authors showed that the anaphase arrest is reversible upon wash out of GlcN and restored levels of PfSlp expression. I'm including this comment as a "minor points" because it is a only suggestion. I understand that carrying out these experiments is not within the scope of this work. However, if the authors decided to pursue this, it would certainly strengthen the manuscript.

We highly appreciate the suggestion made by the reviewer and already considered ways to inactivate the putative spindle assembly checkpoint or reverse the phenotype. Wash out of GlcN would theoretically be an option although we are unsure that the kinetics of the subsequent protein synthesis would unfold on a short enough time scale. As suggested by Reviewer 2 we try to remain cautious about directly addressing the checkpoint issue, since e.g. PfSlp due to its localization can’t be a direct component of the checkpoint itself. The mention of “checkpoints” has also been removed from the introduction. We are, however, excited that using our time lapse microscopy protocols there now is a framework to investigate this in more depth in the future.

Reviewer #3 (Significance (Required)):

Plasmodium species lack centrioles, and display a divergent mitosis. It is therefore of interest and relevance to understand the peculiarities of the centriolar plaque, as it likely underlies the ability of Plasmodium to upscale its numbers.

Our molecular understanding of the underpinning factors controlling nuclear and cell division in Plasmodium is limited to a few recent publications. The data presented herein is novel and contributes to the body of work with molecular insight and high resolution microscopy coming on for the malaria field.

My expertise is in cell division in Apicomplexan parasites

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Referee #2

Evidence, reproducibility and clarity

This manuscript reported the CryoEM ring-like structure of the full-length human E3 assembly ligase UBR5, showing its assembly into a tetramer. The authors identified critical determinants for antiparallel homodimer and tetrameric assembly. They further described AKIRIN2 as UBR5 substrate and provided evidences of a preferential interaction and activity of UBR5 towards monoubiquitinated proteins. Based on these findings, they proposed UBR5 as chain-elongating E3 ligase.

CryoEM data are solid, and the model interpretation of the tetrameric structure provides a precise description of the domain composition of the protein that well fit with biochemical data. Additional experiments are suggested to corroborate few statements of the authors.<br /> We believe they are realistic in terms of time and resource.

1. Authors should address the importance of tetramerization by mutating SBB2 at the tetramerization interface and comparing the mutant with wild type in mass photometry and ubiquitination assays. In silico analysis of the interaction interfaces (e.g by using PISA software) could be useful to select amino acids to be mutated. The authors suggested a role for oligomerization in catalysis and mutants are needed in order to define the real "functional unit" of the enzyme.
2. The authors used sucrose gradient sedimentation assay to prove UBR5 and substrate interaction (Fig. 3). Control experiment that showed UBR5 protein sedimentation in presence of GFP only is instead in Supplementary Fig. 3D. Unfortunately, in that panel the signal of UBR5 is not visible. Main figure should be revised showing proper controls of the experiment.
3. The authors need to better clarify the features of the AKIRIN-UBR5 interaction. According to the data, the enzyme is equally active on both AKIRIN-Ub and Securin-Ub, suggesting a Ub-specific engagement. What would be a correct explanation of these results? Is the UBA domain directly involved in this process? Testing the activity of a UBA-impaired mutant should help to solve this issue.
4. The authors identified a 25 aa sequence, called Plug loop, preceding the HECT domain. In the structure it is inserted between N and C-lobe subdomains of the HECT and appears to lock the enzyme in an open L-conformation. These structural findings are interesting, but no supported by experimental data. Which is the effect of the Plug loop deletion in a ubiquitination assay? Without further validation the last chapter of the results remains purely speculative and may better fit in the discussion.
5. The datasets are clearly affected by preferential orientation as showed by the angular distribution and 2D classes (reason why the authors correctly performed data collection with tilt). A comment on this is required in the experimental section. In addition, it is not clear whether the presented maps (Fig 1 and 2) derive from merging of the two datasets or only the model has been built using the two different datasets.
6. As a general comment, authors should enlarge panels in which structural details are described, highlighting the side chain residues involved in binding interfaces. Fig. 5 and Fig. 6 are particularly small and incomplete. Most of the structural figures miss key labels needed for a proper understanding. E.g. among the others, numbering of the helix composing the armadillo domain.
7. The overall organization of the figures is quite confusing. Pag. 7 Figure 2C should represent a "box stabilized by three zinc ions mediated by two histidine and seven cysteine residues" according to text citation, but none of these details is highlighted in the corresponding figure. The eye in Figure 1,2,4 does not mean much if a proper box is not linked to the actual site to be seen. In addition, arrows indicating the rotation axis is hard to interpret. Few panels miss the legend. Figure 1A and many other panels miss the reference in the text. More details below.

Additional points:

• Mass Photometry data need additional comments and labels. Please comment on the MP concentration used to analyze the samples. Being a dynamic system, you are probably seeing an equilibrium of species at 10 nM in MP. For better completeness of MP figures, labels that includes counts, % of species and sigma should be added to the nice representation of oligomers. Which condition/fraction represent the MP data showed in 1B?
• If Alphafold models are mentioned and used for model building, it would be nice to provide at least a pLDDTscore and ptm score. Since some details of the AF model are described in the text, an additional superposition of the AF model with the final model derived by EM would be useful to the community.
• A simple workflow describing the cryoEM data processing that includes how many particles have been used in each step is required, at least in the methods section. The authors need to show the cryoEM 2D classes of the dimer as well.
• Please add the domain boundaries in Figure 1A and highlight the domains on the alignment included in Supplemental Table 1.
• Pag. 8 please decide which abbreviation to use, either UBR or Ubr.
• Page 8, line 192. I found annoying to find the same sentence used by competitors who posted a bioRxiv paper 3 days before the one we are reviewing (doi.org/10.1101/2022.10.31.514604 page 4, line 135).
• In supp. 1C legend, "high concentration of NaCl" is a bit vague
• Complementary to Supp Fig 2A, a zoom in of the density map with traced model would be beneficial to show the actual map quality obtained.
• Pag. 6 lines 133-134, the helix residues involved in homodimerization are cited in the text, but not highlighted in the Figure 1.
• Figure 1 legend, panels H-I-J description are missing.
• Figure 3, panel B, meaning of the asterisk is not reported in the figure legend.
• Figure 4, 5 panels from A to E are cited in the text while figure reported only 4.

Referees cross-commenting

I think all the reviews are fairly consistent and agree with the comments raised by my colleagues with the one exception of Point 3 of Reviewer 1. The issue is certainly important yet the experiment suggested is not clear. I personally have troubles designing an informative experimental set-up.

Significance

This paper presents the intriguing Cryo-EM structure of the full-length HECT E3 ligase UBR5. As it stands, this work provides evidence of the existence of a tetrameric RING-like conformation that could represent the functional unit of the catalysis. Very little validation of the features identified in the Cryo-EM structure is given, thus the paper remains quite descriptive, but in any case interesting and informative for the ubiquitin field.

Considering that UBR5 is a quite competitive subject in these days (e.g. at least one additional Cryo-EM structure was posted in BioRxiv, doi.org/10.1101/2022.10.31.514604), I would positively consider this manuscript for publication if the authors reply in full to the issues raised.

My field of expertise: Ubiquitin regulation and interactions, biochemistry, biophysics and Cryo-EM.

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Reply to the reviewers

1. General Statements [optional]

We would like to thank the reviewers for taking time in reviewing and commenting on our paper. The comments were very constructive and conscientious, thanks to their expertise in the field. These comments and the revisions would surely make this paper a better and more robust finding in the field.

The comments were about clearer explanations, increasing the quality of the data and additional experiments for a stronger conclusion, all of which we are eager to accomplish. Now we have sorted out the problems and planned the experiments required in the revision, as detailed below.

2. Description of the planned revisions

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

Summary In this manuscript, Komori et al. examined the role of the LRRK2 substrate and regulator Rab29 in the lysosomal stress response. Briefly, in chloroquine (CQ)-treated HEK293 cells the authors observed an apparent LRRK2-independent increased in Rab29 phosphorylation which was accompanied by translocation of Rab29 to lysosomes. Intriguingly, the authors detected a similar increase in Rab29 phosphorylation when Rab29 was tethered to lysosomes in the absence of CQ treatment. Using mass spectrometry, mutagenesis and a phospho-specific anti-body, the authors mapped the CQ-induced phosphorylation site to S185 and demonstrated its independence from LRRK2. Next, the authors found that PKCa was the kinase responsible for S185 phosphorylation and lysosomal translocation of Rab29. Lastly, the authors showed that in addition to PKCa the lysosomal translocation of Rab29 was also regulated by LRRK2. Overall, Komori and colleagues provide interesting new insights into the phosphorylation-dependent regulation of Rab29. However, there are. Number of technical and conception concerns which should be addressed.

Major points 1) Figure 1F: the localization of Rab29 to lysosomes is not convincing at all. The authors should either provide more representative image examples or image the cells at a higher resolution. The authors should also confirm the CQ-induced lysosomal localization of Rab29 in a different cell type (e.g., HEK293).

We will replace Fig 1F pictures with slightly more magnified images with higher resolution. We will also include additional cell types (HEK293, and other cells that are predicted to express endogenous Rab29); Reviewer #2 also raised this point (see Reviewer #2 comment on Significance).

Moreover, the authors should show that prenylation of Rab29 is required for its CQ-induced phosphorylation.

We will test the effect of lovastatin, a HMG-CoA reductase inhibitor that causes the depletion of the prenylation precursor geranylgeranyl diphosphate from cells (Binnington et al., Glycobiology 2016, Gomez et al, J Cell Biol 2019), or 3-PEHPC, a GGTase II specific inhibitor that also causes the inhibition of Rab prenylation (Coxon FP et al, Bone 2005).

2) The rapalog-induced increase in Rab29 phosphorylation in Figure 2D is not convincing since there is at least 2-3-fold more Rab29 in FRB-LAMP1 expressing cells compared to their FRB-FIS1 counterparts. An independent loading control is also missing. This is a key experiment and should be properly controlled and quantified. In addition, can CQ treatment drive 2xFKBP GFP-Rab29 from mitochondria to lysosomes (in the presence of rapalog and FRB-Fis1)?

We will carefully examine another round of rapalog-induced phosphorylation of Rab29, with an independent loading control such as alpha-tubulin. The immunoblot analysis will be made against the intensity of non-p-Rab29. The response to the latter question was described in the section 4 below.

3) Figure 4A-C: Are these stable Rab29 expressing cells? If not, the quantification of "the size of largest lysosome in EACH cell" becomes very problematic. This analysis should be repeated with stable Rab29 variant cells in a background lacking endogenous Rab29. Furthermore, the LAMP1 signal is too dim to see any convincing colocalization (e.g., with WT) or the lack thereof (e.g., in the case of S185D).

The cells shown in Figure 4 are HEK293 cells transiently expressing Rab29, and the issue of quantification was described in the section 3 below. We agree that the signal of LAMP1 was dim, and it turned out that the confocal microscope we used had problems with the sensitivity of the red channels. We will be taking another round of these images with a new confocal microscope.

Lastly, the authors should corroborate their findings with an ultrastructural analysis since the electron microscopy would definitively be more suitable for this type of measurements.

We are planning to obtain electron microscopic images, according to this reviewer’s request. We plan to invite an expert in electron microscopy analysis as a co-author.

4) The lysosomal colocalization of Rab29 in Figure 5C is again not convincing. This analysis needs to be repeated with high resolution imaging.

Again, we will repeat this experiment with a new confocal microscope, with the hope that it would yield better images.

5) The authors need to show the level of LRRK2 depletion (Figure 6). Given the role of LRRK2 in driving lysosomal Rab29 translocation, the importance of the LRRK2 independent pS185 for this process remains unclear.

We will add the level of LRRK2 on its knockdown; we have experienced that LRRK2 knockdown usually occurs with more than 50% efficiency every time. The response to the latter comment was described in the section 3 below.

6) In general, the authors employ an alternative, biochemical assay (e.g., LysoIP) for the lysosomal translocation of Rab29. This would in particular help to clarify the effect of the Rab29 variants and LRRK2 inhibition.

We have previously shown that the overexpressed Rab29 (and LRRK2) is enriched in the lysosomal fraction from CQ-treated cells, which was performed using dextran-coated magnetite (Eguchi et al, PNAS 2018). Using the same biochemical method, we will show the enrichment of endogenous Rab29 in the lysosomal fraction.

Minor points

9) Figure 2C is lacking the control IF staining for mitochondria (to which 2xFKBP-GFP-Rab29 is assumed be recruited upon co-expression with FRB-FIS1).

We will stain the cells with MitoTracker to ensure that anchoring away of 2xFKBP-GFP-Rab29 by FRB-Fis1 results in mitochondrial localization.

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

The data in the manuscript convincingly demonstrates that lysosomal overload by Chloroquine treatment induces Rab29 localisation to the lysosomes and that this membrane association is dependent on PKCalpha-dependent phosphorylation at Ser185.

We have a number of rather minor comments listed below:

Figure 2

The increasing levels of non-phosphorylated Rab29 over the indicated time course of AP21967 treatment in Figure 2B are concerning. First, could you provide an explanation for this clear increase in both non-p-Rab29 and p-Rab29 in the phostag but not the normal gel? Second, could all quantifications of p-Rab29 be made relative to the non-p-Rab29?

We will try another round of rapalog-induced phosphorylation of Rab29, with an independent loading control. The immunoblot analysis will be made against the intensity of non-p-Rab29. Reviewer #1 raised a similar concern on Figure 2D.

Figure 5

To further demonstrate that PKCalpha phosphorylates endogenous Rab29 at Ser185, we recommend reperforming the Go3983/PMA treatment in figure B with the anti-p-Ser185 antibody. It may be sufficient to perform the treatment only at 4 or 8 hours, simply to provide stronger evidence regarding the phosphorylation of endogenous Rab29.

We will give a try, although the anti-phosphorylated protein antibodies that we tried never worked for phos-tag SDS-PAGE. With the conventional western blot, we will be able to try this experiment.

It is not clear whether the activity of PMA in the assay is due to inhibition of PKCalpha. Are the effects ablated by PKCalpha KD

We will test the knockdown of PKCalpha, beta, gamma and delta by siRNAs to further narrow down the effects of PKC-dependent phosphorylation of Rab29.

Reviewer #2 (Significance (Required)):

These cell biology findings are important in the field as both Rab29 and LRRK2 are implicated in the pathogenesis of Parkinson disease. The phosphorilation of Ser185 of Rab29 by PKCalpha is novel and contributes to our understanding of Rab29 and LKRR2 regulation. One limitation of the study is that is conducted in only two cell types quite unrelated to the disease, so how general and disease relevant are the findings it is not clear. Most of the data are solid. There are two experiments whose results are difficult to interpret and a few controls missing. Also a few issues with quantifications, all of which is described in details above and will need to be fixed prior to publication. My expertise for this paper is in the cell biology of lysosomal function.

The issue that only two cell types were analyzed was also raised by reviewer #1, so we will examine additional cell types, especially those that are predicted to express endogenous Rab29. Our responses to other issues raised are described elsewhere. Thank you for these insightful comments.

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

Figure 4A-C: Are these stable Rab29 expressing cells? If not, the quantification of "the size of largest lysosome in EACH cell" becomes very problematic. This analysis should be repeated with stable Rab29 variant cells in a background lacking endogenous Rab29. (Reviewer #1)

As described in the section 2 above, the cells shown in Figure 4 are HEK293 cells transiently expressing Rab29. We are sorry that the description “the size of largest lysosome in each cell” was misleading. As we analyzed only cells overexpressing GFP-Rab29 that were marked with GFP fluorescence, we believe that transient expression should not be a problem. To avoid any misunderstandings, we have described in Figure 4 legends that only lysosomes in Rab29-positive cells (and all cells expressing Rab29) were included in the analysis of the largest lysosome of each cell.

Regarding the effect of endogenous Rab29 in Figure 4 experiments, Reviewer #2 similarly raised the issue on whether Rab29 phosphomimetics are acting as dominant active, preventing lysosomal enlargement. On this point, we have previously reported that knockdown of endogenous Rab29 causes the enhancement of lysosomal enlargement upon CQ treatment (Figure 5I,J of Eguchi et al, PNAS 2018), suggesting that the lysosome-deflating effect by phosphomimetics is a dominant active effect rather than dominant negative suppressing endogenous Rab29. This point is considered significant, and thus has been explained in the results section (page 7, lines 168-171).

Along similar lines: why not all cells in Figure 5E and Figure 5G show Rab29- and LRRK2-positive structures? How do the authors know which of these phenotypes is the prevalent one? (Reviewer #1)

As for the ratio of cells with Rab29- and LRRK2-positive structures, it seems reasonable given that different cells have different levels of exposure to lysosomal stress and that the response is transient and does not occur simultaneously. The ratio of these positive cells may also vary depending on the cell culture conditions. Since Rab29- and LRRK2-positive structures are rarely seen in control cells, we think this would be a meaningful phenotype even if only 20-30% of cells show such structures. The result that the ratio of localization changes is not 100% is now noted in the results section explaining Figure 1G (page 4-5, lines 108-110) where the immunocytochemical data first appears.

Given the role of LRRK2 in driving lysosomal Rab29 translocation, the importance of the LRRK2 independent pS185 for this process remains unclear. (Reviewer #1)

Our data suggested that Rab29 is stabilized on lysosomes only when LRRK2-mediated phosphorylation and S185 phosphorylation both occur on Rab29 molecule (as shown in Figure 7 scheme), so we believe there is no contradiction. We have now described more clearly about this notion at the end of the results section (page 9, lines 235-236).

It is not clear what the authors mean by "lysosomal overload stress". Since mature lysosomal incoming pathways such as autophagy or endocytosis are disrupted by CQ, it is difficult to picture an overload. Maybe rephrasing would help to clarify this. (Reviewer #1)

Chloroquine (CQ) is known as a lysosomotropic agent that accumulates within acidic organelles due to its cationic and amphiphilic nature, causing lysosome overload and osmotic pressure elevation, and this is what we call “lysosomal overload stress”. The well-known effects of CQ to disrupt lysosomal incoming pathways are ultimately caused by the above consequences. Also, we have previously reported that lysosomal recruitment of LRRK2 is caused by CQ but not by bafilomycin A1, the latter being an inducer of lysosomal pH elevation, or by vacuolin-1 that enlarges lysosomes without inducing lysosomal overload/pH elevation (Eguchi et al, PNAS 2018), and further found that not only CQ but also other lysosomotropic agents commonly induced LRRK2 recruitment (Kuwahara et al, Neurobiol Dis 2020). We thus have described the effect of CQ as “overload”. However, it is true that we have not provided a clear explanation for readers, so we have added some notes for lysosomal overload stress in the introduction section (page 3, lines 69-71).

Which cell type is used for the IF analysis in Figure 2C? This information is in general quite sparse. The authors should clearly state the cell type for each experiment/Figure. (Reviewer #1)

We have added cell type information that was missing in several places in the manuscript. We are very sorry for the inconveniences. For clarification, HEK293 cells were used in Figure 2C.

Are the images in figure 1F representative? i.e. does Rab29 always colocalise to such enlarged lysosomes upon CQ treatment and does CQ treatment always drastically alter the cellular distribution of Rab29? (Reviewer #2)

The images in Figure 1F are representative of when Rab29 is recruited, but it is not seen in all cells, and the ratio of recruitment (~80%) is shown in Figure 1G. Reviewer #1 also asked why Rab29 recruitment is not seen in all cells, and we gave the same answer above. It may be reasonable to speculate that different cells have different levels of exposure to lysosomal stress and that the response is transient and does not occur simultaneously. The ratio of these positive cells may also vary depending on the cell culture conditions. For the readers’ clarity, we have added that the ratio of localization change of Rab29 is not 100% and is comparable to that of LRRK2 previously reported (page 4-5, lines 108-110).

Considering that the "forced localisation technique" induces a non-physiological colocalization of non-endogenous Rab29 to lysosomes, it may be an overestimation to conclude just from these data that phosphorylation of Rab29 occurs on the lysosomal surface. This is also quite in contrast with the later finding that phosphorylation by PKCalpha promotes lysosome localization of Rab29. It seems more reasonable to conclude that Rab29 can be phosphorylated when localised at the lysosomes (as opposed to other organelles such as mitochondria). If the authors feel strongly about this point they might need to find a less non-physiological assay. (Reviewer #2)

Yes, it could be an overestimation, and as we do not have better means to conduct a less non-physiological assay, we have modified the description from “occurred on the lysosomal surface” to “could occur on the lysosomal surface” (page 5, line 112 (subtitle) and line 128).

Regarding the comparison with the later finding that phosphorylation by PKCalpha promotes lysosome localization of Rab29, these data (Figure 2 and 5) could be explained with a single speculation: phosphorylation of Rab29 on lysosomal membranes could retain Rab29 on the membranes for a longer time. It is not easy to decipher which comes first, association with membranes or phosphorylation of Rab29, in a physiological assay, but considering reports that show PKCalpha activation happens on membranes (Prevostel et al., J Cell Sci 2000), at least the data favor our conclusion over the idea of PKCalpha phosphorylating Rab29 in the cytoplasm and then promoting lysosomal localization. This point is now clearly described in the discussion (page 10, lines 248-251).

It is not clear how the Rab29 phosphomimetics are acting as dominant active preventing lysosomal enlargement. Authors should speculate or repeat the experiments in absence of endogenous Rab29 to clarify the matter. (Reviewer #2)

A similar concern about the effect of endogenous Rab29 was also raised by Reviewer #1 (see above). We have previously reported that knockdown of endogenous Rab29 causes the enhancement of lysosomal enlargement upon CQ treatment (Figure 5I,J of Eguchi et al, PNAS 2018), suggesting that the lysosome-deflating effect by phosphomimetics is a dominant active effect rather than dominant negative suppressing endogenous Rab29. This point is considered important and thus has been explained in the results section (page 7, lines 168-171).

Overall, there is some missing information regarding repeats for Western blots, such as those in figure 3C, 3D and 3E. Please add indications about repeats in the figure legend or methods. (Reviewer #2)

We have added the repeat information to each figure legend where it was missing. We are very sorry for the inconveniences.

The model in figure 7 however seems to suggest that Rab29 associates to lysosomal membranes independently, and is then stabilised at the membranes by LRRK2 and PKCalpha - a point which is not directly supported by the data. (Reviewer #2)

As noted earlier, we consider that phosphorylation of Rab29 on lysosomal membranes could retain Rab29 on the membranes for a longer time, given the present data and previous reports that phosphorylation of Rab29 is more likely to happen on the lysosomal membrane than in the cytosol. Also, as inhibition of either of the two phosphorylations ends up in disperse Rab29 localization, we have made this figure as a model of what is plausible right now. This explanation is now added in the discussion (page 10, lines 248-251).

English proofreading should be improved: "CQ was treated to HEK293" (page 4), "As we assumed that this phosphorylation is independent of LRRK2" as an opening line (page 5) (Reviewer #2)

Thank you for pointing out these incorrect wordings. They were corrected.

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

In addition, can CQ treatment drive 2xFKBP GFP-Rab29 from mitochondria to lysosomes (in the presence of rapalog and FRB-Fis1)? (Reviewer #1)

We do not think that a comparison between the affinities of FKBP-rapalog-FRB and Rab29-[unknown factor that directs Rab29 to lysosomes] is necessary, as the former has a Kd in the single digit nM range (Banaszynski et al, JACS 2005), whereas the latter (based on estimations from related PPIs) is estimated to be in the μM range, which shows a much weaker affinity than the former (McGrath et al, Small GTPases 2019). Furthermore, even if Rab29 appears to have migrated from mitochondria to lysosomes as a result of this experiment, one cannot rule out the possibility that a small portion of the mitochondrial membrane was incorporated into the lysosomal membrane that was enlarged by CQ treatment.

Molecular weight markes should be provided for all immunoblot experiments. (Reviewer #1)

The immunoblot pictures without molecular weight markers in our paper are all Phos-tag SDS-PAGE blot analyses. Phos-tag SDS-PAGE results in band shifts of phosphorylated proteins, and writing in markers would be misleading. Moreover, previous representative studies heavily using Phos-tag (e.g., Kinoshita et al, Proteomics 2011, Ito et al, Biochemical Journal 2016) also did not show the molecular weight markers. Here we performed phos-tag SDS-PAGE analysis only to find differences in the phosphorylation state of Rab proteins.

The use of the quantification ratio of cells with Rab29-positive lysosomes in figure 1G might be slightly misleading as it does not allow the reader to understand to what extent Rab29 localisation at lysosomes upon CQ treatment. We recommend using a simpler quantification, such as by measuring the average colocalisation of Rab29 and LAMP1 per cell. (Reviewer #2)

For figure 5D and 5F, As with figure 1G, we recommend using a more straightforward and impartial method of quantification such as simply measuring the colocalisation of Rab29 with LAMP1. (Reviewer #2)

Popular colocalization analyses using Pearson’s or Mander’s coefficients would be a good choice if the amounts of Rab29 varied greatly between lysosomes. However, this may not apply in this case; the amount of Rab29 or LRRK2 on each lysosome is considered to saturate quickly and a relatively low amount of them may not be detected on immunofluorescence observations, whereas the probability of finding these structures has been shown to exhibit a moderate sigmoid curve (as seen in Figure 1E or 2H of Eguchi et al., PNAS 2018). Therefore, the amount of Rab29 or LRRK2 could be approximated to a Bernoulli distribution in terms of colocalization with lysosomes, and this is the reason why we chose to quantify “the ratio of cells with Rab29-positive lysosomes”.

We recommend using a more transparent and simple quantification method, such as average size of lysosomes per cell. (Reviewer #2)

As one can see in the inset of Figure 4B, unenlarged lysosomes are unfortunately too small for the quantification of their size, much less tell two small lysosomes apart in our experimental settings and laboratory resources, so we decided to analyze the largest lysosome in each cell as a representative of the cells to minimize measurement errors. This measurement only includes GFP-Rab29 positive cells, and by comparing against CQ-untreated cells we intended to increase the validity of this analysis. This quantification method was also used in our previous report (Eguchi et al, PNAS 2018).

Author Response

1) Response to the Editor

We thank the Editor and the Reviewers for the kind words, the helpful suggestions, and the points of critique, which have all helped us substantially strengthen the manuscript in this revised version. Regarding the 3 general critiques highlighted by the Editor:

Essential Revisions:

1) Some hypothesis, and in particular the one that all individuals have the same inter-burst interval distribution should be tested/justified/discussed.

(a) We have generalized the theory to directly address this point by relaxing the assumption of an identical inter-burst interval for all individuals. In short: the main insights continue to hold and we discuss the nuances in the text.

(b) Experimentally, the hypothesis that all single fireflies isolated from the group exhibit the same interburst interval (IBI) distribution could not be rigorously tested. The main reason is practical: in order to compare IBI distributions across individuals, we would need to collect a large number of fireflies and track them for long durations, which was not realistic given our experimental setup and the short window of firefly emergence. In addition, external environmental factors might slightly alter behaviors as well, making comparisons even more complex. Thus, due to paucity of field data, we eventually use the assumption that all individual fireflies follow the same IBI distribution.

2) Comparison between the models and the data must be improved, in particular through a quantification of the differences between distributions and sensitivity analysis of the numerical results.

(a) Regarding the comparison of the agent-based simulations with experimental data, in Fig. 7, we compare the underlying distributions using the two-sided Kolgomorov-Smirnov statistical test for goodness-of-fit. These appear to us the most straightforward and informative approaches, without over-fitting.

(b) Regarding sensitivity analysis for the agent-based simulations, for each β value from 0 to 1 we statistically compared simulations to the experimental distributions to find the most well-fitted β.

(c) Finally, owing to experimental constraints leading to sparsity of available data in characterizing the interburst distribution, we strive to strike a delicate balance between sophisticated statistical tools to compare theoretical and simulation distributions (with unrestricted access to large sample sizes) to the finite samples in the empirical distributions. As such, we think it is the apposite to use the first two moments of respective distributions In Fig. 3 to show the striking similarity of trends.

3) More discussion of the modeling in connection to past theoretical results and existing literature is necessary to better contextualize the present work and assess its originality.

We have done this closely following the specific suggestions from reviewers.

2) Revised terminology: removing usage of “model”

Since unintended ambiguity may be caused by use of the word “model”, which could refer to either (1) the theoretical framework, principle of emergent periodicity, and attendant analytic calculation , or (2) the agent-based simulation in the computational realization, we have removed all instances of the word “model” from the results presented in the paper, and replaced by the specific meaning (theory or simulation) in each context.

Similarly, in responding to Reviewers’ comments, we clarify what we understand by their use of the word “model” in each case.

3) Addressing an error in the agent-based simulation code

We (OM and OP) have now addressed an inadvertent unit typo in the agent-based simulation code. The discharging time (Td) before the typo was fixed was set to 10000ms. After the fix, the Td value was correctly set to 100ms. This caused very slow discharges, keeping the voltage high until any beta addition was received, resulting in more frequent bursts than we’d actually expect from the model dynamics. This has been fixed, and in our responses to the reviewers, we address the results of this fix by referring to the “unit typo”. We corrected the panels corresponding to agent-based simulation in Figs. 3 and 5 to reflect the new numerical simulation results, as well as the corresponding sections in the text of the paper.

4) Addressing changes to experimental dataset

We increased the size of our N=1 dataset (N is number of fireflies) to correctly match what was reported in the original text of 10 samples. Additionally, we have added characterization of the size of the datasets for N=5, 10, 15, and 20 fireflies.

5) Response to Reviewer 1

We thank the Reviewer for kind remarks, and the highlights of the strengths of the paper.

Regarding concerns raised, point by point:

Reviewer #1 (Public Review):

Weaknesses:

The work presented here is an excellent start at understanding the collective behavior of this particular species of firefly. However, the model does not apply to other species in which individual males are intrinsically rhythmic. So the model is less general than it may appear at first.

We take the Reviewer’s point well. We have added text to the paper to clearly highlight this point.

The modeling framework is also developed under the very stylized conditions of experiments conducted in a small tent. While that is a natural place to begin, future work should consider the conditions that fireflies encounter in the wild. Swarms that are spread out in space would require a model with a more complicated structure, perhaps with network connectivity and coupling strengths that both change in time as fireflies move around. This is not so much a weakness of the present work as a call to arms for future research.

We agree with the Reviewer that this is an exciting call to arms for future research!

Other comments:

This assumption that all individuals have the same IBI distribution could be directly tested. Has this been done? If not, why not? e.g. Are there difficulties with letting one firefly flash long enough to collect sufficient data to fill out the distribution?

1. We have generalized the theory to directly address this point by relaxing the assumption that all individuals exhibit the same inter-burst interval distribution. In short: the main insights continue to hold and we discuss the nuances in the text.

2. Experimentally, hypothesis that all single fireflies isolated from the group exhibit the same interburst interval (IBI) distribution could not be rigorously tested. The main reason is practical: in order to compare IBI distributions across individuals, we would need to collect a large number of fireflies and track them for long durations, which was not realistic given our experimental setup and the short window of firefly emergence. In addition, external environmental factors might slightly alter behaviors as well, making comparisons even more complex. Thus, due to paucity of field data, we eventually use the assumption that all individual fireflies follow the same IBI distribution.

The derivation given in 6.2.1 is clearer than the approach taken here, which unnecessarily introduces Q, q, and c and then never uses them again.

We agree with the Reviewer and have accordingly revised the manuscript.

We have also implemented the suggested edits in the marked up manuscript. We are grateful for the detailed feedback, which helped us substantially extend results, and improve presentation and clarity.

6) Response to Reviewer 2

We thank the Reviewer for their thorough feedback. We provide point by point responses below.

Reviewer #2 (Public Review):

1) The biological relevance of certain hypotheses is insufficiently discussed. This is important because if the observed behaviour is a universal one, alternative models may explain it as well.

We thank the reviewer for raising this point. The main hypotheses underlying our models are: 1) individual fireflies in isolation flash at random intervals; 2) these random intervals are drawn from the empirical distribution reported (implicitly: all fireflies follow the same distribution); 3) once a firefly flashes, it triggers all others. Hypothesis 1) is directly supported by the data presented. Hypothesis 2) is comprehensively addressed in the revised manuscript, as discussed previously. Hypothesis 3) is central to the proposed principle, and enables intrinsically non-oscillating individuals to oscillate periodically when in a group. The resulting phenomenon has been compared to experimental data and extensively discussed in the manuscript. Further, we have also simulated the effect of changing the strength of coupling between fireflies based on this hypothesis in the revised section on agent-based simulation.

2) Comparison between the models and the data could be improved, in particular through quantification of the differences between distributions and sensitivity analysis of the numerical results.

1. Regarding the comparison of the agent-based simulations with experimental data, in Fig. 7, we compare the underlying distributions using the two-sided Kolgomorov-Smirnov statistical test for goodness-of fit. These appear to us the most straightforward and informative approaches, without over-fitting.

2. Regarding sensitivity analysis for the agent-based simulations, for each β value from 0 to 1 we statistically compared simulations to the experimental distributions to find the most well-fitted β.

3. Finally, owing to experimental constraints leading to sparsity of available data in characterizing the interburst distribution, we strive to strike a delicate balance between sophisticated statistical tools to compare theoretical and simulation distributions (with unrestricted access to large sample sizes) to the finite samples in the empirical distributions. As such, we think it is the apposite to use the first two moments of respective distributions In Fig. 3 to show the striking similarity of trends.

Reviewer #2 (Recommendations for the authors):

A. The assumption that single-firefly spikes obey the same distribution (there is no individual variation in the frequency, or even of the composing number of bursts, of the flash) does not seem to have been verified on the data, that are instead pulled together in one single distribution (Fig. 1D). Moreover, the main feature of such distribution is that it has a minimum at 12 secs (discarding the faster bursts that are not considered in the model) and that it is sufficiently skewed so that it takes a minimal coupling for collective synchrony to emerge. I think that the agreement between the distributions for different N would be more meaningfully discussed having previous work as a reference, whereas now this is relegated to the discussion, so that it is unclear how much of the theoretical results are novel and/or unexpected. Quantification of the distance between distributions would also be interesting: it looks like the two models (analytical and simulations) disagree more among themselves than with the data.

Regarding the hypothesis that all individual fireflies exhibit the same interflash interval, please see our response to Main Point 1. Regarding comparing the analytical theory and numerical simulation analysis, Figs. 3 and 5 have been revised after a unit typo was found in the code (see Section 2). Following the update, the analytical and numerical models agree in (1) the location of the peak in Fig. 3 for all N values, and (2) the peak approaches the minimum of the input distribution as N increases.

B. If I understand correctly, simulations are introduced as a way to get a dependence on the intensity of the coupling (\beta). There are several issues here. First, I do not see how the coupling constant could change in the present experimental setup, where all fireflies presumably see each other (different from when there is vegetation). Second, looking at Fig. 3, the critical coupling strength appears to depend very weakly from N, and it is not clear how the 'detailed comparison' that leads to the fit is realized (in fact, the fitted \betas look larger that those at which the transition occurs in Fig. 3A). I think a sensitivity analysis is needed in order to understand how do results change when \beta is changed, and also what is the effect of the natural Tb distribution (Fig. 2 F). Results of the simulations might be clearer if instead of using the envelope of the experimental results, the authors tried to fit it to a standard distribution (ex. Poisson) so that it can be regularized. This should allow to trace with higher resolution the boundary between asynchronous and synchronous firing.

We have included agent-based numerical simulations as a way to provide a concrete instantiation of the theory principle and analytical results in the preceding section. While the analytic theory results are fitting parameters free, in the agent-based simulations, we introduce an additional fitting parameter, to see what happens when we relax one hypothesis of the analytical theory: the instantaneous triggering of all fireflies upon an initial flasher. Additionally, the agent-based simulations pave the way for future work, allowing for convenient exploration of the connectivity between individuals and analysis of the behavior of individual fireflies. in this context, please note that Fig. 5 has been corrected (see above), leading to a stronger co-dependence of β and N. In addition to the envelopes, we also report the trends in the first empirical moments (mean and STD) for comparison and tracking of the transition to synchrony.

C. More care should be put in explaining what are the initial conditions hypothesized for the different models. For instance, the results of paragraph 3 are understandable if all fireflies are initialized just after firing, something that is only learnt at the end of the paragraph. I also wonder whether initial conditions may be involved with T_bs in the low-coupling region of Fig. 3A not being uniformly distributed, as I would have expected for a desynchronized population.

We have clarified that, indeed, all fireflies are re-initialized after firing. The initial conditions then become a new random vector of interflash intervals. Importantly, we found after receiving the reviews that, due to inconsistent units in our numerical simulation code, Fig. 5 was incorrect. With proper units, the new results show a much more widespread distribution at low coupling, as expected by the Reviewer.

D. I found that equations were hard to understand either because one of the variables was not precisely (or at all) defined, or because some information was missing: Eq. 1: q is not defined Eq. 2: explain what it means: the prob. that others have not flashed times that that one flashes. Also, say explicitly what is the 'corresponding PDF. Eq. 3: the equation for \epsilon(t) to which this is coupled is missing Why introduce \beta_{i,j} and T_bi if they are then taken independent of the indexes? Definitions of collective and group burst interval should be provided. It would be clearer if t_b0 was defined in the first paragraph of the results, so as to clarify as well its relation with T_b. Define T^i_b in the caption of Fig. 3 (they are defined later than the figure is first discussed). The definition of 'the vertical axis label' (maybe find a word for that...) is pretty cumbersome. I could imagine that other definitions would allow the lines in Fig. 3 E to converge to the same line for large betas, which would make more sense, considering that in the strong coupling limit I see no reason why the collective spiking should not be the same for different N (the analytical model could help here).

Thank you for these comments; we have incorporated these and related changes.

E. I think that the author's reading of the two 'dynamical quorum sensing' papers they cite is incorrect: De Monte et al. was not about the Kuramoto model, but the same limit cycle oscillators as in Strogatz; Taylor et al. considers excitable systems, potentially closer to noisy integrate-and-fire, at least in that they do not have self-sustained oscillations. Both papers show that oscillations appear above a certain density threshold, and that the frequency of oscillations increases with density, as found in this work. A more accurate link to previous publications in the field of synchronization theory, including the models by Kurths and colleagues for fireflies, would be useful both in the introduction and in the discussion, and would help the reader to position this work and appreciate its original contributions.

1. Thank you for pointing out an inaccuracy in our literature citations regarding synchronization. We have now made corrections to address this point.

2. While we take the Reviewer’s points well, our theory framework (“model”), building off of the principle of emergent periodicity we propose here, is fundamentally different in the nature of individuals from extant “models”. The reference in question has individuals as oscillators, and the fastest frequency is the frequency of the fastest individual oscillator. In contrast, in our work there is no fastest individual oscillator and the “fastest frequency” has a completely different meaning, since individuals do not have a particular frequency associated with them. In this sense, our work is not inspired by theirs. That said, we have included citations as suggested by the Reviewer.

F. The authors say that part of the data is unpublished. I guess they mean that the whole data set will be published with this manuscript. I think the formulation is ambiguous.

Thank you for this comment. We have now clarified that the data will indeed be published with the manuscript.

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)):

Basier and Nurse revisit the fundamental question of how the rates of RNA and protein synthesis scale with cell size. The strong null hypothesis is that synthesis scales linearly with cell size: cells that are twice as big should make stuff twice as fast. This hypothesis has been tested many times, in many systems, using many approaches over the past century and, in general, the null hypothesis has been sustained. However, there have been many examples of evidence for more complicated synthetic patterns. Whether these results indicate that biosynthesis rates vary across the cell cycle, or in response to other factors, in addition to increasing with cell size, or whether observed deviations from the predictions of the null hypothesis has been due to artifacts of cell synchronization and labeling, is thus an open, interesting and, because biosynthesis rates have critical implications in cellular function and metabolic robustness, important question.

The authors address the question in fission yeast using metabolic pulse labeling with a ribonucleoside or amino acid analog in asynchronous cells and single cell analysis to directly compare incorporation levels with cell size and cell cycle stage. The experiments are well designed, well executed and well controlled. Furthermore, the data is well presented and appropriately interpreted. In particular, the presentation of the size-v.-label data in Figures 2A and D, with the averages and variances in 2B and E and the normalized data in 2C and F are easy understand and interpret. It is thus notable that the size-v.-label data for the longer (cdc22-22) cells is omitted in favor of just the average (2H,J) and normalized (2I,K) data. This size-v.-label data should be added to Figure 2.

We added two panels to the Figure supplementary 2 showing the requested data, the size-v.-global translation (S2E) and size-v.-global transcription (S2F).

The authors should also explicitly state how they chose 15 µm as the inflection point in 2H; 16-17 µm seems like it would give a horizontal plateau, which would better fit their saturation explanation.

This comment relates to the second comment of reviewer 4, see below for the detailed answer.

The authors measure DNA content with a DNA-binding dye, the signal from which should linearly scale with DNA content. However, instead of reporting and analyzing total signal from the DNA-binding dye (or better yet, total signal in the nucleus, which they could do, having segmented the nucleus in their images), they report max signal. Using max signal is complicated because, as cells and thus nuclei increase in size the concentration of DNA and thus the max (but not total) DNA-binding-dye signal in in the nucleus decreases, requiring two-dimensional dye/size analysis (such as shown in Figure 3B) to distinguish G1 and G2 cells. The authors should use the more straight forward measure of total nuclear DNA-binding dye signal, or explicitly explain why they can't or prefer not to do so.

The total fluorescence intensity signal of the DNA-binding dye is noisy because we had to use a low concentration of the dye. This was necessary as it allows a clearer distinction between cells with a one 1C DNA content and cells with a 2C DNA content that higher concentrations did not. The maximum signal per cell-v.-cell length produces distinct populations of cells in G1, or G2/M phase (see Figure 3H, and Figure 4B), and populations identified in this way have the distributions of total fluorescence intensity expected from cells in G1 and G2 or M phase (see Figure 3I and Figure S4D). We added one extra panel to Supplementary Figure 4 showing the distributions of the total fluorescence intensity signal of the DNA-binding dye for the G1, S, and G2 or M populations (S4D) for comparison.

The authors should state in figure legends the strain numbers used for all experiments.

We have modified all the figure legends to include the strain numbers.

They should also cite the source of all the constituent parts (e.g. hENT1, hsvTK, EGFP-pcn1, and synCut3-mCherry) of their strains.

The missing reference for the source of hENT1 and hsvTK (Sivakumar et al. 2004) has been added, the references for EGFP-pcn1 (Meister et al., 2003) and synCut3-mCherry (Patterson et al., 2021) were already present.

CROSS-CONSULTATION COMMENTS My colleagues make constructive points. I agree with all of them, although I am less concerned about the use of cdc2-22 and CCP∆ to alter cell length and cell cycle distribution. Although these mutations alter CDK specific activity (and thus length and distribution) and could alter specific patterns of translation, the fact that they double at normal rates makes it seem unlikely that they could be significantly changing bulk synthesis rates.

Reviewer #1 (Significance (Required)):

As noted above, this work addresses an open, interesting and important question. Moreover it provides useful data in a specific system and a useful example of a general experimental approach to the problem. However, it does not settle the question of how biosynthesis scales with size, even in the specific case of fission yeast. In particular, it shows that protein synthesis plateaus just above normal cell size, whereas RNA synthesis scales up to twice normal cell size. This observation is striking, because there is no obvious mechanism that would (and the authors offer no suggestion of how to) explain how protein synthesis could be limited if RNA synthesis is not. Therefore, the strength of the paper is that it identifies an intriguing phenomena and its limitation is that it does not provide any testable hypotheses to explain that phenomena.

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

Summary: Basier and Nurse investigate how "cell size, the amount of DNA, and cell cycle events affect the global cellular production of proteins and RNA molecules". Both transcription and translation, driving the production of biomass, have been shown to increase as a function of cell size in various systems. However, whilst cell size generally correlates with cell cycle progression there are inconsistent results in the literature if global cellular translation and transcription is affected by cell cycle state. They argue that this might be due to perturbations induced by different synchronisation methods used in the various studies.

Therefore, in this study, to avoid potential perturbation from synchronisation methods, they developed a system that allows to assay unperturbed exponentially growing populations of fission yeast cells. The assay is based on single-(fixed)cell measurements of cell size, cell cycle stage, and the levels of global cellular translation and transcription. This allows them to correlate cell cycle state, cell size and global cellular translation and transcription levels at the single cell level under unperturbed conditions.

Their results show that translation and transcription steadily increase with cell size, but that the rate of translation, but not transcription, becomes rapidly restricted when cells become larger than wild type dividing cells. This suggests that it is unlikely that the synthesis of RNA is the limiting factor for translation rate in large cells. In addition, their data indicates that translation scales with size, but that the rate increases faster at late S-phase/early G2 and even faster in early in mitosis before decreasing in mitosis and return to interphase. Transcription, on the other hand, increases as a combination of size and the amount of DNA. Overall, this suggests that cell cycle control affects global cellular translation and transcription, which is in line with some studies, but not others. As far as I can tell the assays and data analysis are robust and the data supports the general conclusions.

Major comments I agree that inconsistent results published on this topic might be due to perturbations induced by different synchronisation methods used in the various studies. However, but much less emphasised in the paper, it also likely depends on the model system used. For example, in budding yeast there is strong evidence for gene expression homeostasis, i.e. gene expression increases as a function of size, independent of gene copy number. Do the authors believe this is a budding yeast specific phenomenon or is this a consequence of specific synchronisation methods used in budding yeast?

Gene expression homeostasis has been suggested for budding yeast, but in contrast recent work in budding yeast also suggests that gene expression increases with the genome copy number and therefore the gene copy number in addition to cell size (Swaffer et al., 2022 – currently on bioRxiv). The differences that have been reported might be due to perturbations such as synchronisation methods as well as differences between yeast species.

Whether growth rate increases linearly or exponentially has been the topic of decade long debates. Their data indicates that the translation rate increases faster at late S-phase/early G2 and even faster early in mitosis before decreasing in mitosis and return to interphase, 'resetting' the growth rate. This suggest an exponential, rather than linear, increase in biomass (i.e. growth rate?), but this is not explicitly pointed out. It would be good to get the authors opinion on this in the discussion.

Assuming that protein degradation remains constant throughout growth, the increase of translation with cell size suggests that the growth rate increases as cells grow in size, possibly exponentially. In addition, our data showing that the translation rate increases from G1 to G2 for the same cell size, suggests that for cells of a given size the growth rate is faster in G2 than in G1. Thus, growth could be basically exponential but the speed of increase accelerates at the transition between S and G2, and early in mitosis, slowing down later in mitosis. We added the following sentence to the discussion section “Global transcription and translation increase with cell size possibly exponentially, but the changes in global translation during transitions through cell cycle stages suggest that the speed of growth is modulated by cell cycle progression, increasing between S and G2, and early in mitosis, and slowing down later in mitosis.”.

The authors state that their approach has allowed them to determine how cellular changes are arising from progression through the cell cycle. However, they use fixed cells, rather than live cell imaging, so can't claim to have established changes during cell cycle progression, but only a correlation with cell cycle state/phase. Whilst this could be used as a proxy for progression it should be clearly stated in the abstract and elsewhere to prevent confusion. I for one, based on the abstract, thought they developed a live cell imaging strategy to look at this.

We have modified the abstract to reflect the fact that the cells were fixed in our assays (line 36).

In reference to the Stonyte, et al., study, in addition to different conditions (temperature shift and isoleucine medium), why do the authors think their findings are different? Is it the lack of correlation to cell size in the Stonyte paper or something else? For example, would using different growth conditions (as in the Stonyte paper). where fission yeast cells spend more time in G1, be used instead of the CCP mutant? Can the authors exclude that the lack of G1-S/cyclin-CDKs is not at the basis of a lower rate of translation in G1 and S phase cells? Either these experiments should be carried out or this should be discussed in more detail.

In the study carried out by Stonyte et al., the relative translation rate per cell (a measurement related to our measurement of translation normalised per unit of length) of wild type fission yeast cells grown asynchronously in isoleucine minimal medium is constant between the G1 and the S phase cell populations, and is higher in the G2 population compared to the S phase population (Figure 2D of Stonyte et al., 2018). This is consistent with the lack of increase that we observe for a given cell size from G1 to G2, and the increase we observe from S to G2 in Figure 3K. In the same figure, Stonyte at al., find no difference between the G2 and the M-G1 populations but are not able to distinguish cells at different stages of mitosis or in early G1. Our study suggests that translation increases early in mitosis before decreasing after anaphase A, thus in the Stonyte et al study, pooling all stages of mitosis and early G1 cells might mask the dynamics of what is happening during mitosis. The lack of G1-S/cyclin-CDK could be the basis for the lower rate of translation in G1 and S-phase. We discuss this further in a reply to the first question of the significance part of reviewer 2 and have added a section to the discussion of the paper (see below for details).

If the signal to noise signal is reduced by 20 minutes EU incubation (rather than 10 minutes) why wasn't it used in all experiments?

To measure RNA production as closed as possible to the instantaneous rate of RNA synthesis, we sought to use the shortest pulse possible. We did this because the half-lives of some RNA species are short, in particular, the half-life of the pool of mRNA has been reported to be around 13.1 minutes in budding yeast (Chan et al., 2017). In longer pulses, some RNA molecules that have been synthesised after addition of EU will therefore have been degraded before cells are fixed, producing a measurement that underestimates the rate of RNA synthesis. We chose to incubate cells for 10 minutes as we estimated it to be the shortest time generating a signal to noise ration above 1 (Figure 1F). The one exception to this was with the pulsing of the CCP∆ EGFP-pcn1 hENT1 hsvTK mutant cells which incorporates less EU during the same time frame so we incubated this strain for 20 minutes to generate enough signal to be quantifiable (see line 237, “we assayed CCP∆ EGFP-pcn1 hENT1 hsvTK cells for global transcription using a 20-minute EU incubation to compensate for their lower signal production”).

And the conclusion that the increase in transcription is not showing any discontinuities, are they referring to the triplicates in the supplementary figure 2?

We think there might be a misunderstanding. We conclude that the increase in transcription shows no discontinuity because the median transcription increases steadily with cell length in Figure 2E. We have added “since global transcription increases smoothly with cell length (Figure 2E)” to clarify the text.

Minor comments Lines 168-169: should be Figure 2F, S2C, S2D rather than Figure 2C, S2A, S2B.

The figure numbers have been corrected in the manuscript.

Line 179: doubling time instead of growth rate?

The mention of “growth rate” has been changed to “doubling time” in the manuscript.

Lines 184-186: There is an overall trend of slight decrease in transcription per length in cdc25-22 cells but a slight increase in wild-type cells. How does this differ to wild-type cells? Are these non-significant changes and could these be attributed to the low signal to noise ratio?

These changes may be due to the low signal to noise ratio in the cdc25-22 transcription assay. We have added “The decrease with cell length in transcription that we observe in the cdc25-22 hENT1 hsvTK (Figure 2K) cells but not in the hENT1 hsvTK cells (Figure 2F) may be due to the low signal to noise ratio”.

There is no cell size that is specific to S phase, it falls within the range of G1 and G2 cells. Since this strain has a variable onset of S phase, the phase durations could differ. Therefore, could time spent in each phase affect the translation rate (live cell imaging, i.e. progression, could address this, but not fix cell correlation)?

It is possible that the phase duration of G1 and G2 could differ from one cell to another. There is no evidence that the length of S-phase varies in these cells. It would be interesting to measure how the phase length influences translation, but our techniques do not allow for the measurement of global translation in living cells.

The data reflects translation/transcription in single cells at a specific cell cycle phase, not during the transition between cell cycle phases. Therefore, it would be more appropriate to only use G1, S, G2 and M rather than S/G2 transition or early G2.

Our data represents cells at fixed cell cycle phases and we do not monitor the transition themselves directly. However, the discontinuity in signal for cells of the same size in consecutive stages of the cell cycle (for instance the discontinuity in translation between S and G2 cells of the same size in Figure 3J) is indicative that the transition between the two cell cycle phases is a consequence of a rate change.

In figure 4C, there is a decrease in global transcription after 13 um (black line showing all cells), which they don't see in cdc25-22 mutants. Their conclusion that global transcription is constantly increasing with cell size is based on cdc-25 cells but the experiment in CCP mutant cells shows a decrease in the median of transcription. Are there replicates for these experiments as in figure 2 and supplementary figure S2? Maybe an average trend can be plotted too? Apart from the first set of experiments (figure 2 and supplementary figure 2), they don't show replicates for other strains. Maybe they can include another graph as in figure 3D and 3K of average replicate values?

The apparent decrease in transcription on Figure 4C in long cells is seen in only one length bin (13.5 µm), which has a smaller number of cells compared to the ones directly before (89 cells, compared to 216 cells for the 12.5 µm bin and 316 cells for the 11.5 µm bin). This might have resulted in a higher variability in the measurement of the population median. We do not see the same decrease at 13.5 µm in the wild type (Fig 5G), the cdc25-22 mutant (Fig 2J), or the CCP∆ strain (Fig S4B) so on balance we favour the interpretation that the decrease observed in the longer length bin of Figure 3J is due to variability caused by the lower number of cells in that bin.

CROSS-CONSULTATION COMMENTS I believe that since the whole premise of this study is that by using unperturbed conditions their findings are different from previously published work they should either clearly point out that this difference might be due to using mutations affecting CDK activity or carry out an experiment in media that induces a G1 population. CDK has been strongly implicated in promoting translation. Using a strain that lacks the G1 and S cyclin CDKs or compromised M-CDK is therefore likely to have an effect on translation, which could be at the basis of the increase in translation during the G2 (and S) phase of the cell cycle.

This is addressed in the next comment.

Reviewer #2 (Significance (Required)):

As far as I can tell the assays and data analysis are robust and the data supports the general conclusions. However, whilst the cells are assessed in unperturbed conditions, they do use CDK mutants and the cdc25ts mutant to establsih gene expression during the different phases of the cell cycle, which could affect translation/transcription rates. This should either be clearly pointed out or complemented with an experiment where WT cells are grown in conditions that induces distinct G1-S-G2 populations of cells.

The cell cycle stage and CDK activity are intrinsically linked. CDK activity defines the cell cycle stage so that an increase in CDK activity through the cell cycle is responsible for cells progressing through G1, S, G2, and mitosis (Coudreuse and Nurse, 2010, Swaffer et al., 2016). Nutritional conditions that induce a G1 also rely on repression of CDK activity through increased production of the Rum1 inhibitor (Rubio et al., 2018) to generate a G1 population. Therefore, uncoupling CDK activity from the cell cycle would not be possible in an unperturbed cell population. We have added the following paragraph to the discussion to address the comment “The cell cycle stage of a cell and the activity of its CDK molecules are intrinsically linked since CDK activity defines the cell cycle stage of a cell. CDK activity increases through the cell cycle and is responsible for cells progressing through G1, S, G2, and mitosis [44,53] so that an unperturbed asynchronous population of cells in G1 is achieved by a low CDK activity. Thus our results reflect changes happening through the cell cycle as the CDK regulation network undergoes modifications, and an unperturbed cell cycle therefore cannot be uncoupled from CDK activity.”.

Overall, the work presented suggests that cell cycle control affects global cellular translation and transcription, which is in line with some studies, but not others. Whilst the study falls short of testing/establishing the (potential) mechanisms involved, these are important findings, which can be used to guide new studies into how the production of biomass is controlled as cells proceed through the cell cycle.

The cell size field, which is considerable and growing, will be interested in this work.

I have expertise in cell cycle control and genome stability, with a focus on the G1-to-S transition and cell cycle checkpoints during interphase.

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

Summary Basier and Nurse use fission yeast as a model system to investigate how transcription and translation are coupled to cell-cycle progression. They use metabolic labeling in exponentially growing cells and analyze single cells by microscopy. They find that translation scales with size and increases at S/G2 and early mitosis while transcription increases with both size and the amount of DNA. They suggest that changes in CDK activity regulate changes in global translation rates.

Major comments: 1) The paper addresses a much-disputed question in the field. The approach makes the most of the fission-yeast model system and the experiments are beautifully performed. The conclusions are well supported by the data. The experiments are replicated adequately and the statistical analyses are appropriate.

2) The use of cdc25 and in particular the cig1Δ cig2Δ puc1Δ mutants to manipulate cell size is not without challenges when monitoring translation rates. A number of reports in different model organisms suggest that CDK activity can regulate translation. Work from the Nurse lab identified translation factors as CDK substrates (Swaffer et al, 2016), RNApolIII activity and thus tRNA levels are regulated in the cell cycle by CDK in budding yeast (Herrera et al, 2018), phosphorylation of the ribosomal protein RPL12 by CDK1 is required for translation of at least some proteins in mitosis in human cells (Imami et al, 2018), as is phosphorylation of DENR (Clemm von Hohenberg et al, 2022). The authors also suggest that changes in CDK activity might be responsible for the observed changes in global translation rates. It is important to consider whether using mutants impinging on CDK activity might lead to under- or overestimating cell-cycle dependent translation. The authors should either discuss this issue and tune down the hypothesis that CDK activity regulates changes in global translation rates, or use another approach to address the issue. One could use a replication mutant such as cdc17 or cdc20 to alter cell size without interfering with CDK activity. These experiments would strengthen the conclusions and might support the idea that CDK activity regulates changes in global translation rates. References Clemm von Hohenberg K, Müller S, Schleich S, Meister M, Bohlen J, Hofmann TG, Teleman AA (2022) Cyclin B/CDK1 and Cyclin A/CDK2 phosphorylate DENR to promote mitotic protein translation and faithful cell division. Nat Commun 13: 668 Herrera MC, Chymkowitch P, Robertson JM, Eriksson J, Bøe SO, Alseth I, Enserink JM (2018) Cdk1 gates cell cycle-dependent tRNA synthesis by regulating RNA polymerase III activity. Nucleic Acids Res 46: 11698-11711 Imami K, Milek M, Bogdanow B, Yasuda T, Kastelic N, Zauber H, Ishihama Y, Landthaler M, Selbach M (2018) Phosphorylation of the Ribosomal Protein RPL12/uL11 Affects Translation during Mitosis. Mol Cell 72: 84-98 e89 Swaffer MP, Jones AW, Flynn HR, Snijders AP, Nurse P (2016) CDK Substrate Phosphorylation and Ordering the Cell Cycle. Cell 167: 1750-1761 e1716

As discussed above in the reply to reviewer 2, the cell cycle stage and CDK activity are intrinsically linked, CDK activity defines the cell cycle stage so that an increase in CDK activity through the cell cycle is responsible for cells progressing through G1, S, G2, and mitosis (Coudreuse and Nurse, 2010, Swaffer et al., 2016). Therefore, uncoupling CDK activity from the cell cycle is not possible in an unperturbed population. Temperature sensitive mutants of cdc20 (Ramirez et al., 2015, Win et al., 2002) and cdc17 (Jimenez et al., 1992) cause loss of viability when cells are shifted to the restrictive temperature so it cannot be assumed that they are in unperturbed conditions which makes results hard to interpret. It should be noted as far as possible in these experiments we have tried to avoid perturbations. In addition, the fraction of cells permeabilised in our assay decreases significantly when cells are grown above 30 °C, making it difficult to assay such temperature shifts.

Minor comments: 1) The figures are beautifully presented, easy to understand and the cartoons present the experimental strategies very clearly.

2) A major feature of the approach is that translation and transcription are monitored in exponentially growing cells, which are not exposed to any stress such as cell-cycle synchronization. However, one could argue that the analogues used for labeling impose some kind of stress, even if this is not very likely at the labeling times employed. A simple control experiment where the growth rates of labeled and unlabeled cells are compared would strengthen the claim that these are indeed happily growing cells.

It is possible that incubating cells with the analogues could impose some kind of stress on the cell although that could be said about almost any experimental procedure. We have added two supplementary figures with the suggested experiments, showing that incubating cells with EU has little or no impact on their doubling time (we see at most a 2.4 % increase in doubling time in hENT1 hsvTK cells incubated with 20 µM EU, Figure S1I) and that incubating cells with HPG has little impact on their doubling time (we see a 8.6 % increase in doubling time in wild type cells incubated with 10 µM HPG, Figure S1H). Considering the small impact of analogue incubation on the doubling time of the population, and the fact that cells are only exposed to the analogue for a short time in our assays (compared to continuous growth in the presence of the analogue in the growth curves presented in Figure S1H and I), we conclude that the stress imposed is low.

3) Please comment why the length of the EU labeling differs from figure to figure. In fig 2C, S2C and S2D the labeling on the y axes states 10 min, in Fig 4C it says 20 min.

Please refer to the reply to reviewer 2 on the same topic.

4) Lines 118-119 "The pulse signal was five times the background signal." Figure S2A,B show large variation in signal intensity after 5 min labelling. It is not clear how the pulse signal was estimated to be five times the background signal.

We have added two panels for the supplementary figure 2 showing how the signal to noise ratio was computed for the HPG assay after 5 minutes of incubation (Figure S2G) and for the EU assay after 10 minutes of incubation (Figure S2H).

5) In Fig S4C transcription is up by ca 60 % from G1 to G2, while in Fig 4D transcription is up by ca 25-30%, also from G1 to G2. The only difference I can see is the use of PCNA-GFP. Please comment what the reason might be.

In Figure 4D, transcription is up 33 % from G1 to G2 and in Figure S4C, transcription is up 62 % from the 1C to the 2C population. It is possible that the EGFP-pcn1 strain might have a small growth defect which could possibly explain its lower signal production, the slower growth rate might mean that the concentration of RNA polymerase could be lower in this strain and the dynamic equilibrium model predicts that this would results in a smaller increase from G1 to G2 compared to cells with a higher concentration of RNA polymerase. But obviously this is speculative.

6) Fig 1 B images of unlabeled control cells should also be shown.

We have added 2 panels to the supplementary figure 1 showing the background controls in which cells are fixed immediately after addition of the analogue for the HPG assay (Figure S1F) and for the EU assay (Figure S1G).

7) Lines 156 "to investigate how global cellular translation and transcription are affected by cell size, and by progression through the cell cycle" should be amended. Throughout the description of data in figure 2 binucleated and septated cells were excluded from the analyses, meaning that the data only represent cells in G2. The text should make this clear.

"to investigate how global cellular translation and transcription are affected by cell size, and by progression through the cell cycle" has been changed to "to investigate how global cellular translation and transcription are affected by cell size and by progression through G2" to reflect the fact that binucleated and septated cells are excluded from the analysis on this figure.

8) Lines 241-243 "the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations of around 20-25 %." And Lines 310-313 "the rate of transcription is increased in cells undergoing S-phase by 20 % and is 35 % higher in G2 cells which have completed S-phase, indicating that DNA content is limiting the global rate of transcription." It is unclear what the percentage values refer to and which populations exactly are being compared.

"the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations of around 20-25 %" has been changed to “the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations with an increase of around 20-25 % compared to the G1 subpopulation” and “the rate of transcription is increased in cells undergoing S-phase by 20 % and is 35 % higher in G2 cells which have completed S-phase, indicating that DNA content is limiting the global rate of transcription” has been changed to “the rate of transcription is increased in cells undergoing S-phase by 20 % compared to G1 cells and is 35 % higher in G2 cells which have completed S-phase compared to G1 cells, indicating that DNA content is limiting the global rate of transcription”. These changes hopefully will clarify what populations comparisons the percentage values are referring to.

9) Line 85 "Asynchronous cultures ... have not detected" rephrase; change detected to displayed or similar.

“detected” has been changed to “displayed”

10) Line 243 Figure 4J, K should read Figure 4C, D.

“Figure 4j, K” has been changed to “Figure 4D, C”

CROSS-CONSULTATION COMMENTS

I also agree with the comments made by the colleagues. As for the use of the cyclin and cdc25 mutants: I agree with Reviewer #1 that it is unlikely that bulk synthesis rates are conisedarably different, since these strains are going at more or lass normal rates. However, I also agree with reviewer #2 that these mutants cannot be considered as unperturbed conditions. I suspect subtle regulation and in particular cell-cycle dependent regulation might well be lost. At the very least the focus of the interpretation should be on translation/transcription as a function of size, rather than in terms of cell-cycle regulation.

Reviewer #3 (Significance (Required)):

Basier and Nurse address a long-standing question in the cell-cycle field, namely how/whether transcription and translation are coupled to cell-cycle progression. This is technically challenging to address, and many previous studies were hampered by the necessity to synchronize the cells in the cell cycle. The approach of this study of using metabolic labeling in non-synchronized cells is not novel in itself. However, the analysis by microscopy is superior to previous flow-cytometry based strategies in that it allows the use of cell-cycle markers and thereby precise identification of cells in each cell-cycle phase. In addition, it allows accurate measurements of cell size and thus addressing questions of correlations between cell size and transcription / translation rates. A further strength of the study design is that they investigate both transcription and translation in parallel. The authors very nicely review the existing literature and point out the likely reasons for conflicting conclusions (synchronization methods, choice of model system). The advantages of their approach, such as single-cell analyses in non-synchronized cells and the use of cell-cycle markers make their conclusions less likely to be flawed and thus represent an important advance in the field. These findings are of interest for researchers working on the cell-cycle field and on the translation field. There have been significant technical advances in the translation field in recent years, allowing studying not only global translation but also translation of specific mRNAs. I expect that the old questions of coupling cell cycle and cell growth will be revisited also by others, exploiting these new approaches. My field of expertise extends to the cell-cycle field and the regulation of translation and the use of fission yeast.

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

Summary Single cell measurements (flow cytometry and imaging) from unperturbed cells are obtained to investigate scaling of transcription and translation in fission yeast. A key finding is that translation and transcription are somewhat differentially responding to changes in cell size and cell cycle. Perhaps the most central finding of this manuscript is that transcription is not a limiting factor to translation and suggests that transcription is not limiting growth (increase in biomass).

Major comments: What I like in this manuscript is that the translation and transcription measurements have been carefully checked to reflect the initial rates before the HPG and EU signals lose their linearity. More generally, experiments have been conducted with appropriate controls, and the analysis of unperturbed cells in each cell cycle phase is likely to be highly relevant for resolving some of the controversies in the field. Most claims and the conclusions are well supported by the data. Although it is encouraging that the results for translation match the single cell mass measurements in mammalian cells (e.g., ref 18), I would have liked to see some more discussion about the potential caveats of the performed analyses such as the low signal to noise ratio in EU incorporation and other potential technical issues, which might have confounded the results. As an example, looking at Figs 1B and E, most of the protein and RNA synthesis signal is nuclear localized. Is this due to nucleolar staining and incorporation of the labels into nascent ribosomes? Yet the manuscript mentions that roughly half of RNA is for rRNA and for ribosomal proteins the fraction of HPG incorporation might be even lower. This statement does not sound entirely consistent with the experimental images shown in Fig 1. Please clarify.

We had initially performed modelling to estimate the proportion of rRNA in transcription but after reconsideration we agree that is difficult to assess whether the special pattern we observe is consistent with the statement that roughly half of the nascent RNA is rRNA. There is signal in the cytoplasm indicating that within the pulse time some RNA are exported from the nucleus, thus the localisation of the RNA signal is not necessarily an accurate indication of the fractions of the different RNA types in global transcription. We have removed the statement “Although the precise fractions of the different types of RNA in global transcription have not been fully characterised, recent work indicated that only half of the newly synthesised RNA consists of ribosomal RNA molecules, suggesting that a significant portion of transcription is dedicated to the production of messenger and other RNA molecules [27].” It cannot be concluded that most of the protein synthesis is nuclear located in Figure 1B. As mentioned in the text we cannot differentiate between proteins being synthesised in the nucleus and proteins being rapidly imported, we also cannot say what fraction of the proteins synthesised are related to ribosome biogenesis.

A curious thing that has been glossed over is that the transcription and translation seem not to be completely linear but to display opposite patterns (translation slightly reducing, transcription slightly overshooting with cell size compared to a linear model). It remains possible that this could be experimental noise and a visual pattern that is not real, but it could also be relevant for growth control. For example, my interpretation from Fig. 2B is that the signal is not linear and starts to saturate around 10.5 um cell length as seen from the upper IQR. Related to this, I think it is oversimplification to force the data to appear as a discontinuous linear trend by splitting the data in 2H into two segments. Such a treatment will obviously match the data better than a single linear regression, but perhaps some nonlinear model would be actually much more accurate, unless you can point out some kind of regulatory event at the intersection of these two linear segments. In my opinion the current data looks more like a typical (logarithmic) growth curve of the cell population reaching saturation. Please comment.

We agree that fitting two linear regressions for cells shorter and longer than 15 µm is in Figure 2H and 2I was an oversimplification which could result in a false discontinuity in the data. This echoes a comment from reviewer 1 pointing out that 15 µm might not be the length at which the transition occurs. We have removed the linear regressions and added a locally estimated scatterplot smoothing (LOESS) function which capture the nonlinear transition between the increase of translation with size and the saturation, and we have changed the cell length at the estimated saturation from 18 to 19 µm in the text to better reflect the trend.

The main conclusion presented in the abstract is that scaling in transcription may result from dynamic equilibrium between RNA polymerases and available DNA template. This is a bit of speculative part, which I was not too fond of. The dynamic equilibrium idea has been suggested also elsewhere (refs 47) and is not well developed in this manuscript. There is a lack of mechanistic understanding and no formal (mathematical) model to support this idea. For example, global transcription increases much less (1.3-1.4x) than expected based on the increase in DNA content from G1 to G2 (2x). Is this expected based on the dynamic equilibrium model?

The dynamic equilibrium model has been proposed and developed by Swaffer et al. (2022 – currently on bioRxiv) based on mass action kinetics describing the interaction between RNA polymerases and DNA. The model predicts that transcription increases with cell size and with the amount of DNA. With this model, the increase in transcription with DNA for a given cell size is also a function of cell size. Smaller cells are predicted to have a smaller relative increase in transcription from 1C to 2C DNA content than larger cells. This implies that depending on the cell size to DNA ratio of a cell, the span increase in transcription produced by a doubling in the amount of DNA goes from a small increase (at small cell size to DNA ratio) to a doubling (at large cell size to DNA ratio). Thus, in our view the 1.3-1.4x increase in transcription we observe from G1 to G2 is consistent with the dynamic equilibrium model.

I am somewhat concerned about the interpretation of the S phase data in the global transcription measurement. The quantification in Fig. 4D shows S phase being intermediate between G1 and G2. Yet, when you look at the data in Fig. 4C, the S phase median is clearly discontinuous, with higher transcription in smaller S cells. I believe this could affect the normalized data in Fig. 4D and result in the apparent increase in transcription in S phase cells. Having said that, I am not sure if this small S phase transcription is noise (low cell counts?) or a real S phase specific regulation of transcription which is not DNA content dependent. This results is one of the most central ones in this paper to differentiate between transcriptional and translational scaling. Therefore, additional data or insights would be highly appreciated.

It is possible that the discontinuity in the medians of the S phase population in Figure 4C could be the result of noise due to the low cell count in the short size bins (115 cells at 6.5 µm, 404 at 7.5 µm). In addition, because we cannot measure DNA with a degree of accuracy high enough to identify how advanced in S-phase each cell is, we do not know the distribution of the advancement into S-phase of cells for each length bin. This is complicated by the fact that some cells of the CCP∆ mutant start S-phase whilst still septated and might be in a late S-phase stage by the time the cell splits so the median global transcription of the shorter length bin does not necessary reflect the median of early S-phase cells. Hence the discontinuity observed with cell length does not necessarily suggest that there is a discontinuity happening through S-phase. We suggest that since the mean global transcription per cell length of cells in S-phase is in between the mean global transcription per cell length of cells in G1 and in G2, the increase happens through S-phase. To reflect this possibility we have added “It is also possible that the increase happens at a certain stage of S-phase independent of the amount of DNA since we do not know the extent of S-phase of each cell.”

Minor comments: Line 61: "patterns of protein RNA". I guess this refers to patterns of protein/RNA synthesis?

“patterns of protein and RNA” has been changed to “patterns of protein and RNA synthesis”.

Line 248: typo "Tanslation"

“Tanslation” has been changed to “Translation”.

Line 410 and 416: Move interquartile ranges from line 416 to line 410 as this is the first occurrence of the IQR abbreviation.

“Interquartile ranges” has been moved from line 416 to line 410.

Line 473: "Almost linear". This is a subjective expression, please provide some measure such as the R2 value to quantitatively evaluate linearity in this strain.

We have added a measure of the deviation from linearity in the text “, 15 % deviation from the OLS linear regression shown in Figure 1F”. Line 547: Is there a reason to stress in this experiment that the AREA of the fluorescence signal was measured as the area indicates the total fluorescence intensity?

“area of the” has been replaced by “total” so the sentence refers to the total fluorescence intensity signal of Sytox Green. Fig1A: The schematic mentions peptides, shouldn't it be more accurate to use "polypeptides" or "proteins" when discussing protein synthesis?

“Peptides has been changed to Polypeptides”

Fig 5G: Y axis scale has a typo in the word transcription.

“Trancription” has been changed to “Transcription”

CROSS-CONSULTATION COMMENTS I also agree with the points raised by the colleagues. There will always be some technical or interpretation issues related to every experimental technique, every model system and every mutant strain used. I believe after addressing these limitations as pointed out in the reviews, most of those issues have been clarified for the readers.

Reviewer #4 (Significance (Required)):

Basier and Nurse revisit the classic question regarding growth and cell size control by examining scaling of global translation and transcription in fission yeast. Knowing how cells alter their transcription and translation has important consequences in cellular functions during proliferation and cellular aging and is of broad general interest. The main driver for this current work is that previous experiments both in fission yeast and other model organisms have yielded conflicting results, possibly due to different cell cycle synchronization methods. The strength of the paper is indeed in the single cell analyses of well defined yeast strains which allow accurate assessment of the cell cycle dependent changes and accurate measurements of cell size using the cell length.

Reassuringly, the single cell analyses from unperturbed yeast cells resemble those recently obtained from unperturbed growth of individual mammalian cells. The main conclusion that transcription is not limiting translation, and consequently not limiting growth of the cells, is interesting as it is not consistent with some of the prevailing ideas in the cell size field. These ideas include ploidy dependent gene expression where DNA content is thought to be limiting growth or the model for minimal gene expression which assumes RNA polymerases are limiting gene expression and growth. In this regard, this manuscript provides important insights for future thinking of how growth is controlled.

keywords: cell cycle, cell size control

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Reply to the reviewers

1. General Statements

We thank the reviewers for their critical analysis of our manuscript. We have addressed all reviewer concerns and questions in our revised version. Along with other improvements requested by the reviewers, we added an MTT assay to validate our flow cytometry assays, normalized binding to surface area to better compare toxin binding between Leishmania and HeLa cells, and revised the discussion. We believe the revised contribution provides important novel insights into membrane integrity in a non-standard organism that will appeal to a broad audience.

Reviewer comments below are in italics.

Point-by-point description of the revisions

Reviewer 1

*Major Comments. The experimental work has been carried out carefully, including multiple biological replicates, convincing statistical analysis. Data presentation is extensive, including 6 supplementary figures. It is likely that the experiments could be reproduced by others, as the approaches do not seem to be especially difficult, and the methods are well documented. *

We thank the reviewer for this assessment.

*My major comment regarding revision is that this paper is quite long and extensive given the relatively restricted body of experiments and discrete conclusions. The principal discovery is that sphingolipids protect Leishmania parasites against somewhat artificial treatment with bacterial sterol-binding pore forming toxins, but they do not do so by obstructing toxin binding to sterols. A similar effect is seen for the antileishmanial drug amphotericin B, the most important agent studied. No further mechanistic insights are provided regarding the process whereby sphingolipids blunt toxicity of either the CDCs or amphotericin B. In addition, the experimental approach relies largely upon one methodology, dose-response curves. A report with such highly focused scope should be presentable with considerably more economy. In particular, the Discussion is long and diffuse, obscuring the presentation of the major conclusions. It could probably be cut in half and would in the process present the major deliverables of the paper with higher impact. *

We have condensed the discussion as requested, and to address Reviewer 2’s concerns, we provided a summary articulating the significance.

Significance

*The most notable advance is the observation that sphingolipids protect Leishmania parasites from the cytotoxic activity of the first line antileishmanial drug amphotericin B that binds to the major sterol in the parasite plasma membrane, ergosterol, and induces pore formation. This discovery suggests that parallel treatments with agents that selectively reduce sphingolipid levels in the parasite might act synergistically with amphotericin B, potentially allowing treatment with lower doses of this inherently toxic drug. This work will likely be of most interest to those with a focus on pharmacology and drug development for this and related parasites, but it will also be of some interest to those working on the basic biochemistry of these organisms. The senior authors are major workers in sphingolipid biochemistry in Leishmania parasites and thus are well positioned to address the relevant background in the field, much of which has come out of their laboratories.

The major limitation of this study is its relatively circumscribed scope, resulting in one principal conclusion: Leishmania sphingolipids blunt the potency of toxins or drugs that target sterols for pore formation, but they do not do so by impairing binding of these agents to sterols, as they do in mammalian cells. The work would be of higher impact if it addressed mechanistically how sphingolipids do decrease toxicity, e.g., do they prevent these agents from oligomerizing or from intercalating into the membrane to form pores. Such studies would require the application of an expanded repertoire of experimental methodologies going beyond the measurement of dose-response curves with various mutants and drugs.*

We agree with the reviewer that next steps include determining if Leishmania sphingolipids interfere with oligomerization or pore-insertion. One challenge is that these tools need to first be validated in Leishmania.

To address the reviewer concern about the limited range of experimental methodologies, we added an MTT assay (Supplementary Fig S2E) as validation of our flow cytometry assays. We have better summarized the significance and broad impact of our work in lines 466-476.

Reviewer 2

*In the abstract the authors describe that the pore-forming toxins engage with ceramide and other lipids and while it's clear that the levels of sphingolipids are important for the effect of these toxins there is limited evidence to show they physically interact as the word engage suggests. *

We agree with the reviewer that we do not show physical interaction. In the abstract, we are careful to only use the word “engage” in association with our proposed model. Our proposed model both explains our data, and uses those data to open new horizons by making falsifiable predictions that can be tested in the future. Direct engagement of toxins with lipids is one such prediction. For these reasons, we prefer to retain the word “engage” in the abstract.

*The authors conclude that the ergosterol on the Leishmania cell membrane is less accessible to the CDCs as it does not bind as much CDCs as a HeLa cell. What is the relative abundance of sterols in the HeLa membrane in comparison to a Leishmania cell. A HeLa cell is much bigger than a Leishmania cell and will therefore be able to bind a lot more CDC, was the MFI normalised for cell size? This would be important to know as the difference in intensity may be purely related to the difference in cell size. *

We thank the reviewer for this insight. We had not normalized MFI by cell surface area. We added MFI normalized to cell size (described on lines 573-577) and found that when area was accounted for, the promastigotes bound more toxin than HeLa cells. These data are now included as Supplementary Fig S1A, and discussed on lines 187-189.

*The authors are keen to prosecute that ceramide is important for differences between PFO and SLO action as the inhibitor has a much greater effect on the PFO treatment of ipcs- cells than SLO, as ceramide will accumulate in these cells. But for the SLO analysis they stated that the treatment of spt2- with myriocin had no change on the LC50 as the target of myriocin was spt2 while they noted was there a drop in the LC50 with PFO. Based on this I think the importance of ceramide is being overstated here, as spt2- cells have little ceramide in them. Moreover the authors also suggest that changes to the lipid environment rather than a single species might be important. Are there alternative targets the myriocin might inhibit when there is no spt2-, it is intriguing that there is a decrease in LC50 for PFO on spt2- myriocin treated cells. *

Clearly, IPC is very important for determining the cytotoxicity for the CDCs in Leishmania but I think the evidence for the role of ceramide and the sensing of it is less clear cut and the strength of the conclusions about this should be modified. In the results the authors conclude that the L3 loop is sensing ceramide and the data shows that the L3 loop is important but in the discussion they are more circumspect about the moieties L3 can detect. The authors should qualify these conclusions in the results a bit more.

As requested by the reviewer, we have qualified our statements in the results, lines 282, 297, 315.

*Minor comments *

*It would be helpful for the review process to include line and page numbers to highlight areas that I have concerns about. *

We agree with the reviewer and have added line numbers.

*In the first paragraph of the results is there a reference for the spt2- cell line that was used here. *

We have added the Zhang 2003 reference to the first paragraph of the results, line 161.

*In the second paragraph there is a disconnect between the statements about the phenotype of the ipcs- cells and the reference/evidence for it. *

We have added the reference to the earlier mention of the ipcs cells, and in the introduction, lines 118-120 and 167-169.

*On many of the graphs the letters a, b, c are alongside many of the symbols but it was unclear what they represented. *

The letters represent statistically distinct groups. These are used instead of stars and bars to reduce clutter on the figure. We have now explained the difference in the first figure legend in which they are used, lines 818-823.

*The colour scheme for figure 4 was confusing - yellow diamonds in A/B are spt2-/+spt2 but in C/D are iscl-, this makes it hard to compare between them. *

We have changed the color and symbols for the iscl- mutant in Fig 4 and Fig S6.

*The methodology states that various tests were used to define whether differences were significant but it was not clear from the figures when these were being applied only a few graphs had '*' associated with them. *

We have clarified this in the figure legends.

*There is no overall conclusion to the study at the end of the discussion just a series of limitations of the study, which is good to acknowledge but feels an odd way to finish the manuscript. *

We have revised the discussion in response to Reviewer 1, and included a summary to tie everything together, lines 466-476.

*Significance: *

Overall this is a strong manuscript with a set of experiments that have a clear strategy and purpose that was well written. This paper outlines the importance of the lipid composition for the cytotoxicity of both sterol specific toxins and amphotericin B in Leishmania, which will have significant implications for their study for other pathogens but also for the development of combination therapies to enhance the potency of amphotericin B, as such I think this will be of interest to both researchers interested in drug discovery and those interested in lipid metabolism.

We thank the reviewer for this assessment.

Reviewer 3

Major comments: 1) The idea that sphingolipids do not block toxin access relies on the work of CDC-based probes binding the accessible pool of cholesterol in mammalian membranes. The authors make the observation that ergosterol is not shielded by sphingolipids because the presence of them does not prevent CDC binding. Is it possible to show that Leishmania sphingolipids are able to actually sequester ergosterol or would it all be considered free and available to toxin binding?

Our interpretation of the binding data is that the Leishmania sphingolipids fail to sequester ergosterol from toxins, so ergosterol accessibility is independent of sphingolipids. Similar to mammalian cells, there could be an “essential” pool of ergosterol bound to other proteins/lipids that is inaccessible to toxins. However, detecting that pool is technically challenging.

We have revised the manuscript to clarify this, lines 454-456.

* 2) The statistical analysis applied to each experiment, while defined in the figure legends, are presented mostly using uncommon methods of presentation, making it difficult to determine if the correct analysis was applied.*

We have clarified the statistics and use of letters. The letters represent statistically distinct groups. These are used instead of stars and bars to reduce clutter on the figure. We have now explained the difference in the first figure legend in which they are used, lines 818-823.

* 3) The binding of these toxins to Leishmania cells appears to be independent of their lipid composition, but Figure 1A-D suggests that these toxins do not bind very well to Leishmania; a ~65 fold increase in toxin added only results in a maximal 3 fold change in amount of toxin bound. Therefore, the authors need to demonstrate that this increase in binding is not simply the result of adding more ug of each CDC. *

Leishmania are smaller than HeLa cells, which accounts for the apparent reduced binding. We added Supplementary Fig S1A, which normalized MFI to estimated surface area. When normalized to surface area, Leishmania bound to toxin better than HeLa cells. We further note that the dose-dependent increase in cytotoxicity argues against non-specificity of increased toxin.

* 4) The authors use HeLa cells to compare the ability of these toxins to bind to sterol containing membranes, but it is unclear how a mammalian cell line, which lacks ergosterol, can inform upon the differences in binding to Leishmania membranes when their data shows almost no cholesterol is found in the Leishmania membrane. The use of HeLa cells to compare the toxicity of these CDCs is simply a control experiment for the lytic activity of these proteins, and should not be used as a direct comparison of their LC50s, as a mammalian plasma membrane lipid composition is significantly different from that of Leishmania. If the authors want to use HeLa cells as a direct comparison to show that sphingolipids in mammalian cells also protect them from CDC pore formation, they must demonstrate the HeLa cells which have genetic defects in sphingolipid biology or which have been treated with sphingomyelinases are more sensitive to these CDCs. *

We agree with the reviewer that to argue sphingolipids in mammalian cells are protective would require additional data beyond the scope of this manuscript. We are not making any statements about the role of sphingolipids in mammalian cells, which have a controversial role in CDC damage and membrane repair (see e.g. Schoenauer et al 2019. PMID: 29979630). Since the head group of sphingomyelin interacts with cholesterol (Endapally et al 2019), but the IPC head group is not expected to interact similarly with ergosterol, we choose to remain focused on Leishmania sphingolipids.

Given our focus on Leishmania, why include HeLa cells at all? We think including HeLa cells provides an important and relevant point of reference because there are situations where both human cells and Leishmania promastigotes could encounter pore-forming toxins. This comparison provides insight to the following question: “In a mix of promastigotes and human cells (for example during a blood meal), which cells would die first from the bacterial PFT?” Comparing cytotoxicity to HeLa cells provides a point of reference in judging how cytotoxic CDCs are to Leishmania promastigotes, and how sensitive the spt- promastigotes become.

We have rephrased the manuscript (lines 208-209) to better clarify that HeLa cells are a reference point so readers can evaluate the relative sensitivity of sphingolipid-deficient promastigotes.

* 5) The authors need to demonstrate that the mutant cholesterol recognition motif (CRM) and the glycan binding mutant proteins can still bind to both Leishmania and Hela cell membranes to serve as controls for their lack of lytic activities. Without this, they cannot conclude that "Leishmania membranes engage the same binding determinants used by CDCs to target mammalian cells". *

The glycan binding and ΔCRM mutants are unable to bind to HeLa cells. These toxin mutations were previously characterized (Mozola & Caparon, 2015 and Farrand et al 2010), showing that their defect lies in binding to cells, but not oligomerization or pore-formation. Since their defect lies solely in binding, if these toxins were able to bind to spt2- cells, they would kill the spt2- cells. This enables us to use these toxin mutants to ask if the CRM or glycan-binding is essential for toxin binding to Leishmania. Since the only defect in these mutant toxins is binding (either to glycans or cholesterol), the failure of these mutants to kill allows us to conclude that both of these binding surfaces on the toxin are essential for cytotoxicity in L. major.

We have clarified the manuscript, lines 236-240. *

Minor comments: 6) Multiple figures lack adequately defined axes. Examples include, but are not limited to: Figure 1A-D where the X-axis is plotted as logarithmic based 2 but this is not defined. Figure 2 the Y axis is plotted as logarithmic based 10 but is not defined. *

We have updated the figure legends to indicate where log axes are used.

7) The authors state that "Promastigotes with inactivated de novo sphingomyelin synthesis has a significant increase in total sterols" in reference to Figure 1E. Not only is there no significance indicated for the spt2-/-, the authors only indicate a significance point for the Myr (not yet defined) + WT sample in "Other sterols".

We have rephrased this to indicate a trend, line 181.

8) The authors use increases in membrane permeability as a read out for specific lysis using PI uptake, however, they then refer to this read out as killing of Leishmania, without measuring the viability of these cells. Therefore, the authors should provide additional experiments that demonstrate the death of the different Leishmania strains treated with the cytolysins.

As requested, we have now provided an additional experiment to validate Leishmania death. We have now added MTT assay as Fig S2E, and discussed in the results, lines 202-205.

9) It is not clear how the authors calculated their LC50 values in Figure 2. According to the figure legends, the authors used HU/ml ranges that would be sub lethal or not completely lysed within this range to most of the Leishmania strains tested. The data presented in Figure are not clear that the correct LC50 calculations were used as none of the Specific Lysis curves do not reach saturation with the concentrations presented, and one does not even reach 50% Lysis.

We thank the reviewer for catching this discrepancy. The legend in Fig 2 did not include the correct ranges of toxin dose used for PFO. We have corrected the legend to indicate the toxin range used. To calculate LC50, we used linear regression on the linear portion of the death curve to determine the concentration at 50% lysis. This gives us a way to determine LC50 even without the use of very large (and costly) amounts of toxin to get extensive saturation on the kill curve.

* 10) Figure 4 and Figure S6 are very difficult to interpret. Figure S6 would benefit by breaking up each graph into multiple graphs that would allow the reader to see more of the curves individually. Additionally, there are multiple conditions were it appears that a different number of experiments (2-4 totals) were preformed but statistical analysis was applied to these data. *

We updated the labels on Fig 4 for improved readability. We broke Fig S6 up into multiple graphs. We have removed unpaired data (eg the n of 4 noted by the reviewer), and re-checked our stats. This change did not alter our conclusions. The apparent n of 2 was overlap of data points due to poor jittering of the datapoints. We have increased the jitter on the data points to make all three reps more distinct.

* 11) The authors state "In contrast to myriocin-treated ipcs- L. major, which contain low levels of ceramide, myriocin treated iscl- L. major contain low levels of IPC" but do not provide a reference or point to data to support this claim. *

We have qualified these statements to say ‘are expected to’ on lines 306-307.

* 12) Figure 5 E would benefit in presentation by being broken up into 4 separate graphs based on the toxin used, as it is difficult to determine which data points are being compared. *

We compare by toxin used in Fig 5A-D. The purpose of Fig 5E is to compare between toxins. We included all of the data points (including resistant control strains) for completeness. The main focus is the spt2- and ipcs- parts of Fig 5E.

* 13) The authors state that "myriocin did not inhibit growth more than 25% promastigotes at 10 μM" but this data is not presented. *

We have now added these data as Fig 6A.

14) Multiple graphs lack legends or have axis that are not defined.

In order to improve readability and avoid cluttering the figures, where the legends and axes are the same across multiple graphs, they are included only once for a given row and/or column.*

Significance:

Overall, the experiments presented were conducted to analyze each question, but many of the results are observational, without considering the impact of altered lipid species on the findings. The data suggests an existence of a protective mechanism for the parasite from CDCs, but it unclear how these finding inform upon the CDC or Leishmania fields. CDCs have been known to target sterols within membranes and that altered local membrane environments can have substantial impacts on CDC binding. This work suggests that the altered lipid species of Leishmania membranes, compared to a mammalian membrane, could dramatically effect the sequestering power of sphingolipids or other lipids, and thus change how CDCs bind to them. This work advances is likely to have specialized audience of Leishmania researchers looking at the dynamics of their membranes.*

We believe this work will be valuable to a broad audience because it will be of interest to researchers studying membranes in general, pathogenic eukaryotes and pore-forming toxins. Most membrane biology work is done either in opisthokonts or in model liposomes, so there are few studies on biomembranes in other taxonomic groups, including many different human pathogens. We provide a blueprint for examining the membranes of non-standard organisms, establish L. major as a pathogenically relevant model system, and report on key differences in sterol sequestration compared to mammalian cells. These findings provide important perspectives for the generalization of biomembranes, especially when compared to prior work in opisthokonts.

We have clarified our significance in lines 466-476.

Author Response

Reviewer #1 (Public Review):

This paper tests whether people vary their reliance on episodic memory vs. incremental learning as a function of the uncertainty of the environment. The authors posit that higher uncertainty environments should lead to more reliance on episodic memory, and they find evidence for this effect across several kinds of analyses and across two independent samples.

The paper is beautifully written and motivated, and the results and figures are clear and compelling. The replication in an independent sample is especially useful. I think this will be an important paper of interest to a broad group of learning, memory, and decisionmaking researchers. I have only two points of concern about the interpretation of the results:

1) My main concern regards the indirect indicator of participants' use of episodic memory on a given trial. The authors assume that episodic memory is used if the value of the chosen object (as determined by its value the last time it was presented) does not match the current value of the deck it is presented in. They find that these mismatch choices happen more often in the high-volatility environment. But if participants simply choose in a more noisy/exploratory way in the high volatility environment, I believe that would also result in more mismatched judgments. What proportion of the trials labeled as episodic should we expect to be a result of noise or exploration? It seems conceivable that a judgment to explore could take longer, and result in the observed RT effects. Perhaps it could be useful to match up putative episodic trials with later recognition memory for those particular items. The across-subjects correlations are an indirect version of this, but could potentially be subject to a related concern if participants who explore more (and are then judged as more episodic) also simply have a better memory.

Thank you for this important suggestion. We agree that noisy/exploratory choices could potentially masquerade as episodic on the episodic-based choice index used as one of our behavioral measures. As pointed out, this is because participants may be more likely to make noisier incremental value-based decisions in the high volatility compared to the low volatility environment. In our revision, we provided a new analysis that shows that, as the reviewer predicted, choices are indeed more noisy in the high volatility environment. We answer this concern in two ways. First, we took this noise into account in our analysis of the episodic/incremental tradeoff and show that it does not account for the main findings. And second, we provided a new analysis of subsequent memory that shows that choices that are defined as episodic during the decision-task are also associated with better recognition memory later on. These new analyses are described below as well.

We used a mixed-effects logistic regression model to test for an interaction effect of environment and model-estimated deck value on whether the orange deck was chosen. We fit this model only to trials without the presence of a previously seen object in order to achieve a more accurate measure of noise specific to incremental learning. In both the main and replication samples, participants did indeed make noisier incremental decisions in the high compared to the low volatility environment (Main: 𝛽 = −1.589, 95% 𝐶𝐼 = [−2.091, −1.096], Replication: 𝛽 = −1.255, 95% 𝐶𝐼 = [−1.824, −0.675]). To account for the possibility that the measured difference between environments in our episodic-based choice index may be related to this difference in incremental noise between the environments, we included each participant’s random effect of the environment by deck value interaction from this model as a covariate in our analysis of the effect of environment on the episodic-based choice index. While each participants’ propensity to choose with greater noise in the high volatility environment did have an effect on the episodic-based choice index (Main: 𝛽 = 0.042, 95% 𝐶𝐼 = [0.012, 0.072], Replication: 𝛽 = 0.055, 95% 𝐶𝐼 = [0.027, 0.082]), the effect of environment was similar to that originally reported in the manuscript for both samples following this adjustment. The reported effects (lines 178 and Appendix 1) and methods (lines 643-655) have been updated to reflect these changes.

We applied a similar logic to the reaction time analysis, to address the possibility that decisions based on exploration may take longer compared to decisions based on exploitation of learned deck value. We included a covariate in the analysis of the effect of episodic-based choices on reaction time that captured possible slowing due to switching from choosing one deck to the other (lines 656-662) and found that the slower reaction times on episodic choices are not fully explained by exploration. Because in this task a decision to explore is captured by switching from one deck to another, the effect of episodic-based choices on reaction time reported in the manuscript should account for this behavior. We have clarified this reasoning in the methods (lines 661-662).

Finally, thank you for the idea to sort objects in the recognition memory test by whether they were from episodic- or incremental-based choice trials to provide a further test of whether our approach for sorting episodic decisions withstands an independent test. We performed this analysis and found that, in both samples, participants had better memory for objects from episodic-based choice trials. This result provides further support for the putative episodic nature of these trials and is now reported in the Results (lines 300-304 and Appendix 1), Methods (lines 737-742) and appears as a new panel in Figure 5 (Figure 5A).

2) The paper is framed as tapping into a trade-off between the use of episodic memory vs. incremental learning, but it is not clear why participants would not use episodic memory in this particular task setup whenever it is available to them. The authors mention that there is "computational expense" to episodic memory, but retrieval of an already-established strong episodic memory could be quite effortless and even automatic. Why not always use it, since it is guaranteed in this task to be a better source of information for the decision? If it is true that RT is higher when using episodic memory, that is helpful toward establishing the trade-off, so this links to the concern above about how confident we can be about the use of episodic memory in particular trials.

Thank you for raising this important point and for giving us the opportunity to clarify. We now address this point in two ways: first, we provide a new analysis of episodic memory and choice behavior and we address this point explicitly in the discussion.

As now emphasized in the paper (lines 118-122 and lines 384-388), in this task, it is true that an observer with perfect episodic memory should always make use of it whenever available (i.e. on trials featuring previously seen objects). However, human memory is fallible and resourcelimited, and we find that participants with less reliable episodic memory overall actually relied less on this strategy and more on incremental learning throughout the task (Figure 5C and 5D). In other words, there is noise and uncertainty also in the episodic memory trace. While it is not the main focus of our study, the noise in episodic memory is indeed another reason why trading off between episodic memory and incremental learning is advantageous for behavior. We further agree that while the RT effects show that, relative to using incremental value, episodic memory retrieval takes longer, we cannot make strong statements about effort or “computational expense” per se from our data. Accordingly, we have removed the “computational expense” phrase (line 491), as well as our suggestion that episodic retrieval is “perhaps more effortful overall” (line 181), from the paper.

Reviewer #2 (Public Review):

This manuscript addresses the broad question of when humans use different learning and memory systems in the service of decision-making. Previous studies have shown that, even in tasks that can be performed well using incremental trial-and-error learning, choices can sometimes be based on memories of individual past episodes. This manuscript asks what determines the balance between incremental learning and episodic memory, and specifically tests the idea that the uncertainty associated with each alters the balance between them in a rational way. Using a task that can separate the influence of incremental learning and episodic memory on choice in two large online samples, several lines of evidence supporting this hypothesis are reported. People are more likely to rely on episodic memory in more volatile environments when incremental learning is more uncertain and during periods of increased uncertainty within a given environment. Individuals with more accurate episodic memories are also more likely to rely on episodic memory and less likely to rely on incremental learning. These data are compelling, even more so because all of the main findings are directly replicated in a second sample. These data extend the notion of uncertainty-based arbitration between different forms of learning/memory, which has been proposed and evaluated in other contexts, to the case of episodic memory versus incremental learning.

The weaknesses in the paper are mostly minor. One potential weakness is the nature of the online sample. Many participants apparently did not respond to the volatility manipulation, making it impossible to test whether this altered their choices. It is unclear whether this is a feature of online samples (where people can be distracted, unmotivated, etc.) or of human performance more generally.

Thank you for your comments. Indeed, we also found it interesting that many participants were insensitive to the manipulation of volatility in our study, as assessed and filtered based on the initial deck learning task. As you note, our study is not positioned to determine the cause and whether this is due to the online population or human performance more generally, and we added a discussion of this point to the paper (lines 477-485). Also, fractions exceeding 1/3 apparently inattentive participants are very much the norm in our experience with other online studies across many tasks. While there is much to say about the implications of this (see e.g. Zorowitz, Niv & Bennett PsyArXiv 2021), our basic philosophy (which we follow here) is that it is best practice, and conservative, to exclude aggressively so as to focus analyses on those participants for whom the experimental questions can meaningfully be asked.

Reviewer #3 (Public Review):

The purpose of this work is to test the hypothesis that uncertainty modulates the relative contributions of episodic and incremental learning to decisions. The authors test this using a "deck learning and card memory task" featuring a 2-alternative forced choice between two cards, each showing a color and an object. The cards are drawn from different colored decks with different average values that stochastically reverse with fixed volatility, and also feature objects that can be unfamiliar or familiar. Objects are not shown more than twice, and familiar objects have the same value as they did when shown previously. This allows the authors to construct an index of episodic contributions to decision-making: in cases where the previous value of the object is incongruous with the incrementally observed value, the subject's choice reveals which strategy they are relying on.

The key manipulation is to introduce high- and low- volatility conditions, as high volatility has been shown to induce uncertainty in incremental learning by causing subjects to adopt an optimal low learning rate. The authors find that the subjects show a higher episodic choice index in the high-volatility condition, and in particular immediately after reversals when the model predicts uncertainty is at a maximum. The authors also construct a trial-wise index of uncertainty and show that episodic index correlates with this measure. The authors also find that at the subject level, the overall episodic choice index correlates with the ability to accurately identify familiar objects, and the reason that this indicates higher certainty in episodic memory is predicting the usage of episodic strategies. The authors replicate all of their findings in a second subject population.

This is a very interesting study with compelling results on an important topic. The task design was a clever way to disentangle and measure different learning strategies, which could be adopted by others seeking to further understand the contributions of different strategies to decision-making and its neural underpinnings. The article is also very clearly written and the results clearly communicated.

A number of questions remain regarding the interpretation of the results that I think would be addressed with further analysis and modeling.

At a conceptual level, I was unsure about the equivalence drawn between volatility and uncertainty: the main experiments and analyses all regard reversals and comparisons of volatility conditions, but the conclusions are more broadly about uncertainty. Volatility, as the authors note, is only one way to induce uncertainty. It also doesn't seem like the most obvious way to intervene on uncertainty (eg manipulated trial-wise variance seems more obvious). The trial-wise relative uncertainty measurements in Fig 4 speak a bit more to the question of uncertainty more generally, but these were not the main focus and also do not disambiguate between trial-wise uncertainty derived from reversals versus within block variation.

Thank you for your comments. We agree that this distinction was unclear and appreciate the opportunity to clarify. We hope the manuscript is now clear about the conceptual distinction between uncertainty as the construct of theoretical interest vs. volatility as the operational manipulation being used to access it. We have adjusted the presentation and added discussion to clarify this, and also enhanced the trial-wise analyses to strengthen the interpretation of results in terms of uncertainty more generally. Regarding obviousness, we think perhaps there is a difference between areas of study on this point. While trial-wise outcome variance (which we call stochasticity) has been widely used to manipulate uncertainty in perceptual and sensorimotor studies, it has been more rarely manipulated in reward learning studies, where instead the volatility manipulation we use has predominated. We have a recent paper reviewing examples of both and arguing that the field has underemphasized the importance of stochasticity, so we are sympathetic here (Piray and Daw, Nature Communications 2021).

In any case, to address these points on revision, we have reframed the first section of the results, where we look at effects of environment on episodic-based choice, to focus primarily on volatility. Specifically, we have expanded on our explanation of how volatility induces uncertainty, changed the subtitle of the section from ‘uncertainty’ to ‘volatility’, and have specified that the prediction in this section is primarily about volatility (lines 97 and 116-123). We also reframed the second section of the results to be primarily about the uncertainty induced by volatility: while differences between the environments capture coarse effects of volatility, trialwise uncertainty should be present following reversals across both environments. We have now focused our explanation in this section on trial-wise uncertainty within the environments rather than volatility between the environments (lines 184-192). Further, we agree that there are other sources of uncertainty besides volatility that we did not manipulate in the paper, and that it remains for future work whether their manipulation would produce similar results. To amend this, we have added a new paragraph to the discussion covering these alternative sources and further qualifying the scope of our conclusions (lines 434-446).

We also agree that our analyses in Figure 4 did not yet speak to differences in episodic-based choice that may arise due to blockwise volatility (as captured by the categorical effect of environment) vs. trial-to-trial fluctuations in uncertainty (as captured by relative uncertainty, over and above the blockwise effect). We have addressed this by adding an additional, separate effect of the interaction between environment and episodic value to our combined choice models which is explained in more detail in the recommendations for the authors portion of our response. These changes and results are described in the Methods (lines 686-694) and Results (lines 276-277; Figure 4C).

Another key question I had about design choice was the decision to use binary rather than drifting values. Because of this, the subjects could be inferring context rather than continuously incrementing value estimates (eg Gershman et al 2012, Akam et al 2015): the subjects could be inferring which context they are in rather than tracking the instantaneous value + uncertainty. I am not sure this would qualitatively affect the results, as volatility would also affect context confidence, but it is a rather different interpretation and could invoke different quantitative predictions. And it might also have some qualitative bearing on results: the subjects have expectations about how long they will stay in a particular environment, and they might start anticipating a context change after a certain amount of time which would lead to an increase in uncertainty not just immediately after switches, but also after having stayed in the environment for a long period of time. Moreover, depending on the variance within context, there may be little uncertainty following context shifts.

Thank you for raising this important point. To address the possibility that the task structure could have encouraged participants to infer context rather than engage in incremental learning, we added an alternative contextual inference (CI) model, based on a hidden Markov model with two hidden states (e.g. that either the red deck is lucky and the blue deck unlucky or vice versa). This model is now described in the Results of the main text (lines 226-228), listed in the Methods (line 674), and explained in detail in Appendix 3 alongside the computational models of incremental learning. Following model comparison, we found that this model provided a worse fit than the incremental learning models we previously presented in both samples, suggesting that incremental learning is a better descriptor of participants’ choices in this task than contextual inference. The results of this comparison are reflected in an updated Figure 3A.

Author Response

Reviewer #1 (Public Review):

The study by Xie et al., investigates whether the entorhinal-DG/CA3 pathway is involved in working memory maintenance. The main findings include a correlation between stimulus and neural similarities that was specific for cued stimulus and entorhinal-DG/CA3 locations. The authors observed similar results (cuing and region specificity) using inverted encoding modeling approach. Finally, they also showed that trials in which participants made a smaller error showed a better reconstruction fidelity on the cued side (compared to un-cued). This effect was absent for larger-error trials.

The study challenges a widely held traditional view that working memory and episodic memory have largely independent neural implementations with the MTL being critical for episodic memory but not for working memory. The study adds to a large body of evidence showing involvement of the hippocampus across a range of different working memory tasks and stimuli. Nevertheless, it still remains unclear what functions may hippocampus play in working memory.

We thank the reviewer’s positive appraisal of the current research, which adds to the growing research interest in the MTL’s contribution to WM.

Reviewer #2 (Public Review):

Xie et al. investigated the medial temporal lobe (MTL) circuitry contributions to pattern separation, a neurocomputational operation to distinguish neutral representations of similar information. This presumably engages both long-term memory (LTM) and working memory (WM), bridging the gap between the working memory (WM) and long-term memory (LTM) distinction. Specifically, the authors combined an established retro-cue orientation WM task with high-resolution fMRI to test the hypothesis that the entorhinal-DG/CA3 pathway retains visual WM for a simple surface feature. They found that the anterior-lateral entorhinal cortex (aLEC) and the hippocampal DG/CA3 subfield both retained item-specific WM information that is associated with fidelity of subsequent recall. These findings highlight the contribution of MTL circuitry to item-specific WM representation, against the classic memory models.

I am a long-term memory researcher with expertise in representational similarity analysis, but not in inverted encoding modeling (IEM). Therefore, I cannot verify the correctness of these models and I will leave it to the other reviewers and editors. However, after an in-depth reading of the manuscript, I could evaluate the significance of the present findings and the strength of evidence supporting these findings. The conclusions of this paper are mostly well supported by data, but some aspects of image acquisition and data analysis need to be clarified.

We thank the reviewer for positive appraisal of the current study.

I would like to list several strengths and weaknesses of this manuscript:

Strengths:

• Methodologically, the authors addressed uncertainty in previous research resulting from several challenges. Namely, they used a high-resolution fMRI protocol to infer signals from the MTL substructures and an established retro-cue orientation WM task to minimize the task load.

• The authors selected a control ROI - amygdala - irrelevant for the experimental task, and at the same time adjacent to the other MTL ROIs, thus possibly having a similar signal-to-noise ratio. The reported effects were observed in the aLEC and DG/CA3, but not in the amygdala.

• Memory performance, quantified as recall errors, was at ceiling - an average recall error of 12 degrees was only marginally away from the correct grating towards the closest incorrect grating (predefined with min. 20 degrees increments). However, the authors controlled for the effects of recall fidelity on MTL representations by comparing the IEM reconstructions between precise recall trials and imprecise recall trails (resampled to an equal number of trials). The authors found that precise recall trails have yielded better IEM reconstruction quality.

• The author performed a control analysis of time-varying IEM to exclude a possibility that the mid-delay period activity in the aLEC-DG/CA3 contains item-specific information that could be attributed to perceptual processing. This analysis showed that the earlier TR in the delay period contains information for both cued and uncued items, whereas the mid-delay period activity contains the most information related to the cued, compared to uncued, item.

We thank the reviewer for highlighting the multiple strengths of the current study.

Weaknesses:

• The authors formulate their main hypothesis building on an assumption related to the experimental task. This task requires correctly selecting the cued grating orientation while resisting the interference from internal representations of the other orientation gratings. The authors hypothesize that if this post-encoding information selection function is supported by the MTL-s entorhinal-DG/CA3 pathway, the recorded delay-period activity should contain more information about the cued item that the uncued item (even if both are similarly remembered). Thus, the assumption here is that resolving the interference would be reflected by a more distinct representation in MTL for the cued item. Could it be the opposite, namely the MTL could better represent the unresolved interference, for example by the mechanism of hippocampal repulsion (Chanales et al., 2017). It could strengthen the findings if the authors comment on the contrary hypothesis as well.

We thank the reviewer for pointing out this interesting alternative hypothesis. Because of the different task design (e.g., over the course of learning vs. WM) and stimuli (e.g., spatial memory vs. orientation grating), it is hard to directly compare Chanales et al.’s findings with the current results. That said, we think the idea that the representation of similar information would lead to greater task demand on the MTL is consistent with our intuition regarding the role of the MTL in supporting the qualitative aspect of WM representation. We have now further discussed this issue in our revised manuscript to invite further consideration of the suggested alternative hypothesis,

“Our data suggest that this process would result in more similar and stable representations for the same remembered item across trials, as detected by multivariate correlational and decoding analyses in the current study. However, under certain task conditions (e.g., learning spatial routes in a naturalistic task over many repetitions), the MTL may maximally orthogonalize overlapping information to opposite representational patterns (hence “repulsion”) to minimize mnemonic interference (Chanales et al., 2017). It remains to be determined how these learning-related mechanisms in a more complex setting are related to MTL’s contributions to WM of simple stimulus features.”

• It is not clear for me why the authors chose the inverted encoding modelling approach and what is its advantage over the others multivoxel pattern analysis approaches, for example representational similarity analysis also used in this study. How are these two complementary? Since the IEM is still a relatively new approach, maybe a little comment in the manuscript could help emphasizing the strength of the paper? Especially that this paper is of interest to researchers in the fields of both working memory and long-term memory, the latter being possibly not familiar with the IEM.

We thank the reviewer for this suggestion. In principle, the IEM is a multivariate pattern classification analysis based on an encoding model. There is no fundamental difference between this approach and other machine-learning or classification approaches, except that the IEM is a more model-based approach and therefore can be more computationally efficient (see Xie et al., 2023 for a conceptual overview for multivariate analysis of high-dimensional neural data). The relationship between IEM and representational similarity is grounded in item-specific information that could lead to shared neural variance. How these two analyses are complimented each other is well characterized by a recent theoretical review (Kriegeskorte & Wei, 2021). The rationale is that trial-wise RSA reveals shared neural variance between items, implying the presence of item-specific information in the recorded neural data. And the IEM approach or other classification algorithms can more directly test this item-specific information under a prediction-based framework (e.g., train the data and test on a hold-out set). As a result, the findings of these two methods are correlated at the subject-level (Figure S4), which is important to note for the purpose of analytical reliability. Furthermore, using the IEM also allows us to compare our current findings with that from the previous research (Figure S3), addressing some replicability questions in the field (e.g., Ester et al., 2015).

We have clarified more on this issue in the paragraph when we first introduce IEM,

“To directly reveal the item-specific WM content, we next modeled the multivoxel patterns in subject-specific ROIs using an established inverted encoding modeling (IEM) method (Ester et al., 2015). This method assumes that the multivoxel pattern in each ROI can be considered as a weighted summation of a set of orientation information channels (Figure 3A). By using partial data to train the weights of the orientation information channels and applying these weights to an independent hold-out test set, we reconstruct the assumed orientation information channels to infer item-specific information for the remembered item – operationalized the resultant vector length of the reconstructed orientation information channel normalized at 0° reconstruction error (Figure S2). As this approach verifies the assumed information content based on observed neural data, its results can be efficiently computed and interpreted within the assumed model even when the underlying neuronal tuning properties are unknown (Ester et al., 2015; Sprague et al., 2018). This approach, therefore, complements the model-free similarity-based analysis by linking representational geometry embedded in the neural data with item-specific information under a prediction-based framework (Kriegeskorte and Wei, 2021; Xie et al., 2023). Based on this method, previous research has revealed item-specific WM information in distributed neocortical areas, including the parietal, frontal, and occipital-temporal areas (Bettencourt and Xu, 2015; Ester et al., 2015; Rademaker et al., 2019; Sprague et al., 2016), which are similar to those revealed by other multivariate classification methods (e.g., support vector machine, SVM, Ester et al., 2015). We have also replicated these IEM effects in the current dataset (Figure S3).”

Overall, this work can have a substantial impact of the field due to its theoretical and conceptual novelty. Namely, the authors leveraged an established retro-cue task to demonstrate that a neurocomputational operation of pattern separation engages both working-memory and long-term memory, both mediated by the MTL circuitry, beyond the distinction in classic memory models. Moreover, on the methodological side, using the multivariate pattern analyses (especially the IEM) to study neural computations engaged in WM and LTM seems to be a novel and promising direction for the field.

Thanks for the reviewer for this positive appraisal of the current study.

Reviewer #3 (Public Review):

This work addresses a long-standing gap in the literature, showing that the medial temporal lobe (MTL) is involved in representing simple feature information during a low-load working memory (WM) delay period. Previously, this area was suggested to be relevant for episodic long-term memory, and only implicated in working memory under conditions of high memory load or conjunction features. Using well-rounded analyses of task-dependent fMRI data in connection with a straightforward behavioural experiment, this paper suggests a more general role of the medial temporal lobe in working memory delay activity. It also provides a replication of previous findings on item-specific information during working memory delay in neocortical areas.

We thank the reviewer for highlighting the contribution of the current study to fill a gap in the literature.

Strengths:

The study has strengths in its methods and analyses. Firstly, choosing a well-established cueing paradigm allows for straightforward comparison with past and future studies using similar paradigms. The authors themselves show this by replicating previous findings on delay-period activity in parietal, frontal, and occipito-temporal areas, strengthening their own and previous findings. Secondly, they use a template with relatively fine-grained MTL-subregions and choose the amygdala as a control area within the MTL. This increases confidence in the finding that the hippocampus in particular is involved in WM delay-period activity. Thirdly, their combined use stimulus-based representational similarity analysis as well as Inverted Encoding Modeling and the convergence on the same result is encouraging. Finally, despite focusing on the delay period in their main findings, extensive supplementary materials give insight into the time-course of processing (encoding) which will be helpful for future studies.

We thank the reviewer for highlighting multiple strengths of this current study.

Weaknesses:

While the evidence generally supports the conclusions, there are some weaknesses in behavioural data analysis. The authors demonstrated fine stimulus discrimination in the neural data using Inverted Encoding Modeling (IEM), however the same standard is not applied in the behavioural data analysis. In this analysis, trials below 20 degrees and trials above 20 degrees of memory error are collapsed to compare IEM decoding error between them. As a result, the "small recall error" group encompasses a total range of 40 degrees and includes neighbouring stimuli. While this is enough to demonstrate that there was information about the remembered stimulus, it does not clarify whether aLEC/CA3 activity is associated with target selection only or also with reproduction fidelity. It leaves open whether fine-grained neural information in MTL is related to memory fidelity.

We thank the reviewer for this cautious note. As the current task is optimized to reveal the neural representation during visual WM and as our participants are cognitively normal college students, participants’ behavioral performance in the current experiment tends to be very good (Figure 1). This leaves us relatively small variation to further probe the behavioral outcomes of the task. We have recently generalized our findings using intracranial EEG and confirmed that trial-by-trial mnemonic discrimination during a short delay is indeed associated with the fidelity of item-specific WM representation (Xie, Chapeton, et al., in press).

We have further discussed this issue in the revised Discussion,

“… These two approaches are therefore complementary to each other. Nevertheless, these analyses are correlational in nature. Hence, although fine-grained neural representations revealed by these analyses are associated with participants’ behavioral outcomes (Figure 4), it remains to be determined whether the entorhinal-DG/CA3 pathway contributes to the fidelity of the selected WM representation or also to the selection of task-relevant information. Strategies for resolving this issue can involve generalizing the current findings to other WM tasks without an explicit requirement of information selection (e.g., intracranial stimulation of the MTL in a regular WM task without a retro-cue manipulation, Xie et al., in press) and/or further exploring how the frontal-parietal mechanisms related to visual selection and attention interact with the MTL system (Panichello and Buschman, 2021).”

Moreover, the authors could be more precise about the limitations of the study and their conclusions. In particular, the paper at times suggests that the results contribute to elucidating common roles of the MTL in long-term memory and WM, potentially implementing a process called pattern separation. However, while the paper convincingly shows MTL-involvement in WM, there is no comparison to an episodic memory condition. It therefore remains an open question whether it fulfils the same role in both scenarios. Moreover, the paradigm might not place adequate pattern separation demands on the system since information about the un-cued item may be discarded after the cue.

We thank the reviewer for this cautious note. We have now included a more detailed discussion on this issue.

In the Discussion,

“To more precisely reveal the MTL mechanisms that are shared across WM and long-term memory, future research should examine the extent to which MTL voxels evoked by a long-term memory task (e.g., mnemonic similarity task, Bakker et al., 2008) can be directly used to directly decode mnemonic content in visual WM tasks using different simple stimulus features.”

Author Response

Reviewer #2 (Public Review):

In the current manuscript, Feng et al. investigate the mechanisms used by acute leukemia to get an advantage for the access to the hematopoietic niches at the expense of normal hematopoietic cells. They propose that B-ALLs hijack the niche by inducing the downmodulation of IL7 and CXCL12 by stimulating LepR+ MSCs through LTab/LTbR signaling. In order to prove the importance of LTab expression in B-ALL growth, they block LTab/LTbR signaling either through ligand/receptor inactivation or by using a LTbR-Ig decoy. They also show that CXCL12 and the DNA damage response induce LTab expression by B-ALL. They finally propose that similar mechanisms also favor the growth of acute myeloid leukemia.

Although the proposed mechanism is of particular interest, further experiments and controls are needed to strongly support the conclusions.

1/ Globally, statistics have to be revised. The authors have to include a "statistical analysis" section in the Material and Methods to explain how they proceeded and specify for each panel in the figure legend which tests they used according to the general rules of statistics.

We apologize for the lack of details. This has been corrected in the revised manuscript.

2/ The setup of each experiment is confusing and needs to be detailed. Cell numbers are not coherent from one experiment to the other. As an example, there are discrepancies between Fig1 and Fig2. Based on the setup of the experiment in Fig.2 (Injection of B-ALL to mice followed by 2 injections of treatment every 5 days), mice have probably been sacrificed 12-14 days post leukemic cell injection. However, according to Fig.1, B cells and erythroid cells at this time point should be decreased >10 times while they are only decreased 2-4 times in Fig.2. This is also the case in Fig.4B-J or Fig.5D with even a lower decrease in B cells and erythroid cells despite a high number of leukemic cells. Please explain and give the end point for each experiment in each figure (main and supplemental).

We understand the reviewer concern but we’d like point out the following: kinetic experiments such as these were reproduced multiple times in the laboratory. However, when comparing side-by-side experiments performed over the course of several months discrepancies in the exact days when leukemia shuts-down hematopoiesis are bound to happen. This is because there are numerous variables at play that we can minimize to the extent possible, but we cannot completely eliminate. For example, we took all possible steps to work with stable batches of preB-ALL cells. However, it is impossible to be absolutely certain that the batch in one experiment is identical to another experiment. Cells have to be expanded for adoptive transfer, which inevitably carries some variability (all biological systems undergo random mutations, including purchased C57Bl6/J from reputable vendors); slight differences in ALL engraftment (i.e. injection variability) can occur such that kinetics may change by a couple of days, etc. The findings we reported here are highly reproducible: ALL shuts down lymphopoiesis and erythropoiesis acutely, less so myelopoiesis; that LTbR signaling is the major mechanism shutting down lymphopoiesis but not erythropoiesis; that ALLs up-regulate LTbR ligands when compared to non-leukemic cells of the same lineage and at a similar developmental stage; that CXCR4 and DSB pathways both promote lymphotoxin a1b2 expression. The exact kinetics of these experiments will vary, or at least carry a margin of error that is to the best of our capability impossible to eliminate.

3/ To formally prove that the observed effect is really due to LTab/LTbR signaling, the authors must perform further control experiments. LTbR signaling is better known for its positive role on lymphocyte migration. They cannot rule out by blocking LTbR signaling, that they inhibit homing of leukemic cells into the bone marrow through a systemic/peripheral effect, more than through an impaired crosstalk with BM LepR+ cells. They must confirm for inhibited/deficient LTbR signaling conditions, as compared to control, that similar B-ALL numbers home to the BM parenchyma at an early time point after injection. Furthermore, they cannot exclude that the effect on the expression of IL7 (and other genes), and consequently the effect on B cell numbers, is not simply due to the tumor burden. Indeed, B-ALL numbers/frequencies are different between control and inhibited/deficient signaling conditions at the time of analysis. The analyses should thus be performed at similar low and high tumor burden in the BM for both control and inhibited/deficient LTbR signaling conditions.

We performed ALL homing experiments into control and LTbR∆ and found no significant differences in ALL frequency or number in BM 24h after transplantation. These data have been included in Figure 4A.

We also performed experiments to control for the number of ALL cells in the bone marrow. Briefly, we compared the impact of 3 million WT ALLs with that of 3 and 9 million Ltb-deficient ALLs on Il7-GFP expression in BM MSCs. The number of Ltb-deficient ALLs in the BM of mice recipient of 9 million ALLs was equivalent to that of mice that received 3 million WT ALLs 7 days after transplantation. Importantly, Il7 was only downregulated in mice transplanted with WT ALLs. These data have been included in Figure 4R and 4S.

4/ LT/LTbR signaling is particularly known for its capacity to stimulate Cxcl12 expression. How do the authors explain that they see the opposite?

The reviewer is alluding to a well-known role of LTbR signaling as an organizer of immune cells in secondary lymphoid organs such as spleen and lymph nodes, and particularly its role in promoting CXCL13, CCL19, CCL21 production by fibroblastic reticular cells of these organs. Both the B cell follicle and the T-zone do not express CXCL12 abundantly. Furthermore, in the B cell follicle niche, LTbR signaling is critical for the maturation of Follicular Dendritic Cells, yet FDCs hardly produce CXCL12 as well. So, while LTbR is a well-known regulator of cell organization through the production of homeostatic chemokines and lipid chemoattractants, CXCL12 itself is not one of the major chemokines controlled by this pathway. In summary, we do not think our data is in any way incompatible with prior studies on the LTbR pathway, and even if it was, to our knowledge this is the first study on cell-intrinsic effects of LTbR signaling in BM MSCs.

5/ The authors show that CXCL12 stimulates LTa expression in their cell line. They then propose that CXCR4 signaling in leukemic cells potentiates ALL lethality by showing that a CXCR4 antagonist reverses the decrease in IL7 and improves survival of the mice. This experiment is difficult to interpret. CXCL12 has been shown to be important for migration/retention of B-ALL in the BM and the decreased tumor burden is probably linked to a decreased migration more than an impaired crosstalk with LepR+ cells (see also point 3). If CXCL12 increases LTab expression, CXCR4 blockade should do the opposite. This result should be presented. The contradiction is that if B-ALLs induce a decrease in CXCL12 in the BM (in addition to IL7) and that CXCL12 regulates LTab levels, leukemic cells should be exhausted. Similarly, IL7 has been previously shown to stimulate LTab expression and B-ALL cells express the IL7R. Again, a decrease in IL7 should be unfavorable to B-ALL. How do they explain these discrepancies?

We thank the reviewer suggestion of testing the impact of CXCR4 blocking in vivo on LTa1b2 expression. We performed these experiments which have now been included in the revised manuscript (Fig. 5C and 5D). In summary, we observed reduced LTa1b2 on ALLs transplanted into mice treated with AMD3100, a well-known CXCR4 antagonist. These data also show that CXCR4 signaling is not the only mechanism driving LTa1b2. These results further strengthen the main conclusions of the manuscript. Finally, to our knowledge no study has reported Lymphotoxin a1b2 upregulation in B-ALLs by IL-7.

6/ In Supp 4A, RAG-/- mice are blocked at the pro-B cell stage and do not have pre-B cells. Please compare LTa and LTb expression by Artemis deficient pre-B cell to wt pre-B cells. In this experiment, the authors show that similarly to B-ALL artemis-/- pre-leukemic pre-B cells express high levels of LTab and induce IL7 downmodulation. Using mice deficient for LTbR in LepR+ cells, they show that IL7 expression is increased. However, in opposition to leukemic cells (see Figure 4F), pre-leukemic cells are increased in absence of LTab/LTbR signaling. Please explain this discrepancy. The authors use only one B-ALL model cell line for their demonstration (BCR-ABL expressing B-ALL). Another model should be used to confirm whether LTab/LTbR signaling does favor leukemic/pre-leukemic B cell growth.

We apologize for the confusion. The mice that were used in this study were initially described by Barry Sleckman and colleagues (Bredemeyer et al. Nature 2008). Briefly, they crossed Artemis-deficient mice with VH147 IgH transgenic and EμBcl-2 transgenic mice to generate mice in which B cell development is arrested at the preB cell stage. The Vh147 heavy chain allows their development to the pre-BCR+ preB cell stage but Artemis deficiency prevents Rag protein re-expression and hence B cell can’t recombine light chain genes. The EμBcl-2 transgene allows preB cells to survive despite carrying unrepaired double-strand DNA breaks (DSB).

Regarding the discrepancy noted by the reviewer we argue that this is not a discrepancy. While ALLs can grow in vitro and in vivo in the absence of IL7, non-leukemic developing B cells are strictly IL7 dependent. PreB cells carrying unrepaired DSBs still express IL7 receptor and although no data is currently available on whether these cells are also IL7-dependent, we speculate that they are. Because up-regulation of Lymphotoxin a1b2 in preB cells carrying unrepaired DSBs promotes IL7 downregulation we speculate that this mechanism may contribute to the efficient elimination of pre-leukemic preB cells in vivo. We revised the manuscript to include this explanation of the mouse model and discussion on how we think the LTbR pathway may play a role in pre-leukemic states.

Finally, the data presented in this study includes two distinct leukemia mouse models. It also includes data from human B-ALL and AML samples that is in agreement with the mouse data presented here. We respectfully disagree with the reviewer that a third model is needed to confirm a role for the LTa1b2/LTbR pathway in leukemia.

7/ Pre-B cells are composed of large pre-B cells (pre-BCR+) and small pre-B cells (pre-BCR-). BCR-ABL B-ALL cells express the pre-BCR. What is the level of expression of LTa and LTb by each of these 2 subsets as compared to BCR-ABL B-ALL?

This is a misconception. The difference between large and small preB cells is simply that large preB cells are in S/G2 phase of the cell cycle. Their increased size is a mere consequence of doubling DNA, protein, membrane content, etc.

Author Response

Reviewer #1 (Public Review):

It is a strength of the current manuscript that it provides a near-complete picture of how the metamorphosis of a higher brain centre comes about at the cellular level. The visualization of the data and analyses is a weakness.

I do not see any point where the conclusions of the authors need to be doubted, in particular as speculations are expressly defined as such whenever they are presented.

The fact that molecular or genetic analyses of how the described metamorphic processes are organized are not presented should, I think, not compromise enthusiasm about what is provided at the cellular level.

We appreciate the comments and guidance that Reviewer #1 has given us on data presentation. We have tried to simplify figures and make the images larger. For the developmental figures, a couple of illustrative examples are provided in the main figure with the remainder given in “figure supplements”

Reviewer #2 (Public Review):

This very nice piece of work describes and discusses the developmental progression of larval neurons of the mushroom body into those in the adult Drosophila brain. There are many surprising findings that reveal a number of strategies for how brain development has evolved to serve both the early functions specific to the larval brain and then their eventual roles in the adult brain. I think it is fascinating biology and I was educated while reviewing the paper.

Line 115-116. 'Output from PPL1 compartments direct avoidance behavior, while that from PAM compartments results in attraction'. This is not correct and is actually reversed. The learning rule is depression so that aversive learning reduces the drive to approach pathways whereas appetitive learning reduces the drive to avoidance pathways. This should be corrected and reference made to studies demonstrating learning-directed depression.

Line 222. It provides feed-forward inhibition from y4>2>1. I could be wrong but I'm not aware that there is functional evidence for this glutamatergic neuron being inhibitory. It's currently speculation.

We have noted that this function was proposed by Aso et al.

Line 242. I think it would be nice if the authors focused on extreme changes and showed larger and nicer images. The rest can be summarized but why not pick a few of the best examples to illustrate the strategies they consider in the discussion?

We have reduced the number of neurons shown in the new Figs 5 and 6. Hopefully, the images are now large enough to appreciate. Data for the remaining neurons are now in Figure Supplements for Figs 5 and 6.

Line 249 'became sexually dimorphic'. I may have missed it somewhere but this immediately made me think about the sex of all the images that are shown. Is this explicitly stated somewhere? Was it tracked in all larvae, pupae, and adults?