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Manuscript number: RC-2025-03130

Corresponding author(s): Ellie S. Heckscher

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

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1. General Statements [optional]

We thank all three reviewers for their feedback on the paper. Reviewers stated that the paper was of broad interest to developmental biologists and neurobiologists. However, we want to ensure that our two key conceptual contributions are clear. We clarify in the following paragraph and include a revised abstract. We will update the introduction and paper to better reflect these advances. We also attach a supplemental table 1, which was inadvertently omitted from the previous submission due to our error.

The first advance is that serially homologous neuroblasts follow a multimodal production model: In principle, stem cells can divide any number of times, from once to throughout the entire lifetime of the animal. And, on each division, a stem cell can generate either a proliferative daughter cell or a post-mitotic neuron. Together, therefore, there is a vast potential number of neurons any given stem cell could produce. From the literature on the vertebrate neocortex, we had the following models: (1) "random production" model, in which any number of neurons could be made by a stem cell; or (2) "unitary production" model, in which the same number of neurons (~eight) is produced by a stem cell regardless of context. Our data revealed an entirely new "multi-modal production" model, which could not have been predicted by prior literature. In the context of serially homologous neuroblasts arrayed along the Drosophila larval body axis, sets of five to seven neurons are produced in increments of one, two, or four. These increments correspond to units called temporal cohorts. Temporal cohorts are lineage fragments, or small set of neurons that share synaptic partners, making them lineage-based units of circuit assembly. Thus, in a multimodal production model, serially homologous stem cells produce different numbers of temporal cohorts depending on location. Our data advance the field by showing that stem cells produce circuit-relevant sets of neurons by adding or omitting temporal cohorts from a region, to meet regional needs.

Key to understanding the second advance is that there are multiple types of temporal cohorts: early-born Notch OFF, early-born Notch ON, late-born Notch OFF, and late-born Notch ON. One temporal cohort type, the early-born Notch OFF, is found in every segment, which we term the "ubiquitous" temporal cohort. The other temporal cohort types can be produced in various combinations depending on the stem cell division pattern and segmental location. In a result that could not have been predicted, we found that the ubiquitous temporal cohorts are refined both in terms of the number of neurons and their connectivity, depending on body region. In contrast, when other temporal cohort types are produced, they are not refined to the same degree.

The impact of this work is to advance how we think about stem cell-based circuit assembly.

2. Description of the planned revisions

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

*Summary: The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. *

Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

• *Thank you! In addition to the contributions highlighted by the reviewer, we also showed that all segments have ELs with early-born molecular identities, but only a subset have ELs with late-born identities (Figure 5). And we showed that early-born temporal cohorts can be mapped into different circuits depending on the axial region (Figure 6).

*Major comments: The authors performed careful analyses of the NB3-3 lineage using EL neurons. My main concerns are limited applicability of their findings and lack of mechanisms as how NB3-3 generate various numbers of EL neurons. Their findings are exclusively relevant to the NB3-3 lineage despite their effort in highlighting that other NB lineages also generate temporal cohorts of EL neurons. *

  Thank you for raising these points. First, to clarify, as Reviewer 4 also mentioned, NB3-3 is the only lineage to produce EL neurons. We will ensure that this is clearly stated in the revised text.

We agree that our findings might not apply beyond the NB3-3 lineage. However, as this is the first study of its kind, it is impossible to know a priori to what extent the concepts surfaced here are generalizable. In our opinion, this speaks to the novelty and impact of the study. A contribution is to motivate a need for future studies. We will make this explicit in our updated manuscript in the Discussion section.

  Our manuscript provides cell biological mechanisms that explain how stem cells give rise to different numbers of EL neurons in different regions, including stem cell division duration and type, neural cell death, identity gene expression, and differentiation state. If the reviewer is interested in genetic or molecular mechanisms, this is an interesting point. Several prior studies using NB3-3 as a model (e.g., Tsuji et al., 2008, Birkholz et al., 2013, Baumgardt et al., 2014) have elucidated the genetic regulation of specific cell biological processes. However, these studies provided fragmentary insight with regard to serially homologous stem cell development along the body axis. A comprehensive understanding of how the NB3-3 lineage, or any other serially homologous lineage, develops was missing. This is what makes our study both novel and needed. Without an analysis that both examines every segment and assays multiple cell biological processes, we would have missed key insights: that there is a ubiquitous type of temporal cohort, and that neurons within the ubiquitous temporal cohort are selectively refined post-mitotically (See General Statements for more details).

*I disagreed with their conclusion that failure to express Eve as a mechanism for controlling EL neuron numbers when Eve serves as the marker for these neurons. Are there any other strategy to assess the fates and functions of these cells beside relying solely on Eve expression? I am not familiar with the significance of Eve expression on the functions of these neurons. Is it possible to perform clonal analyses of NB3-3 mutant for Eve and see if these neurons adopt different functionalities/identities? *

• We agree that if Eve were only a marker, our logic would be circular. The Eve homolog, Evx1/2 is crucial for vertebrate interneuron cell fate (Moran-Rivard et al., 2001). Eve is essential for motor neuron morphology in Drosophila *(Fujioka et al., 2003). Eve is critical in Even-skipped for both the morphology and function of Even-skipped interneurons (Marshall et al., 2022). Hence, ELs cannot fully differentiate or incorporate into circuits without Eve. Thus, we use the failure to express Eve as a mechanism for controlling EL number. Furthermore, our prior study (Wang et al., 2022) showed that NB3-3 Notch OFF neurons in A1 that fail to express Eve have small soma and "stick-like" neurite projections that are typical of undifferentiated neurons. We will be sure to add this context to the revised manuscript.

*If NB3-3 in the SEZ continually generate GMCs based on the interpretation of clonal analyses and depicted in Fig. 2A, why is the percent of clones that are 1:0 virtually at or near 100% from division 6-11 shown in 2G? *

Admittedly, the ts-MARCM heat-shock-based lineage tracing experiments are inherently messy. This is part of the reason why we included the G-TRACE lineage tracing experiments in Figure 3. In Figure 3E, one can see that the number of Notch ON/A neurons in SEZ3 is equal to the number of ELs in that segment (Figure 1E). This is a second independent method that supports the assertion that in SEZ, NB3-3 stem cells continually generate GMCs. Given this independent observation, it leads us to believe that this question is most likely explained by technical issues inherent in ts-MARCM. These issues include but are not limited to: cell-type specific accessibility/success of heat-shock induced recombination; variably effective RNAi; and idiosyncrasies of the EL-GAL4 line used to detect recombination events. If the question is why the data is only reported for division 6-11, the answer is that the ts-MARCM dataset, which included SEZ clones only used later heat-shock time points (line from the paper "for the SEZ-containing dataset, inductions started at NB3-3's 5th division"). Along with this revision plan, we will include Supplemental Table 1, which was inadvertently omitted from the previous submission due to our error. This table shows all of the clonal data. We will include a section in the discussion to describe limitations in ts-MARCM.

The authors also indicate that NB3-3 in the abdomen directly generate Notch OFF/B cells that assume EL neuronal identity. In this scenario, shouldn't the percent of 1:0 clones be 100% in later divisions in Fig. 2G? Based on the number of clones in abdomen shown in Fig. 2E, I cannot seem to understand how the authors come to the percent of 1:0 clones shown in Fig. 2G

  We agree that one might expect the 12th division to be 100% 1:0 clones in the abdomen. Unfortunately, we didn't sample that late in our dataset, and even when we sampled the inferred 11th division, we had a small sample size (Figure 2E). Other studies suggest that NB3-3 in the abdomen directly generates Notch OFF/B neurons (Baumgardt et al., 2014), which served as our starting point. We will revise the text to make this clearer. As you can see from Figure 3E, there is only one NB3-3 Notch ON/ A neuron produced in each abdominal segment in comparison to the number of NB3-3 Notch OFF/B/EL neurons (Figure 1E). According to two independent assessments, Figure 3 and Baumgardt et al., 2014, the data support the conclusion that NB3-3 in the abdomen directly generates Notch OFF/B cells that assume EL identity for all but one of their divisions. Again, we believe technical issues make the ts-MARCM dataset messy. We will include a section in the discussion to describe limitations in ts-MARCM.

*There are many potentially interesting questions related to this study that can significantly broaden the impact of this study. For example, are other NB lineages that also generate distinct temporal cohorts of EL neurons display similar proliferation patterns (type 1 division in SEZ, early termination of cell division in thoracic segments and type 0 division in abdomen)? *

• *NB3-3 is the only lineage that makes ELs; Many lineages switch proliferation fates along the body axis. Previous studies have described how this switch in division patterns produces the wedge-shaped CNS: Cobeta et al., 2017. In the revision, we will be sure to clarify both points.

*Why does NB3-3 in the thoracic segment become quiescence so much sooner than SEZ and abdominal segments? *

• *NB3-3 in the thorax enters quiescence due to Hox genes and temporal transcription factors (Tsuji et al., 2008). In the revision, we will be sure to clarify this point.

The authors' observations suggest that NB3-3 in SEZ and abdomen generate a similar number of EL neurons despite the difference in their division patterns (type 1 vs type 0). Are the mechanisms that promote EL neuron generate in NB3-3 in SEZ and abdomen the same? Anything else is known beside Notch OFF?

• We agree this is an interesting point. Previous work has detailed NB3-3 division patterns, showing Type 1 divisions in the thorax, and Type 1 to Type 0 switch in the abdomen (Baumgardt et al., 2014). However, the proliferation pattern of NB3-3 in the SEZ had not been addressed until our study. Figures 2 and 3 suggest the following (1) SEZ proliferates for the duration of embryonic neurogenesis; (2) It produces a GMC on each division; (3) the GMC divides to produce one EL Notch OFF neuron and one Notch ON neuron. In our revision, we will manipulate the Notch pathway using two mutants, sanpodo, which produces two Notch OFF cells, and numb*, which produces two Notch ON cells (Skeath et al., 1998), to specifically test how ELs in the SEZ are regulated by Notch signaling. The other difference we know of between the SEZ, and abdomen is Hox gene expression. In Figure S2, we show that a subset of ELs in the SEZ express the anterior Hox genes, Sex combs reduced (Scr). The role of Hox genes in this lineage is an interesting question, as addressed in the discussion. This is an important future direction that merits in-depth study and is beyond the scope of what of this study is trying to accomplish.

Minor commentsThe authors' writing style is highly unusual especially in the result section. There is an overwhelming large amount of background information in the result section but very thin description on their observations. The background information portion also includes previously published observations. Since the nature of this study is not hypothesis-driven, it is very confusing to read in many places and difficult to distinguish their original observations from previously published results and making. One easily achievable improvement is to insert relevant figure numbers into the text more often.

Thank you for this comment. It is invaluable. In the revision, we will expand the background into a more comprehensive introduction and present the results more clearly. We will certainly insert relevant figure numbers. In responding to the reviewer's comments above, we can see where our writing lacked clarity and will improve these areas. Thank you again.

Reviewer #1 (Significance (Required)):

The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

Because this text is the same as the summary, please see our response to that section.

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

In this manuscript, Vasudevan et al provide a detailed characterisation of the different numbers and temporal birthdates of Even-skipped Lateral (EL) neurons produced at in different segments from the same neuroblast, NB3-3. The work highlights the differences in EL neuronal generation across segments is achieved through a combination of different division patterns, failure to upregulate EL marker Eve and segment-specific program cell death. For neurons born within the same window and segment, the authors describe additional heterogeneity in their circuit formation. The work underscores the large diversity that the same neuroblast can generate across segments.

Thank you!

Major comments:

- Based on the ts-MARCM 1:0 clones representing 100% of the SEZ clones at any given inferred cell division, the authors conclude "NB3-3 neuroblasts generate proliferative daughter GMCs in the SEZ and thorax on most divisions". Figure 2G does not have any data for SEZ before inferred division 5, whereas there is data in other regions. The authors also state "In the SEZ and abdomen, ELs were labelled regardless of induction time." In reference to Fig 2F, which seems inaccurate given there are no SEZ clones before inferred division 5. There is no comment on this fact, which is surprising give their focus on temporal cohorts. The authors should explain this discrepancy, if known, or modify their statements to reflect the data.

• *Thank you for raising this point. The reason is because we produced two ts-MARCM datasets. One had SEZ clones, the other did not. The dataset with SEZ clones used heat shock protocols only for later time points, because those were most informative. The text from the paper is "We combined a published ts-MARCM (Wang et al., 2022) dataset with a new one (Table S1). The differences between the datasets are (1) CNSs were imaged either at low resolution for all regions (SEZ to terminus) or higher resolution for nerve cords (thorax to terminus); (2) for the SEZ-containing dataset, inductions started at NB3-3's 5th division. The combined data includes ~12 different heat shock protocols, 80 CNS, and 234 clones (Table S2)". In response to this comment, however, we will further clarify this point. In addition, we are submitting Supplemental table 1, which contains all the clonal data, as you can see experiments a-h lack SEZ data and experiments i-k contain SEZ data.

- The temporal cohort (early-born vs late-born) identity is exclusively examined based on markers. Given the absence of SEZ clones from early NB3-3 divisions, a time course showing that the SEZ generate early-born Els or some other complementary method would be desirable.

Thank you for raising this point. We show early-born versus late-born identity using markers in Figure 5. We conducted the time-course experiment as suggested and can confirm that there are early-born ELs in the SEZ at stage 13. We will include a new Supplemental Figure that includes a time course of EL number at stages 11, 13, 15, and 17 for segments SEZ3 to Te2 in the revision. See figure below.

- The authors repeatedly refer to their work as showing how a stem cell type can have "flexibility". Flexibility would imply that NB3-3 from one segment could adopt a different behaviour (different division pattern, or cell death or connectivity) if it were placed in a different segment. This is not what is being shown. In my opinion, "heterogeneity" of the same neuroblast across different segments would be more appropriate.

• *Thank you for this comment. We will change the wording to heterogeneity in the revision.

Minor comments:

- Figure 2A depicts a combination of known data and conclusions from their own (mainly SEZ). The authors might consider editing the figure to highlight what is new. A possibility would be for figure A to be a diagram of the experimental design and their summary division pattern to be shown after the new data instead of being panel A.

Thank you for this suggestion. We will make the suggested change.

- The authors state that they combined published ts-MARCM with their new one, which differed in a number ways that they list, but they don't specify which limitations are associated with the published vs new dataset. Could the authors please clarify?

  We now include Supplemental Table 1, which shows the complete combined datasets. In the first dataset, experiments a-h, the CNS was imaged at high resolution, but in a smaller region. The limitation is that the SEZ is missing. In the second dataset, i-k, inductions started at NB3-3's 5th division. The limitation is that we fail to sample early time points. This was a strategic decision. There were two possible scenarios: (1) in the SEZ, NB3-3 divided early, made GMCs, but both daughters expressed Eve. (2) in the SEZ, NB3-3 divided for the entirety of the embryonic neurogenesis, making GMCs, with only the Notch OFF daughters expressing Eve-our data support (2). Only late heat shocks were needed to distinguish between these possibilities. As these experiments are labor-intensive, we focused our efforts on the later time points. We will make this clearer in our revised text.

- The title refers exclusively to "temporal cohorts", which in the manuscript are defined quite narrowly and do not seem to apply to all segments.

• *Thank you! This, in our opinion, is a central, not a minor point to raise, because the impact of this study involves temporal cohort biology. We outlined the essential concepts in Part 1 "general statements" section of this revision plan. We did not mean to use "temporal cohort" in a limited sense, and we can see how the writing of our results section led to this comment. We will revise to make this clear.

- Several cited references are missing from the Reference list at the end. Could the authors please double check this? (e.g. Matsushita, 1997; Sweeney et al., 2018)

• *Thank you, we will remedy this!

- Legend for figure 2 is a bit confusing, there is a "(A)" within the legend for (D), which indicates that segments A1-A7 are shown (this seems inaccurate, as it only goes to A6).

Thank you, we will remedy this!

Reviewer #3 (Significance (Required)):

This study provides a comprehensive analysis of different cell biological scenarios for a neuroblast to generate distinct progeny across repeating axial units. The strength is the detailed and systematic approach across segments and possible scenarios: different division patterns, cell death, molecular marker expression. While it focuses on one specific neuroblast of the ventral nerve cord of Drosophila, the authors have done extensive work to place their findings and interpretation in the context of other cell types and across model organisms both in the introduction and discussion. This makes the work of interest for developmental biologists in general, neurodevelopment research in particular and those interested in circuit assembly, beyond their specialised community. This point of view comes from someone working in vertebrate CNS development.

Thank you!

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

Summary

This manuscript addresses the question of how the number of neurons produced by each progenitor in the nervous system is determined. To address this question the authors use the Drosophila embryo model. They focus on a single type of neural stem cell (neuroblast), with homologues in each hemisegment along the anterior-posterior axis.

Using a combination of clonal labelling, antibody stainings, and blockade of programmed cell death, they provide a detailed description of segment-specific differences in the proliferation patterns of these neuroblasts, as well as in the fate and survival of their neuronal progeny.

Furthermore, by employing trans-synaptic labelling, they demonstrate that neurons derived from the same progenitor type receive distinct patterns of synaptic input depending on their segmental origin, in part due to their temporal window origin.

Overall this work shows that different mechanisms contribute to the final number and identity of the neuronal progeny arising from a single progenitor, even within homologous progenitors along the anterior posterior body axis.

Thank you!

Major Comments

I would suggest adding line numbers to the text for future submissions, this massively helps providing comments.

  Thank you for this comment. We will definitely add line numbers to the revised manuscript. We also thank you for providing comments despite this oversight on our part. We appreciate your time, and did not mean to make extra work.

*The authors propose that all neuroblasts produce the same type of temporal cohort (early born) and that, by changing the pattern of cell division, different temporal cohorts can be added. The way this this presented in the abstract sounds like an obvious thing, what would be the alternative scenario/s? *

  Thank you for raising the point that the abstract should be updated. We have included a revised abstract. The things that are obvious are: (1) changing a neuroblast's division pattern will change the number of neurons produced, and (2) if you have late-born neurons, the stem cell must at some point, have made early-born neurons. However, within those bounds is an extremely large parameter space. Each stem cell can choose to divide or not, and it can also choose to produce a proliferative daughter or not. The stem cell must navigate these choices at every division. The field had two models for what a stem cell might do - a "random production" model and a "unitary production" model. Our data support a third "multimodal production" model, which could not have been predicted based on prior literature or data.

We had raised these points in the discussion as follows-

"Under a null model, the durations and types of proliferation would vary stochastically across segments, resulting in a continuous and unstructured distribution of neuron numbers (Llorca et al., 2019). In a unitary production model, based on the vertebrate neocortex, there is a fixed neurogenic output of ~8-9 neurons per progenitor (Gao et al., 2014). However, our data support a third model, a multimodal production model. In a multimodal model, serially homologous neuroblasts generate different numbers of neurons depending on the segment."

We will now update the text to address this concern.

Here it's the late born neurons that lack in thoracic segments because of early NB quiescence, but it cannot be excluded that different neuroblast types adopt a different strategy.

• *True. Neural development is complex. Other lineages could easily employ alternative strategies. Our study presents a new conceptual framework that should inspire future research.

I found the ts-MARCM results confusing for 2 reasons:

1- It's not clear to me why there are so many single cell clones in div 3 and 4 in abdominal segments. This is not compatible with the division model depicted for abdominal segments, unless GMCs are produced in those division window and the MARCM hits the GMC, as also mentioned in the legend for G. This aspect is important because, either the previous model by Baumgardt et al. - please correct cit. currently Gunnar et al. 2026 - is wrong, or something strange happens in this experiment, or the relative temporal order is incorrect.

Thank you for raising this point. Having multiple single-cell (i.e., 1:0) clones in divisions 3 and 4 is not precisely what would be predicted by the model in Figure 2C. In part because heat-shock-based recombination methods in fly are stochastic and inherently "messy", we also conducted a second set of lineage tracing experiments, as shown in Figure 3, using G-TRACE. Figure 3E shows one Notch ON/A neuron in each abdominal segment, suggesting there is only one GMC present during lineage progression. But Figure 3E's result does not localize the GMC to any particular division. One possibility is that the GMC is generated once, but randomly throughout lineage progression. This possibility is consistent with the idea that the relative temporal order is incorrect and suggests that Baumgardt is erroneous. However, the Baumgardt data are strong, so we do not favor this idea. A second possibility, which we favor, is that something strange happened in this experiment. Here is how we envision the strange occurrence: heterogeneity in the EL driver. Ts-MARCM's recombination timing dictates the upper limit for the number of cells within a clone. However, recombination is detected by GAL4. So, if the GAL4 driver for some reason detects fewer cells than one expects, then one would see unusually small clones as is the case in question. To detect Ts-MARCM recombination in Figure 2, we used the EL-GAL4 driver. The EL-GAL4 driver is an enhancer fragment, ~400KB, meaning that it does not capture the full regulatory context of the eve locus. In our experience (e.g., Manning et al., 2012), drivers using small enhancers tend to give highly-specific, but somewhat variable expression, and this is the case for EL-GAL4 in our experience. We will update the discussion to discuss the ts-MARCM dataset and its limitations. And, we will correct the citation to Baumgardt et al., 2014, not Gunnar. Thank you!

2- In segments other than abdomen, it is quite rare to hit proper clones, it appears that only GMCs are hit by recombination, with very few exceptions. Could the author please provide an explanation for this or at least mention this aspect?

• *This is true. We cannot explain it. It could have something to do with the RNAi cassettes that are used in ts-MARCM, because in the original paper they mention that RNAi can be differently regulated in GMCs versus neuroblasts (Yu et al., 2009). We will mention it in the revised discussion about ts-MARCM limitations.

It is also unclear whether in F the graph includes all types of clones (including 1:0 clones). This is important, because the timing of division for NBs and GMCs is different, and inclusion of 1:0 might lead to a wrong estimate of the NB proliferation window (longer than it actually is because GMCs divide for longer). This is particularly important for the SEZ, where most clones in normalised division 10 and 11 are with ratio 1:0, thus compatible with both terminal division as well as GMC division.

• *The graph in F does include all types of clones. We provide Supplemental Table 1, which shows the full dataset. Unfortunately, we do not have enough data to analyze only NB clones. We agree that the estimate of the NB proliferation window is coarse using this analysis method and could overrepresent the division time by one cell division. We will mention this in the discussion and make sure that our results text is free from any overreaching claims about the precision of these measurements.

To obtain an estimate of the timing of division, the authors normalise clone size to the size of the bigger clone in the abdomen. What happened to those samples where no abdominal clones were hit? Were they simply excluded from the analysis?

  From the analysis in Figure 2, we excluded the clones that were SEZ, thorax, or terminus only. They were rare. They are shown in Supplemental Table 1, which will now be added in our revision plan.

It is proposed that in the thorax late temporal cohort neurons are not produced, yet the ts-MARCM experiment detects some 1:0 clones. What is the fate of these cells? Are they all derived from GMC division and therefore decoupled from the temporal identity window? Or is this a re-activation of division?

Figure 2F shows at the inferred 11th NB3-3 division, 100% of thoracic clones are of the 1:0 type. This is an n=1 observation (Supplemental Table 1, row f-Jan20-2). When we look at the morphology of this thoracic EL, we can see that it is a fully differentiated neuron that crosses the midline and ascends to the CNS, which is similar to EL morphologies in A1, so we don't think it's a whole new cell type. We have no way of determining whether this neuron was derived from a GMC division. It is also possible that this is an infrequent event or a technical anomaly. To address the question of reactivation of the thoracic NB3-3 division, we plan to include a Supplemental Figure of EL number over developmental time (stages 11, 13, 15, 17) for segments SEZ3 to Te2. This is the same data that we mentioned to Reviewer 3. This will reveal the extent to which the thorax produces late-born ELs.

*"in A1, a majority of segments had one Notch OFF/B neuron that failed to label with Eve" does "the majority" in this sentence mean that there were cases where all B neurons were labelled with Eve? If yes, where would this stochasticity come from? *

• • Yes, "the majority" in this sentence means that there were cases where all B neurons were labeled by Eve. In Figure 3F, for segment A1, that number is four. In contrast, there are 6 cases where B neurons failed to label with Eve. We can only speculate about the origin of the stochasticity. It could be biological (e.g., low level of Eve expression) or technical (e.g., poor antibody penetration). We plan to mention this in the discussion.

Additionally, there is no evidence that it's the first born NotchOFF neuron in A1 that does not express Eve. The authors should clarify where this speculation comes from.

• *The evidence that the first-born Notch OFF neuron in A1 does not express Eve comes from our ts-MARCM data: "So far, our ts-MARCM analyses grouped segments into regions (Figure 2A-C), however, EL number varies on a segment-by-segment basis (Figure 1). Therefore, we looked for segment-by-segment differences in ts-MARCM data (Table S1). The only detectable difference was between A1 and the other abdominal segments: When both A1 and another abdominal segment were labeled in a single CNS, a majority had smaller A1 clones. These data suggest that the production of ELs by NB3-3 neuroblasts lags in A1 compared to A2-A7." We will add a representation of these data to the ts-MARCM figure. As we stated above, we will add a Supplemental Figure of EL number over developmental time (stages 11, 13, 15, 17) for segments SEZ3 to Te2, which could strengthen this point.

When discussing trends shared with other phyla:

A- "In the mammalian spinal cord, more neurons are present in regions that control limbs (Francius et al., 2013). Analogously, EL numbers do not smoothly taper from anterior to posterior; instead, the largest number of ELs is found in two non-adjacent regions, SEZ and the abdomen." It's unclear what is the link between the figure in the mammalian spinal cord and the Drosophila embryo. The embryo doesn't even have limbs and the number of neurons measured here refer only to a single lineage, while there could be (and in fact there are) lineage-to-lineage differences that could depict a different scenario.

Thank you for this comment. We will rewrite this sentence, "in the mammalian spinal cord, more neurons are present in regions that control limbs (Francius et al., 2013)" to more accurately reflect the data in the Francius paper, and make the parallel more explicit. We will say "the size of columns of V3, V1, V2a, V2b, and V0v neurons differ at brachial compared to lumbar levels in the developing spinal cord." This removes the confusion about limbs and somewhat mitigates the concern about lineage-to-lineage differences, at least from the perspective of the spinal cord.

B- The parallelism between V1 mouse neurons and EL Drosophila neurons is also unclear to me. The similarity in fold change across segments could be a pure coincidence and, from what I understand, the two cell types are not functionally linked.

  Thank you for this comment. We believe this is the sentence in question (sorry about no line numbers). "(3) In the mouse spinal cord, ~10-fold differences in molecular subtypes for V1 neurons (Sweeney et al., 2018). In *Drosophila*, NB3-3 neuroblasts show differences in EL number, depending on region, with similar fold changes, suggesting this trait is shared across phyla."  The emphasis was intended to be on the fold-changes, not cell types. Coincidence or not, it is parallel. We will update the sentence to say "(3) In the mouse spinal cord, ~10-fold differences in molecular subtypes for V1 neurons (Sweeney et al., 2018). Although V1 neurons are not direct homologs of EL neurons, the number also varies ~10-fold depending on the region. One possibility is that this trait is shared across phyla." And, we will remove the final part of the paragraph, which distracts from the point "Thus, for this study and future research, NB3-3 development now offers a uniquely tractable, detailed, and comprehensive model for studying how stem cells flexibly produce neurons."

Minor comments:

I found the manuscript somewhat difficult to follow, even though I am familiar with both the model and the topic. For non-specialist readers, I expect it will be even more challenging. The presentation of the results often feels fragmented, at times resembling a sequence of brief statements rather than a continuous narrative. I would encourage the authors to provide more synthesis and interpretation, for example by summarising key findings, rather than listing in detail the number of neurons labelled in each segment for every experiment. This would make the results more accessible and easier to digest.

• *Thank you for this comment. We will provide more synthesis and interpretation in results by summarizing key findings.

From the way the MS is written it's not clear from the beginning that the work focuses exclusively on embryonic-born neurons. Since in Drosophila neuronal stem cells undergo two rounds of neurogenesis, one in the embryo and one in the larva, this omission could lead to confusion.

  Thank you for this comment. We will mention this in the abstract, introduction and discussion.

In the abstract, what would be the other temporal cohorts generated in specific regions? (ref to: "In specific regions, NB3-3 neuroblasts produce additional types of temporal cohorts, including but not limited to the late-born EL temporal cohort.")

  In this manuscript, we use lineage tracing to identify four types of temporal cohorts- early-born Notch ON, early-born Notch OFF, late-born Notch ON, and late-born Notch OFF. This is now reflected in the revised abstract. ELs are early-born Notch OFF and/or late-born Notch OFF.

This sentence in the introduction is inaccurate: "The Drosophila CNS is

organized into an anterior hindbrain-like subesophageal zone (SEZ) and a posterior spinal cord-like nerve cord". The anterior hindbrain-like portion of the CNS is in fact the supraesophageal ganglion (or cerebrum), while the SEZ is a posterior-like region.

  Thank you. We will change this sentence to: "The *Drosophila* CNS is

organized into a hindbrain-like subesophageal zone (SEZ) and a spinal cord-like nerve cord".

Fig 1E: the encoding of the significance is not immediately clear. In the legend the 4 stars could also be arranged in the same way for clarity.

• *Thank you. We will change it for clarity.

Fig 2E legend: it is mentioned that B corresponds to a 1:4 clone, however the MARCM example is shown for C and it's a 1:5.

Thank you. We will fix this.

The occurrence of "undifferentiated" neurons in Th segments is in less than 10% of the clones, I wonder if this a stochastic or deterministic event and to what extent small cell bodies could just be the consequence of local differences in tissue architecture.

• Because we are using a stochastic technique, it is difficult for us to determine whether the occurrence of neurons with small somas is a stochastic or deterministic event. Several papers suggest neurons with small axons are found across insect species (Pearson and Fourtner, 1975; Burrows, 1996). Neurons with a small soma and short axons/ axonless are found in the Drosophila embryonic abdominal nerve cord (Lacin et al., 2009). In our unpublished work from the Drosophila* nerve cord at a first instar larval stage, we found small somas with short axons in segment A1 (see Figure 4.6 below). This leads us to believe it is not a consequence of local tissue architecture.

Fig 2I: it's unclear what the purple means (I suppose it might be Eve expression) and why in J there should be one purple cell not labelled by the ts-MARCM when this is not present in H and I.

Purple is Eve. We will add labels for stains used in H and I, and remove the extra purple cell from the illustration in J.

"When synapses do occur, they are numerically similar from segment to segment". It's unclear where the evidence for this statement comes from, please clarify or remove the sentence.

We calibrated our trans-Tango data against available connectomic data using segment A1 as a reference. We learned that the trans-tango method only identifies strongly (>15 synapses) connected neurons.

"First, we calibrated trans-Tango for use in larval Drosophila, focusing on segment A1, where connectome data are available (Wang et al., 2022). In the connectome, of the five early-born ELs in A1, three are strongly connected to CHOs (>15 synapses), two are weakly connected (15 synapses) connected to somatosensory neurons."

  We will modify this sentence to say "when synapses do occur they are of similar strengths from segment to segment"

"In SEZ2, NB3-3 divides 10 times (Figure 2F)". Figure 2F does not support this statement and Figure 7 shows 12 divisions. Possibly SEZ2 and 3 have been inverted in this statement, please clarify.

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

**Referees cross-commenting**

I agree with most of the comments/suggestions provided by the other two reviewers.

In particular:

I agree with reviewer #1's comment about failure to express Eve being a mechanism for controlling neurons number, as this is a circular argument.

• *We address this earlier and direct you to that text. Briefly, Eve is not just a marker, but a key differentiation gene for ELs.

I agree with reviewer #2's concern about the use of the word "flexibility"; "heterogeneity" would be a more appropriate term, as I would associate the word "flexibility" to the ability of a single neuroblast in a single segment to produce neurons with different fates under, for example, unusual growth conditions. Here no genetic/epigenetic manipulations were performed to address flexibility and the observed (stereotypical) differences result from axial patterning.

• *We will change this, thank you.

*As a note, Reviewer #1 asks about other temporal cohorts of EL neurons produced by other lineages, but these neurons are specifically generated from NB3-3. *

• *Thank you for adding this clarification.

To generalise the observations reported in this study, the authors would need to focus on other molecularly defined temporal cohorts or, more generally, on other lineages, which, however, are likely to adopt different combinations of mecahnisms to tune progeny number across segments.

• *We agree that further studies are needed to assess the generalizability of our findings.

Reviewer #4 (Significance (Required)):

In Drosophila melanogaster, the relationship between neural progenitors and their neuronal progeny has been studied in great detail. This work has provided a comprehensive description of the number of progenitors present in each embryonic segment, their molecular identities, the number of neurons they produce, and the temporal transcriptional cascades that couple progenitor temporal identity to neuronal fate.

This work adds to the existing knowledge a detailed characterisation of intersegmental differences in the pattern of proliferation of a single type of neuronal progenitor as well as in post-divisional fate depending on anterior-posterior position in the body axis (i.e. programmed cell death and Notch signalling activation). This is a first step towards understanding the cellular and molecular mechanisms underlying such differences, but it's not disclosing them.

We have disclosed the cellular mechanisms- stem cell division duration and type, neural cell death, identity gene expression, and differentiation state -unless something else is envisaged by this comment. The molecular mechanisms are beyond the scope of this paper.

That homologous neuroblasts can generate variable numbers of progeny neurons depending on their segmental position has been established previously. What this manuscript adds is the demonstration that these differences arise through a combination of altered division patterns and differential programmed cell death, thereby revealing a more complex and less predictable scenario than could have been anticipated from existing knowledge in other contexts. The advance provided by this study is therefore incremental, refining rather than overturning our understanding of how segmental diversity in neuroblast lineages is achieved.

The key conceptual advances provided by this study are described in the General Statements section above. We don't overturn, but we advance the field.

By touching on the general question of how progenitors generate diversity, this work could be of broad interest to developmental neuroscientists beyond the fly field. However, the way it is currently written does not make it very accessible to non-specialists.

Thank you for this comment. We will endeavor to make it more accessible in the revised manuscript. Reviewer 3, an expert in vertebrate neurobiology, agreed that our work was of broad interest.

My expertise: Drosophila neurodevelopment, nerve cord, cell types specification

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

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

With this Revision Plan, we submit a revised abstract, and a supplemental table 1. We plan to address every point raised by the reviewers.

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

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

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript addresses the question of how the number of neurons produced by each progenitor in the nervous system is determined. To address this question the authors use the Drosophila embryo model. They focus on a single type of neural stem cell (neuroblast), with homologues in each hemisegment along the anterior-posterior axis.

Using a combination of clonal labelling, antibody stainings, and blockade of programmed cell death, they provide a detailed description of segment-specific differences in the proliferation patterns of these neuroblasts, as well as in the fate and survival of their neuronal progeny. Furthermore, by employing trans-synaptic labelling, they demonstrate that neurons derived from the same progenitor type receive distinct patterns of synaptic input depending on their segmental origin, in part due to their temporal window origin. Overall this work shows that different mechanisms contribute to the final number and identity of the neuronal progeny arising from a single progenitor, even within homologous progenitors along the anterior posterior body axis.

Major Comments

I would suggest adding line numbers to the text for future submissions, this massively helps providing comments.

The authors propose that all neuroblasts produce the same type of temporal cohort (early born) and that, by changing the pattern of cell division, different temporal cohorts can be added. The way this this presented in the abstract sounds like an obvious thing, what would be the alternative scenario/s? Here it's the late born neurons that lack in thoracic segments because of early NB quiescence, but it cannot be excluded that different neuroblast types adopt a different strategy.

I found the ts-MARCM results confusing for 2 reasons:

1. It's not clear to me why there are so many single cell clones in div 3 and 4 in abdominal segments. This is not compatible with the division model depicted for abdominal segments, unless GMCs are produced in those division window and the MARCM hits the GMC, as also mentioned in the legend for G. This aspect is important because, either the previous model by Baumgardt et al. - please correct cit. currently Gunnar et al. 2026 - is wrong, or something strange happens in this experiment, or the relative temporal order is incorrect.
2. In segments other than abdomen, it is quite rare to hit proper clones, it appears that only GMCs are hit by recombination, with very few exceptions. Could the author please provide an explanation for this or at least mention this aspect? It is also unclear whether in F the graph includes all types of clones (including 1:0 clones). This is important, because the timing of division for NBs and GMCs is different, and inclusion of 1:0 might lead to a wrong estimate of the NB proliferation window (longer than it actually is because GMCs divide for longer). This is particularly important for the SEZ, where most clones in normalised division 10 and 11 are with ratio 1:0, thus compatible with both terminal division as well as GMC division.

To obtain an estimate of the timing of division, the authors normalise clone size to the size of the bigger clone in the abdomen. What happened to those samples where no abdominal clones were hit? Were they simply excluded from the analysis?

It is proposed that in the thorax late temporal cohort neurons are not produced, yet the ts-MARCM experiment detects some 1:0 clones. What is the fate of these cells? Are they all derived from GMC division and therefore decoupled from the temporal identity window? Or is this a re-activation of division?

"in A1, a majority of segments had one Notch OFF/B neuron that failed to label with Eve" does "the majority" in this sentence mean that there were cases where all B neurons were labelled with Eve? If yes, where would this stochasticity come from? Additionally, there is no evidence that it's the first born NotchOFF neuron in A1 that does not express Eve. The authors should clarify where this speculation comes from. When discussing trends shared with other phyla:

A- "In the mammalian spinal cord, more neurons are present in regions that control limbs (Francius et al., 2013). Analogously, EL numbers do not smoothly taper from anterior to posterior; instead, the largest number of ELs is found in two non-adjacent regions, SEZ and the abdomen." It's unclear what is the link between the figure in the mammalian spinal cord and the Drosophila embryo. The embryo doesn't even have limbs and the number of neurons measured here refer only to a single lineage, while there could be (and in fact there are) lineage-to-lineage differences that could depict a different scenario.

B- The parallelism between V1 mouse neurons and EL Drosophila neurons is also unclear to me. The similarity in fold change across segments could be a pure coincidence and, from what I understand, the two cell types are not functionally linked.

Minor comments:

I found the manuscript somewhat difficult to follow, even though I am familiar with both the model and the topic. For non-specialist readers, I expect it will be even more challenging. The presentation of the results often feels fragmented, at times resembling a sequence of brief statements rather than a continuous narrative. I would encourage the authors to provide more synthesis and interpretation, for example by summarising key findings, rather than listing in detail the number of neurons labelled in each segment for every experiment. This would make the results more accessible and easier to digest.

From the way the MS is written it's not clear from the beginning that the work focuses exclusively on embryonic-born neurons. Since in Drosophila neuronal stem cells undergo two rounds of neurogenesis, one in the embryo and one in the larva, this omission could lead to confusion.

In the abstract, what would be the other temporal cohorts generated in specific regions? (ref to: "In specific regions, NB3-3 neuroblasts produce additional types of temporal cohorts, including but not limited to the late-born EL temporal cohort.")

This sentence in the introduction is inaccurate: "The Drosophila CNS is organized into an anterior hindbrain-like subesophageal zone (SEZ) and a posterior spinal cord-like nerve cord". The anterior hindbrain-like portion of the CNS is in fact the supraesophageal ganglion (or cerebrum), while the SEZ is a posterior-like region.

Fig 1E: the encoding of the significance is not immediately clear. In the legend the 4 stars could also be arranged in the same way for clarity.

Fig 2E legend: it is mentioned that B corresponds to a 1:4 clone, however the MARCM example is shown for C and it's a 1:5.

The occurrence of "undifferentiated" neurons in Th segments is in less than 10% of the clones, I wonder if this a stochastic or deterministic event and to what extent small cell bodies could just be the consequence of local differences in tissue architecture.

Fig 2I: it's unclear what the purple means (I suppose it might be Eve expression) and why in J there should be one purple cell not labelled by the ts-MARCM when this is not present in H and I.

"When synapses do occur, they are numerically similar from segment to segment". It's unclear where the evidence for this statement comes from, please clarify or remove the sentence.

"In SEZ2, NB3-3 divides 10 times (Figure 2F)". Figure 2F does not support this statement and Figure 7 shows 12 divisions. Possibly SEZ2 and 3 have been inverted in this statement, please clarify.

Referees cross-commenting

I agree with most of the comments/suggestions provided by the other two reviewers. In particular: I agree with reviewer #1's comment about failure to express Eve being a mechanism for controlling neurons number, as this is a circular argument. I agree with reviewer #2's concern about the use of the word "flexibility"; "heterogeneity" would be a more appropriate term, as I would associate the word "flexibility" to the ability of a single neuroblast in a single segment to produce neurons with different fates under, for example, unusual growth conditions. Here no genetic/epigenetic manipulations were performed to address flexibility and the observed (stereotypical) differences result from axial patterning. As a note, Reviewer #1 asks about other temporal cohorts of EL neurons produced by other lineages, but these neurons are specifically generated from NB3-3. To generalise the observations reported in this study, the authors would need to focus on other molecularly defined temporal cohorts or, more generally, on other lineages, which, however, are likely to adopt different combinations of mecahnisms to tune progeny number across segments.

Significance

In Drosophila melanogaster, the relationship between neural progenitors and their neuronal progeny has been studied in great detail. This work has provided a comprehensive description of the number of progenitors present in each embryonic segment, their molecular identities, the number of neurons they produce, and the temporal transcriptional cascades that couple progenitor temporal identity to neuronal fate. This work adds to the existing knowledge a detailed characterisation of intersegmental differences in the pattern of proliferation of a single type of neuronal progenitor as well as in post-divisional fate depending on anterior-posterior position in the body axis (i.e. programmed cell death and Notch signalling activation). This is a first step towards understanding the cellular and molecular mechanisms underlying such differences, but it's not disclosing them.

That homologous neuroblasts can generate variable numbers of progeny neurons depending on their segmental position has been established previously. What this manuscript adds is the demonstration that these differences arise through a combination of altered division patterns and differential programmed cell death, thereby revealing a more complex and less predictable scenario than could have been anticipated from existing knowledge in other contexts. The advance provided by this study is therefore incremental, refining rather than overturning our understanding of how segmental diversity in neuroblast lineages is achieved. By touching on the general question of how progenitors generate diversity, this work could be of broad interest to developmental neuroscientists beyond the fly field. However, the way it is currently written does not make it very accessible to non-specialists.

My expertise: Drosophila neurodevelopment, nerve cord, cell types specification

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Vasudevan et al provide a detailed characterisation of the different numbers and temporal birthdates of Even-skipped Lateral (EL) neurons produced at in different segments from the same neuroblast, NB3-3. The work highlights the differences in EL neuronal generation across segments is achieved through a combination of different division patterns, failure to upregulate EL marker Eve and segment-specific program cell death. For neurons born within the same window and segment, the authors describe additional heterogeneity in their circuit formation. The work underscores the large diversity that the same neuroblast can generate across segments.

Major comments:

• Based on the ts-MARCM 1:0 clones representing 100% of the SEZ clones at any given inferred cell division, the authors conclude "NB3-3 neuroblasts generate proliferative daughter GMCs in the SEZ and thorax on most divisions". Figure 2G does not have any data for SEZ before inferred division 5, whereas there is data in other regions. The authors also state "In the SEZ and abdomen, ELs were labelled regardless of induction time." In reference to Fig 2F, which seems inaccurate given there are no SEZ clones before inferred division 5. There is no comment on this fact, which is surprising give their focus on temporal cohorts. The authors should explain this discrepancy, if known, or modify their statements to reflect the data.
• The temporal cohort (early-born vs late-born) identity is exclusively examined based on markers. Given the absence of SEZ clones from early NB3-3 divisions, a time course showing that the SEZ generate early-born Els or some other complementary method would be desirable.
• The authors repeatedly refer to their work as showing how a stem cell type can have "flexibility". Flexibility would imply that NB3-3 from one segment could adopt a different behaviour (different division pattern, or cell death or connectivity) if it were placed in a different segment. This is not what is being shown. In my opinion, "heterogeneity" of the same neuroblast across different segments would be more appropriate.

Minor comments:

• Figure 2A depicts a combination of known data and conclusions from their own (mainly SEZ). The authors might consider editing the figure to highlight what is new. A possibility would be for figure A to be a diagram of the experimental design and their summary division pattern to be shown after the new data instead of being panel A.
• The authors state that they combined published ts-MARCM with their new one, which differed in a number ways that they list, but they don't specify which limitations are associated with the published vs new dataset. Could the authors please clarify?
• The title refers exclusively to "temporal cohorts", which in the manuscript are defined quite narrowly and do not seem to apply to all segments.
• Several cited references are missing from the Reference list at the end. Could the authors please double check this? (e.g. Matsushita, 1997; Sweeney et al., 2018)
• Legend for figure 2 is a bit confusing, there is a "(A)" within the legend for (D), which indicates that segments A1-A7 are shown (this seems inaccurate, as it only goes to A6).

Significance

This study provides a comprehensive analysis of different cell biological scenarios for a neuroblast to generate distinct progeny across repeating axial units. The strength is the detailed and systematic approach across segments and possible scenarios: different division patterns, cell death, molecular marker expression. While it focuses on one specific neuroblast of the ventral nerve cord of Drosophila, the authors have done extensive work to place their findings and interpretation in the context of other cell types and across model organisms both in the introduction and discussion. This makes the work of interest for developmental biologists in general, neurodevelopment research in particular and those interested in circuit assembly, beyond their specialised community. This point of view comes from someone working in vertebrate CNS development.

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Referee #1

Evidence, reproducibility and clarity

Summary: The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

Major comments: The authors performed careful analyses of the NB3-3 lineage using EL neurons. My main concerns are limited applicability of their findings and lack of mechanisms as how NB3-3 generate various numbers of EL neurons. Their findings are exclusively relevant to the NB3-3 lineage despite their effort in highlighting that other NB lineages also generate temporal cohorts of EL neurons. I disagreed with their conclusion that failure to express Eve as a mechanism for controlling EL neuron numbers when Eve serves as the marker for these neurons. Are there any other strategy to assess the fates and functions of these cells beside relying solely on Eve expression? I am not familiar with the significance of Eve expression on the functions of these neurons. Is it possible to perform clonal analyses of NB3-3 mutant for Eve and see if these neurons adopt different functionalities/identities? If NB3-3 in the SEZ continually generate GMCs based on the interpretation of clonal analyses and depicted in Fig. 2A, why is the percent of clones that are 1:0 virtually at or near 100% from division 6-11 shown in 2G? The authors also indicate that NB3-3 in the abdomen directly generate Notch OFF/B cells that assume EL neuronal identity. In this scenario, shouldn't the percent of 1:0 clones be 100% in later divisions in Fig. 2G? Based on the number of clones in abdomen shown in Fig. 2E, I cannot seem to understand how the authors come to the percent of 1:0 clones shown in Fig. 2G

There are many potentially interesting questions related to this study that can significantly broaden the impact of this study. For example, are other NB lineages that also generate distinct temporal cohorts of EL neurons display similar proliferation patterns (type 1 division in SEZ, early termination of cell division in thoracic segments and type 0 division in abdomen)? Why does NB3-3 in the thoracic segment become quiescence so much sooner than SEZ and abdominal segments? The authors' observations suggest that NB3-3 in SEZ and abdomen generate a similar number of EL neurons despite the difference in their division patterns (type 1 vs type 0). Are the mechanisms that promote EL neuron generate in NB3-3 in SEZ and abdomen the same? Anything else is known beside Notch OFF?

Minor comments:

The authors' writing style is highly unusual especially in the result section. There is an overwhelming large amount of background information in the result section but very thin description on their observations. The background information portion also includes previously published observations. Since the nature of this study is not hypothesis-driven, it is very confusing to read in many places and difficult to distinguish their original observations from previously published results and making. One easily achievable improvement is to insert relevant figure numbers into the text more often.

Significance

The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

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Reply to the reviewers

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

Summary: This work by Matsui et al. examined the function of a gene Stand Stil (stil) in Drosophila in regulation of germ cell death in the female germline. They show that stil mutants contain many apoptotic cells, leading to germ cell loss and infertility. Gene expression analysis showed upregulation of pro-apoptotic genes such as rpr in stil mutant. DamID experiment further showed that stil binds to rpr promoter region to repress its expression. Additionally, they also show that undifferentiated germ cells are resistant to cell death in stil mutant (but stil mutant still eventually loses all germ cells).

Major comments: Overall, experiments adhere to a general standard of rigor, and each result is fairly convincing. In that sense, this paper warrants publication, as a paper that revealed a new gene important for preventing germ cell death. With that said, I feel that this paper does not reveal a new biological insight. In a nutshell, this paper is about a transcriptional repressor for pro-apoptotic gene, hence its depletion leads to cell death. Data is solid and the conclusion is well supported. But the readers will be left wondering why nature implemented such control? Unless one can show what kind of defects stil rpr double mutant (which rescues germ cell loss phenotype) exhibits, there is no insight why the balance of pro-apoptotic gene and its repressor is important. The paper discusses the 'molecular' mechanisms that explain the phenomenon, but it does not provide insights. The lack of conceptual advancement is the limitation of this work.

Response:

We thank the reviewer for pointing out a biological insight into the evolutionary rationale underlying the adoption of such a regulatory mechanism in nature. To address this point, we assessed the evolutionary conservation of rpr and stil through BLAST searches and comparative analyses. Our results showed that both genes are Diptera-restricted, whereas their key domains (the rpr IAP-binding motif and the Stil BED finger) are widely conserved across metazoans. In this phylogenetic context, we propose that Stil acts as a dedicated repressor of rpr in the Drosophila female germline, thereby establishing an apoptotic control architecture in which hid predominates and rpr is repressed by Stil. This explains why the balance between a potent effector (Rpr) and its repressor (Stil) is critical in oogenesis; preventing catastrophic germline loss while preserving hid-mediated responsiveness.

We have incorporated these phylogenetic analyses and the perspective into the revised Discussion section as follows.

Revised Page 22, Line 475; rpr is conserved only within Diptera, although its IAP-binding motif, essential for apoptosis induction, is broadly conserved across metazoans (Du et al., 2000; Gottfried et al., 2004; Hegde et al., 2002; Shi, 2002; Verhagen et al., 2000; Vucic et al., 1998; Wing et al., 2001; L. Zhou, 2005) (Fig. S7). Similarly, stil is also restricted to Diptera, predominantly within Drosophila, whereas its BED-type zinc finger domain is widely conserved among diverse organisms (Aravind, 2000; Hayward et al., 2013; Tue et al., 2017b; H. Zhou et al., 2016). Phylogenetic patterns across Diptera are consistent with a model in which stil acts as a dedicated repressor of rpr in the Drosophila germline cells (Fig. S7). Due to its potent pro-apoptotic activity, rpr must be stringently repressed in a spatiotemporal manner through mechanisms that are specific to both cell type and developmental stage. During embryogenesis, repression of rpr is mediated by the Dpp-signaling factor Shn, which binds to the rpr regulatory region, whereas in intestinal stem cells (ISCs), its expression is suppressed through chromatin conformation. In Drosophila female germline cells, hid serves as the primary regulator of apoptosis, while rpr activity is generally suppressed (Park et al., 2019; Xing et al., 2015). However, rpr mutants exhibit reduced fertility despite producing viable eggs (Fig. 3H), suggesting that rpr-mediated apoptosis may be required for proper egg development. Accordingly, we propose that stil restrains rpr in the Drosophila female germline, allowing hid to predominate in apoptotic regulation.

New Fig. S7;

The legend of new Fig. S7;

Figure S7 Conservation of Rpr and Stil within Diptera

Homologs of Drosophila melanogaster Rpr and Stil were identified by BLASTp, aligned, and analyzed phylogenetically. Homologs are present across Dipteran lineages, with the genus Drosophila highlighted in blue. Branch lengths indicate the expected number of substitutions per site, as shown by the scale bar.

Minor comments: Although this is a minor point, and this is not specifically pointing a finger at the author of this paper, I really don't like the term 'safeguard'. This term is now overutilized to add hype to papers, when 'is necessary' is sufficient. In this case, unless the answer is provided as to 'against what stil is safeguarding germ cells', this term is not meaningful. For example, if one can show that stil specifically senses germline-specific threat and tweaks the regular apoptotic pathway based on germline-specific needs, then the term 'safeguard' may be warranted.

Response:

In light of the reviewer's comment, we have revised the title of the manuscript to replace 'safeguard' with 'ensure,' which better reflects the demonstrated function of Stil without overstating its role. The new title of the manuscript is: 'Transcriptional Repression of reaper by Stand Still Ensures Female Germline Development in Drosophila'

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

In this well-executed study, Matsui et al. investigate how the female Drosophila germline prevents inappropriate apoptosis during development. They identify stand still (stil) as a key germline-specific repressor of apoptosis. Stil mutant flies are homozygous viable but female sterile due to widespread germ cell loss at the time of eclosion, which is driven by activation of the pro-apoptotic gene reaper (rpr) and caspase-dependent cell death. Germline-specific expression of anti-apoptotic factors such as p35 can rescue this phenotype, confirming that the defect lies in apoptotic regulation. The authors show that Stil directly represses rpr transcription through its BED-type zinc finger domain. Notably, undifferentiated germline cells remain resistant to apoptosis in the absence of stil, which the authors attribute to a silenced chromatin state at the rpr locus, marked by H3K9me3. These findings support a dual mechanism of protection: transcriptional repression of rpr by Stil, and a potential parallel chromatin-based silencing mechanism operating specifically in undifferentiated cells.

Major Issues:

1. Clarify cell identity in Figure 2E: It is unclear whether the apoptotic cells shown are somatic or germline in origin. Including a somatic marker such as 1B1 would allow the reader to clearly distinguish the apoptotic population and better interpret the figure.

Response:

We thank the reviewer for this helpful suggestion. Occasionally, the signal of the germline marker Vasa can be attenuated in dying germline cells. As suggested by the reviewer, we also tested α-Spectrin (a plasma membrane and fusome marker) instead of 1B1 together with TUNEL labeling, but this approach did not clearly distinguish somatic from germline apoptotic cells. To directly clarify cell identity, we now provide an improved co-stained image in which TUNEL-positive nuclei are surrounded by Vasa-positive cytoplasm, indicating a germline origin. Figure 2E has been updated accordingly.

New Fig. 2E;

Quantification of undifferentiated cells in mutants: There appears to be inconsistency in the representation of undifferentiated germ cells across figures. Early panels show near-complete germline loss, while later analyses focus on undifferentiated cells that are reportedly apoptosis-resistant. The authors should quantify the proportion of ovarioles retaining undifferentiated cells and present this data in Figure 1 or the supplements to resolve this discrepancy.

Response:

Thank you for raising the important point regarding the apparent inconsistency in the representation of undifferentiated germ cell populations. In early panes (Fig.1C, D), we analyzed adult ovaries of stil loss-of function mutants where all germline cells including undifferentiated germline stem cells (GSCs) are almost completely lost (Fig. 1C), showing nearly 100% agametic ovarioles. However, in later analysis such as those in Fig. 5A, B, we showed 3rd instar-larval ovaries of stil loss-of function mutants containing a few surviving germline cells nearby the future cap cell, the niche providing stem cell ligand, Decapentaplegic (Dpp) (Xie & Spradling, 1998). This suggests that Dpp-responsive undifferentiated germline cells may be relatively resistant to apoptosis caused by stil loss.

Indeed, the GSC-like cells generated by the overexpression of a constitutively active form of Dpp receptor, Thickveins (Tkv.CA) or loss of the differentiation factor bam, were resistant to apoptosis caused by stil loss (Fig. 5C, D). These GSC-like cells may possess enhanced stemness, owing to either excessively elevated Dpp signaling or complete loss of bam, which could lead to stronger repression of rpr expression through tighter chromatin compaction.

We added this argument in the Results section of the revised manuscript as follows.

Revised Page 16, Line 361; Compared to GSCs, which were almost completely lost in stil mutants, GSC-like cells may retain a more robust stemness owing to the extremely elevated Dpp signaling pathway, potentially resulting in stronger repression of rpr expression.

Interpretation of chromatin state at the rpr locus: The claim that H3K9me3, but not H3K27me3, marks the rpr locus is not fully convincing given the low ChIP-seq signal shown. Including a comparison to a known positive control locus would strengthen the argument. Alternatively, the authors could broaden the discussion to include global chromatin reorganization during germ cell to maternal transition, as reported in Kotb et al., 2024 and how such changes may impact rpr accessibility. Also stl mutant rescued with P53 have a "string of pearls" phenotype that are associated with germ cell to maternal transition defects (Figure S3, p53 OE)

Response:

We thank the reviewer for the thoughtful and constructive comment regarding the interpretation of chromatin state at the rpr locus. To strengthen the inference that the rpr locus shows H3K9me3 enrichment, whereas clear H3K27me3 enrichment is not evident, we have now included ChIP-seq signal profiles for known positive control loci, using light (lt) as an H3K9me3-enriched locus (Akkouche et al., 2017; Greil et al., 2003) and Ultrabithorax (Ubx) as a canonical H3K27me3 target (Torres-Campana et al., 2022). These comparisons support our interpretation that H3K9me3, rather than H3K27me3, characterize chromatin around the rpr locus in GSCs. Accordingly, while we do not exclude a minor H3K27me3 contribution, our analyses indicate H3K9me3 as the predominant signature at rpr in GSCs.

New Fig.6B and 6C;

The legend of new Fig. 6B and Fig. 6C;

(B) H3K9me3 ChIP-seq signal at the rpr locus and the lt locus (H3K9me3-positive control) in GSCs and 4C NCs. (C) H3K27me3 ChIP-seq signal at the rpr locus and the Ubx locus (H3K27me3-positive control) in GSCs and 32C NCs.

A sentence of Result section was revised as below.

Revised Page 17, Line 396; As internal controls, we confirmed H3K9me3 enrichment at the light (lt) locus and H3K27me3 enrichment at the Ultrabithorax (Ubx) locus, consistent with their established chromatin states (Akkouche et al., 2017; Greil et al., 2003; Torres-Campana et al., 2022); relative to these controls, the rpr locus shows H3K9me3 but no clear H3K27me3 enrichment in GSCs.

Regarding the suggestion to broaden the discussion to include global chromatin reorganization during the germline-to-maternal transition, as reported in Kotb et al., 2024, we agree that this is an important avenue for understanding rpr accessibility. The "string of pearls" phenotype observed in stil mutants rescued with P35 overexpression (Figure S3) is consistent with perturbations during this transition. However, a detailed analysis of such chromatin reorganization and its potential impact on rpr regulation lies beyond the scope of the present study and represents a valuable direction for future work.

Broader analysis of rpr regulation in somatic cells: It would be informative to examine publicly available chromatin or transcriptional data for the rpr locus in somatic ovarian cells. This could help clarify whether rpr regulation by Stil is truly germline-specific or reflects broader developmental trends. This will also clarify why the flies are homozygous viable but female sterile.

Response:

We thank the reviewer for this insightful suggestion. We agree that exploring chromatin accessibility and transcriptional regulation at the rpr locus in somatic ovarian cells would provide valuable insights into tissue- or cell-type-specific chromatin environments that influence rpr expression.

However, to our knowledge, there are currently no publicly available ATAC-seq or comparable chromatin datasets for purified ovarian somatic cells, including follicle cells or ovarian somatic cells (OSCs). As such, we are unable to incorporate this analysis in the current study. Nevertheless, we fully recognize the importance of this line of inquiry and consider it a valuable direction for future research.

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

Summary:

This manuscript describes the characterization of stand still (stil), a previously identified gene needed for germ cell survival in Drosophila. The molecular function of Stil has until now remained poorly understood. This new work shows that loss of stil results in reaper (rpr)-dependent apoptosis within female germ cells. Loss of rpr suppresses many of the phenotypes observed in stil mutants. Experiments performed using Drosophila cell culture suggest that Stil binds to elements within the rpr promoter. DamID and structure/function experiments indicate that Stil likely directly represses the transcription of rpr within germ cells.

In general, the experiments are well executed, and the data largely support the basic claims of the authors. Replicates are included and appropriate statistical analyses have been provided. The text and figures clear and accurate. Appropriate references were cited. There are a few things the authors should address or rephrase before publication.

On page 9 line 190-192. The authors state "Altogether, these findings indicate that the loss of stil function not only triggers apoptosis that can be suppressed by apoptosis inhibitors but also causes defects in oogenesis progression that are not rescued by blocking cell death." Failure to rescue defects during mid-oogenesis could be due to insufficient transgene expression. Indeed, loss of rpr appears to rescue the fertility of stil mutants. The conclusions of this section should be restated.

Response:

We agree that the failure to rescue mid-oogenesis defects by P35 overexpression may, at least in part, be due to insufficient transgene expression. This explanation is particularly plausible given that loss of rpr more effectively restored fertility in stil mutants. As suggested by the reviewer, we have revised the relevant sentences, to avoid misinterpretation as below.

Revised Page 9, Line 191; Altogether, these findings indicate that the loss of stil function triggers apoptosis that can be suppressed by apoptosis inhibitors.

Revised Page 12, Line 253; The complete rescue of germline survival in stil rpr double mutants also suggests that the failure of P35 overexpression to restore mid-oogenesis defects may partly reflect insufficient transgene expression (Fig. S3).

The authors should present the overlap between genes that change expression in a stil mutant and those in which the DamID experiments indicate are directly bound by Stil protein. DamID can sometimes give spurious results depending on expression levels. Further discussion along this point is necessary.

Response:

We thank the reviewer for raising this issue. As suggested, we have now analyzed the overlap between genes that are differentially expressed in stil mutant ovaries (identified by RNA-seq with stil mutant expressing P35) and genes that are potentially bound by Stil based on DamID-seq data (promoter-proximal peaks {less than or equal to}1 kb) as Supplementary Table 4. The list includes genes with DamID peaks within promoter regions and that also exhibit significant differential expression (|log2FC| > 1, adjusted p The overlap between DamID-seq and RNA-seq comprises 682 genes, including rpr, supporting the idea that Stil regulates rpr expression through interaction with its upstream promoter region. However, the detected peak signal at rpr was 3.41, which was not that strong, suggesting that Stil may also bind to and regulate other genes in female germline cells. Investigating the potential role of Stil in regulating other genes represents an important future direction of our study.

We have included this analysis and argument in the revised manuscript as below.

Revised Page 13, Line 280; A total of 682 genes with Stil-enriched peaks detected at promoter regions ({less than or equal to}1 kb) showed significantly altered expression in RNA-seq analysis of stil mutants expressing P35, including rpr (Supplementary Table 4).

Revised Page 20, Line 440; Notably, the DamID peak intensity at the rpr locus reached 3.41, which is moderate rather than strong (Supplementary Table 4). This suggests that, in addition to repressing rpr, Stil may bind to and regulate other genomic loci in the female germline. Investigating the repertoire of Stil target genes and elucidating their roles in germline cells will be an important future direction of this study.

For structure function experiments, a western blot showing expression levels of the different transgenes in ovaries should be included.

Response:

We thank the reviewer for this helpful comment. To address this point, we examined the expression levels of the four Stil variants (FL, NT, CT, and AAYA) in ovaries driven by a germline driver under a wild-type background using Western blotting. The representative blot and quantification from three biological replicates showed comparable expression levels among the variants, with the CT variant displaying a slightly reduced signal. Importantly, AAYA showed expression comparable to FL yet, like CT, failed to rescue, indicating that the rescue failure is not explained by expression-level differences. These data instead support a requirement for the BED-type zinc finger for Stil function in the germline. While we cannot fully exclude a minor contribution from the slightly lower expression of the CT variant to the lack of rescue, the AAYA result argues that loss of BED-type zinc-finger function is the primary cause; we note this caveat in the revised text. The corresponding data are now presented in Figure S6A of the revised manuscript.

New Fig. S6A;

The legend of new Fig. S6A;

(A) Western blot analysis of 6×Myc-tagged Stil variants (FL, NT, CT, and AAYA) driven by NGT40-Gal4; NosGal4-VP16, with y w as a control. Stil variants were detected with anti-Myc, and α-Tubulin (αTub) served as a loading control. Arrowheads indicate Stil variant proteins. The lower panel shows quantification of the Myc/αTub signal ratio normalized to FL. Error bars indicate standard deviation (s.d.) (n = 3).

A sentence of Result section was revised as below.

Revised Page 13, Line 291; The expression of all four Stil variant proteins from the transgenes was confirmed, although Stil-CT showed a slightly reduced expression level (Fig. S6A)

Revised Page 14, Line 305; Although CT shows slightly lower expression, AAYA fails to rescue despite FL-like expression, indicating that expression level is not limiting and that loss of the BED-type zinc finger underlies the phenotype.

"With the addition of the new Fig. S6A, the following figure labels have been updated;

Fig. S6A →S6B

Fig. S6B → S6C

Fig. S6C → S6D

Fig. S6D → S6E

Individual data points should be shown in each graph in place of simple bar graphs. This type of presentation was inconsistent throughout the paper.

Response:

We thank the reviewer for this constructive comment. In line with the reviewer's suggestion, we have revised the relevant graphs to include individual data points overlaid on bar plots with error bars. This modification enables readers to better assess data variability. We also ensured consistency in data presentation among the revised figures while maintaining clarity throughout the manuscript.

Reference "G & D., 1997" should be properly formatted.

Page 6 line 117 and 121- a couple of instances where "cell" should be "cells"

Page 14 line 304- typo "Still"

Response:

As suggested, we have revised all figures to display individual data points in each graph instead of using simple bar graphs. This change has been applied consistently throughout the manuscript to improve data transparency and readability. The revised figures include Figure 1A, 2B, S1A, and S2A.

We have also corrected the following textual issues;

・The reference "G & D., 1997" has been properly formatted as "Pennetta & Pauli, 1997".

・On page 6, lines 119 and 123, "cell" has been corrected to "cells" to ensure grammatical accuracy.

・On page 14, line 315, the typo "Still" has been corrected to "Stil".

Reviewer #3 (Significance (Required)):

The significance of the work lies in characterizing a previously unknown function of Stil. By showing that Stil acts to repress transcription of the cell death gene rpr, the authors provide new insights into how programmed cell death is regulated in the Drosophila female germline. Readers interested in reproductive biology, cell death, chromatin, and general developmental biology will find value in these new findings.

One thing to consider is the possibility that Stil represses rpr in the context of the double strand breaks that form during meiosis. Experiments in the paper indicate that stil knockdown results in TUNEL labeling in region 2A/2B of the germarium. The authors should consider co-labeling for a meiosis marker (C(3)G or gammaH2Av) to see if this PCD correlates with this expression. In addition, they could test whether loss of Spo11 (mei-W68) suppresses stil phenotypes during early germ cell development. Relating the function of Stil to repression of cell death during this critical time of germ cell development would elevate the impact and significance of the paper. However, this may be considered beyond the scope of the current study.

Response:

We deeply thank the reviewer for this insightful and thought-provoking suggestion.

As suggested, we conducted co-staining with γH2Av (DBS marker), as well as genetic interaction experiments with Spo11 (mei-W68) mutants to address this question shown below. In region 2 across all genotypes including y w control, and stil heterozygous and homozygous ovaries expressing P35, γH2Av signals were discernible and subsequently lost in region 3 through the meiotic recombination-specific DNA repair program (Additional Figure A). In stil mutants, however, an additional strong γH2Av signal was specifically observed in the oocyte, beyond the expected meiotic pattern. Furthermore, loss of meiotic recombination factors, including mei-W68, in stil mutants partially rescued the germline loss phenotype, although not to the same extent as in rpr mutants (Additional Figure B, C: 43.5 % in mei-W68-GLKD, 23.9 % in mei-P22P22 and 12.8 % in vilya826 versus 100 % with loss of rpr in Fig. 3E, F of the revised manuscript). These findings suggest that accumulation of meiotic DSBs is not the main cause of rpr upregulation in stil mutants. We feel that these analyses are beyond the scope of the current study, which focuses on identifying Stil as a transcriptional repressor of rpr and characterizing its role in germline apoptosis. Elucidating other mechanisms that elevate rpr expression in stil mutants will be the focus of future work. Hence, we are providing these data here for the reviewer's reference, but if the reviewer prefers, we would be happy to incorporate them into the manuscript.

Additional Figure (A) Immunostaining of ovarioles from y w, stilEY16156/CyO; P35 OE (NGT40; NosGal4-VP16> P35), stilEY16156; P35 OE flies with antibody against DNA double-strand break marker H2Av (green), Vasa (red), and DAPI (blue). Insets show enlarged views of egg chamber. White dots indicate oocyte nuclei, Scale bar: 50 μm (ovariole) and 20 μm (egg chamber). (B) Immunofluorescence of Vasa (red) and DAPI (blue) in ovaries from stilEY16156, stilEY16156; mei-W68-GLKD (driven by NGT40; NosGal4-VP16), stilEY16156; meiP22P22, and stilEY16156; vilya826. Scale bar: 50 μm. (C) Quantification of the percentage of ovarioles containing germline cells in 2-3-day-old females. The genotypes of females are indicated below the x-axis, and the number of germaria analyzed is shown above each bar. Error bars represent the standard deviation (s.d.).

Akkouche, A., Mugat, B., Barckmann, B., Varela-Chavez, C., Li, B., Raffel, R., Pélisson, A. & Chambeyron, S. (2017). Piwi Is Required during Drosophila Embryogenesis to License Dual-Strand piRNA Clusters for Transposon Repression in Adult Ovaries. Molecular Cell, 66(3), 411-419.e4. https://doi.org/10.1016/j.molcel.2017.03.017

Greil, F., Kraan, I. van der, Delrow, J., Smothers, J. F., Wit, E. de, Bussemaker, H. J., Driel, R. van, Henikoff, S. & Steensel, B. van. (2003). Distinct HP1 and Su(var)3-9 complexes bind to sets of developmentally coexpressed genes depending on chromosomal location. Genes & Development, 17(22), 2825-2838. https://doi.org/10.1101/gad.281503

Röper, K. & Brown, N. H. (2004). A Spectraplakin Is Enriched on the Fusome and Organizes Microtubules during Oocyte Specification in Drosophila. Current Biology, 14(2), 99-110. https://doi.org/10.1016/j.cub.2003.12.056

Torres-Campana, D., Horard, B., Denaud, S., Benoit, G., Loppin, B. & Orsi, G. A. (2022). Three classes of epigenomic regulators converge to hyperactivate the essential maternal gene deadhead within a heterochromatin mini-domain. PLoS Genetics, 18(1), e1009615. https://doi.org/10.1371/journal.pgen.1009615

Xie, T. & Spradling, A. C. (1998). decapentaplegic Is Essential for the Maintenance and Division of Germline Stem Cells in the Drosophila Ovary. Cell, 94(2), 251-260. https://doi.org/10.1016/s0092-8674(00)81424-5

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Referee #3

Evidence, reproducibility and clarity

Summary:

This manuscript describes the characterization of stand still (stil), a previously identified gene needed for germ cell survival in Drosophila. The molecular function of Stil has until now remained poorly understood. This new work shows that loss of stil results in reaper (rpr)-dependent apoptosis within female germ cells. Loss of rpr suppresses many of the phenotypes observed in stil mutants. Experiments performed using Drosophila cell culture suggest that Stil binds to elements within the rpr promoter. DamID and structure/function experiments indicate that Stil likely directly represses the transcription of rpr within germ cells.

In general, the experiments are well executed, and the data largely support the basic claims of the authors. Replicates are included and appropriate statistical analyses have been provided. The text and figures clear and accurate. Appropriate references were cited. There are a few things the authors should address or rephrase before publication.

On page 9 line 190-192. The authors state "Altogether, these findings indicate that the loss of stil function not only triggers apoptosis that can be suppressed by apoptosis inhibitors but also causes defects in oogenesis progression that are not rescued by blocking cell death." Failure to rescue defects during mid-oogenesis could be due to insufficient transgene expression. Indeed, loss of rpr appears to rescue the fertility of stil mutants. The conclusions of this section should be restated.

The authors should present the overlap between genes that change expression in a stil mutant and those in which the DamID experiments indicate are directly bound by Stil protein. DamID can sometimes give spurious results depending on expression levels. Further discussion along this point is necessary.

For structure function experiments, a western blot showing expression levels of the different transgenes in ovaries should be included.

Individual data points should be shown in each graph in place of simple bar graphs. This type of presentation was inconsistent throughout the paper.

Reference "G & D., 1997" should be properly formatted. Page 6 line 117 and 121- a couple of instances where "cell" should be "cells" Page 14 line 304- typo "Still"

Referee cross-commenting

I also agree with the points raised by the other two reviewers. I think we are in general agreement on the strengths and weaknesses of the study.

Significance

The significance of the work lies in characterizing a previously unknown function of Stil. By showing that Stil acts to repress transcription of the cell death gene rpr, the authors provide new insights into how programmed cell death is regulated in the Drosophila female germline. Readers interested in reproductive biology, cell death, chromatin, and general developmental biology will find value in these new findings.

One thing to consider is the possibility that Stil represses rpr in the context of the double strand breaks that form during meiosis. Experiments in the paper indicate that stil knockdown results in TUNEL labeling in region 2A/2B of the germarium. The authors should consider co-labeling for a meiosis marker (C(3)G or gammaH2Av) to see if this PCD correlates with this expression. In addition, they could test whether loss of Spo11 (mei-W68) suppresses stil phenotypes during early germ cell development. Relating the function of Stil to repression of cell death during this critical time of germ cell development would elevate the impact and significance of the paper. However, this may be considered beyond the scope of the current study.

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Referee #2

Evidence, reproducibility and clarity

In this well-executed study, Matsui et al. investigate how the female Drosophila germline prevents inappropriate apoptosis during development. They identify stand still (stil) as a key germline-specific repressor of apoptosis. Stil mutant flies are homozygous viable but female sterile due to widespread germ cell loss at the time of eclosion, which is driven by activation of the pro-apoptotic gene reaper (rpr) and caspase-dependent cell death. Germline-specific expression of anti-apoptotic factors such as p35 can rescue this phenotype, confirming that the defect lies in apoptotic regulation. The authors show that Stil directly represses rpr transcription through its BED-type zinc finger domain. Notably, undifferentiated germline cells remain resistant to apoptosis in the absence of stil, which the authors attribute to a silenced chromatin state at the rpr locus, marked by H3K9me3. These findings support a dual mechanism of protection: transcriptional repression of rpr by Stil, and a potential parallel chromatin-based silencing mechanism operating specifically in undifferentiated cells.

Major Issues:

1. Clarify cell identity in Figure 2E: It is unclear whether the apoptotic cells shown are somatic or germline in origin. Including a somatic marker such as 1B1 would allow the reader to clearly distinguish the apoptotic population and better interpret the figure.
2. Quantification of undifferentiated cells in mutants: There appears to be inconsistency in the representation of undifferentiated germ cells across figures. Early panels show near-complete germline loss, while later analyses focus on undifferentiated cells that are reportedly apoptosis-resistant. The authors should quantify the proportion of ovarioles retaining undifferentiated cells and present this data in Figure 1 or the supplements to resolve this discrepancy.
3. Interpretation of chromatin state at the rpr locus: The claim that H3K9me3, but not H3K27me3, marks the rpr locus is not fully convincing given the low ChIP-seq signal shown. Including a comparison to a known positive control locus would strengthen the argument. Alternatively, the authors could broaden the discussion to include global chromatin reorganization during germ cell to maternal transition, as reported in Kotb et al., 2024 and how such changes may impact rpr accessibility. Also stl mutant rescued with P53 have a "string of pearls" phenotype that are associated with germ cell to maternal transition defects (Figure S3, p53 OE)
4. Broader analysis of rpr regulation in somatic cells: It would be informative to examine publicly available chromatin or transcriptional data for the rpr locus in somatic ovarian cells. This could help clarify whether rpr regulation by Stil is truly germline-specific or reflects broader developmental trends. This will also clarify why the flies are homozygous viable but female sterile.

Referee cross-commenting

I agree with the assessment of the other two reviewers. I think reviewer 3 point of "the overlap between genes that change expression in a stil mutant and those in which the DamID experiments indicate are directly bound by Stil" is important and needs to be addressed.

Significance

This study provides important insight into how germline cells in Drosophila evade apoptosis through both transcriptional and chromatin-based regulation. While reaper is a well-known effector of apoptosis, the identification of stil as a direct repressor in the female germline adds a new layer of cell type-specific control. The authors also delineate an epigenetic mechanism that protects undifferentiated germline cells, highlighting stage-specific differences in apoptotic susceptibility. This dual mechanism is conceptually significant and expands our understanding of how cell survival is maintained during gametogenesis. However, the precise novelty of stil relative to other rpr regulators could be articulated more clearly, and some data interpretations would benefit from additional clarification.

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Referee #1

Evidence, reproducibility and clarity

Summary: This work by Matsui et al. examined the function of a gene Stand Stil (stil) in Drosophila in regulation of germ cell death in the female germline. They show that stil mutants contain many apoptotic cells, leading to germ cell loss and infertility. Gene expression analysis showed upregulation of pro-apoptotic genes such as rpr in stil mutant. DamID experiment further showed that stil binds to rpr promoter region to repress its expression. Additionally, they also show that undifferentiated germ cells are resistant to cell death in stil mutant (but stil mutant still eventually loses all germ cells).

Major comments: Overall, experiments adhere to a general standard of rigor, and each result is fairly convincing. In that sense, this paper warrants publication, as a paper that revealed a new gene important for preventing germ cell death. With that said, I feel that this paper does not reveal a new biological insight. In a nutshell, this paper is about a transcriptional repressor for pro-apoptotic gene, hence its depletion leads to cell death. Data is solid and the conclusion is well supported. But the readers will be left wondering why nature implemented such control? Unless one can show what kind of defects stil rpr double mutant (which rescues germ cell loss phenotype) exhibits, there is no insight why the balance of pro-apoptotic gene and its repressor is important. The paper discusses the 'molecular' mechanisms that explain the phenomenon, but it does not provide insights. The lack of conceptual advancement is the limitation of this work.

Minor comments: Although this is a minor point, and this is not specifically pointing a finger at the author of this paper, I really don't like the term 'safeguard'. This term is now overutilized to add hype to papers, when 'is necessary' is sufficient. In this case, unless the answer is provided as to 'against what stil is safeguarding germ cells', this term is not meaningful. For example, if one can show that stil specifically senses germline-specific threat and tweaks the regular apoptotic pathway based on germline-specific needs, then the term 'safeguard' may be warranted.

Referee cross-commenting

I also agree with other reviewers.

Significance

As I summarized above, as is, this manuscript's impact is limited to identifying a gene that is required to prevent germ cell death.

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Reply to the reviewers

Point-by-Point Response to Reviewers for Manuscript #RC-2024-02720

Manuscript Title: Molecular and Neural Circuit Mechanisms Underlying Sexual Experience-dependent Long-Term Memory in Drosophila.

Corresponding Author: Woo Jae Kim

We extend our sincere gratitude to the Managing Editor and both reviewers for their diligent and insightful evaluation of our manuscript. The comprehensive feedback provided has been invaluable, guiding us to significantly strengthen the manuscript's scientific rigor, logical cohesion, and overall impact. We have undertaken a substantial revision, incorporating new experimental evidence, reframing the central narrative, and improving data presentation to address all concerns raised.

The major revisions include:

1. New Experimental Evidence: We have performed three new sets of experiments to address key questions raised by the reviewers. First, we used the protein synthesis inhibitor cycloheximide to pharmacologically validate that the observed memory is indeed a form of long-term memory (LTM). Then, we performed genetic intersectional analyses to determine if the identified Yuelao (YL) neurons express the canonical sex-determination transcription factors doublesex (dsx) and fruitless (fru).
2. Narrative Reframing and Logical Restructuring: We fully agree with the reviewers that the logic of the original manuscript was confusing, particularly regarding the distinction between the broad Mushroom Body (MB) Kenyon Cell (KC) population and the specific YL neurons. The manuscript has been extensively rewritten to present a clear, hypothesis-driven narrative. We now frame the initial KC-related findings as part of a broader screening effort that logically led to the identification and focused investigation of the YL neuron circuit.
3. Refined Central Claim: Guided by the reviewers' feedback and our new data, we have sharpened our central claim. We now propose that YL neurons constitute a critical circuit for forming attractive taste- and pheromone-based memories derived from Gr5a neuronal inputs. This form of appetitive memory is distinct from the previously characterized internal reward state associated with ejaculation, adding a new layer to our understanding of how male flies remember and evaluate reproductive experiences.
4. Improved Data Quality and Analysis: In response to valid critiques, all imaging figures have been replaced with high-resolution versions. Furthermore, our methods for fluorescence quantification, particularly for the TRIC calcium imaging experiments, have been corrected to include normalization against an internal reference channel, adhering to established best practices. All requested genetic control experiments have been performed. We are confident that these comprehensive revisions have fully addressed all concerns and have transformed our manuscript into a much stronger, more focused, and logically sound contribution. We thank you again for the opportunity to improve our work and look forward to your evaluation of the revised manuscript.

Responses to Reviewer #1

General Comments: This study explores the molecular and neural circuitry mechanisms underlying sexual experience-dependent long-term memory (SELTM) in male Drosophila. The authors use behavioral, imaging, and bioinformatics approaches to identify YL neurons, a subset of mushroom body (MB) projecting neurons, as crucial for SELTM formation. They propose that YL neurons receive inputs from WG neurons via the sNPF-sNPFR pathway and implicate molecular players such as orb2, fmr1, MDAR2-CaMK, and synaptic plasticity in their function.

However, the evidence presented does not adequately support the authors' claims. The data fail to cohesively tell a logical story, and key conclusions appear to be based on assumptions and correlations rather than robust evidence.

• Answer: We are deeply grateful to both reviewers for their thorough and constructive evaluation of our manuscript. Their collective feedback has been instrumental in helping us to clarify the study's rationale, strengthen our interpretations, and significantly improve the overall quality and impact of the work. We appreciate the recognition of our study's potential to advance the understanding of how sexual experience modifies future mating behaviors and to elucidate the neuronal and molecular mechanisms of how memory regulates a key sexual behavior in male Drosophila*.

• *In response to the general comments, we have undertaken a major revision of the manuscript to improve the clarity, logic, and presentation. We have rewritten the Abstract and Introduction to more clearly define "sexual experience-dependent long-term memory" (SELTM) and articulate its significance in the context of adaptive decision-making and interval timing. The entire manuscript has been restructured to present a more logical, hypothesis-driven narrative that clearly distinguishes our initial broad screening from the focused investigation of the YL neuron circuit. We have also incorporated alternative interpretations of our data, particularly regarding the role of the YL circuit in regulating baseline mating duration in naive males, which has added more depth to the study. Finally, all figures have been remade in high resolution, and all requested genetic controls and methodological clarifications have been added to ensure rigor and reproducibility. We are confident that these revisions have addressed the reviewers' concerns and have resulted in a much stronger manuscript.

Comment 1: The study identifies the knowledge gap (lines 103-104) but fails to integrate relevant literature, particularly Shohat-Ophir et al., Science (2012), and Zer-Krispil et al., Curr Biol (2018). These studies established that ejaculation induces appetitive memory in male Drosophila via corazonin and NPF neurons. The current study does not provide direct evidence that the "act of mating itself" drives SELTM, as it includes both courtship and copulation.

Response: Thank you for highlighting these two landmark studies. We fully agree that Shohat-Ophir et al., Science (2012) and Zer-Krispil et al., Curr Biol (2018) were pivotal in demonstrating that ejaculation—and the accompanying corazonin/NPF signalling—can establish an appetitive memory in males.

In the revised manuscript we have now integrated both papers on lines 111-118:

“Previous work has shown that successful copulation is intrinsically rewarding to male Drosophila: a single mating encounter elevates brain neuropeptide F (NPF) levels and suppresses subsequent ethanol preference19. Importantly, Zer-Krispil et al. further demonstrated that ejaculation itself—artificially induced by optogenetic activation of corazonin (Crz) neurons—is sufficient to mimic this reward state, driving appetitive memory formation and up-regulation of NPF. These findings indicate that the act of ejaculation, rather than the entire courtship sequence, is the critical sensory event that gates post-mating reward.”

Comment 2: The nature of the observed long-lasting reduced mating duration requires clearer characterization: Is this an associative memory or experience-dependent behavioral plasticity? Can the formation of this long-term memory be blocked by protein synthesis inhibitors, such as cycloheximide?

Response: We thank the reviewer for this excellent suggestion to pharmacologically characterize the nature of the memory. To definitively test whether the observed SMD is a form of protein synthesis-dependent long-term memory (LTM), we performed a new experiment as suggested.

We have now included data in new Figure supplement 1I showing that feeding males the protein synthesis inhibitor cycloheximide (CXM) for 24 hours immediately following the sexual experience completely blocks the formation of the long-lasting SMD phenotype. Control flies fed a vehicle solution exhibited robust SMD. This result provides strong evidence that SELTM is not merely a form of transient behavioral plasticity but is a genuine form of LTM that requires de novo protein synthesis for its consolidation, a hallmark of LTM across species.[1]

The revised text was put on lines 173-176:

" To determine whether the persistent reduction in mating duration (SMD) depends on de-novo protein synthesis, we fed males the translational inhibitor cycloheximide (CXM). Under this regimen, CXM completely abolished the SMD phenotype (Fig. 1I)."

Comment 3: While schematics illustrate the working hypotheses, the text lacks detailed explanations, leaving the reader unclear about the rationale behind certain conclusions.

__Response: __Thank you very much for this insightful comment. We fully agree that the original manuscript did not provide sufficient textual justification for the conclusions derived from the schematics. In the revised version we have therefore added comprehensive explanations immediately following each figure (or schematic) that explicitly state the underlying rationale, the key observations supporting our hypotheses, and the logical steps leading to each conclusion. We believe these additions now make the reasoning transparent and easy to follow. We appreciate your feedback, which has substantially improved the clarity of our work.

• *

Comment 4*: The logic to draw certain conclusions was confusing and misleading. - For instance, the role of orb2 in SELTM is examined via knockdown in MB Kenyon cells (KCs) (using ok107>orb2-RNAi), which is irrelevant to the claim that orb2 functions in YL neurons. Additionally, RNAseq analyses (Fig. 1N-S) focusing on orb2 expression in a/b KCs are irrelevant to and cannot support the claim that Orb2 functions in YL neurons. *

*- Similarly, the claim (lines 302-303) that sNPF-R expression is exclusive to MB KCs conflicts with data showing effects when sNPF-R is knocked down in YL neurons. How can knocking-down a gene, which is exclusively expressed in neural population A, in neural population B affect a phenotype? This inconsistency undermines the interpretation of the results. *

*- Other examples include lines 223-227 and lines 246-249. It is very confusing how the authors came to the indications. *

- The authors also kept confusing the readers and themselves by mistakenly referring to MB KC a-lobe and YL a-lobe projection. They may know the difference between the two neural populations but they did not always refer to the right one in the text.

Response: We agree completely with the reviewer that the logic in the original manuscript was confusing and failed to clearly distinguish between the general MB Kenyon Cell (KC) population and the specific YL projection neurons. This was a major flaw, and we are grateful for the opportunity to correct it. We have undertaken a major revision of the manuscript's narrative and structure to present a clear, logical progression of discovery.

The new logical flow of the manuscript is as follows:

1. We first establish that sexual experience induces a robust, long-lasting SMD behavior that is dependent on protein synthesis
2. We then perform initial experiments to implicate the MB as a key brain region. We show that broad inhibition of MB KCs (using the ok107-GAL4 driver) disrupts SMD behavior.This result establishes the general involvement of the MB but lacks cellular specificity.
3. The remainder of the manuscript then focuses specifically on dissecting the molecular and cellular properties of these YL neurons. Finally, we have meticulously edited the entire manuscript to ensure that we always use precise terminology, clearly distinguishing between "YL neuron projections to the MB α-lobe" and the "MB KC α-lobe."

Comment 5*: The imaging figures provided are unfocused and poorly resolved, making it difficult to assess data quality. *

*- Colocalization analyses of orb2 and YL are unconvincing... Maximum intensity projection images are insufficient... complete image stacks with staining of orb2, YL, and KCs (MB-dsRed) are needed for validation. *

- Quantification of imaging data appears flawed. For example, claims of orb2 and CaMKII upregulation in MB a-lobe projections (e.g., Fig. S2F-J, Fig. 3M,N) are confounded by widespread increases in intensity across the brain, lacking specificity.

• *

*- The TRIC experiment analysis should normalize GFP signals to internal reference channel (RFP in the TRIC construct)... *

- In Fig. 6H-J, methods for counting synapse numbers are not described. How are synapse numbers counted in these low-resolution images?

Response: We sincerely apologize for the poor quality of the imaging data presented in the original manuscript. We agree with the reviewer's critiques and have taken comprehensive steps to rectify these issues.

• Image Quality: We apologize for not including the full image data in the original submission. The complete figure is now presented in revised Fig. 2J .
• Fluorescence Quantification: The fluorescence quantification has been re-analyzed. The Methods section now includes a detailed description of our protocol.
• TRIC Normalization: We apologize for not stating this explicitly in the previous version. As now described in the revised Methods subsection “Quantitative Analysis of Fluorescence Intensity”, all TRIC images were acquired with identical laser power and exposure settings. The GFP signal was background-corrected and then normalized to the RFP fluorescence encoded by the TRIC construct itself (UAS-mCD8RFP), which serves as an internal reference for construct expression and mounting thickness.

• Synapse Counting: We agree with the reviewer that the resolution of our images was insufficient for accurate synapse particle counting. We have therefore removed the problematic analysis from the former Fig 6H-J. Our conclusions regarding synaptic plasticity now rest on the more robust and quantifiable data showing a significant increase in the total area of dendritic (DenMark) and presynaptic (syt.eGFP) markers. Comment 6: The study presents data from unrelated learning paradigms (e.g., olfactory associative learning, courtship conditioning; Fig. 7) without justifying how these paradigms relate to SELTM. Particularly, the authors claimed that SELTM is related to Gr5a, which leads to appetitive memories, which involve PAM dopaminergic neurons and MB horizontal lobes. However, the olfactory associative learning with electric shock and courtship conditioning lead to aversive memories, that involve PPL1 dopaminergic neurons and the vertical lobes.

• *

Response: We thank the reviewer for requesting clarification on the rationale for including these experiments. The purpose of these assays was to test the specificity of the YL neuron circuit. A key question is whether YL neurons represent a general-purpose LTM circuit or one specialized for a particular memory modality.

The data show that knockdown of Orb2 or Nmdar2 specifically in YL neurons has no effect on the formation of LTM for aversive olfactory conditioning or aversive courtship conditioning. These negative results are critically important, as they demonstrate that the YL circuit is

not required for all forms of LTM. This finding strongly supports our revised central claim that YL neurons are specialized for processing appetitive memories derived from the specific sensory context of mating (i.e., taste and pheromonal cues from Gr5a neurons).

To improve the narrative flow of the main text, We rearranged the order of the articles. The relevant description is in lines 398-401:

“To determine whether YL neurons constitute a general LTM circuit or are dedicated to the appetitive context of mating, we tested two canonical aversive paradigms: electric-shock olfactory conditioning and courtship conditioning. If YL neurons serve as a universal LTM module, their genetic impairment should also impair aversive memory.”

lines 469-472:

“The inability of YL perturbation to impair aversive memories (Fig. 7) corroborates that this micro-circuit is dedicated to Gr5a-dependent SELTM rather than acting as a generic LTM hub”

Minor Issues

Comment 1: Fig 2F. YL projections are labeled as MBONs. Clarify whether YL neurons are the upstream or downstream (MBON) of KCs.

__Response: __Thank you for this helpful comment. As Huang et al., 2018[2] (Nat. Commun. 9:872) have mentioned, the MB093C-GAL4 driver is the MBON-α3 mushroom body output neuro. Consequently, YL neurons are positioned downstream of the MBON-α3.

We have now clarified this point in the revised manuscript lines 217-222:

“Each of these neurons extends a vertical fiber to the dorsal brain region, where they form dense arbors within the α-lobes of the mushroom body. Because the MB093C-GAL4 driver labels MBON-α3 output neuron[51], these YL arbors are positioned postsynaptically within the α-lobe and relay mushroom-body output to the anterior, middle, and posterior superior-medial protocerebrum.”

Comment 2: Extensive language polishing is required, as several sentences are unclear (e.g., lines 169-172).

Response: We apologize for the lack of clarity in the original text. The entire manuscript has undergone extensive revision and professional language editing to improve readability, precision, and grammatical accuracy.

Responses to Reviewer #2

Major Comments

Comment 1: Clearer articulation of the rationale, motivation, and significance of the overall study design and individual experiments can strengthen the manuscript and promote readership. For example, the beginnings of the abstract and introduction should define what authors mean by sexual experience-dependent long-term memory and its significance (including why it is "significant for reproductive success" (lines 46 and 92)). Similarly, employing more concrete language throughout the text will help anchor and contextualize the study. Interpretation is occasionally insufficient or does not follow directly from the data provided.

Response: We thank the reviewer for this valuable advice. We agree that the motivation and significance of our study were not articulated clearly enough. We have rewritten the Abstract and the beginning of the Introduction to address this. The revised text now explicitly defines SELTM as a protein synthesis-dependent, appetitive memory formed in response to gustatory and pheromonal cues. We explain its significance in the context of adaptive behavior, linking it to interval timing, a process by which male flies strategically adjust their mating investment (i.e., mating duration) based on prior experience to optimize reproductive success and energy expenditure. This framing provides a clearer context for our investigation into its underlying neural and molecular mechanisms.

Comment 2: Long term memory: I do not work on Drosophila memory, but a cursory search suggests that the field generally considers long term memory in Drosophila to last for 24 hr to days (courtship memory lasts for >24 hr). SMD decays between 12-24 hr after copulation. Could SMD be considered a short-term effect?

Response: This is an important point of clarification, as described in our response to Reviewer #1 (Major Comment 2), we have performed a new experiment demonstrating that the formation of SMD is blocked by the protein synthesis inhibitor cycloheximide (Figure 1I). This dependence on de novo protein synthesis is a defining characteristic of LTM, distinguishing it from short- and intermediate-term memory forms.[1] where memories lasting 12-24 hours are well-established as forms of LTM.[3] Therefore, based on both its duration and its molecular requirements, SMD represents a bona fide form of LTM.

The relevant statement is in lines 174-178:

"To determine whether the persistent reduction in mating duration (SMD) depends on de-novo protein synthesis, we fed males the translational inhibitor cycloheximide (CXM). Under this regimen, CXM completely abolished the SMD phenotype (Fig. 1I). This finding suggests that the reduction in mating investment is contingent upon the formation of LTM."

Comment 3: Fig 1B-E share the same control (naive) group. If these experiments were performed in the same replicate(s), they should be plotted in the same figure. If not, please provide more details on how experimental blocks were set up and how controls compared between replicates.

Response: Thank you for this helpful suggestion. We understand that sharing the same naive control across multiple panels (Fig. 1B–E) may raise concerns about data independence. However, we chose to present these panels separately for the following reasons:

1. Clarity and Readability: Each panel (B–E) represents a distinct temporal condition (0 h, 6 h, 12 h, 24 h post-isolation). Separating them avoids visual clutter and allows readers to focus on one time point at a time, improving interpretability.

__ Consistency with Internal Controls:__

Although the naive group is identical across panels, each experimental block (i.e., each isolation time point) was run independently on same days, with internal controls (naive vs. experienced) included in every block. This ensures that statistical comparisons remain valid within each panel, even if the naive data overlap.

We have now added a clear statement in the figure legend explaining that the naive group is shared across panels and that each time point was tested independently with internal controls. This maintains transparency while preserving the visual clarity of the current layout.

Comment 4: Serial mating (Fig 1F-H): please provide details on the methods. How much time elapsed between successive matings? Is a paired statistical test used? Sperm depletion also affects mating duration, and without this information the authors' conclusion (lines 155-156) does not automatically follow from the data.

Response:

1. __ Interval between successive matings__ We have rewritten the Methods to state explicitly that “as soon as one copulation ended the male was transferred immediately to a fresh virgin female, so the next mating began immediately.”

we add new method:

" Serial mating ____duration ____assay

Serial mating duration assay was identical to the standard procedure except that each male was presented with four DF virgin females in immediate succession: upon termination of the first copulation the male was immediately put into a fresh chamber containing the next virgin, the timer was restarted at first contact, and this step was repeated until four complete matings were recorded or 5 min elapsed without initiation, whichever came first."

__ Statistical test__

We apologize for omitting this detail. Unpaired t-test was used: for male the mating duration before (naïve) and after sexual experience was recorded, yielding paired observations. Prism’s unpaired t-test module was therefore applied to evaluate the mean difference.

The figure legend now states “with error bars representing SEM. Asterisks represent significant differences, as revealed by the Unpaired t test and ns represents non-significant difference (**p __ Mating duration versus sperm depletion__

We apologize for not having made it clear that these two observations are complementary, not contradictory. Previous work has shown that when male Drosophila copulate repeatedly, mating duration remains stable even though the number of sperm transferred—and thus the number of progeny sired—declines progressively [4]

The revised text is as follows (lines235-241):

"Previous work has shown that when male Drosophila copulate repeatedly, mating duration remains stable even though the number of sperm transferred—and thus the number of progeny sired—declines progressively. This dissociation confirms that the constant mating duration we observe in our serial-mating experiment (Fig. 1F–H) is consistent with normal sperm depletion and does not compromise the conclusion that the experience-dependent reduction in mating duration reflects long-term memory."

Thank you for helping us improve the clarity of our study.

Comment 5: Mating duration assay: Which isolation interval was chosen for the rest of the SMD experiments? The 12 hr en masse mating setup is relatively uncommon among studies on courtship/copulation/post-copulatory phenotypes, and introduces uncertainty and variability in the number and timing of matings that occurred during the 12 hr-window. This source of variability and its implication in interpreting the data should be acknowledged. Moreover, the 3 studies referenced in the methods all house males in groups of 4, whereas this study uses groups of 40. Could density confound the manifestation of SMD?

Response: We thank the reviewer for these important methodological questions.

• Isolation Interval: We have clarified in the Methods that virgin females were introduced into vials for last 1 day before assay.
• Housing Density: This is an excellent point. To control for any potential effects of housing density itself, we have clarified that our "naive" control males are also housed in groups of 40 for the same duration as the "experienced" males. Therefore, the only difference between the two groups is the presence of females, isolating the effect of sexual experience from the effect of social density. Comment 6: SMD behavior: comparing orb2 mutants and controls (Fig 1M and Fig S1K-L), loss of orb2 actually reduces the mating duration in native males (mean ~15 min) relative to controls (~20 min), and have possibly no effect on experienced males (~15 min). This is inconsistent with the SMD behavior demonstrated in Fig 1B-E. The same pattern is found for mushroom body silencing (Fig 1P, Fig S1M-N), orb2 knockdown in YL neurons (Fig 2D, Fig S2A-B), Fmr1 knockdown in YL neurons (Fig 3D, Fig S2B, S3D) and most other experiments where mating duration is not significantly different between naive and experienced males. This might demonstrate a separate role of YL neurons and its related circuit in regulating mating duration in naive males. Could the authors discuss this interpretation? As an aside, plotting genetic controls next to experimental groups is customary and facilitates comparisons between relevant groups.

Response: Thank you very much for this insightful observation.

1. Baseline differences among genotypes We agree that absolute mating duration differs slightly between genotypes (e.g. naive orb2∆/+ about 15 min vs. wild-type CS about 20 min). Such differences are common when mutations or transgenes are introduced into distinct genetic backgrounds, and they do not affect the within-genotype comparison that is the essence of SMD (sexual-experience-dependent shortening of mating duration). Therefore, for every experiment we compared naive vs. experienced males of the identical genotype, keeping all other variables constant.

Consistency of SMD across figures

In every manipulation that disrupts SMD memory (orb2∆, MB silencing, orb2-RNAi in YL neurons, Fmr1-RNAi in YL neurons, etc.) the naive–experienced difference disappears, whereas the genetic controls retain a significant ΔMD. This is fully consistent with Fig. 1B–E and demonstrates that the memory trace, not the basal duration, is abolished.

Figure layout

Following your suggestion, we have re-ordered all bar graphs so that the relevant genetic controls are placed immediately adjacent to the experimental groups, making within-panel comparisons easier.

We hope these clarifications and adjustments address your concerns.

Comment 7: Bitmap figures: unfortunately the bitmap figures are compressed and their resolution makes it difficult to evaluate the visual evidence.

Response: We apologize for the poor quality of the figures. All figures in the revised manuscript, including the scRNA-seq plots, have been remade as high-resolution vector graphics to ensure clarity and detail. For better understanding, different colored illustrations are also placed next to the scRNA-seq.

Comment 8: Sexual dimorphism of YL neurons: many neurons involved in sexual behaviors express dsx and/or fru. Do YL neurons express them?

Response: This is an excellent question. To address it, we performed a new set of experiments using genetic intersectional tools to test for the expression of doublesex (dsx) and fruitless (fru) in YL neurons. Our analysis, presented in figure supplement 2B, reveals that YL neurons are indeed fru-negative and dsx-negative. We therefore conclude that YL neurons do not belong to the canonical fru- or dsx-expressing neuronal classes and are unlikely to be intrinsically sex-specific.

We add explanation in lines 223-229:

"Our further analysis confirmed the presence of only three pairs of nuclei near the SOG in male brains, whereas female brains exhibit a greater number of nuclei near the AL (Fig. 2I), suggesting subtle sexual dimorphisms in GAL4MB093C-expressing neurons. Importantly, these neurons do not overlap with either fru- or dsx-expressing cells: co-immunostaining for GFP and Fru or Dsx revealed almost no colocalization in any brain region examined (Fig. S2B), indicating that YL neurons are distinct from the canonical sex-specific fru/dsx circuits."

Comment 9: Genetic controls for some crucial experiments are not provided, e.g. Fig 2J, Fig S3C, Fig S3E-F Fig 5B-C, F, Q-R, Fig S5A-E.

Response: We thank the reviewer for their careful attention to detail. We have now performed all the missing genetic control experiments.

Comment 10: Colocalization experiments: please provide more detail on how fluorescence is normalized for each channel across images, especially when the overall expression of an effector is up- or down-regulated after mating.

Response: We have updated the Methods section under "Quantitative Analysis of Fluorescence Intensity" and "Colocalization Analysis" to provide a detailed description of our normalization procedure.

Comment 11: Please resolve this apparent contradiction on the expression of Nmdar1 and 2 in YL neurons. On line 261: "both receptors co-expressing in Orb2-positive MB Kenyon cells"; on line 279-281 "Nmdar1 is not expressed with YL neurons [...] whereas Nmdar2 is expressed in a single pair of YL neurons..."

Response: We apologize for this contradiction, which arose from the confusing narrative structure of the original manuscript. As detailed in our response to Reviewer #1 (Major Comment 4), we have reframed the manuscript.

Comment 12: Particle analysis (Fig 6H-J): experienced males seem to have more synapses but trend towards smaller average size. It would be helpful to show number of synapses and average size as paired data, or show that the total particle area is larger in experienced males.

Response: We agree with the reviewer that this analysis was inconclusive and potentially misleading due to the limitations of image resolution. As noted in our response to Reviewer #1, we have removed this particle analysis (former Fig 6H-J) from the revised manuscript. Our claim for increased synaptic plasticity is now supported by the more robust measurement of the total fluorescence area of the pre- and postsynaptic markers, which shows a significant increase in experienced males.

Minor Comments

We thank the reviewer for their meticulous attention to detail. We have addressed all minor comments as follows:

Comment 1: 1. Some figures (e.g. Fig 3M-R) and experiments (e.g. oenocyte scRNA-seq) are not referenced in the text. dnc data is shown alongside amn and rut but the rationale for its inclusion is not provided.

__Response: __Original Fig. 3M-R (now Fig,3 M-O) was referenced on line 283. The rationale for including dnc data (as a canonical memory mutant) is now clarified in the text on lines 187-189:

"To ask whether the same molecular machinery underlies the SMD that follows sexual experience, we tested three classical memory mutants: dunce (dnc), amnesiac (amn), and rutabaga(rut)."

Comment 2: Some references might not point to the intended article (e.g. ref 123).

__Response: __The reference list has been checked and corrected.

Comment 3. Please plot genetic controls next to experimental genotypes as they are a crucial part of the experiment.

__Response: __All relevant figures now include plots of genetic controls next to experimental genotypes.

Comment 4. The "estimation statistics" plots are not necessary since the authors show individual data points. To further enhance data transparency, the authors may consider reducing the alpha and/or dot size so the individual data points are more readily visible.

Response: Thank you for this helpful suggestion! We fully agree that data transparency is essential. After carefully testing lower alpha values and smaller dot sizes, we found that either change markedly obscured the dense regions of the distributions. So we didn't change the size of the point.

The estimation-statistics overlays are kept for two courteous reasons: (i) they provide an immediate visual estimate of the mean difference and its 95 % confidence interval, which is the key statistic we base our conclusions on, and (ii) they spare readers from having to cross-reference separate tables.

Comment 5. For accessibility, please avoid using green and red in the same plot.

__Response: __We fully agree that red–green combinations can be problematic for colour-vision-impaired readers. In the present manuscript, however, the only panel that juxtaposes pure red and pure green is the Fly-SCOPE co-expression data. These scRNA-seq plots are provided only as supportive reference; the actual quantitative conclusions are based on independent genetic and imaging experiments that use magenta, cyan, yellow, and greyscale palettes. Moreover, the scope images are accompanied by detailed text descriptions of the overlapping cell clusters, so no essential information is lost even if the colours are indistinguishable

Comment 6. Fly Cell Atlas: please show color scales used for each gene as the color thresholds are gene-specific by default.The 3-color overlap on SCope also makes it very difficult to see the expression pattern for each gene. One possibility is outlining the Kenyon cells on the tSNE plots and showing the expression for each gene of interest.

Response: Thank you for this helpful suggestion. To avoid the ambiguity that arises from RGB blending in the three-colour overlay, we have added a small colour-mixing diagram next to the t-SNE plots (revised Fig. 1). This key shows the exact hues produced by pairwise and three-way overlaps:

• Red + Green = Yellow

• Red + Blue = Magenta

• Green + Blue = Cyan

• Red + Green + Blue = White

Thus, yellow, magenta or cyan dots indicate co-expression of two genes, while white dots mark cells where all three genes are detected. this diagram allows readers to interpret overlap colours at a glance without re-entering SCope.

Comment 7. Please also refer to Fly Cell Atlas as such. SCope is a visualization platform that houses multiple datasets.

__Response: __The reference to Fly Cell Atlas was added.

Comment 8. Please introduce acronyms and genetic reagents the first time they are mentioned.

__Response: __All acronyms and genetic reagents are now defined upon their first use.

Comment 9. Line 184: please specify "split-GAL4 reagents" instead of "advanced genetic tools".

__Response: __We have replaced "advanced genetic tools" with the more specific term "Split-GAL4 reagents."

Comment 10. Line 187: there are a few other lines with p>0.05 or p>0.01, so "uniquely" is inaccurate. Are the p-values in Table 1 corrected for multiple testing?

__Response: __The term "uniquely" has been revised for accuracy. No correction for multiple testing was applied because each entry in Table 1 represents a single pairwise comparison (naive vs. exp). Thus only one p-value was generated per experiment.

Comment 11. Some immunofluorescence panels lack scale bars.

__Response: __Scale bars have been added to all immunofluorescence panels.

Comment 12. Fig S2G-I: do authors mean "naive" instead of "group"?

__Response: __The term "group" in Fig S2G-I has been corrected to "naive."

Comment 13. Movie 1 should be referenced when YL neurons are first introduced.

__Response: __Movie 1 is now referenced when YL neurons are first introduced in the text.

Comment 14. Is Fig 4L similar to Fig 6L-N?

__Response: __This error has been corrected after the article was reformatted

Comment 15. Fig 7: please plot olfactory conditioning experiment results as either percentages, preference index, or paired numbers. "Number of flies/tube" is not as informative.

__Response: __Thank you for pointing this out. The bars in Fig. 7 indeed represent paired numbers, but we realise this was not stated explicitly. We apologize for the lack of clarity. In the revised manuscript we explained it in detail in figure legend and method. In the figure, we also marked the percentage of flies that chose to avoid the side of the stimulus with gas, and explained it in the Figure legend.

Reference

1. Lagasse F, Devaud J-M, Mery F. A Switch from Cycloheximide-Resistant Consolidated Memory to Cycloheximide-Sensitive Reconsolidation and Extinction in Drosophila. J Neurosci. 2009;29: 2225–2230. doi:10.1523/jneurosci.3789-08.2009
2. Huang C, Maxey JR, Sinha S, Savall J, Gong Y, Schnitzer MJ. Long-term optical brain imaging in live adult fruit flies. Nat Commun. 2018;9: 872. doi:10.1038/s41467-018-02873-1
3. Tonoki A, Davis RL. Aging Impairs Protein-Synthesis-Dependent Long-Term Memory in Drosophila. J Neurosci. 2015;35: 1173–1180. doi:10.1523/jneurosci.0978-14.2015
4. Macartney EL, Zeender V, Meena A, Nardo AND, Bonduriansky R, Lüpold S. Sperm depletion in relation to developmental nutrition and genotype in Drosophila melanogaster. Evol Int J Org Evol. 2021;75: 2830–2841. doi:10.1111/evo.14373

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Referee #2

Evidence, reproducibility and clarity

Summary:

Sun et al. show that Orb2-expressing, glutamatergic mushroom body neurons (YL neurons) are central to the "shorter mating duration (SMD)" behavior, where males reduce their mating duration up to 12 hours after the initial copulation. The authors use SMD as a model for understanding sexual experience-dependent long-term memory in males. A few genes implicated in long-term memory (Fmr1, CrebB) are required in YL neurons for SMD. The Nmdar-CaMKII signaling pathways is also implicated, and mating attenuates Ca2+ signaling and increases synaptic plasticity in the mushroom body and subesophageal ganglion.

Major comments:

1. Clearer articulation of the rationale, motivation, and significance of the overall study design and individual experiments can strengthen the manuscript and promote readership. For example, the beginnings of the abstract and introduction should define what authors mean by sexual experience-dependent long-term memory and its significance (including why it is "significant for reproductive success" (lines 46 and 92)). Similarly, employing more concrete language throughout the text will help anchor and contextualize the study. Interpretation is occasionally insufficient or does not follow directly from the data provided.
2. Long term memory: I do not work on Drosophila memory, but a cursory search suggests that the field generally considers long term memory in Drosophila to last for 24 hr to days (courtship memory lasts for >24 hr). SMD decays between 12-24 hr after copulation. Could SMD be considered a short-term effect?
3. Fig 1B-E share the same control (naive) group. If these experiments were performed in the same replicate(s), they should be plotted in the same figure. If not, please provide more details on how experimental blocks were set up and how controls compared between replicates.
4. Serial mating (Fig 1F-H): please provide details on the methods. How much time elapsed between successive matings? Is a paired statistical test used? Sperm depletion also affects mating duration, and without this information the authors' conclusion (lines 155-156) does not automatically follow from the data.
5. Mating duration assay: Which isolation interval was chosen for the rest of the SMD experiments? The 12 hr en masse mating setup is relatively uncommon among studies on courtship/copulation/post-copulatory phenotypes, and introduces uncertainty and variability in the number and timing of matings that occurred during the 12 hr-window. This source of variability and its implication in interpreting the data should be acknowledged. Moreover, the 3 studies referenced in the methods all house males in groups of 4, whereas this study uses groups of 40. Could density confound the manifestation of SMD?
6. SMD behavior: comparing orb2 mutants and controls (Fig 1M and Fig S1K-L), loss of orb2 actually reduces the mating duration in native males (mean ~15 min) relative to controls (~20 min), and have possibly no effect on experienced males (~15 min). This is inconsistent with the SMD behavior demonstrated in Fig 1B-E. The same pattern is found for mushroom body silencing (Fig 1P, Fig S1M-N), orb2 knockdown in YL neurons (Fig 2D, Fig S2A-B), Fmr1 knockdown in YL neurons (Fig 3D, Fig S2B, S3D) and most other experiments where mating duration is not significantly different between naive and experienced males. This might demonstrate a separate role of YL neurons and its related circuit in regulating mating duration in naive males. Could the authors discuss this interpretation? As an aside, plotting genetic controls next to experimental groups is customary and facilitates comparisons between relevant groups.
7. Bitmap figures: unfortunately the bitmap figures are compressed and their resolution makes it difficult to evaluate the visual evidence.
8. Sexual dimorphism of YL neurons: many neurons involved in sexual behaviors express dsx and/or fru. Do YL neurons express them? If they do, they might be a subset of characterized and named dsx/fru neurons.
9. Genetic controls for some crucial experiments are not provided, e.g. Fig 2J, Fig S3C, Fig S3E-F Fig 5B-C, F, Q-R, Fig S5A-E.
10. Colocalization experiments: please provide more detail on how fluorescence is normalized for each channel across images, especially when the overall expression of an effector is up- or down-regulated after mating.
11. Please resolve this apparent contradiction on the expression of Nmdar1 and 2 in YL neurons. On line 261: "both receptors co-expressing in Orb2-positive MB Kenyon cells"; on line 279-281 "Nmdar1 is not expressed with YL neurons [...] whereas Nmdar2 is expressed in a single pair of YL neurons in both male and female brains".
12. Particle analysis (Fig 6H-J): experienced males seem to have more synapses but trend towards smaller average size. It would be helpful to show number of synapses and average size as paired data, or show that the total particle area is larger in experienced males.

Minor comments:

1. Some figures (e.g. Fig 3M-R) and experiments (e.g. oenocyte scRNA-seq) are not referenced in the text. dnc data is shown alongside amn and rut but the rationale for its inclusion is not provided.
2. Some references might not point to the intended article (e.g. ref 123).
3. Please plot genetic controls next to experimental genotypes as they are a crucial part of the experiment.
4. The "estimation statistics" plots are not necessary since the authors show individual data points. To further enhance data transparency, the authors may consider reducing the alpha and/or dot size so the individual data points are more readily visible.
5. For accessibility, please avoid using green and red in the same plot.
6. Fly Cell Atlas: please show color scales used for each gene as the color thresholds are gene-specific by default.The 3-color overlap on SCope also makes it very difficult to see the expression pattern for each gene. One possibility is outlining the Kenyon cells on the tSNE plots and showing the expression for each gene of interest.
7. Please also refer to Fly Cell Atlas as such. SCope is a visualization platform that houses multiple datasets.
8. Please introduce acronyms and genetic reagents the first time they are mentioned.
9. Line 184: please specify "split-GAL4 reagents" instead of "advanced genetic tools".
10. Line 187: there are a few other lines with p>0.05 or p>0.01, so "uniquely" is inaccurate. Are the p-values in Table 1 corrected for multiple testing?
11. Some immunofluorescence panels lack scale bars.
12. Fig S2G-I: do authors mean "naive" instead of "group"?
13. Movie 1 should be referenced when YL neurons are first introduced.
14. Is Fig 4L similar to Fig 6L-N?
15. Fig 7: please plot olfactory conditioning experiment results as either percentages, preference index, or paired numbers. "Number of flies/tube" is not as informative.

Significance

The manuscript describes an extensive and comprehensive set of experiments aimed at elucidating the role of a subset of mushroom body neurons in mediating a male post-mating sexual behavior, which the authors use as a model for sexual experience-dependent long-term memory. Long-term post-mating responses in females have been well characterized in Drosophila and other insects, but post-mating long term memory in males are less well understood despite a few studies reporting their importance in mating success. How males adjust their mating duration based on internal and external cues can reveal insights about decision making and interval timer mechanisms. This study represents a functional advancement in the neuronal and molecular mechanisms of how memory and experience regulates a sexual behavior in male Drosophila. Overall, the manuscript can significantly benefit from general editing on clearer articulation of rationale and more appropriate interpretations of data. Higher resolution versions of bitmap figures is also crucial. The SMD experiments invite an alternative interpretation of data that centers on YL neurons' role on regulating mating duration in naive males, which alongside other roles of the mushroom body demonstrated in this manuscript, could add more depth to the study.

The findings in this manuscript will be of interest to a specialized audience interested in memory, neural circuits of behavior, and Drosophila sexual behavior. I work on Drosophila sexual behavior and circuits, but lacking experience on memory research, I am not as familiar with the mushroom body and conditioning experiments.

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Referee #1

Evidence, reproducibility and clarity

This study explores the molecular and neural circuitry mechanisms underlying sexual experience-dependent long-term memory (SELTM) in male Drosophila. The authors use behavioral, imaging, and bioinformatics approaches to identify YL neurons, a subset of mushroom body (MB) projecting neurons, as crucial for SELTM formation. They propose that YL neurons receive inputs from WG neurons via the sNPF-sNPFR pathway and implicate molecular players such as orb2, fmr1, MDAR2-CaMK, and synaptic plasticity in their function.

However, the evidence presented does not adequately support the authors' claims. The data fail to cohesively tell a logical story, and key conclusions appear to be based on assumptions and correlations rather than robust evidence.

Major comments:

1. The study identifies the knowledge gap (lines 103-104) but fails to integrate relevant literature, particularly Shohat-Ophir et al., Science (2012), and Zer-Krispil et al., Curr Biol (2018). These studies established that ejaculation induces appetitive memory in male Drosophila via corazonin and NPF neurons. The current study does not provide direct evidence that the "act of mating itself" drives SELTM, as it includes both courtship and copulation.
2. The nature of the observed long-lasting reduced mating duration requires clearer characterization: Is this an associative memory or experience-dependent behavioral plasticity? Can the formation of this long-term memory be blocked by protein synthesis inhibitors, such as cycloheximide?
3. While schematics illustrate the working hypotheses, the text lacks detailed explanations, leaving the reader unclear about the rationale behind certain conclusions.
4. The logic to draw certain conclusions was confusing and misleading.
   • For instance, the role of orb2 in SELTM is examined via knockdown in MB Kenyon cells (KCs) (using ok107>orb2-RNAi), which is irrelevant to the claim that orb2 functions in YL neurons. Additionally, RNAseq analyses (Fig. 1N-S) focusing on orb2 expression in a/b KCs are irrelevant to and cannot support the claim that Orb2 functions in YL neurons.
   • Similarly, the claim (lines 302-303) that sNPF-R expression is exclusive to MB KCs conflicts with data showing effects when sNPF-R is knocked down in YL neurons. How can knocking-down a gene, which is exclusively expressed in neural population A, in neural population B affect a phenotype? This inconsistency undermines the interpretation of the results.
   • Other examples include lines 223-227 and lines 246-249. It is very confusing how the authors came to the indications.
   • The authors also kept confusing the readers and themselves by mistakenly referring to MB KC a-lobe and YL a-lobe projection. They may know the difference between the two neural populations but they did not always refer to the right one in the text.
5. The imaging figures provided are unfocused and poorly resolved, making it difficult to assess data quality.
   • Colocalization analyses of orb2 and YL are unconvincing, especially given that orb2 is well-documented in literature as expressed in MB a-KCs and YL projection wrapping MB a-lobe. Maximum intensity projection images are insufficient for confirming colocalization; complete image stacks with staining of orb2, YL, and KCs (MB-dsRed) are needed for validation.
   • Quantification of imaging data appears flawed. For example, claims of orb2 and CaMKII upregulation in MB a-lobe projections (e.g., Fig. S2F-J, Fig. 3M,N) are confounded by widespread increases in intensity across the brain, lacking specificity.
   • The TRIC experiment analysis should normalize GFP signals to internal reference channel (RFP in the TRIC construct), as per established protocols in the original paper.
   • In Fig. 6H-J, methods for counting synapse numbers are not described. How are synapse numbers counted in these low-resolution images?
6. The study presents data from unrelated learning paradigms (e.g., olfactory associative learning, courtship conditioning; Fig. 7) without justifying how these paradigms relate to SELTM. Particularly, the authors claimed that SELTM is related to Gr5a, which leads to appetitive memories, which involve PAM dopaminergic neurons and MB horizontal lobes. However, the olfactory associative learning with electric shock and courtship conditioning lead to aversive memories, that involve PPL1 dopaminergic neurons and the vertical lobes.
7. Some figures are not referred to in the text. For example, Fig S1 K and L (also, what's the difference between these two figures?) and Fig 3M-R. What is MB-V3 in Fig 4J-K?

Minor issues

1. Fig 2F. YL projections are labeled as MBONs. Clarify whether YL neurons are the upstream or downstream (MBON) of KCs.
2. Extensive language polishing is required, as several sentences are unclear (e.g., lines 169-172).

Significance

This study potentially advances our understanding of how sexual experience modifies future mating behaviors. While previous work has shown that mating induces appetitive memory in males, the mechanisms linking this memory to future mating behavior remain poorly understood. This work could provide valuable insights into these mechanisms, pending appropriate revisions.

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The authors do not wish to provide a response at this time.

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Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript presents IGNITE (Inference of Gene Networks using Inverse kinetic Theory and Experiments), an unsupervised machine learning framework for constructing gene regulatory networks from single-cell RNA sequencing (scRNA-seq) data. IGNITE utilizes a kinetic inverse Ising model to infer gene interactions from binarized expression data and can predict genetic perturbation effects, such as those from knockout experiments. Although the application of inverse Ising models to network reconstruction is not entirely novel, IGNITE's specific implementation and its application to single-cell RNA sequencing data represent a new development. The method is tested on the transition from naive to formative states in murine pluripotent stem cells, a system the authors are highly knowledgeable about, and its performance is compared to state-of-the-art alternative methods.

Major concerns

My concern regards the generality of the method, particularly the entire pipeline presented, and the fairness of the performance comparison. These concerns can be easily addressed by the authors by better explaining their choices and their general applicability, and by toning down the conclusions about the comparison with existing inference methods.

The pre-processing steps are extensive, and their rationale is not always clear, though the results heavily depend on this analysis. Several steps appear to involve arbitrary choices optimized for specific outcomes, potentially introducing biases. The authors should better explain the rationale behind their choices to mitigate these concerns.

Specifically, part of the pipeline seems to be built to reproduce a specific expression pattern of 24 genes that some of the authors discovered in a previous paper. Although this prior knowledge could be useful and relevant in this specific system, it could limit the generality of the method. For example, the authors selected approximately 2000 genes based on prior knowledge and used a combination of t-SNE and UMAP for dimensionality reduction (although the two techniques have a similar goal). This specific combination seems to reproduce the pseudotime alignment the authors were expecting to find, but such prior information might not be available in general. Therefore, feature selection and the methods used to project data need more justification, especially if the goal is to create a general tool applicable across different biological systems.

Analogously, the clustering seems manually adjusted to match known expression patterns of 24 relevant genes, rather than being the result of an optimized clustering method. Additionally, the clusters overlap with different time points, raising concerns about potential batch effects. These issues should be addressed to strengthen the validity of the method.

The claims about the comparison with existing methods should be toned down. While the comparisons are useful and interesting, they might be biased due to the method's fine-tuning for the specific system studied. The claim that the model requires only scRNA-seq data is misleading, as strong prior biological knowledge was used to select, for example, the genes analyzed.

Significance

The manuscript is scientifically sound, clearly written, and deserves publication. The proposed method is quantitative, novel, theoretically grounded, and was tested in detail with appropriate null models and statistical methods. Moreover, IGNITE can be applied to various biological systems as the availability of scRNA-seq datasets is continuously growing. The paper will be of interest to a broad community of computational biologists and biology labs interested in gene regulation using scRNA-seq data.

The limitation, in my opinion, is the method's (particularly the pre-processing pipeline) fine-tuning for the specific biological system tested. Testing IGNITE on another biological system without pre-selected pre-processing steps or detailed biological priors would be more convincing and make the paper's conclusions much stronger. The comparison with other methods also may be slightly biased due to this fine-tuning.

My background is in statistical physics, with expertise in biological physics, specifically in mathematical modeling and data analysis in molecular biology.

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Referee #2

Evidence, reproducibility and clarity

Corridori et al introduce IGNITE, a computational framework to infer gene regulatory networks (GRNs) from scRNA-seq data leveraging the kinetic Ising model, which can be used to simulate synthetic gene expression and perform in-silico knockout experiments. Other similar frameworks exist, but none combine these three aspects together. The authors have generated a scRNA-seq of murine ESCs differentiation which they use to compare their method with others. Specifically they show that they can infer known regulatory interactions, that they can generate similar data than the original and that it can potentially predict gene expression changes in transcription factor knock-out perturbations.

Major comments:

• Many of the authors' claims are backed by qualitative results and not properly quantified. In Fig2, authors qualitatively compare intra gene correlations between genes for the original data and their prediction. Instead of just visualizing they should compute and report the Spearman correlation between the original expression and the predicted one. The Fraction of Agreement is not a good metric to compare knockout predictions since it is completely dependent on the class imbalance of signs, for example if the selected genes are 75% positive and 25% negative, a naive predictor that only outputs positive predictions will still have a high score. Instead, the authors should quantify this with Spearman correlation or RMSE and compare across methods. In FigS4a-b the authors qualitatively claim that other methods could not predict the expected cell composition, which they should quantify and report the values across methods. When comparing against the ground truth network, the fraction of correctly inferred interactions is technically the same as precision but is ignoring recall. I suggest the authors compute precision, recall and a combined F1 score to compare the evaluated methods. Authors claim that the method is scalable to a larger number of genes but no data is provided, they should show how their method compares to others when using a different number of cells and number of genes at memory usage and running time.
• The authors need to better describe which tests were performed when talking about significance, which thresholds and which corrections, if any, were employed.
• To reduce the number of dimensions of scRNA-seq data the authors use t-SNE and then from the obtained result UMAP to project the data into a lower dimensional space. This is fundamentally wrong since distances are not well preserved in t-SNE. Instead the authors should first employ PCA and then UMAP. Additionally, the authors use UMAP distances in the Slingshot pseudotime calculation. Similar to t-SNE, UMAP distances have no real meaning and should only be used for visualization purposes. Instead, the authors should provide Slingshot the obtained PCA embeddings.
• Dictys (PMID: 37537351) is a known GRN inference method that also can simulate gene expression but is missing in the benchmark, the authors should add it to the method comparison.
• The current manuscript is not reproducible since it is missing the method's code, the code to reproduce the figures and the generated scRNA-seq data.
• Authors claim that the method is scalable to a larger number of genes but no data is provided to back this claim. They should show how their method compares to others when using a different number of cells and number of genes.

Minor points:

• In the introduction, authors mention multimodal GRN inference methods but do not provide any references.
• In Table 1, CellOracle is annotated as not being able to do multiple KO which is wrong. Additionally, the authors mention that IGNITE uses no prior knowledge which is not really true since it requires pseudotime ordering. The authors should add a column to Table 1 whether methods require pseudotime.
• It is unclear what the dashed arrow of Fig1b means. Moreover, plotting gene expression values on top of UMAPs can be misleading, instead authors should plot the gene expression distributions binned by pseudotime.
• The authors report a p-value of 1.04x10-171 which is below detection limit (see PMID: 30921532). Authors should change it to an interval such as p < 2.2×10-16.
• To make CellOracle results easier to interpret and more comparable, authors should run it at the atlas level instead of at the cell type level, this way generating only one GRN. This can be achieved by assigning the same cluster label to all cells.
• Experimental values in FigS3b seem to have been repeated and do not match the previous ones for IGNITE and SCODE.
• It is unclear what the different circles mean in Fig5b.

Significance

This manuscript is an incremental and methodological work for specialized audiences. Its strengths are that the authors employ kinetic Ising model for GRN inference and that they provide a single framework capable of inferring, simulating and perturbing gene expression. The main limitations are that the claims should be better quantified and that the code and data need to be made accessible.

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Referee #1

Evidence, reproducibility and clarity

Summary

Corridori and colleagues propose IGNITE, a novel method to recover Gene Regulatory Networks (GRN) from single cell RNA-sequencing (scRNA-seq) data. Their method solves the inverse Ising problem generating a cohort of candidate GRN optimising it to minimise the difference to the input expression matrix. Authors report the IGNITE is able to predict wild type data and simulate both single and multiple gene knockouts. Authors benchmark this method on a in-house data set of differentiating pluripotent stem cells (PSC). They focus on a small set of genes known to be involved in PSC differentiation into formative cells. Authors benchmark IGNITE against state of the art tools (SCODE, MaxEnt and CELLORACLE). They evaluate IGNITE ability to predict wild type gene expression by comparing their data with experimental data and with SCODE. They conclude the tool has generative capacity comparable with SCODE. They also evaluate IGNITE ability to recover known interactions with respect to other tools without finding it to significantly outperform them.

Major comments

• Are the key conclusions convincing?

Conclusions appear convincing although model generalizability could be shown in a more thorough manner. For instance, analysing some other publicly available dataset could help demonstrate hyperparameters effects on GRN predictions and their robustness across different experiments. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

Claims are well supported by data. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

I think the work would benefit from an additional benchmark on a different cellular system. This experiment would show how hyperparameters generalise across datasets and would provide potential users insights how to tweak them.

Also, how does the model scale with the number of genes? A benchmark on computation time and resources required to infer GRN of growing size would be valuable in the adoption of this tool.

In addition, I think the GRN comparison benchmark presented in section (3.4) would benefit from a quantitative discussion. Authors show inferred GRNs in Figure 4 and S5. For instance, measuring matrix similarity (when appropriate) would help understanding how predicted GRN compare. I understand authors attempt to do so by focusing on validated interactions and computing the fraction of correctly inferred interactions (FCI) but I think a measurement of the overall similarity (eg. Pearson correlation) would add on this.

Another comment regards the dependency between Correlation Matrices Distance (CMD) and FCI, shown in Figure 5. I understand that IGNITE GRN that maximise FCI are not the same that minimise CMD. However, it looks like GRN that maximise FCI have higher value in terms of biological information. I wonder whether optimization for one or the other metric could be left to the end user as a tunable parameter.

Authors should discuss why the expression of some genes does not follow the expected trends (Fig 1C vs Fig S1A). Out of the 24 genes they select for their analysis, at least four do not follow the expected trends: Sox2, according to literature, is a Naive gene, however, in Figure 1C its gene expression pattern is more similar to Formative late genes. Other genes with similar "unexpected" patterns are Zic3, Etv4 and Sall4.

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

I think suggested experiments are doable as long as authors get publicly available data, i.e. the in-house dataset they generated for this study is enough to show applicability. For example datasets analysed in SCODE paper (https://doi.org/10.1093/bioinformatics/btx194) could be used as second benchmark. The point of applying the tool to another dataset is to show how it generalises across different biological systems, experiments and, potentially, sequencing technologies. - Are the data and the methods presented in such a way that they can be reproduced?

The methods section is really clear. To enable reproducibility both raw scRNA-seq data, the IGNITE source code and code written to benchmark it should be released in the public domain in appropriate repositories (eg. ENA, GitHub, Binder etc). - Are the experiments adequately replicated and statistical analysis adequate?

Yes.

Minor comments

• Specific experimental issues that are easily addressable.

Related to the Sox2 expression pattern is the binarization shown in Figure 2D. How is it possible that Sox2 is always marked as active? Could the authors clarify how these outlier behaviours emerge and propose mitigation strategies, if any?

In section 5.11.2 it is unclear if xi are in log scale or not. Since the model starts from binarized, log transformed expression values, should not generated ones be in the same scale as the input? - Are prior studies referenced appropriately?

Yes, referencing is clear. - Are the text and figures clear and accurate?

Yes, figures appear to be clear, readable and well documented both in captions and main text. - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Section 3.3 could be improved by better describing experimental datasets. Only in the methods section it is clearly stated that experimental data for single KO experiments were retrieved from the literature.

Check typesetting:

• parenthesis missing in Eq. 1
• Leftover $ in section 3.1
• Parenthesis missing in Section 3.3
• Misplaced comma in section 5.2.1

Significance

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

The paper presents a method to infer GRN from scRNA-seq data alone. Applications include GRN prediction and their perturbations. This paper represents a technical advance in the field as it is the first application of the inverse Ising problem GRN inference. - Place the work in the context of the existing literature (provide references, where appropriate).

The paper itself presents the landscape of GRN inference tools using scRNA-seq data: SCODE, MaxEnt and CELLORACLE. More tools exist, for instance SCENIC (https://doi.org/10.1038/nmeth.4463) mainly relies on co-expression matrices. Other tools exist but require additional data types e.g. GRaNIE and GRaNPA (https://doi.org/10.15252/msb.202311627) leverage on physical interaction data (ATAC-seq, ChIP-seq). Similarly DeepFlyBrain uses deep neural networks to infer eGRN in Drosophila (https://doi.org/10.1038/s41586-021-04262-z). The value of tools like IGNITE and its competitors is that they do not require additional data types, which, in turn, helps in controlling experimental costs. - State what audience might be interested in and influenced by the reported findings.

The paper might be of interest to biologists interested in regulation of gene expression. The tool might turn out to be useful in planning experimental work by guiding the choice of perturbations to introduce in experimental systems. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am a computational biologist.

I have no sufficient expertise to evaluate the mathematical details of the method.

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Reply to the reviewers

We appreciated the positive, detailed and helpful feedback from all three reviewers.

Reviewer 1.

Minor comments.

1. In the introduction, on page 2, the authors seem a little confused about the Plk1 Polo-box domain - text as written: "...kinase domain linked to tandem Polo-box domains (PBD)", and cite a review paper. Actually, there is only a single Polo-box domain in these kinases, which contains both Polo-boxes and a bit of the upstream linker region. The "PBD" terminology denotes his 2-Polo-box +linker structure. Perhaps it would be better here to cite the PBD structure (Elia et al., Cell, 2002) as a primary citation here.

Response: Thank you for finding this error, the text has been updated and the new citation included within the text on line 65.

1. Similarly, the line "...during the G2/M transition following successful DNA damage repair" cites the Seki et al paper, but those findings are shown in the Macurek et al paper, not the Seki et al paper.

_Response: _Thank you for finding this error, the new citation included within the text on line 69.

1. Using the model of the ternary complex as shown in Figure 1B, deletion constructs of Bora missing regions within the disordered loops, but still retaining the residues that bind the PBD, FW pocket and Aurora A, can be modeled and tested to see if such deletions can improve the ipTM scores and binding affinity.

Response: ____AlphaFold3 modelling was attempted with shorter regions of Bora to see the effect on the ipTM scores. Unfortunately, when Bora was reduced to shorter sequences, such as 18-88 or 18-45 modelled with 68-120, the models became inconsistent and of a low quality. Models were also created including the short region of Bora surrounding Ser252 that interacts with the polo box domain as well as Bora 18-120, but this had minimal effect on the calculated iPTM scores.

1. On page 5, "S112A" within the sentence "Unexpectedly, the F56A/W58A Bora was less efficiently phosphorylated on S112A (Supplementary Figure S11, F compared to H and Supplementary Table S4)." This should be "S112".

Response: ____Thank you for spotting this, the error has been corrected.

1. In the assays shown in Figure 2D, the presence of excess F56AW58A Bora that remained unphosphorylated on S112 may complicate the interpretation of the results. Can the authors show that the S112-phosphorylated F56AW68A Bora is predominantly bound to Aurora A in such a mixture, perhaps by NMR using labelled pS112 F56AW58A Bora and unlabeled S112 F56AW58A Bora?

_Response: _15N13C labelled of Bora 18-120 F56A W58A was produced and assigned. We then phosphorylated a sample using ERK2, tracking with NMR, and when the reaction had progressed to a 50:50 mixture of pSer112 and Ser112 (based on peak intensities) the kinase activity was quenched by addition of EDTA to sequester Mg2+. This produced a solution containing both pS112 and unphosphorylated S112 Bora species with marker peaks in HSQC spectra that could be used to directly compare Aurora-binding to the two species. Aurora-A was introduced to the sample and the peak intensities were monitored. Although both species are affected, there is much greater peak loss from the pS112 related peaks than those for unphosphorylated S112. This indicates that Aurora-A still preferentially binds pS112 Bora over S112 Bora when the F56A W58A mutation is present. This data has been included in Supplementary Figure S11.

1. Please expand Figure 3A to better show the FW pocket-forming residues on Plk1.

Response: ____Figure 3 has been amended to reduce the size of the sequence alignments so that 3A could be made slightly larger.

1. It would be helpful to label the peaks in the mass spectra in Fig. S11 with the phospho-species that they correspond to.

Response: ____This information has been added to the mass spectra in Fig. S11 (now supplementary Figure S14) to make them easier to view.

1. In the last paragraph on page 7, "see we" in the sentence "As well as a decrease in intensity around pSer112 in Bora, see we an overall effect with decreased intensity across most of the Bora sequence." Should be corrected to "we see".

Response: ____Thank you for spotting this, the error has been corrected.

1. While not required, it would be helpful if binding or Bora to Aurora A after Erk2 phosphorylation could be shown using fluorescence polarization or ITC to lend additional support to the NMR data for S112 and S59 phosphorylation and for CEP192 and TPX2 competition.

Response: ____This question has been partially answered in previous work by Tavernier et al. (2021), who showed improved binding of Aurora-A to Bora after Erk phosphorylation (by SPR), and they used labelled-TPX2 for a series of competition FP assays in that and the recent parallel study (Pillan et al. 2025).

We made initial efforts to perform additional FP assays using longer sections of Bora with different phosphorylation states but without success (perhaps due to the multisite-binding nature of the Bora–Aurora interaction, and difficulties with directly expressing phosphorylated Bora). The revised manuscript now includes some additional NMR data to show improved Bora–Aurora-A interaction after phosphorylation at Ser59 (Supplementary Figure S12).

1. The Aurora A phosphorylation motif has been further defined beyond that reported by the Pinna lab in 2005. Notably, the Ser-59 sequence on Bora (F-R-W-S-I), has, in addition to dominant selection for AR in the -2 position, both favorable -1 (W) and +1 (I) positions based on peptide library measurements (Alexander et al., Science Signaling 2011), further arguing that it may be an excellent Aurora A phosphorylation site.

Response: ____Thank you for highlighting this publication and how it further reinforces the likelihood of Ser59 being an effective substrate for Aurora-A, this should have been included in the original manuscript. This citation has now been included.

1. Have the authors tried to model the Drosophila melanogaster Aurora A-Bora-Polo complex to see if the Asn substitution of Bora Ser59, and the expected loss of the interactions between Bora pSer59 and Plk1 Arg59 and Aurora A Arg205 are compensated by other features?

Response: ____A ternary complex between the Drosophila melanogaster orthologues was modelled using AlphaFold3 (Uniprot code PLK1 (Q9VVR2 72-165), Aurora-A kinase (Q9VGF9) 151-411 and PLK1 (P52304 21-280)). This model was analysed using PDBe PISA to identify potential interactions between the three proteins, focusing on residues that are not conserved between the human and Drosophila sequences. From this model a potential salt bridge was identified between Drosophila Bora Lys120 and PLK1 Glu93 that would not occur in the human ternary complex given Lys120 is replaced with an asparagine. This could be an alternative (kinase-independent) method for improved Bora-PLK1 interaction. When comparing the Bora:Aurora-A side of the predicted interface and focusing on the short region of Bora in between Aurora-A and PLK1, there were no clear differences seen in the residues predicted to bind to Aurora-A. This modelling has been included in Supplementary Figure S10 C and D.

1. Given the relevance of the recent publication from Zhu et al. to this study, the authors may want to comment on, or test, the relative importance of PKA and Aurora A as a potential kinase for Bora S59. While those authors argue that PKA phosphorylates Bora on Ser-59, one could easily imagine a model in which either PKA or Aurora A could initially phosphorylate that site followed by a propagation step after initial Aurora A activation, in which Aurora A phosphorylation of Bora Ser-59 is the dominant process.

Response: ____A brief discussion of this recent publication has been added to the discussion, highlighting the similarities between the two publications and the importance of pSer59, as well as suggesting that in cellulo this modification could be achieved via more than one pathway. We also include some additional NMR data to show improved Bora–Aurora-A interaction after phosphorylation at Ser59 (Supplementary Figure S12).

Reviewer 2.

Minor comments.

Page 5: '... a K82R PLK1 mutant was used to increase the stability of the protein' - It is not clear how this mutation confers increased stability of the protein. The authors do not show any data to support this. Isn't the PLK1 K82R an ATP-binding-deficient, kinase-inactive mutant?

Response: ____Thank you for spotting this, the text has been updated to clarify that this version of PLK1 was used as it is acting as a substrate in the in vitro assay as we didn’t want to see any PLK1 activity within this assay.

All panels showing the Alphabridge diagram - it would be helpful if pictorial definitions of the colour codes were provided with corresponding score ranges (in addition to the description in the figure legend).

Response:____The AlphaBridge images have been updated to include details about the plDDT scores each of the different colours refer to.

Fig 2B - The Fluorescence anisotropy assay curves do not reach a plateau. Though the effect of mutation on binding affinity is pretty clear, if possible, I suggest including more data points at higher concentrations and estimating apparent Kd values.

__Response:____The direct binding assay was repeated with a higher concentration of PLK1 in order to try and see a top plateau. This was successful and has been included in Figure 2B (shown in black). The measured Kd was 24 ± 3 µM. __

The cartoon representation of the structures and molecular interfaces - better to avoid shadows, as they compromise the clarity of the figures, particularly the ones where side chains are shown in stick representation.

Response:____The structural images have been remade to remove the shadows and improve the clarity of the images.

It is important to discuss how the parallel studies by Verza et al. and Pillan et al. complement this study, highlighting similarities and differences.

Response:____References to these two publications and details on the similarities and differences seen are now included in the discussion.

Reviewer 3.

Major comments

It would be helpful to measure the level of pThr210 PLK1 in some experiments and graph the data. The current presentation is Fig. 2D-E is qualitative rather than quantitative.

Response:____Graphs displaying the levels of pThr210 produced in the assay are now shown in Supplementary Figure S4.

Have the authors measured the binding affinity of the F/W mutant Bora for PLK1 using the assay in Fig. 2B? Likewise, for Fig. 7 the S59 mutant could be tested to see if it affects PLK1 binding or activation.

Response:____The direct binding assay has been repeated with the use of a FAM-Bora peptide that incorporates the F56A W58A mutation which shows reduced binding (Figure 2B, shown in blue). A version of the Bora peptide phosphorylated on Ser59 was also tested in the direct binding assay and this shows a similar affinity for PLK1 to the wild-type sequence (Figure 2B, shown in red compared to the wild-type shown in black).

It would be helpful if measurements of pThr210 PLK1 for all conditions were shown in the graph Fig. 7F.

Response:____This graph has been updated to include the levels of phosphorylation seen for PLK1 in all of the conditions tested.

Minor comments

I found Figure S1B easier to understand than Fig S1A and Fig 1A-B. Some of the supplemental data Fig. S1C-E could be moved to a revised Figure 1, dropping the current Fig. 1A-B. Can the interaction plots (Fig. S1C-D) be rotated to have the same original at the top and order of proteins (i.e. Bora > Aurora A > {plus minus} PLK1 depending on the plot).

Response:____Figure 1 and S1 have been rearranged to hopefully make them easier to understand, with all AlphaFold3 models of the full-length sequences kept in the supplementary figure and the focus in 1B just on the truncated model. The AlphaBridge plots have been rotated as suggested.

Figure 3F. Typo "Strongyl" not "Strongly".

Response:____Thank you for spotting this, this has been corrected in the updated manuscript.

Figure 3 could be supplemental material.

Response:__Thank you for your suggestion, but we have decided to keep this as a main figure.

Fig. 7E. Run a positive control reaction +ERK2 on the second gel to allow direct comparison of pThr210 across all the conditions tested.

Response:____These samples have been rerun on the same membrane and the levels of phosphorylation have been quantified and included in Figure 7F.

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Referee #3

Evidence, reproducibility and clarity

Summary.

Miles and co-workers have carried out a careful and high-quality study of the activation mechanisms of the mitotic kinase PLK1. Multiple proteins have been implicated in PLK1 activation and localisation as cell enter and pass through mitosis. Initial activation of PLK1 is promoted by a complex of Bora with another kinase Aurora A. Later in mitosis, this activated PLK1 associates with mitotic spindle and centrosome proteins regulating different aspects of mitosis and cytokinesis. In this study, Miles et al. extend previous work on this question by proposing and testing detailed models for Bora/Aurora A-mediated activation of PLK1 to elucidate the mechanism of this reaction.

Using the latest Alphafold they generate a series of models of the PLK1/Bora/Aurora A complex to home in on the key regions mediating interactions of the three proteins. This approach suggests an arrangement where the first ~120 amino acids of Bora wrap Aurora A and create an interaction surface for the N-terminal kinase domain of PLK1. This orients Thr210 in PLK1 towards Aurora A creating a situation likely favourable for phosphorylation, although has the authors discuss there are some caveats to this. A further prediction of the modelling helps explain the requirement for Bora phosphorylation to promote the interaction with Aurora A. This data is presented in Fig. 1 and Fig. S1-S3.

In the subsequent figures the details of this model are tested using biochemical assays and structural biology methods to validate key predictions. First the PLK1 interaction with Bora was shown to require the conserved F/W motif of Bora and a conserved pocket close to R106 on PLK1 (Fig. 2 and 3). In reconstituted PLK1 activation assays the F/W motif mutant Bora showed greatly attenuated pThr210 phosphorylation. This reaction also required phosphorylation of Bora at S112, presumably due to the interaction with Aurora A. An R106A mutant PLK1 showed reduced binding to Bora and reduced kinase activation. This data is clear and provides compelling support for the model.

Using NMR the authors then investigate the interaction between Bora and Aurora A, and more specifically the requirement for Bora phosphorylation at Ser112. The NMR data in Fig. 4 and Fig. 6 provide good support for the Alphafold model. A helpful comparison with known Aurora A binding proteins is also shown to highlight the way CEP192, TPX2 and TACC3 contact a series of conserved pockets on the surface of Aurora A which are common to the Bora interaction. S59 phosphorylation by Aurora A is also shown to play an important role in contacting PLK1 and is required for pThr210 phosphorylation.

In summary, the authors have made valuable progress in working out details of the PLK1 activation mechanism, that extends previous work in the field.

Major comments.

It would be helpful to measure the level of pThr210 PLK1 in some experiments and graph the data. The current presentation is Fig. 2D-E is qualitative rather than quantitative.

Have the authors measured the binding affinity of the F/W mutant Bora for PLK1 using the assay in Fig. 2B? Likewise, for Fig. 7 the S59 mutant could be tested to see if it affects PLK1 binding or activation.

It would be helpful if measurements of pThr210 PLK1 for all conditions were shown in the graph Fig. 7F.

Minor comments.

I found Figure S1B easier to understand than Fig S1A and Fig 1A-B. Some of the supplemental data Fig. S1C-E could be moved to a revised Figure 1, dropping the current Fig. 1A-B. Can the interaction plots (Fig. S1C-D) be rotated to have the same original at the top and order of proteins (i.e. Bora > Aurora A > {plus minus} PLK1 depending on the plot). Figure 3F. Typo "Strongyl" not "Strongly". Figure 3 could be supplemental material. Fig. 7E. Run a positive control reaction +ERK2 on the second gel to allow direct comparison of pThr210 across all the conditions tested.

Significance

Timely and orchestrated activation of multiple mitotic protein kinases is crucial for the alignment and segregation of chromosomes, and for the process of cell division. In this study the authors explore how activation of the mitotic kinase PLK1 is triggered by another mitotic kinase Aurora A, and the role played by a scaffold protein Bora.

Strengths: Detailed analysis of mechanism using biochemical and structural approaches.

Limitations: The study is focussed on the biochemical and structural mechanisms rather than the cellular outcomes. Some data would benefit from additional quantitative measurement.

Relevance: Cancer and cell biology due to the role of Aurora A in many cancers.

Reviewer expertise: Biochemistry, molecular and cell biology.

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Referee #2

Evidence, reproducibility and clarity

Summary:

PLK1 is one of the master regulators of cell division. The activation of PLK1 requires the activation loop phosphorylation at T210, mediated by Aurora A kinase. However, Aurora A phosphorylation of PLK1 T210 requires Bora, one of the several activators of Aurora A kinase. While the molecular requirement of Aurora A kinase and Bora for PLK1 activation is well established, the mechanistic understanding of how Bora facilitates PLK1 activation by Aurora A has remained an important open question for a long time. Exploiting the latest development in AI-driven structure prediction, three independent studies provide a structural and mechanistic basis for PLK1 activation by Aurora A and Bora. Here, Miles et al. have generated AlphaFold models, further characterised some of the interfaces using NMR, and validated the contribution of intermolecular interactions at suggested interfaces in vitro using recombinant proteins in kinase assays. Overall, this is a well-executed work providing important new insights into our understanding of the activation of the critical regulator of cell division, PLK1. However, as the authors have highlighted in the discussion section, one limitation of this modelling study is that the models still do not entirely explain how these interactions facilitate the phosphorylation of Thr210ur, as this residue is oriented far away from Aurora A's active site for the reaction to take place. Despite this limitation, I believe this is an important work that advances our understanding significantly.

Comments:

Experimental data satisfactorily support claims. Hence, most of my comments are minor in nature.

Points to consider during revision:

Page 5: '... a K82R PLK1 mutant was used to increase the stability of the protein' - It is not clear how this mutation confers increased stability of the protein. The authors do not show any data to support this. Isn't the PLK1 K82R an ATP-binding-deficient, kinase-inactive mutant?

All panels showing the Alphabridge diagram - it would be helpful if pictorial definitions of the colour codes were provided with corresponding score ranges (in addition to the description in the figure legend).

Fig 2B - The Fluorescence anisotropy assay curves do not reach a plateau. Though the effect of mutation on binding affinity is pretty clear, if possible, I suggest including more data points at higher concentrations and estimating apparent Kd values.

The cartoon representation of the structures and molecular interfaces - better to avoid shadows, as they compromise the clarity of the figures, particularly the ones where side chains are shown in stick representation.

It is important to discuss how the parallel studies by Verza et al. and Pillan et al. complement this study, highlighting similarities and differences.

Significance

As highlighted in the summary, a mechanistic understanding of how PLK1 is activated by Aurora A kinase and its activator Bora has remained a long-standing open question. As PLk1 is one of the major regulators of cell division, which exerts its function (via phosphorylating numerous substrates) during different stages of mitosis, understanding its activation mechanism is of critical interest for those working on the cell cycle in general and cell division in particular. A key limitation of this study is the lack of any cellular functional evaluation of the interaction interfaces.

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Referee #1

Evidence, reproducibility and clarity

Miles et al. used a combination of AlphaFold modeling, biochemical assays of mutant constructs and NMR spectroscopy to model the ternary complex of Aurora A, Bora and Plk1, and elucidate how Bora can act as a molecular bridge that facilitates the phosphorylation of the activation loop Thr210 within Plk1 by Aurora A. Their studies identified an interaction between residues 52-73 within Bora and the 'FW' pocket on the N-terminal lobe of Plk1, which binds Phe56 and Trp58 of Bora. Additionally, Ser59 of Bora was identified as a good Aurora A substrate using a Bora peptide array, and pSer59 was predicted to form bridging interactions with Aurora Arg205 and Plk1 Arg59. This was supported by NMR and biochemical assays. In addition, the authors validate that phosphorylation of Ser-112 on Bora enhances stabilization of the Aurora A-Bora complex Overall, the model revealed novel details of the interactions within the Aurora A-Bora-Plk1 ternary complex that are supported by the biochemical and NMR data. The work will be of significant interest to basic scientists whose work involves protein kinase signaling, cell division/mitosis, signal transduction, and cancer biology. We recommend publication of this manuscript with the following minor changes and additions.

1. In the introduction, on page 2, the authors seem a little confused about the Plk1 Polo-box domain - text as written: "...kinase domain linked to tandem Polo-box domains (PBD)", and cite a review paper. Actually, there is only a single Polo-box domain in these kinases, which contains both Polo-boxes and a bit of the upstream linker region. The "PBD" terminology denotes his 2-Polo-box +linker structure. Perhaps it would be better here to cite the PBD structure (Elia et al., Cell, 2002) as a primary citation here.
2. Similarly, the line "...during the G2/M transition following successful DNA damage repair" cites the Seki et al paper, but those findings are shown in the Macurek et al paper, not the Seki et al paper.
3. Using the model of the ternary complex as shown in Figure 1B, deletion constructs of Bora missing regions within the disordered loops, but still retaining the residues that bind the PBD, FW pocket and Aurora A, can be modeled and tested to see if such deletions can improve the ipTM scores and binding affinity.
4. On page 5, "S112A" within the sentence "Unexpectedly, the F56A/W58A Bora was less efficiently phosphorylated on S112A (Supplementary Figure S11, F compared to H and Supplementary Table S4)." This should be "S112".
5. In the assays shown in Figure 2D, the presence of excess F56AW58A Bora that remained unphosphorylated on S112 may complicate the interpretation of the results. Can the authors show that the S112-phosphorylated F56AW68A Bora is predominantly bound to Aurora A in such a mixture, perhaps by NMR using labelled pS112 F56AW58A Bora and unlabeled S112 F56AW58A Bora?
6. Please expand Figure 3A to better show the FW pocket-forming residues on Plk1.
7. It would be helpful to label the peaks in the mass spectra in Fig. S11 with the phospho-species that they correspond to.
8. In the last paragraph on page 7, "see we" in the sentence "As well as a decrease in intensity around pSer112 in Bora, see we an overall effect with decreased intensity across most of the Bora sequence." Should be corrected to "we see".
9. While not required, it would be helpful if binding or Bora to Aurora A after Erk2 phosphorylation could be shown using fluorescence polarization or ITC to lend additional support to the NMR data for S112 and S59 phosphorylation and for CEP192 and TPX2 competition.
10. The Aurora A phosphorylation motif has been further defined beyond that reported by the Pinna lab in 2005. Notably, the Ser-59 sequence on Bora (F-R-W-S-I), has, in addition to dominant selection for AR in the -2 position, both favorable -1 (W) and +1 (I) positions based on peptide library measurements (Alexander et al., Science Signaling 2011), further arguing that it may be an excellent Aurora A phosphorylation site.
11. Have the authors tried to model the Drosophila melanogaster Aurora A-Bora-Polo complex to see if the Asn substitution of Bora Ser59, and the expected loss of the interactions between Bora pSer59 and Plk1 Arg59 and Aurora A Arg205 are compensated by other features?
12. Given the relevance of the recent publication from Zhu et al. in https://doi.org/10.1038/s41467-025-63352-y to this study, the authors may want to comment on, or test, the relative importance of PKA and Aurora A as a potential kinase for Bora S59. While those authors argue that PKA phosphorylates Bora on Ser-59, one could easily imagine a model in which either PKA or Aurora A could initially phosphorylate that site followed by a propagation step after initial Aurora A activation, in which Aurora A phosphorylation of Bora Ser-59 is the dominant process.

-Dan Lim and Michael Yaffe

Significance

The work is well done and clearly presented.

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Reply to the reviewers

Reviewer #1

Major comments:

(comment #1)- It is interesting that TRF2 loss not only fails to increase γH2AX/53BP1 levels but may even slightly reduce them (e.g., Fig. S2c and the IF images). While the main hypothesis is that TRF2 loss does not trigger telomere dysfunction in NSCs, this observation raises the possibility that TRF2 itself contributes to DDR signaling (ATM-P, γH2AX, 53BP1) in these cells and that in its absence, cells are not able to form those foci. To exclude the possibility that telomere-specific DDR is being missed due to an overall dampened DDR response in the absence of TRF2, it would be informative to induce exogenous DSBs in TRF2-depleted cells and test DDR competence (e.g., IF for γH2AX/53BP1). In other words, are those NSC lacking TRF2 even able to form H2AX/53BP1 foci when damaged? In addition, it would be interesting to perform telomere fusion analysis in TRF2 silenced cells (and TRF1 silenced cells as a positive control).

We acknowledge a slight reduction; however, this difference is not statistically significant (Fig S2c,e). We will quantify the levels of DDR markers upon TRF2 loss and exogenous DSBs and include it in the subsequent revision.

(comment #2)-A TRF2 ChIP-seq should be performed in NSC as this list of genes (named TAN genes in the text) was determined using a ChIP performed in another cell line (HT1080). For the ChIP-qPCR in the various conditions, primers for negative control regions should be included to show the specific binding of TRF2 to the promoter of the genes associated with neuronal differentiation. For example, an intergenic region and/or promoters of genes that are not associated with neuronal differentiation (or don't contain a potential G4). The same comment goes true for the gene expression analysis: a few genes that are not bound by TRF2 should be included as negative controls to exclude a potential global effect of TRF2 loss on gene expression (ideally a RNA-seq would be performed instead). We have performed NSC-specific TRF2 ChIP-seq for an upcoming manuscript, which confirms TRF2 occupancy at multiple promoters of differentiation-associated genes. These data are provided solely for confidential evaluation by the designated reviewers.

Regarding the ChIP-qPCR control experiments: We thank reviewer for pointing this out, indeed we included controls in our PCR assays as positive (telomeric) and TRF2-nonbinding loci (GAPDH, RPS18, and ACTB, based on HT1080 TRF2 ChIP-seq data) as negative controls. These results were not included earlier for clarity given that we were presenting several ChIP-PCR figures - in response to the comment we have included this now in the revised version (Fig. S3d,e). Gene expression analyses show selective upregulation of the TAN genes upon TRF2 loss (data normalised to GAPDH); whereas negative control genes lacking TRF2 binding (RPS18, ACTB) remain unchanged, ruling out non-specific effects. (Fig S3f,g,j,k).

-(comment #3) A co-IP should be performed between the TRF2 PTM mutant K176R or WT TRF2 and REST and PRC2 components to directly show a defect of interaction between them when TRF2 is mutated (a co-IP with DNase/RNase treatment to exclude nucleic-acid bridging). The TRF2 PTM mutant T188N also seems to lead to an increased differentiation (Fig. S5a). Could the author repeat the measure of gene expression and co-IP with REST upon the overexpression of this mutant too?

We confirm that DNase/RNase is routinely included in our pull-down experiments to exclude nucleic-acid bridging, with detailed methodology now elaborated in the Methods section. Not including this in the manuscript Methods was an oversight from our side. Our data demonstrate that only REST directly interacts with TRF2, while TRF2 engages PRC2 indirectly via REST, as also previously shown by us and others (page 6; ref. [62]; Sharma et al., ref. [15]).

We thank the reviewer for noting the apparent differentiation in Fig. S5a. However, this observation represents rare spontaneous differentiation event and is not statistically significant (as shown in Fig S5b). Consistently, gene expression analysis of the TRF2-T188N mutant shows no significant change in TRF2-associated neuronal differentiation (TAN) genes. Therefore, Co-IP for TRF2-T188N with REST was not done.

(comment #4) - The authors show that the G4 ligands SMH14.6 and Bis-indole carboxamide upregulate TAN genes and promote neuronal differentiation, but the underlying mechanism remains unclear. Bis-indole carboxamide is generally considered a G4 stabilizer, while SMH14.6 is less characterized and should be better introduced. The authors should clarify how G4 stabilization would interfere with TRF2 binding, it seems that it would likely be by blocking access. A more detailed discussion, and ideally TRF2 ChIP after ligand treatment and/or G4 helicase treatment, would strengthen the model.

We clarify that Bis-indole carboxamide acts as a G4 stabilizer, while SMH14.6 is also a noted G4-binding ligand that stabilizes G4s (ref. [15]). The exclusion of TRF2 from G4 motifs in gene promoters by G4-binding ligands has also been documented previously (ref. [18]). In line with these findings, ChIP experiments performed following ligand treatment revealed a decreased occupancy of TRF2 at TAN gene promoters, supporting the proposed mechanism (added Fig. 6h).

Minor comments:

• Supp Figures related to the scRNA-seq are difficult to read (blurry).

Corrected

• Fig S1h: The red box mentioned in the legend is not visible

Corrected

• In the text, the Figures 1 f-g are misannotated as Fig 1m and l

Corrected

• The symbol γ of γH2AX is missing in the text

Corrected

• Fig.3d, please indicate in the legend that it is done in SH-SY5Y.

Added SH-SY5Y in the legend of Fig. 3d.

• Fig. S3b: Please consider replotting this panel with an increased y-axis scale. As currently presented, the TRF2 ChIP-seq peaks at several promoters appear truncated by the scaling.

Corrected

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

1. For most of the data graphs in the manuscript, there is no indication of the number of independent biological replicates carried out (which should ideally be plotted as individual dots overlaying the column graphs), or what the error bars represent, or what statistical test was used. All the figure legends and methods have now been updated with the corresponding biological replicates per experiment, with error bars as SD/SEM and the corresponding statistical test along with p values.

Figure S1.1a: needs a marker to show that the tissue is dentate gyrus.

We acknowledge the reviewers' concern that high-magnification images alone make it difficult to verify whether the fields are taken from the correct anatomical location. The dentate gyrus (DG) of the hippocampus is a well-defined structure. In the revised figure (Fig S1.1a), we now include a low-magnification image showing the entire hippocampus, including the CA fields, along with two high-magnification fields specifically from the DG region. Consistent with our claim, the co-immunostaining demonstrates that Sox2-positive neural stem cells in the DG are also positive for TRF2.

Figure 1c (and all other flow cytometry panels throughout the manuscript): it is not clear if the expression of any of these proteins, except maybe MAP2, are significantly different in the presence or absence of TRF2. These differences need to be presented more quantitatively, with the results compiled from multiple biological replicates and analysed statistically. I am not sure that flow cytometry is the best way to determine differences in protein expression levels for non-surface proteins, because many of the reported differences are not at all convincing.

To detect intracellular/nuclear proteins by flow cytometry, cells were permeabilized using pre-chilled 0.2% Triton X-100 for 10 minutes, as described in the Methods section.

We have revised the figures (Fig 1c,e) and now included statistical analysis from three independent biological replicates for these experiments.(Fig S1.4h-j, S2e, S6d)

Fig 1d: has TRF2 been effectively silenced in this experiment? There appears to be just as many TRF2+ nuclei in the "TRF2 silenced" panel vs the control, including in the cells with neurite outgrowths.

Quantification of nuclear levels of TRF2 showing decrease in nuclear TRF2 has been included in supplementary Fig S1g.

Fig 2a-c: these experiments need a positive control, showing increased expression of these proteins in mNSC and SH-SY5Y cells in response to a DNA damaging agent. Again, flow cytometry may not be the best method for this; immunofluorescence combined with telomere FISH would be more convincing.

We confirm that doxorubicin induces 53BP1 foci (IF-FISH Sup Fig. S2b) and TRF1 silencing elevates γH2AX (Sup Fig. S2c) validating DDR sensitivity. Unlike TRF2 loss (Fig. 2a-c), no TIFs appear with IF and telomere probes (Fig. 2d, Sup Fig. 2a), and without TIFs, there is no telomeric fusion. Flow cytometry was performed with Triton X- 100 to target nuclear protein. These findings adequately address the concern; therefore, further IF-FISH experiments were not included in the present study.

To conclude that telomere damage is not occurring, an independent marker of such damage, such as telomere fusions, should also be measured.

In response to uncapped telomeres, ATM kinase activates the DNA damage response (DDR), recruiting γH2AX and 53BP1 to telomeres, which precedes the end-to-end fusions (Takai et al., 2003; Maciejowski & de Lange, 2015; Takai et al., 2003; d'Adda di Fagagna et al., 2003; Cesare & Reddel, 2010; Hayashi et al., 2012; Sarek et al., 2015). We observe no DDR activation or foci (Fig. 2; Sup. Fig. 2). This absence of a DDR response and TIFs indicates no telomere uncapping, negating the need for direct telomere fusion analysis.

Figure S2b is lacking a no-doxorubicin control.

Untreated control has been included Fig. S2b.

Figures 3a and 3b need a positive control (e.g. TRF2 binding to telomeric DNA) and a negative control (e.g. a promoter that did not show any TRF2 binding in the HT1080 ChiP-seq experiment in Fig S3).

We have included positive (telomere) and negative (GAPDH) controls (based on HT1080 TRF2 ChIP-seq data) for the TRF2 ChIP assay in Supplementary Fig. S3d,e. Additionally, positive and negative controls for all ChIP experiments conducted in this study are presented in Supplementary Figs. S3d, S3e, S3h, S3i, S4c-h, and S5c-e

The data in Figure 3 would be more compelling if all experiments were also performed in fibroblasts to confirm the cell-type specificity of the effect.

Our HT1080 fibrosarcoma ChIP-seq data (ref. [18]; Sup. Fig. 3a,b) show TRF2 binding to TAN gene promoters in a fibroblast-derived model, with enrichment in neurogenesis-related genes (refs. [19,20]). In fibroblasts TRF2 depletion, as expected, induce telomere dysfunction and DDR (Fig. 2d; Sup. Fig. 2a), and eventually cell-cycle arrest and cell death as also reported earlier (van Steensel et al., 1998; Smogorzewska & de Lange, 2002). Therefore, the suggested experiments which would require sustained TRF2-depletion are not possible to perform in fibroblasts. TRF2 occupancy on the promoter of the genes in question in cells other than NSC was noted in HT1080 cells (ref. [18]; Sup. Fig. 3a,b).

No references are provided for the TRF2 posttranslational modifications on R17, K176, K190 and T188. What is the evidence for these modifications, and is it known if they participate in the telomeric role of TRF2?

These lines with references have been included in the manuscript (highlighted in blue).

R17 methylation enhances telomere stability (66). K176/K190 acetylation stabilizes telomeres and is deacetylated by SIRT6 (67). T188 phosphorylation facilitates telomere repair after DSBs(68). These PTMs primarily support telomeric roles.

The experiments in Fig 5 should also be performed with WT TRF2, to confirm that effects are not due to the overexpression of TRF2.

WT TRF2 shows no differentiation phenotype and change in TAN gene expression (Fig. 1f,g; 3h, Sup Fig. 5a). Confirming effects are not due to TRF2 overexpression.

Fig 5c has not been described in the text, and there are multiple technical problems with the TRF2 WT experiment: i) There appears to be significant background binding of REST to the IgG beads, though this blot has such high background it is hard to tell (the REST blot in Fig S4b is also of poor quality), ii) TRF2 is migrating at two different positions in the Input and IP lanes, and the TRF2 band in the K176R blot is at a different position to either, and iii) the relative loading of the Input and IP lanes is not indicated, so it's not clear why K176R appears to be so enriched in the IP.

We acknowledge the oversight in not citing Fig 5c in the manuscript. This has been corrected, and, highlighted in blue in the revised manuscript.

i) Multiple optimization attempts were made for the Co-IP experiments, and the presented figure reflects the best achievable result despite REST blot smearing, a pattern also reported previously (Ref. 65). The TRF2-REST interaction is well established, and a similar background was also observed in the cited study

ii)Variable migration patterns of TRF2 were also noted in the cited study (Ref. 65), consistent with our observations. Our primary emphasis, however, is on the TRF2 K176R mutant, which clearly disrupts its interaction with REST.

iii)The input loading corresponds to 10% of the total lysate. As the experiments were conducted independently, variations in transfection and pull-down efficiencies may account for observed differences.

To rule out indirect effects of the G4 ligands on the results in Fig 6g, the binding of BG4 and TRF2 at the promoters of these genes should be measured by ChIP.

To confirm that G4 ligand effects on TAN gene promoters are direct, TRF2 occupancy was assessed using ChIP. Significantly decreased occupancy of TRF2 was noted at TAN gene promoters, (added Fig. 6h). This implies that ligand-induced changes in TRF2 binding are directly linked to promoter-level G4 stabilization.

Minor comments:

1. The size of all the size markers in western blots should be added to the figures. Size has been included in all the western blots

2. There are several figure panels that are incorrectly referenced in the text, e.g. Fig S1.1 (e-f) should be Fig S1.1 (e-h); Fig. 1m should be Fig. 1f; Figs 5e and 5f have been swapped.

Corrected.

1. Fig S1.4 is not referred to in the text. It is not clear what the purpose of Fig S1.4a is.

The following line has been included in the manuscript highlighted in blue.

Neurospheres were characterized using PAX6, a NSC marker (Fig S1.4a).

Are the experiments in Figs 3e, 4a, 4c and 4e using 4-OHT treatment, or siRNA? If the latter, I don't think a control for the effectiveness of the knockdown in this cell type has been included anywhere in the manuscript.

It is using siRNA, a western blot showing the effectiveness of knockdown is presented in supplementary figure S4c (now S4a).

The lanes of the western blots in Fig S4c are not labelled.

Corrected.

1. Given that the experiments in Fig 5 were carried out on a background of endogenous WT TRF2 expression, presumably the K176R mutant is having a dominant negative effect. To understand the mechanism of this effect (e.g, is it simply due to replacement of endogenous WT TRF2 at its genomic binding sites by a large excess of exogenous K176R, or is dimerisation with WT TRF2 needed?) it would be helpful to know the relative expression levels of endogenous and K176R TRF2.

To address the query, qRT-PCR with 3′ UTR-specific primers showed no change in endogenous TRF2 mRNA upon K176R expression in SH-SY5Y cells, while primers detecting total TRF2 revealed ~10-fold higher expression of K176R compared to control (Figure below). This indicates the absence of suppression of endogenous TRF2 mRNA. Given that the mutant's DNA binding is intact (Fig. 5f), the dominant-negative effect of K176R likely arises from overexpression of the exogenous mutant.

For the sentence "...and critical for transcription factor binding including epigenetic functions that are G4 dependent" (bottom of page 3 of the PDF), the authors cite only their own prior papers, but there are examples from others that could be cited.

We have incorporated citations from other research groups, now included as references 23-26.

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Referee #2

Evidence, reproducibility and clarity

This manuscript examines the effects of depletion of the telomeric protein TRF2 in mouse neural stem cells, using mice carrying a floxed allele of TRF2 and inducible Cre recombinase under the control of the stem cell-specific Nestin promoter. The results are also backed up in a human neuroblastoma cell line that has progenitor-like properties. There is no apparent induction of telomere damage in either of these cell types, but there is an increase in expression of neurogenesis genes. This is accompanied by an increase in binding of TRF2 to the relevant promoters, and evidence is provided that this binding involves G-quadruplexes in the promoters.

On the whole, these core findings of this study are interesting, and reasonably robust. However, the study as a whole is marred by a large number of technical issues and missing controls which should be addressed prior to publication:

1. For most of the data graphs in the manuscript, there is no indication of the number of independent biological replicates carried out (which should ideally be plotted as individual dots overlaying the column graphs), or what the error bars represent, or what statistical test was used.
2. Figure S1.1a: needs a marker to show that the tissue is dentate gyrus.
3. Figure 1c (and all other flow cytometry panels throughout the manuscript): it is not clear if the expression of any of these proteins, except maybe MAP2, are significantly different in the presence or absence of TRF2. These differences need to be presented more quantitatively, with the results compiled from multiple biological replicates and analysed statistically. I am not sure that flow cytometry is the best way to determine differences in protein expression levels for non-surface proteins, because many of the reported differences are not at all convincing.
4. Fig 1d: has TRF2 been effectively silenced in this experiment? There appears to be just as many TRF2+ nuclei in the "TRF2 silenced" panel vs the control, including in the cells with neurite outgrowths.
5. Fig 2a-c: these experiments need a positive control, showing increased expression of these proteins in mNSC and SH-SY5Y cells in response to a DNA damaging agent. Again, flow cytometry may not be the best method for this; immunofluorescence combined with telomere FISH would be more convincing.
6. To conclude that telomere damage is not occurring, an independent marker of such damage, such as telomere fusions, should also be measured.
7. Figure S2b is lacking a no-doxorubicin control.
8. Figures 3a and 3b need a positive control (e.g. TRF2 binding to telomeric DNA) and a negative control (e.g. a promoter that did not show any TRF2 binding in the HT1080 ChiP-seq experiment in Fig S3).
9. The data in Figure 3 would be more compelling if all experiments were also performed in fibroblasts to confirm the cell-type specificity of the effect.
10. No references are provided for the TRF2 postranslational modifications on R17, K176, K190 and T188. What is the evidence for these modifications, and is it known if they participate in the telomeric role of TRF2?
11. The experiments in Fig 5 should also be performed with WT TRF2, to confirm that effects are not due to the overexpression of TRF2.
12. Fig 5c has not been described in the text, and there are multiple technical problems with the TRF2 WT experiment: i) There appears to be significant background binding of REST to the IgG beads, though this blot has such high background it is hard to tell (the REST blot in Fig S4b is also of poor quality), ii) TRF2 is migrating at two different positions in the Input and IP lanes, and the TRF2 band in the K176R blot is at a different position to either, and iii) the relative loading of the Input and IP lanes is not indicated, so it's not clear why K176R appears to be so enriched in the IP.
13. To rule out indirect effects of the G4 ligands on the results in Fig 6g, the binding of BG4 and TRF2 at the promoters of these genes should be measured by ChIP.

Minor comments:

1. The size of all the size markers in western blots should be added to the figures.
2. There are several figure panels that are incorrectly referenced in the text, e.g. Fig S1.1 (e-f) should be Fig S1.1 (e-h); Fig. 1m should be Fig. 1f; Figs 5e and 5f have been swapped.
3. Fig S1.4 is not referred to in the text. It is not clear what the purpose of Fig S1.4a is.
4. Are the experiments in Figs 3e, 4a, 4c and 4e using 4-OHT treatment, or siRNA? If the latter, I don't think a control for the effectiveness of the knockdown in this cell type has been included anywhere in the manuscript.
5. The lanes of the western blots in Fig S4c are not labelled.
6. Given that the experiments in Fig 5 were carried out on a background of endogenous WT TRF2 expression, presumably the K176R mutant is having a dominant negative effect. To understand the mechanism of this effect (e.g is it simply due to replacement of endogenous WT TRF2 at its genomic binding sites by a large excess of exogenous K176R, or is dimerisation with WT TRF2 needed?) it would be helpful to know the relative expression levels of endogenous and K176R TRF2.
7. For the sentence "...and critical for transcription factor binding including epigenetic functions that are G4 dependent" (bottom of page 3 of the PDF), the authors cite only their own prior papers, but there are examples from others that could be cited.

Significance

The protein TRF2 was first identified as one of the core proteins that bind to the double-stranded region of telomeric DNA, and its many-faceted role in telomere protection has been well studied over the last 3 decades. More recent data from several labs indicate that TRF2 has additional roles outside the telomere, including in regulating gene expression, but these roles are so far much less characterised. Also, it has recently been shown that mouse ES cells, unexpectedly, do not require TRF2 for telomere protection (references 3 and 4 in this paper).

The findings of the current findings expand the type of stem cells in which TRF2 is likely to be playing more of a role elsewhere in the genome, and not at telomeres, and hence is likely to be of high interest to both researchers of telomere biology, and those interested in the regulation of stem cell biology and neurogenesis.

The strengths of the study are its novelty, its use of an inducible system to knock out TRF2 in the mouse neural stem cells of interest, and a thorough analysis of changes in gene expression and promoter occupancy across a range of genes of relevance to neurogenesis. The major weakness of the study, as descibed above, is the large number of technical problems, missing controls and missing indications of biological reproducibility.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors show that TRF2 binds non-telomeric G-quadruplexes in promoters of a set of genes ("TAN" genes for TRF2-associated neuronal differentiation) and recruits REST/chromatin remodelers to repress those genes in neural stem cells, thereby maintaining the NSC state in a telomere-independent manner. They show that the loss of TRF2 derepresses TAN genes and promotes neuronal differentiation.

However, key experiments are missing to fully support the claims: a genome-wide TRF2 ChIP-seq in NSC to validate binding beyond a restricted set of TAN genes, more robust evidence confirming the absence of telomeric dysfunction, and mechanistic clarification of the effects of G4 ligands on TRF2 binding.

Major comments:

• It is interesting that TRF2 loss not only fails to increase γH2AX/53BP1 levels but may even slightly reduce them (e.g., Fig. S2c and the IF images). While the main hypothesis is that TRF2 loss does not trigger telomere dysfunction in NSCs, this observation raises the possibility that TRF2 itself contributes to DDR signaling (ATM-P, γH2AX, 53BP1) in these cells and that in its absence, cells are not able to form those foci. To exclude the possibility that telomere-specific DDR is being missed due to an overall dampened DDR response in the absence of TRF2, it would be informative to induce exogenous DSBs in TRF2-depleted cells and test DDR competence (e.g., IF for γH2AX/53BP1). In other words, are those NSC lacking TRF2 even able to form H2AX/53BP1 foci when damaged? In addition, it would be interesting to perform telomere fusion analysis in TRF2 silenced cells (and TRF1 silenced cells as a positive control).
• A TRF2 ChIP-seq should be performed in NSC as this list of genes (named TAN genes in the text) was determined using a ChIP performed in another cell line (HT1080). For the ChIP-qPCR in the various conditions, primers for negative control regions should be included to show the specific binding of TRF2 to the promoter of the genes associated with neuronal differentiation. For example, an intergenic region and/or promoters of genes that are not associated with neuronal differentiation (or don't contain a potential G4). The same comment goes true for the gene expression analysis: a few genes that are not bound by TRF2 should be included as negative controls to exclude a potential global effect of TRF2 loss on gene expression (ideally a RNA-seq would be performed instead).
• A co-IP should be performed between the TRF2 PTM mutant K176R or WT TRF2 and REST and PRC2 components to directly show a defect of interaction between them when TRF2 is mutated (a co-IP with DNase/RNase treatment to exclude nucleic-acid bridging). The TRF2 PTM mutant T188N also seems to lead to an increased differentiation (Fig. S5a). Could the author repeat the measure of gene expression and co-IP with REST upon the overexpression of this mutant too?
• The authors show that the G4 ligands SMH14.6 and Bis-indole carboxamide upregulate TAN genes and promote neuronal differentiation, but the underlying mechanism remains unclear. Bis-indole carboxamide is generally considered a G4 stabilizer, while SMH14.6 is less characterized and should be better introduced. The authors should clarify how G4 stabilization would interfere with TRF2 binding, it seems that it would likely be by blocking access. A more detailed discussion, and ideally TRF2 ChIP after ligand treatment and/or G4 helicase treatment, would strengthen the model.

Minor comments:

• Supp Figures related to the scRNA-seq are difficult to read (blurry).
• Fig S1h: The red box mentioned in the legend is not visible
• In the text, the Figures 1 f-g are misannotated as Fig 1m and l
• The symbol  of H2AX is missing in the text
• Fig.3d, please indicate in the legend that it is done in SH-SY5Y.
• Fig. S3b: Please consider replotting this panel with an increased y-axis scale. As currently presented, the TRF2 ChIP-seq peaks at several promoters appear truncated by the scaling.
• Fig S4b: the legends should be fixed, the figure shows TRF2 occupancy upon REST silencing and not the other way around.

Significance

Non-telomeric roles of TRF2 have been reported before: in repressing neuronal genes and promoting a stem-like state by stabilizing REST (PMID: 18818083), in promoter G4 binding and recruitment of chromatin repressors (previous studies from the same lab), and TRF2 was shown to be dispensable for telomere protection in pluripotent stem cells (ES). The novelty of the current study lies primarily in extending/combining these mechanisms to NSCs.

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Reply to the reviewers

We thank the reviewers for their thoughtful and constructive feedback, which helped us strengthen the study on both the computational and biological side. In response, we added substantial new analyses and results in a total of 26 new supplementary figures and a new supplementary note. Importantly, we demonstrated that our approach generalizes beyond tissue outcomes by predicting final-timepoint morphology clusters from early frames with good accuracy as new Figure 4C. Furthermore, we completely restructured and expanded the human expert panel: six experts now provided >30,000 annotations across evenly spaced time intervals, allowing us to benchmark human predictions against CNNs and classical models under comparable conditions. We verified that morphometric trajectories are robust: PCA-based reductions and nearest-neighbor checks confirmed that patterns seen in t-SNE/UMAP are genuine, not projection artifacts. To test whether z-stacks are required, we re-did all analyses with sum- and maximum-intensity projections across five slices; results were unchanged, showing that single-slice imaging is sufficient. From a bioinformatics perspective, we performed negative-label baselines, downsampling analyses to quantify dataset needs, and statistical tests confirming CNNs significantly outperform classical models. Biologically, we clarified that each well contains one organoid, further introduced the Latent Determination Horizon concept tied to expert visibility thresholds, and discussed limits in cross-experiment transfer alongside strategies for domain adaptation and adaptive interventions. Finally, we clarified methods, corrected terminology and a scaler leak, and made all code and raw data publicly available.

Together, these revisions in our opinion provide an even clearer, more reproducible, and stronger case for the utility of predictive modeling in retinal organoid development.

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

This study presents predictive modeling for developmental outcome in retinal organoids based on high-content imaging. Specifically, it compares the predictive performance of an ensemble of deep learning models with classical machine learning based on morphometric image features and predictions from human experts for four different task: prediction of RPE presence and lense presence (at the end of development) as well as the respective sizes. It finds that the DL model outperforms the other approaches and is predictive from early timepoints on, strongly indicating a time-frame for important decision steps in the developmental trajectory.

Response: We thank the reviewer for the constructive and thoughtful feedback. In response to the review as found below, we have made substantial revisions and additions to the manuscript. Specifically, we clarified key aspects of the experimental setup, changed terminology regarding training/validation/test sets, and restructured our human expert baseline analysis by collecting and integrating a substantially larger dataset of expert annotations according to suggestion. We introduced the Latent Determination Horizon concept with clearer rationale and grounding. Most importantly, we significantly expanded our interpretability analyses across three CNN architectures and eight attribution methods, providing comprehensive quantitative evaluations and supplementary figures that extend beyond the initial DenseNet121 examples (new Supplementary Figures S29-S37). We also ensured full reproducibility by making both code and raw data publicly available with documentation. While certain advanced interpretability methods (e.g., Discover) could not be integrated despite considerable effort, we believe the revised manuscript presents a robust, well-documented, and carefully qualified analysis of CNN predictions in retinal organoid development.

Major comments: I find the paper over-all well written and easy to understand. The findings are relevant (see significance statement for details) and well supported. However, I have some remarks on the description and details of the experimental set-up, the data availability and reproducibility / re-usability of the data.

1. Some details about the experimental set-up are unclear to me. In particular, it seems like there is a single organoid per well, as the manuscript does not mention any need for instance segmentation or tracking to distinguish organoids in the images and associate them over time. Is that correct? If yes, it should be explicitly stated so. Are there any specific steps in the organoid preparation necessary to avoid multiple organoids per well? Having multiple organoids per well would require the aforementioned image analysis steps (instance segmentation and tracking) and potentially add significant complexity to the analysis procedure, so this information is important to estimate the effort for setting up a similar approach in other organoid cultures (for example cancer organoids, where multiple organoids per well are common / may not be preventable in certain experimental settings).

Response: We thank the reviewer for this question. We agree that these preprocessing steps would add more complexity to our presented preprocessing steps and would definitely be required in some organoid systems. In our experimental setup, there is only one organoid per well which forms spontaneously after cell seeding from (almost) all seeded cells. There are no additional steps necessary in order to ensure this behaviour in our setup. We amended the Methods section to now explicitly state this accordingly (paragraph ‘Organoid timelapse imaging’).

The terminology used with respect to the test and validation set is contrary to the field, and reporting the results on the test set (should be called validation set), should be avoided since it is used to select models. In more detail: the terms "test set" and "validation set" (introduced in 213-221) are used with the opposite meaning to their typical use in the deep learning literature. Typically, the validation set refers to a separate split that is used to monitor convergence / avoid overfitting during training, and the test set refers to an external set that is used to evaluate the performance of trained models. The study uses these terms in an opposite manner, which becomes apparent from line 624: "best performing model ... judged by the loss of the test set.". Please exchange this terminology, it is confusing to a machine learning domain expert. Furthermore, the performance on the test set (should be called validation set) is typically not reported in graphs, as this data was used for model selection, and thus does not provide an unbiased estimate of model performance. I would remove the respective curves from Figures 3 and 4.

Response: We are thankful for the reviewers comments on this matter. Indeed, we were using an opposite terminology compared to what is commonly used within the field. We have adjusted the Results, Discussion and Methods sections as well as the figures accordingly. Further, we added a corresponding disclaimer for the code base in the github repository. However, we prefer to not remove the respective curves from the figures. We think that this information is crucial to interpret the variability in accuracy between organoids from the same experiments and organoids acquired from a different, independent experiment. The results suggest that the accuracy for organoids within the same experiments is still higher, indicating to users the potential accuracy drop resulting from independent experiments. As we think that this is crucial information for the interpretability of our results, we would like to still include it side-by-side with the test data in the figures.

The experimental set-up for the human expert baseline is quite different to the evaluation of the machine learning models. The former is based on the annotation of 4,000 images by seven expert, the latter based on a cross-validation experiments on a larger dataset. First of all, the details on the human expert labeling procedure is very sparse, I could only find a very short description in the paragraph 136-144, but did not find any further details in the methods section. Please add a methods section paragraph that explains in more detail how the images were chosen, how they were assigned to annotators, and if there was any redundancy in annotation, and if yes how this was resolved / evaluated. Second, the fact that the set-up for human experts and ML models is quite different means that these values are not quite comparable in a statistical sense. Ideally, human estimators would follow the same set-up as in ML (as in, evaluate the same test sets). However, this would likely prohibitive in the required effort, so I think it's enough to state this fact clearly, for example by adding a comment on this to the captions of Figure 3 and 4.

Response: We thank the reviewer for this constructive suggestion. We agree that the curves for human evaluations in the original draft were calculated differently compared to the curves for the classification algorithms, mostly stemming from feasibility of data set annotation at the time. In order to still address this suggestion, we went on to repeat and substantially expand the number of images annotated and thus revised the full human expert annotation. Each one of 6 human experts was asked to predict/interpret 6 images of each organoid within the full dataset. In order to select the images, we divided the time course (0-72h) into 6 evenly spaced intervals of 12 hours. For each interval, one image per organoid and human expert was randomly selected and assigned. This resulted in a total of 31,626 classified images (up from 4000 in the original version of the manuscript), from which the assigned images were overlapping between experts for each source interval but not for the individual images. We then changed the calculation of the curves to be the same as for the classification analysis: F1 data were calculated for each experiment over 6 timeframes and all experts, and plotted within the respective figure. We have amended the Methods section accordingly and replaced the respective curves within Figures 3 and 4 and Supplementary Figures S1, S8 and S19.

It is unclear to me where the theoretical time window for the Latent Determination Horizon in Figure 5 (also mentioned in line 350) comes from? Please explain this in more detail and provide a citation for it.

Response: We thank the reviewer for this important point. The Latent Determination Horizon (LDH) is a conceptual framework we introduced in this study to describe the theoretical period during which the eventual presence of a tissue outcome of interest (TOI) is being determined but not yet detectable. It is derived from two main observations in our dataset: (i) the inherent intra- and inter-experimental heterogeneity of organoid outcomes despite standardized protocols, and (ii) the progressive increase in predictive performance of our deep learning models over time, which suggests that informative morphological features only emerge gradually. We have now clarified this rationale in the manuscript (Discussion section) further and explicitly stated that the LDH is a concept we introduce here, rather than a previously described or cited term.

The timewindow is defined by the TOI visibility, which is defined empirically as indicated by the results of our human expert panel (compare also Supplementary Figure S1).

The intepretability analysis (Figure 4, 634-639) based on relevance backpropagation was performed based on DenseNet121 only. Why did you choose this model and not the ResNet / MobileNet? I think it is quite crucial to see if there are any differences between these model, as this would show how much weight can be put on the evidence from this analysis and I would suggest to add an additional experiment and supplementary figure on this.

Response: We thank the reviewer for this important comment regarding the interpretability analysis and the choice of model. In the original submission, we restricted the attribution analyses shown in originial Figure 4C to DenseNet121, which served as our main reference model throughout the study. This choice was made primarily for clarity and to avoid redundancy in the main figures, as all three convolutional neural network (CNN) architectures (DenseNet121, ResNet50, MobileNetV3_Large) achieved comparable classification performance on our tasks.

In response to the reviewer’s concern, we have now extended the interpretability analyses to include all three CNN architectures and a total of eight attribution methods (new Supplementary Note 1). Specifically, we generated saliency maps for DenseNet121, ResNet50, and MobileNetV3_Large across multiple time points and evaluated them using a systematic set of metrics: pairwise method agreement within each model (new Supplementary Figure S29), cross-model consistency per method (new Supplementary Figure S34), entropy and diffusion of saliencies over time (new Supplementary Figure S35), regional voting overlap across methods (new Supplementary Figure S36), and spatial drift of saliency centers of mass (new Supplementary Figure S37).

These pooled analyses consistently showed that attribution methods differ markedly in the regions they prioritize, but that their relative behaviors were mostly stable across the three CNN architectures. For example, Grad-CAM and Guided Grad-CAM exhibited strong internal agreement and progressively focused relevance into smaller regions, while gradient-based methods such as DeepLiftSHAP and Integrated Gradients maintained broader and more diffuse relevance patterns but were the most consistent across models. Perturbation-based methods like Feature Ablation and Kernel SHAP often showed decreasing entropy and higher spatial drift, again similarly across architectures.

To further address the reviewer’s point, we visualized the organoid depicted in original Figure 4C across all three CNNs and all eight attribution methods (new Supplementary Figures S30-S33). These comparisons confirm and extend analysis of the qualitative patterns described in original Figure 4C and show that they are not specific to DenseNet121, but are representative of the general behavior across architectures.

In sum, we observed notable differences in how relevance was assigned and how consistently these assignments aligned. Highlighted organoid patterns were not consistent enough across attribution methods for us to be comfortable to base unequivocal biological interpretation on them. Nevertheless we believe that the analyses in response to the reviewer’s suggestions (new Supplementary Note 1 and new Supplementary Figures S29-S37) add valuable context to what can be expected from machine learning models in an organoid research setting.

As we did not base further unequivocal biological claims on the relevance backpropagation, we decided to move the analyses to the Supporting Information and now show a new model predicting organoid morphology by morphometrics clustering at the final imaging timepoint in new Figure 4C in line with suggestions by Reviewer #3.

The code referenced in the code availability statement is not yet present. Please make it available and ensure a good documentation for reproducibility. Similarly, it is unclear to me what is meant by "The data that supports the findings will be made available on HeiDoc". Does this only refer to the intermediate results used for statistical analysis? I would also recommend to make the image data of this study available. This could for example be done through a dedicated data deposition service such as BioImageArchive or BioStudies, or with less effort via zenodo. This would ensure both reproducibility as well as potential re-use of the data. I think the latter point is quite interesting in this context; as the authors state themselves it is unclear if prediction of the TOIs isn't even possible at an earlier point that could be achieved through model advances, which could be studied by making this data available.

Response: We thank the reviewer for this comment. We have now made the repository and raw data public on the suggested platform (Zenodo) and apologize for this oversight. The links are contained within the github repository which is stated in the manuscript under “Data availability”.

Minor comments:

Line 315: Please add a citation for relevance backpropagation here.

Response: We have included citations for all relevance backpropagation methods used in the paper.

Line 591: There seems to be typo: "[...] classification of binary classification [...]"

Response: Corrected as suggested.

Line 608: "[...] where the images of individual organoids served as groups [...]" It is unclear to me what this means.

Response: We wanted to express that organoid images belonging to one organoid were assigned in full to a training/validation set. We have now stated this more clearly in the Methods section.

Reviewer #1 (Significance (Required)):

General assessment: This study demonstrates that (retinal) organoid development can be predicted from early timepoints with deep learning, where these cannot be discerned by human experts or simpler machine learning models. This fact is very interesting in itself due to its implication for organoid development, and could provide a valuable tool for molecular analysis of different organoid populations, as outlined by the authors. The contribution could be strengthened by providing a more thorough investigation of what features in the image are predictive at early timepoints, using a more sophisticated approach than relevance backprop, e.g. Discover (https://www.nature.com/articles/s41467-024-51136-9). This could provide further biological insight into the underlying developmental processes and enhance the understanding of retinal organoid development.

Response: We thank the reviewer for this assessment and suggestion. We agree that identifying image features predictive at early timepoints would add important biological context. We therefore attempted to apply Discover to our dataset. However, we were unable to get the system to run successfully. After considerable effort, we concluded that this approach could not be integrated into our current analysis. Instead, we report our substantially expanded results obtained with relevance backpropagation, which provided the most interpretable and reproducible insights for our study as described above (New Supplementary Note 1, new Supplementary Figures S29-S37).

Advance: similar studies that predict developmental outcome based on image data, for example cell proliferation or developmental outcome exist. However, to the best of my knowledge, this study is the first to apply such a methodology to organoids and convincingly shows is efficacy and argues is potential practical benefits. It thus constitutes a solid technical advance, that could be especially impactful if it could be translated to other organoid systems in the future.

Response: We thank the reviewer for this positive assessment of our work and for highlighting its novelty and potential impact. We are encouraged that the reviewer recognizes the value of applying predictive modeling to organoids and the opportunities this creates for translation to other organoid systems.

Audience: This research is of interest to a technical audience. It will be of immediate interest to researchers working on retinal organoids, who could adapt and use the proposed system to support experiments by better distinguishing organoids during development. To enable this application, code and data availability should be ensured (see above comments on reproducibility). It is also of interest to researchers in other organoid systems, who may be able to adapt the methodology to different developmental outcome predictions. Finally, it may also be of interest to image analysis / deep learning researchers as a dataset to improve architectures for predictive time series modeling.

My research background: I am an expert in computer vision and deep learning for biomedical imaging, especially in microscopy. I have some experience developing image analysis for (cancer) organoids. I don't have any experience on the wet lab side of this work.

Response: We thank the reviewer for this encouraging feedback and for recognizing the broad relevance of our work across retinal organoid research, other organoid systems, and the image analysis community. We are pleased that the potential utility of our dataset and methodology is appreciated by experts in computer vision and biomedical imaging. We have now made the repository and raw data public and apologize for this oversight. The links are provided in the manuscript under “Data availability”.

Constantin Pape

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

Summary: Afting et al. present a computational pipeline for analyzing timelapse brightfield images of retinal organoids derived from Medaka fish. Their pipeline processes images along two paths: 1) morphometrics (based on computer vision features from skimage) and 2) deep learning. They discovered, through extensive manual annotation of ground truth, that their deep learning method could predict retinal pigmented epithelium and lens tissue emergence in time points earlier than either morphometrics or expert predictions. Our review is formatted based on the review commons recommendation.

Response: We thank the reviewer for the detailed and constructive feedback, which has greatly improved the clarity and rigor of our manuscript. In response, we have corrected a potential data leakage issue, re-ran the affected analyses, and confirmed that results remain unchanged. We clarified the use of data augmentation in CNN training, tempered some claims throughout the text, and provided stronger justification for our discretization approach together with new supplementary analyses (New Supplementary Figures S26, S27). We substantially expanded our interpretability analyses across three CNN architectures and eight attribution methods, quantified their consistency and differences (new Supplementary Figures S29, S34-S37, new Supplementary Note 1), and added comprehensive visualizations (New S30-S33). We also addressed technical artifact controls, provided downsampling analyses to support our statement on sample size sufficiency (new Supplementary Figure S28), and included negative-control baselines with shuffled labels in Figures 3 and 4. Furthermore, we improved the clarity of terminology, figures, and methodological descriptions, and we have now made both code and raw data publicly available with documentation. Together, we believe these changes further strengthen the robustness, reproducibility, and interpretability of our study while carefully qualifying the claims.

Major comments:

Are the key conclusions convincing?

Yes, the key conclusion that deep learning outperforms morphometric approaches is convincing. However, several methodological details require clarification. For instance, were the data splitting procedures conducted in the same manner for both approaches? Additionally, the authors note in the methods: "The validation data were scaled to the same range as the training data using the fitted scalers obtained from the training data." This represents a classic case of data leakage, which could artificially inflate performance metrics in traditional machine learning models. It is unclear whether the deep learning model was subject to the same issue. Furthermore, the convolutional neural network was trained with random augmentations, effectively increasing the diversity of the training data. Would the performance advantage still hold if the sample size had not been artificially expanded through augmentation?

Response: We thank the reviewer for raising these important methodological points. As Reviewer #1 correctly noted, our use of the terms validation and test may have contributed to confusion. To clarify: in the original analysis the scalers were fitted on the training and validation data and then applied to the test data. This indeed constitutes a form of data leakage. We have corrected the respective code, re-ran all analyses that were potentially affected, and did not observe any meaningful change in the reported results. The Methods section has been amended to clarify this important detail.

For the neural networks, each image was normalized independently (per image), without using dataset-level statistics, thereby avoiding any risk of data leakage.

Regarding data augmentation, the convolutional neural network was indeed trained with augmentations. Early experiments without augmentation led to severe overfitting, confirming that the performance advantage would not hold without artificially increasing the effective sample size. We have added a clarifying statement in the Methods section to make this explicit.

Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Their claims are currently preliminary, pending increased clarity and additional computational experiments described below.

Response: We believe our additionally performed computational experiments qualify all the claims we make in the revised version of the manuscript.

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

• The authors discretize continuous variables into four bins for classification. However, a regression framework may be more appropriate for preserving the full resolution of the data. At a minimum, the authors should provide a stronger justification for this binning strategy and include an analysis of bin performance. For example, do samples near bin boundaries perform comparably to those near the bin centers? This would help determine whether the discretization introduces artifacts or obscures signals.

Response: We thank the reviewer for this thoughtful suggestion. We agree that regression frameworks can, in principle, preserve the full resolution of continuous outcome variables. However, in our setting we deliberately chose a discretization approach. First, the discretized outcome categories correspond to ranges of tissue sizes that are biologically meaningful and allow direct comparison to expert annotations. In practice, human experts also tend to judge tissue presence and size in categorical rather than strictly continuous terms, which was mirrored by our human expert annotation strategy. As we aimed to compare deep learning with classical machine learning models and with expert annotations across the same prediction tasks, a categorical outcome formulation provided the most consistent and fair framework. Secondly, the underlying outcome variables did not follow a normal distribution, but instead exhibited a skewed and heterogeneous spread. Regression models trained on such distributions often show biases toward the most frequent value ranges, which may obscure less common but biologically important outcomes. Discretization mitigated this issue by balancing the prediction task across defined size categories.

In line with the reviewer’s request, we have now analyzed the performance in relation to the distance of each sample from the bin center. These results are provided as new Supplementary Figures S26 and S27. Interestingly, for the classical machine learning classifiers, F1 scores tended to be somewhat higher for samples close to bin edges. For the convolutional neural networks, however, F1 scores were more evenly distributed across distances from bin centers. While the reason for this difference remains unclear, the analysis demonstrates that the discretization did not obscure predictive signals in either framework. We have amended the results section accordingly.

• The relevance backpropagation interpretation analysis is not convincing. The authors argue that the model's use of pixels across the entire image (rather than just the RPE region) indicates that the deep learning approach captures holistic information. However, only three example images are shown out of hundreds, with no explanation for their selection, limiting the generalizability of the interpretation. Additionally, it is unclear how this interpretability approach would work at all in earlier time points, particularly before the model begins making confident predictions around the 8-hour mark. It is also not specified whether the input used for GradSHAP matches the input used during CNN training. The authors should consider expanding this analysis by quantifying pixel importance inside versus outside annotated regions over time. Lastly, Figure 4C is missing a scale bar, which would aid in interpretability.

Response: We thank the reviewer for raising these important concerns. In the initial version we showed examples of relevance backpropagation that suggested CNNs rely on visible RPE or lens tissue for their predictions (original Figure 4C). Following the reviewer’s comment, we expanded the analysis extensively across all models and attribution methods (compare new Supplementary Note 1), and quantified agreement, consistency, entropy, regional overlap, and drift (new Supplementary Figures S29 and S34-S37), as well as providing comprehensive visualizations across models and methods (new Supplementary Figures S30-S33).

This extended analysis showed that attribution methods behave very differently from each other, but consistently so across the three CNN architectures. Each method displayed characteristic patterns, for example in entropy or center-of-mass drift, but the overlap between methods was generally low. While integrated gradients and DeepLiftSHAP tended to concentrate on tissue regions, other methods produced broader or shifting relevance patterns, and overall we could not establish robust or interpretable signals from a biological point of view that would support stronger conclusions.

We have therefore revised the text to focus on descriptive results only, without making claims about early structural information or tissue-specific cues being used by the networks. We also added missing scale bars and clarified methodological details. Together, the revised section now reflects the extensive work performed while remaining cautious about what can and cannot be inferred from saliency methods in this setting.

• The authors claim that they removed technical artifacts to the best of their ability, but it is unclear if the authors performed any adjustment beyond manual quality checks for contamination. Did the authors observe any illumination artifacts (either within a single image or over time)? Any other artifacts or procedures to adjust?

Response: We thank the reviewer for this comment. We have not performed any adjustment beyond manual quality control post organoid seeding. The aforementioned removal of technical artifacts included, among others, seeding at the same time of day, seeding and cell processing by the same investigator according to a standardized protocol, usage of reproducible chemicals (same LOT, frozen only once, etc.) and temperature control during image acquisition. We adhered strictly to internal, previously published workflows that were aimed to reduce any variability due to technical variations during cell harvesting, organoid preparation and imaging. We have clarified this important point in the Methods section.

• In line 434-436 the authors state "In this work, we used 1,000 organoids in total, to achieve the reported prediction accuracies. Yet, we suspect that as little as ~500 organoids are sufficient to reliably recapitulate our findings." It is unclear what evidence the authors use to support this claim? The authors could perform a downsampling analysis to determine tradeoff between performance and sample size.

Response: We thank the reviewer for this important comment. To clarify, our statement regarding the sufficiency of ~500 organoids was based on a downsampling-style analysis we had already performed. In this analysis, we systematically reduced the number of experiments used for training and assessed predictive performance for both CNN- and classifier-based approaches (former Supplementary Figure S11, new Supplementary Figure S28). For CNNs, performance curves plateaued at approximately six experiments (corresponding to ~500 organoids), suggesting that increasing the sample size further only marginally improved prediction accuracy. In contrast, we did not observe a clear plateau for the machine learning classifiers, indicating that these models can achieve comparable performance with fewer training experiments. We have revised the manuscript text to clarify that this conclusion is derived from these analyses, and continue to include Supplementary Figure S11 as new Supplementary Figure S28 for transparency (compare Supplementary Note 1).

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. Yes, we believe all experiments are realistic in terms of time and resources. We estimate all experiments could be completed in 3-6 months.

Response: We confirm that the suggested experiments are realistic in terms of time and resources and have been able to complete them within 6 months.

Are the data and the methods presented in such a way that they can be reproduced? No, the code is not currently available. We were not able to review the source code.

Response: We have now made the repository public. We apologize for this initial oversight. The links are provided in the revised version of the manuscript under “Data availability”.

Are the experiments adequately replicated and statistical analysis adequate?

• The experiments are adequately replicated.

• The statistical analysis (deep learning) is lacking a negative control baseline, which would be helpful to observe if performance is inflated.

Response: We thank the reviewer for this comment. We have calculated the respective curves with neural networks and machine learning classifiers that were trained on data with shuffled labels and have included these results as a separate curve in the respective Figures 3 and 4. We have also amended the Methods section accordingly.

Minor comments:

Specific experimental issues that are easily addressable.

Are prior studies referenced appropriately?

Yes.

Are the text and figures clear and accurate?

The authors must improve clarity on terminology. For example, they should define a comprehensive dataset, significant, and provide clarity on their morphometrics feature space. They should elaborate on what they mean by "confounding factor of heterogeneity".

Response: We thank the reviewer for highlighting the need to clarify terminology. We have revised the manuscript accordingly. Specifically, we now explicitly define comprehensive dataset as longitudinal brightfield imaging of ~1,000 organoids from 11 independent experiments, imaged every 30 minutes over several days, covering a wide range of developmental outcomes at high temporal resolution. Furthermore, we replaced the term significantly with wording that avoids implying statistical significance, where appropriate. We have clarified the morphometrics feature space in the Methods section in a more detailed fashion, describing the custom parameters that we used to enhance the regionprops_table function of skimage.

Do you have suggestions that would help the authors improve the presentation of their data and conclusions? - Figure 2C describes a distance between what? The y axis is likely too simple. Same confusion over Figure 2D. Was distance computed based on tsne coordinates?

Response: We thank the reviewer for pointing out this potential source of confusion. The distances shown in original Figures 2C and 2D were not calculated in tSNE space. Instead, morphometrics features were first Z-scaled, and then dimensionality reduction by PCA was applied, with the first 20 principal components retaining ~93% of the variance. Euclidean distances were subsequently computed in this 20-dimensional PC space. For inter-organoid distances (Figure 2C), we calculated mean pairwise Euclidean distances between all organoids at each imaging time point, capturing the global divergence of organoid morphologies over time in an experiment-specific manner. For intra-organoid distances (Figure 2D), we calculated Euclidean distances between consecutive time points (n vs. n+1) for each individual organoid, thereby quantifying the extent of morphological change within organoids over time. We have revised the Figure legend and Methods section to make these definitions clearer.

• The authors perform a Herculean analysis comparing dozens of different machine learning classifiers. They select two, but they should provide justification for this decision.

Response: We thank the reviewer for this comment. In our initial machine learning analyses, we systematically benchmarked a broad set of classifiers on the morphometrics feature space, using cross-validation and hyperparameter tuning where appropriate. The classifiers that we ultimately focused on were those that consistently achieved the best performance in these comparisons. This process is described in the Methods and summarized in the Supplementary Figures S4 and S15 (for sum- and maximum-intensity z-projections new Supplementary Figures S5/6 and S16/17), which show the results of the benchmarking. We have clarified the text to state that the selected classifiers were chosen on the basis of their superior performance in these evaluations.

• It would be good to get a sense for how these retinal organoids grow - are they moving all over the place? They are in Matrigel so maybe not, but are they rotating?

Can the author's approach predict an entire non-emergence experiment? The authors tried to standardize protocol, but ultimately if It's deriving this much heterogeneity, then how well it will actually generalize to a different lab is a limitation.

Response: We thank the reviewer for these thoughtful questions. The retinal organoids in our study were embedded in low concentrations of Matrigel and remained relatively stable in position throughout imaging. We did not observe substantial displacement or lateral movement of organoids, and no systematic rotation could be detected in our dataset. Small morphological rearrangements within organoids were observed, but the gross positioning of organoids within the wells remained consistent across time-lapse recordings.

Regarding generalization across laboratories, we agree with the reviewer that this is an important limitation. While we minimized technical variability by adhering to a highly standardized, published protocol (see Methods), considerable heterogeneity remained at both intra- and inter-experimental levels. This variability likely reflects inherent properties of the system, similar the reportings in the literature across organoid systems, rather than technical artifacts, and poses a potential challenge for applying our models to independently generated datasets. We therefore highlight the need for future work to test the robustness of our models across laboratories, which will be essential to determine the true generalizability of our approach. We have amended the Discussion accordingly.

• The authors should dampen claims throughout. For example, in the abstract they state, "by combining expert annotations with advanced image analysis". The image analysis pipelines use common approaches.

Response: We thank the reviewer for this comment. We agree that the individual image analysis steps we used, such as morphometric feature extraction, are based on well-established algorithms. By referring to “advanced image analysis,” we intended to highlight not the novelty of each single algorithm, but rather the way in which we systematically combined a large number of quantitative parameters and leveraged them through machine learning models to generate predictive insights into organoid development.

• The authors state: "the presence of RPE and lenses were disagreed upon by the two independently annotating experts in a considerable fraction of organoids (3.9 % for RPE, 2.9% for lenses).", but it is unclear why there were two independently annotating experts. The supplements say images were split between nine experts for annotation.

Response: We thank the reviewer for pointing out this ambiguity. To clarify, the ground truth definition at the final time point was established by two experts who annotated all organoids. These two annotators were part of the larger group of six experts who contributed to the earlier human expert annotation tasks. Thus, while six experts provided annotations for subsets of images during the expert prediction experiments, the final annotation for every single organoid at its last time frame was consistently performed by the same two experts to ensure a uniform ground truth. We have amended this in the revised manuscript to make this distinction clear.

• Details on the image analysis pipeline would be helpful to clarify. For example, why did they choose to measure these 165 morphology features? Which descriptors were used to quantify blur? Did the authors apply blur metrics per FOV or per segmented organoid?

Response: We thank the reviewer for this comment. To clarify, we extracted 165 morphometric features per segmented organoid, combining standard scikit-image region properties with custom implementations (e.g., blur quantified as the variance of the Laplace filter response within the organoid mask). All metrics, including blur, were calculated per segmented organoid rather than per full field of view. This broad feature space was deliberately chosen to capture size, shape, and intensity distributions in a comprehensive and unbiased manner. We now provide a more detailed description of the preprocessing steps, the full feature list, and the exact code implementations are provided in the Methods section (“Large-scale time-lapse Image analysis”) of the revised version of the manuscript as well as in the source code github repository.

• The description of the number of images is confusing and distracts from the number of organoids. The number of organoids and number of timepoints used would provide a better description of the data with more value. For example, does this image count include all five z slices?

Response: We thank the reviewer for this comment. The reported image count includes slice 3 only, which we based our models on. The five z-slices that we used to create the MAX- and SUM-intensity z-projections would increase this number 5-fold. While we agree that the number of organoids and time points are highly informative metrics and have provided these details in the manuscript, we also believe that reporting the image count is valuable, as it directly reflects the size of the dataset processed by our analysis pipelines. For this reason, we prefer to keep the current description.

• The authors should consider applying a maximum projection across the five z slices (rather than the middle z) as this is a common procedure in image analysis. Why not analyze three-dimensional morphometrics or deep learning features? Might this improve performance further?

Response: We thank the reviewer for this valuable suggestion. To address this point, we repeated all analyses using both sum- and maximum-intensity z-projections and have included the results as new Supplementary Figures S8-S10, S13/S14 for TOI emergence and new Supplementary Figures S19-S21, S24/S25 for TOI sizes (classifier benchmarking and hyperparameter tuning in new Supplementary Figures S5/S6 and S16/S17). These additional analyses did not reveal a noticeable improvement in performance, suggesting that projections incorporating all slices are not strictly necessary in our setting. An analysis that included all five z-slices separately for classification would indeed be of interest, but was not feasible within the scope of this study, as it would substantially increase the computational demands beyond the available resources and timeframe.

• There is a lot of manual annotation performed in this work, the authors could speculate how this could be streamlined for future studies. How does the approach presented enable streamlining?

Response: We thank the reviewer for raising this important point. The current study relied on expert visual review, which is time-intensive, but our findings suggest several ways to streamline future work. For instance, model-assisted prelabeling could be used to automatically accept high-confidence cases while routing only uncertain cases to experts. Active sampling strategies, focusing expert review on boundary cases or rare classes, as well as programmatic checks from morphometrics (e.g., blur or contrast to flag low-quality frames), could further reduce effort. Consensus annotation could be reserved only for cases where the model and expert disagree or confidence is low. Finally, new experiments could be bootstrapped with a small seed set of annotated organoids for fine-tuning before switching to such a model-assisted workflow. These possibilities are enabled by our approach, where organoids are imaged individually, morphometrics provide automated quality indicators, and the CNN achieves reliable performance at early developmental stages, making model-in-the-loop annotation a feasible and efficient strategy for future studies. We have added a clarifying paragraph to the Discussion accordingly.

Reviewer #2 (Significance (Required)):

Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The paper's advance is technical (providing new methods for organoid quality control) and conceptual (providing proof of concept that earlier time points contain information to predict specific future outcomes in retinal organoids)

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

• The authors do a good job of placing their work in context in the introduction.

• The work presents a simple image analysis pipeline (using only the middle z slice) to process timelapse organoid images. So not a 4D pipeline (time and space), just 3D (time). It is likely that more and more of these approaches will be developed over time, and this article is one of the early attempts.

• The work uses standard convolutional neural networks.

Response: We thank the reviewer for this assessment. We agree that our work represents one of the early attempts in this direction, applying a straightforward pipeline with standard convolutional neural networks, and we appreciate the reviewer’s acknowledgment of how the study has been placed in context within the Introduction.

State what audience might be interested in and influenced by the reported findings. - Data scientists performing image-based profiling for time lapse imaging of organoids.

• Retinal organoid biologists

• Other organoid biologists who may have long growth times with indeterminate outcomes.

Response: We thank the reviewer for outlining the relevant audiences. We agree that the reported findings will be of interest to data scientists working on image-based profiling, retinal organoid biologists, and more broadly to organoid researchers facing long culture times with uncertain developmental outcomes.

Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. - Image-based profiling/morphometrics

• Organoid image analysis

• Computational biology

• Cell biology

• Data science/machine learning

• Software

This is a signed review:

Gregory P. Way, PhD

Erik Serrano

Jenna Tomkinson

Michael J. Lippincott

Cameron Mattson

Department of Biomedical Informatics, University of Colorado

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

Summary:

This manuscript by Afting et. al. addresses the challenge of heterogeneity in retinal organoid development by using deep learning to predict eventual tissue outcomes from early-stage images. The central hypothesis is that deep learning can forecast which tissues an organoid will form (specifically retinal pigmented epithelium, RPE, and lens) well before those tissues become visibly apparent. To test this, the authors assembled a large-scale time-lapse imaging dataset of ~1,000 retinal organoids (~100,000 images) with expert annotations of tissue outcomes. They characterized the variability in organoid morphology and tissue formation over time, focusing on two tissues: RPE (which requires induction) and lens (which appears spontaneously). The core finding is that a deep learning model can accurately predict the emergence and size of RPE and lens in individual organoids at very early developmental stages. Notably, a convolutional neural network (CNN) ensemble achieved high predictive performance (F1-scores ~0.85-0.9) hours before the tissues were visible, significantly outperforming human experts and classical image-analysis-based classifiers. This approach effectively bypasses the issue of stochastic developmental heterogeneity and defines an early "determination window" for fate decisions. Overall, the study demonstrates a proof-of-concept that artificial intelligence can forecast organoid differentiation outcomes non-invasively, which could revolutionize how organoid experiments are analyzed and interpreted.

Recommendation:

While this manuscript addresses an important and timely scientific question using innovative deep learning methodologies, it currently cannot be recommended for acceptance in its present form. The authors must thoroughly address several critical limitations highlighted in this report. In particular, significant issues remain regarding the generalizability of the predictive models across different experimental conditions, the interpretability of deep learning predictions, and the use of Euclidean distance metrics in high-dimensional morphometric spaces-potentially leading to distorted interpretations of organoid heterogeneity. These revisions are essential for validating the general applicability of their approach and enhancing biological interpretability. After thoroughly addressing these concerns, the manuscript may become suitable for future consideration.

Response: We thank the reviewer for the thoughtful and constructive comments. In response, we expanded our analyses in several key ways. We clarified limitations regarding external datasets. Interpretability analyses were greatly extended across three CNN architectures and eight attribution methods (new Supplementary Figures S29-S37, new Supplementary Note 1), showing consistent but method-specific behaviors; as no reproducible biologically interpretable signals emerged, we now present these results descriptively and clearly state their limitations. We further demonstrated the flexibility of our framework by predicting morphometric clusters in addition to tissue outcomes (new Figure 4C), confirmed robustness of the morphometrics space using PCA and nearest-neighbor analyses (new Supplementary Figure S3), and added statistical tests confirming CNNs significantly outperform classical classifiers (Supplementary File 1). Finally, we made all code and raw data publicly available, clarified species context, and added forward-looking discussion on adaptive interventions. We believe these revisions now further improve the rigor and clarity of our work.

Major Issues (with Suggestions):

1. Generalization to Other Batches or Protocols: The drop in performance on independent validation experiments suggests the model may partially overfit to specific experimental conditions. A major concern is how well this approach would work on organoids from a different batch or produced by a slightly different differentiation protocol. Suggestion: The authors should clarify the extent of variability between their "independent experiment" and training data (e.g., were these done months apart, with different cell lines or minor protocol tweaks?). To strengthen confidence in the model's robustness, I recommend testing the trained model on one or more truly external datasets, if available (for instance, organoids generated in a separate lab or under a modified protocol). Even a modest analysis showing the model can be adapted (via transfer learning or re-training) to another dataset would be valuable. If new data cannot be added, the authors should explicitly discuss this limitation and perhaps propose strategies (like domain adaptation techniques or more robust training with diverse conditions) to handle batch effects in future applications.

Response: We thank the reviewer for this important comment. We fully agree with the reviewer that this would be an amazing addition to the manuscript. Unfortunately we are not able to obtain the requested external data set. Although retinal organoid systems exist and are widely used across different species lines, to the best of our knowledge our laboratory is the only one currently raising retinal organoids from primary embryonic pluripotent stem cells of Oryzias latipes and there is currently only one known (and published) differentiation protocol which allows the successful generation of these organoids. We note that our datasets were collected over the course of nine months, which already introduces variability across time and thus partially addresses concerns regarding batch effects. While we did not have access to truly external datasets (e.g., from other laboratories), we have clarified this limitation as suggested in the revised version of the manuscript and outlined strategies such as domain adaptation and training on more diverse conditions as promising future directions to improve robustness.

Biological Interpretation of Early Predictive Features: The study currently concludes that the CNN picks up on complex, non-intuitive features that neither human experts nor conventional analysis could identify. However, from a biological perspective, it would be highly insightful to know what these features are (e.g., subtle texture, cell distribution patterns, etc.). Suggestion: I encourage the authors to delve deeper into interpretability. They might try complementary explainability techniques (for example, occlusion tests where parts of the image are masked to see if predictions change, or activation visualization to see what patterns neurons detect) beyond GradientSHAP. Additionally, analyzing false predictions might provide clues: if the model is confident but wrong for certain organoids, what visual traits did those have? If possible, correlating the model's prediction confidence with measured morphometrics or known markers (if any early marker data exist) could hint at what the network sees. Even if definitive features remain unidentified, providing the reader with any hypothesis (for instance, "the network may be sensing a subtle rim of pigmentation or differences in tissue opacity") would add value. This would connect the AI predictions back to biology more strongly.

Response: We thank the reviewer for this thoughtful suggestion. We agree that linking CNN predictions to specific biological features would be highly valuable. In response, we expanded our interpretability analyses beyond GradientSHAP to a broad set of attribution methods and quantified their behavior across models and timepoints (new Supplementary Figures S29-S37, new Supplementary Note 1). While some methods (e.g., Integrated Gradients, DeepLiftSHAP) occasionally highlighted visible tissue regions, others produced diffuse or shifting relevance, and overall overlap was low. Therefore, our results did not yield reproducible, interpretable biological signals.

Given these results, we have refrained from speculating about specific early image features and now present the interpretability analyses descriptively. We agree that future studies integrating imaging with molecular markers will be required to directly link early predictive cues to defined biological processes.

Expansion to Other Outcomes or Multi-Outcome Prediction: The focus on RPE and lens is well-justified, but these are two outcomes within retinal organoids. A major question is whether the approach could be extended to predict other cell types or structures (e.g., presence of certain retinal neurons, or malformations) or even multiple outcomes at once. Suggestion: The authors should discuss the generality of their approach. Could the same pipeline be trained to predict, say, photoreceptor layer formation or other features if annotated? Are there limitations (like needing binary outcomes vs. multi-class)? Even if outside the scope of this study, a brief discussion would reassure readers that the method is not intrinsically limited to these two tissues. If data were available, it would be interesting to see a multi-label classification (predict both RPE and lens presence simultaneously) or an extension to other organoid systems in future. Including such commentary would highlight the broad applicability of this platform.

Response: We thank the reviewer for this helpful and important suggestion. While our study focused on RPE and lens as the most readily accessible tissues of interest in retinal organoids, our new analyses demonstrate that the pipeline is not limited to these outcomes. In addition to tissue-specific predictions, we trained both a convolutional neural network (on image data) and a decision tree classifier (on morphometrics features) to predict more abstract morphological clusters defined at the final timepoint using the morphometrics features, showing that both approaches could successfully capture non-tissue features from early frames (new Figure 4C). This illustrates that the framework can be extended beyond binary tissue outcomes to multi-class problems, and predict relevant outcomes like the overall organoid morphology. Given appropriate annotations, the framework could in principle be trained to detect additional structures such as photoreceptor layers or malformations. Furthermore, the CNN architecture we employed and the morphometrics feature space are compatible with multi-label classification, meaning simultaneous prediction of several outcomes would also be feasible. We have clarified this point in the discussion to highlight the methodological flexibility and potential generality of our approach and are excited to share this very interesting, additional model with the readership.

Curse of high dimensionality: Using Euclidean distance in a 165-dimensional morphometric space likely suffers from the curse of dimensionality, which diminishes the meaning of distances as dimensionality increases. In such high-dimensional settings, the range of pairwise distances tends to collapse, undermining the ability to discern meaningful intra- vs. inter-organoid differences. Suggestion: To address this, I would encourage the authors to apply principal component analysis (PCA) in place of (or prior to) tSNE. PCA would reduce the data to a few dominant axes of variation that capture most of the morphometric variance, directly revealing which features drive differences between organoids. These principal components are linear combinations of the original 165 parameters, so one can examine their loadings to identify which morphometric traits carry the most information - yielding interpretable axes of biological variation (e.g., organoid size, shape complexity, etc.). In addition, I would like to mention an important cautionary remark regarding tSNE embeddings. tSNE does not preserve global geometry of the data. Distances and cluster separations in a tSNE map are therefore not faithful to the original high-dimensional distances and should be interpreted with caution. See Chari T, Pachter L (2023), The specious art of single-cell genomics, PLoS Comput Biol 19(8): e1011288, for an enlightening discussion in the context of single cell genomics. The authors have shown that extreme dimensionality reduction to 2D can introduce significant distortions in the data's structure, meaning the apparent proximity or separation of points in a tSNE plot may be an artifact of the algorithm rather than a true reflection of morphometric similarity. Implementing PCA would mitigate high-dimensional distance issues by focusing on the most informative dimensions, while also providing clear, quantitative axes that summarize organoid heterogeneity. This change would strengthen the analysis by making the results more robust (avoiding distance artifacts) and biologically interpretable, as each principal component can be traced back to specific morphometric features of interest.

Response: We thank the reviewer for this mention. Indeed, high dimensionality and dimensionality reductions can lead to false interpretations. We approached this issue as follows: First, we calculated the same TSNE projections and distances using the first 20 PCs and supplied these data as the new Figure 2 and new Supplementary Figure 2. While the scale of the data shifted slightly, there were no differences in the data distribution that would contradict our prior conclusions.

In order to confirm the findings and further emphasize the validity of our dimensionality reduction, we calculated the intersection of 30 nearest neighbors in raw data space (or pca space) compared and 30 nearest neighbors in reduced space (TSNE or UMAP, as we wanted to emphasize that this was not an effect specific for TSNE projections and would also be valid in a dimensionality reduction which is more known to preserve global structure rather than local structure). As shown in the new Supplementary Figure S3 (A-D), the high jaccard index confirmed that our projections accurately reflect the data’s structure obtained from raw distance measurements. Moreover, the jaccard index generally increased over time, which is best explained by a stronger morphological similarity of organoids at timepoint 0 and reflected by the dense point cloud in the TSNE projections at that timepoint. The described effects were independent of the usage of data derived from 20 PCs versus data derived from all 165 dimensions.

We next wanted to confirm the conclusion that data points obtained from organoids at later timepoints were more closely related to each other than data points from different organoids. We therefore identified the 30 nearest neighbor data points, showing that at later timepoints these 30 nearest neighbor data points were almost all attributable to the same organoid (new Supplementary Figure S3 E/F). This was only not the case for experiments that lacked in between timepoints (E007 and E002), therefore misaligning the organoids in the reduced space and convoluting the nearest neighbor analysis.

We have included the respective new Figures and new Supplementary Figures and linked them in the main manuscript.

Statistical Reporting and Significance: The manuscript focuses on F1-score as the metric to report accuracy over time, which is appropriate. However, it's not explicitly stated whether any statistical significance tests were performed on the differences between methods (e.g., CNN vs human, CNN vs classical ML). Suggestion: The authors could report statistical significance of the performance differences, perhaps using a permutation test or McNemar's test on predictions. For example, is the improvement of the CNN ensemble over the Random Forest/QDA classifier statistically significant across experiments? Given the n of organoids, this should be assessable. Demonstrating significance would add rigor to the analysis.

Response: We thank the reviewer for this helpful suggestion. Following the recommendation, we quantified per-experiment differences in predictive performance by calculating the area under the F1-score curves (AUC) for each classifier and experiment. We then compared methods using paired Wilcoxon signed-rank tests across experiments, with Holm-Bonferroni correction for multiple comparisons. This analysis confirmed that the CNN consistently and significantly outperformed the baseline models and classical machine learning classifiers in validation and test organoids, while CNNs were notably but not significantly better performing in test organoids for RPE area and lens sizes compared to the machine learning classifiers. In summary, the findings add the requested statistical rigor to our findings. The results of these tests are now provided in the Supplementary Material as Supplementary File 1.

Minor Issues (with Suggestions):

1. Data Availability: Given the resource-intensive nature of the work, the value to the community will be highest if the data is made publicly available. I understand that this is of course at the behest of the authors and they do mention that they will make the data available upon publication of the manuscript. For the time being, the authors can consider sharing at least a representative subset of the data or the trained model weights. This will allow others to build on their work and test the method in other contexts, amplifying the impact of the study.

Response: We have now made the repository and raw data public and apologize for this oversight. The link for the github repository is now provided in the manuscript under “Data availability”, while the links for the datasets are contained within the github repository.

Discussion - Future Directions: The Discussion does a good job of highlighting applications (like guiding molecular analysis). One minor addition could be speculation on using this approach to actively intervene: for example, could one imagine altering culture conditions mid-course for organoids predicted not to form RPE, to see if their fate can be changed? The authors touch on reducing variability by focusing on the window of determination; extending that thought to an experimental test (though not done here) would inspire readers. This is entirely optional, but a sentence or two envisioning how predictive models enable dynamic experimental designs (not just passive prediction) would be a forward-looking note to end on.

Response: We thank the reviewer for this constructive suggestion. We have expanded the discussion to briefly address how predictive modeling could go beyond passive observation. Specifically, we now discuss that predictive models may enable dynamic interventions, such as altering culture conditions mid-course for organoids predicted not to form RPE, to test whether their developmental trajectory can be redirected. While outside the scope of the present work, this forward-looking perspective emphasizes how predictive modeling could inspire adaptive experimental strategies in future studies.

I believe with the above clarifications and enhancements - especially regarding generalizability and interpretability - the paper will be suitable for broad readership. The work represents an exciting intersection of developmental biology and AI, and I commend the authors for this contribution.

Response: We thank the reviewer for the positive assessment and their encouraging remarks regarding the contribution of our work to these fields.

Novelty and Impact:

This work fills an important gap in organoid biology and imaging. Previous studies have used deep learning to link imaging with molecular profiles or spatial patterns in organoids, but there remained a "notable gap" in predicting whether and to what extent specific tissues will form in organoids. The authors' approach is novel in applying deep learning to prospectively predict organoid tissue outcomes (RPE and lens) on a per-organoid basis, something not previously demonstrated in retinal organoids. Conceptually, this is a significant advance: it shows that fate decisions in a complex 3D culture model can be predicted well in advance, suggesting the existence of subtle early morphogenetic cues that only a sophisticated model can discern. The findings will be of broad interest to researchers in organoid technology, developmental biology, and biomedical AI.

Response: We thank the reviewer for this thoughtful and encouraging assessment. We agree that our study addresses an important gap by prospectively predicting tissue outcomes at the single-organoid level, and we appreciate the recognition that this represents a conceptual advance with relevance not only for retinal organoids but also for broader applications in organoid biology, developmental biology, and biomedical AI.

Methodological Rigor and Technical Quality:

The study is methodologically solid and carefully executed. The authors gathered a uniquely large dataset under consistent conditions, which lends statistical power to their analyses. They employ rigorous controls: an expert panel provided human predictions as a baseline, and a classical machine learning pipeline using quantitative image-derived features was implemented for comparison. The deep learning approach is well-chosen and technically sound. They use an ensemble of CNN architectures (DenseNet121, ResNet50, and MobileNetV3) pre-trained on large image databases, fine-tuning them on organoid images. The use of image segmentation (DeepLabV3) to isolate the organoid from background is appropriate to ensure the models focus on the relevant morphology. Model training procedures (data augmentation, cross-entropy loss with class balancing, learning rate scheduling, and cross-validation) are thorough and follow best practices. The evaluation metrics (primarily F1-score) are suitable for the imbalanced outcomes and emphasize prediction accuracy in a biologically relevant way. Importantly, the authors separate training, test, and validation sets in a meaningful manner: images of each organoid are grouped to avoid information leakage, and an independent experiment serves as a validation to test generalization. The observation that performance is slightly lower on independent validation experiments underscores both the realism of their evaluation and the inherent heterogeneity between experimental batches. In addition, the study integrates interpretability (using GradientSHAP-based relevance backpropagation) to probe what image features the network uses. Although the relevance maps did not reveal obvious human-interpretable features, the attempt reflects a commendable thoroughness in analysis. Overall, the experimental design, data analysis, and reporting are of high quality, supporting the credibility of the conclusions.

Response: We thank the reviewer for their very positive and detailed assessment. We appreciate the recognition of our efforts to ensure methodological rigor and reproducibility, and we agree that interpretability remains an important but challenging area for future work.

Reviewer #3 (Significance (Required)):

Scientific Significance and Conceptual Advances:

Biologically, the ability to predict organoid outcomes early is quite significant. It means researchers can potentially identify when and which organoids will form a given tissue, allowing them to harvest samples at the right moment for molecular assays or to exclude organoids that will not form the desired structure. The manuscript's results indicate that RPE and lens fate decisions in retinal organoids are made much earlier than visible differentiation, with predictive signals detectable as early as ~11 hours for RPE and ~4-5 hours for lens. This suggests a surprising synchronization or early commitment in organoid development that was not previously appreciated. The authors' introduction of deep learning-derived determination windows refines the concept of a developmental "point of no return" for cell fate in organoids. Focusing on these windows could help in pinpointing the molecular triggers of these fate decisions. Another conceptual advance is demonstrating that non-invasive imaging data can serve a predictive role akin to (or better than) destructive molecular assays. The study highlights that classical morphology metrics and even expert eyes capture mainly recognition of emerging tissues, whereas the CNN detects subtler, non-intuitive features predictive of future development. This underlines the power of deep learning to uncover complex phenotypic patterns that elude human analysis, a concept that could be extended to other organoid systems and developmental biology contexts. In sum, the work not only provides a tool for prediction but also contributes conceptual insights into the timing of cell fate determination in organoids.

Response: We thank the reviewer for this thoughtful and positive assessment. We agree that the determination windows provide a valuable framework to study early fate decisions in organoids, and we have emphasized this point in the discussion to highlight the biological significance of our findings.

Strengths:

The combination of high-resolution time-lapse imaging with advanced deep learning is innovative. The authors effectively leverage AI to solve a biological uncertainty problem, moving beyond qualitative observations to quantitative predictions. The study uses a remarkably large dataset (1,000 organoids, >100k images), which is a strength as it captures variability and provides robust training data. This scale lends confidence that the model isn't overfit to a small sample. By comparing deep learning with classical machine learning and human predictions, the authors provide context for the model's performance. The CNN ensemble consistently outperforms both the classical algorithms and human experts, highlighting the value added by the new method. The deep learning model achieves high accuracy (F1 > 0.85) at impressively early time points. The fact that it can predict lens formation just ~4.5 hours into development with confidence is striking. Performance remained strong and exceeded human capability at all assessed times. Key experimental and analytical steps (segmentation, cross-validation between experiments, model calibration, use of appropriate metrics) are executed carefully. The manuscript is transparent about training procedures and even provides source code references, enhancing reproducibility. The manuscript is generally well-written with a logical flow from the problem (organoid heterogeneity) to the solution (predictive modeling) and clear figures referenced.

Response: We thank the reviewer for this very positive and encouraging assessment of our study, particularly regarding the scale of our dataset, the methodological rigor, and the reproducibility of our approach.

Weaknesses and Limitations:

Generalizability Across Batches/Conditions: One limitation is the variability in model performance on organoids from independent experiments. The CNN did slightly worse on a validation set from a separate experiment, indicating that differences in the experimental batch (e.g., slight protocol or environmental variations) can affect accuracy. This raises the question of how well the model would generalize to organoids generated under different protocols or by other labs. While the authors do employ an experiment-wise cross-validation, true external validation (on a totally independent dataset or a different organoid system) would further strengthen the claim of general applicability.

Response: We thank the reviewer for this important point. We agree that generalizability across batches and experimental conditions is a key consideration. We have carefully revised the discussion to explicitly address this limitation and to highlight the variability observed between independent experiments.

Interpretability of the Predictions: Despite using relevance backpropagation, the authors were unable to pinpoint clear human-interpretable image features that drive the predictions. In other words, the deep learning model remains somewhat of a "black box" in terms of what subtle cues it uses at early time points. This limits the biological insight that can be directly extracted regarding early morphological indicators of RPE or lens fate. It would be ideal if the study could highlight specific morphological differences (even if minor) correlated with fate outcomes, but currently those remain elusive.

Response: We thank the reviewer for raising this important point. Indeed, while our models achieved robust predictive performance, the underlying morphological cues remained difficult to interpret using relevance backpropagation. We believe this limitation reflects both the subtlety of the early predictive signals and the complexity of the features captured by deep learning models, which may not correspond to human-intuitive descriptors. We have clarified this limitation in the Discussion and Supplementary Note 1 and emphasize that further methodological advances in interpretability, or integration with complementary molecular readouts, will be essential to uncover the precise morphological correlates of fate determination.

Scope of Outcomes: The study focuses on two particular tissues (RPE and lens) as the outcomes of interest. These were well-chosen as examples (one induced, one spontaneous), but they do not encompass the full range of retinal organoid fates (e.g., neural retina layers). It's not a flaw per se, but it means the platform as presented is specialized. The method might need adaptation to predict more complex or multiple tissue outcomes simultaneously.

Response: We agree with the reviewer that our study focuses on two specific tissues, RPE and lens, which served as proof-of-concept outcomes representing both induced and spontaneous differentiation events. While this scope is necessarily limited, we believe it demonstrates the general feasibility of our approach. We have clarified in the Discussion that the same framework could, in principle, be extended to additional retinal fates such as neural retina layers, or even to multi-label prediction tasks, provided appropriate annotations are available. We now provide additional experiments showing that even abstract morphological classes are well predictable. This will be an important next step to broaden the applicability of our platform.

Requirement of Large Data and Annotations: Practically, the approach required a very large imaging dataset and extensive manual annotation; each organoid's RPE and lens outcome, plus manual masking for training the segmentation model. This is a substantial effort that may be challenging to reproduce widely. The authors suggest that perhaps ~500 organoids might suffice to achieve similar results, but the data requirement is still high. Smaller labs or studies with fewer organoids might not immediately reap the full benefits of this approach without access to such imaging throughput.

Response: We thank the reviewer for highlighting this important point. We agree that the generation of a large imaging dataset and the associated annotations represent a substantial investment of time and resources. At the same time, we consider this effort highly relevant, as it reflects the intrinsic heterogeneity of organoid systems rather than technical artifacts, and therefore ensures robust model training. We have clarified this limitation in the discussion. While our full dataset included ~1,000 organoids, our downsampling analysis suggests that as few as ~500 organoids may already be sufficient to reproduce the key findings, which we believe makes the approach feasible for many organoid systems (compare new Supplementary Note 1). Moreover, as we outline in the Discussion, future refinements such as combining image- and tabular-based features or incorporating fluorescence data could further enhance predictive power and reduce annotation effort.

Medaka Fish vs. Other Systems: The retinal organoids in this study appear to be from medaka fish, whereas much organoid research uses human iPSC-derived organoids. It's not fully clear in the manuscript as to how the findings translate to mammalian or human organoids. If there are species-specific differences, the applicability to human retinal organoids (which are important for disease modeling) might need discussion. This is a minor point if the biology is conserved, but worth noting as a potential limitation.

Response: We thank the reviewer for pointing out this important consideration. We have now explicitly clarified in the Discussion that our proof-of-concept study was performed in medaka organoids, which offer high reproducibility and rapid development. While species-specific differences may exist, the predictive framework is not inherently restricted to medaka and should, in principle, be transferable to mammalian or human iPSC/ESC-derived organoids, provided sufficiently annotated datasets are available. We have amended the Discussion accordingly.

Predicting Tissue Size is Harder: The model's accuracy in predicting how much tissue (relative area) an organoid will form, while good, is notably lower than for simply predicting presence/absence. Final F1 scores for size classes (~0.7) indicate moderate success. This implies that quantitatively predicting organoid phenotypic severity or extent is more challenging, perhaps due to more continuous variation in size. The authors do acknowledge the lower accuracy for size and treat it carefully.

Response: We thank the reviewer for this observation and agree with their interpretation. We have already acknowledged in the manuscript that predicting tissue size is more challenging than predicting tissue presence/absence, and we believe we have treated these results with appropriate caution in the revised version of the manuscript.

Latency vs. Determination: While the authors narrow down the time window of fate determination, it remains somewhat unclear whether the times at which the model reaches high confidence truly correspond to the biological "decision point" or are just the earliest detection of its consequences. The manuscript discusses this caveat, but it's an inherent limitation that the predictive time point might lag the actual internal commitment event. Further work might be needed to link these predictions to molecular events of commitment.

Response: We agree with the reviewer. As noted in the Discussion, the time points identified by our models likely reflect the earliest detectable morphological consequences of fate determination, rather than the exact molecular commitment events themselves. Establishing a direct link between predictive signals and underlying molecular mechanisms will require future experimental work.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This manuscript by Afting et. al. addresses the challenge of heterogeneity in retinal organoid development by using deep learning to predict eventual tissue outcomes from early-stage images. The central hypothesis is that deep learning can forecast which tissues an organoid will form (specifically retinal pigmented epithelium, RPE, and lens) well before those tissues become visibly apparent. To test this, the authors assembled a large-scale time-lapse imaging dataset of ~1,000 retinal organoids (~100,000 images) with expert annotations of tissue outcomes. They characterized the variability in organoid morphology and tissue formation over time, focusing on two tissues: RPE (which requires induction) and lens (which appears spontaneously). The core finding is that a deep learning model can accurately predict the emergence and size of RPE and lens in individual organoids at very early developmental stages. Notably, a convolutional neural network (CNN) ensemble achieved high predictive performance (F1-scores ~0.85-0.9) hours before the tissues were visible, significantly outperforming human experts and classical image-analysis-based classifiers. This approach effectively bypasses the issue of stochastic developmental heterogeneity and defines an early "determination window" for fate decisions. Overall, the study demonstrates a proof-of-concept that artificial intelligence can forecast organoid differentiation outcomes non-invasively, which could revolutionize how organoid experiments are analyzed and interpreted.

Recommendation:

While this manuscript addresses an important and timely scientific question using innovative deep learning methodologies, it currently cannot be recommended for acceptance in its present form. The authors must thoroughly address several critical limitations highlighted in this report. In particular, significant issues remain regarding the generalizability of the predictive models across different experimental conditions, the interpretability of deep learning predictions, and the use of Euclidean distance metrics in high-dimensional morphometric spaces-potentially leading to distorted interpretations of organoid heterogeneity. These revisions are essential for validating the general applicability of their approach and enhancing biological interpretability. After thoroughly addressing these concerns, the manuscript may become suitable for future consideration.

Major Issues (with Suggestions):

1. Generalization to Other Batches or Protocols: The drop in performance on independent validation experiments suggests the model may partially overfit to specific experimental conditions. A major concern is how well this approach would work on organoids from a different batch or produced by a slightly different differentiation protocol. Suggestion: The authors should clarify the extent of variability between their "independent experiment" and training data (e.g., were these done months apart, with different cell lines or minor protocol tweaks?). To strengthen confidence in the model's robustness, I recommend testing the trained model on one or more truly external datasets, if available (for instance, organoids generated in a separate lab or under a modified protocol). Even a modest analysis showing the model can be adapted (via transfer learning or re-training) to another dataset would be valuable. If new data cannot be added, the authors should explicitly discuss this limitation and perhaps propose strategies (like domain adaptation techniques or more robust training with diverse conditions) to handle batch effects in future applications.
2. Biological Interpretation of Early Predictive Features: The study currently concludes that the CNN picks up on complex, non-intuitive features that neither human experts nor conventional analysis could identify. However, from a biological perspective, it would be highly insightful to know what these features are (e.g., subtle texture, cell distribution patterns, etc.). Suggestion: I encourage the authors to delve deeper into interpretability. They might try complementary explainability techniques (for example, occlusion tests where parts of the image are masked to see if predictions change, or activation visualization to see what patterns neurons detect) beyond GradientSHAP. Additionally, analyzing false predictions might provide clues: if the model is confident but wrong for certain organoids, what visual traits did those have? If possible, correlating the model's prediction confidence with measured morphometrics or known markers (if any early marker data exist) could hint at what the network sees. Even if definitive features remain unidentified, providing the reader with any hypothesis (for instance, "the network may be sensing a subtle rim of pigmentation or differences in tissue opacity") would add value. This would connect the AI predictions back to biology more strongly.
3. Expansion to Other Outcomes or Multi-Outcome Prediction: The focus on RPE and lens is well-justified, but these are two outcomes within retinal organoids. A major question is whether the approach could be extended to predict other cell types or structures (e.g., presence of certain retinal neurons, or malformations) or even multiple outcomes at once. Suggestion: The authors should discuss the generality of their approach. Could the same pipeline be trained to predict, say, photoreceptor layer formation or other features if annotated? Are there limitations (like needing binary outcomes vs. multi-class)? Even if outside the scope of this study, a brief discussion would reassure readers that the method is not intrinsically limited to these two tissues. If data were available, it would be interesting to see a multi-label classification (predict both RPE and lens presence simultaneously) or an extension to other organoid systems in future. Including such commentary would highlight the broad applicability of this platform.
4. Curse of high dimensionality: Using Euclidean distance in a 165-dimensional morphometric space likely suffers from the curse of dimensionality, which diminishes the meaning of distances as dimensionality increases. In such high-dimensional settings, the range of pairwise distances tends to collapse, undermining the ability to discern meaningful intra- vs. inter-organoid differences. Suggestion: To address this, I would encourage the authors to apply principal component analysis (PCA) in place of (or prior to) tSNE. PCA would reduce the data to a few dominant axes of variation that capture most of the morphometric variance, directly revealing which features drive differences between organoids. These principal components are linear combinations of the original 165 parameters, so one can examine their loadings to identify which morphometric traits carry the most information - yielding interpretable axes of biological variation (e.g., organoid size, shape complexity, etc.). In addition, I would like to mention an important cautionary remark regarding tSNE embeddings. tSNE does not preserve global geometry of the data. Distances and cluster separations in a tSNE map are therefore not faithful to the original high-dimensional distances and should be interpreted with caution. See Chari T, Pachter L (2023), The specious art of single-cell genomics, PLoS Comput Biol 19(8): e1011288, for an enlightening discussion in the context of single cell genomics. The authors have shown that extreme dimensionality reduction to 2D can introduce significant distortions in the data's structure, meaning the apparent proximity or separation of points in a tSNE plot may be an artifact of the algorithm rather than a true reflection of morphometric similarity. Implementing PCA would mitigate high-dimensional distance issues by focusing on the most informative dimensions, while also providing clear, quantitative axes that summarize organoid heterogeneity. This change would strengthen the analysis by making the results more robust (avoiding distance artifacts) and biologically interpretable, as each principal component can be traced back to specific morphometric features of interest.
5. Statistical Reporting and Significance: The manuscript focuses on F1-score as the metric to report accuracy over time, which is appropriate. However, it's not explicitly stated whether any statistical significance tests were performed on the differences between methods (e.g., CNN vs human, CNN vs classical ML). Suggestion: The authors could report statistical significance of the performance differences, perhaps using a permutation test or McNemar's test on predictions. For example, is the improvement of the CNN ensemble over the Random Forest/QDA classifier statistically significant across experiments? Given the n of organoids, this should be assessable. Demonstrating significance would add rigor to the analysis.

Minor Issues (with Suggestions):

1. Data Availability: Given the resource-intensive nature of the work, the value to the community will be highest if the data is made publicly available. I understand that this is of course at the behest of the authors and they do mention that they will make the data available upon publication of the manuscript . For the time being, the authors can consider sharing at least a representative subset of the data or the trained model weights. This will allow others to build on their work and test the method in other contexts, amplifying the impact of the study.
2. Discussion - Future Directions: The Discussion does a good job of highlighting applications (like guiding molecular analysis). One minor addition could be speculation on using this approach to actively intervene: for example, could one imagine altering culture conditions mid-course for organoids predicted not to form RPE, to see if their fate can be changed? The authors touch on reducing variability by focusing on the window of determination; extending that thought to an experimental test (though not done here) would inspire readers. This is entirely optional, but a sentence or two envisioning how predictive models enable dynamic experimental designs (not just passive prediction) would be a forward-looking note to end on.

I believe with the above clarifications and enhancements - especially regarding generalizability and interpretability - the paper will be suitable for broad readership. The work represents an exciting intersection of developmental biology and AI, and I commend the authors for this contribution.

Novelty and Impact:

This work fills an important gap in organoid biology and imaging. Previous studies have used deep learning to link imaging with molecular profiles or spatial patterns in organoids, but there remained a "notable gap" in predicting whether and to what extent specific tissues will form in organoids. The authors' approach is novel in applying deep learning to prospectively predict organoid tissue outcomes (RPE and lens) on a per-organoid basis, something not previously demonstrated in retinal organoids. Conceptually, this is a significant advance: it shows that fate decisions in a complex 3D culture model can be predicted well in advance, suggesting the existence of subtle early morphogenetic cues that only a sophisticated model can discern. The findings will be of broad interest to researchers in organoid technology, developmental biology, and biomedical AI.

Methodological Rigor and Technical Quality:

The study is methodologically solid and carefully executed. The authors gathered a uniquely large dataset under consistent conditions, which lends statistical power to their analyses. They employ rigorous controls: an expert panel provided human predictions as a baseline, and a classical machine learning pipeline using quantitative image-derived features was implemented for comparison. The deep learning approach is well-chosen and technically sound. They use an ensemble of CNN architectures (DenseNet121, ResNet50, and MobileNetV3) pre-trained on large image databases, fine-tuning them on organoid images. The use of image segmentation (DeepLabV3) to isolate the organoid from background is appropriate to ensure the models focus on the relevant morphology. Model training procedures (data augmentation, cross-entropy loss with class balancing, learning rate scheduling, and cross-validation) are thorough and follow best practices. The evaluation metrics (primarily F1-score) are suitable for the imbalanced outcomes and emphasize prediction accuracy in a biologically relevant way. Importantly, the authors separate training, test, and validation sets in a meaningful manner: images of each organoid are grouped to avoid information leakage, and an independent experiment serves as a validation to test generalization. The observation that performance is slightly lower on independent validation experiments underscores both the realism of their evaluation and the inherent heterogeneity between experimental batches. In addition, the study integrates interpretability (using GradientSHAP-based relevance backpropagation) to probe what image features the network uses. Although the relevance maps did not reveal obvious human-interpretable features, the attempt reflects a commendable thoroughness in analysis. Overall, the experimental design, data analysis, and reporting are of high quality, supporting the credibility of the conclusions.

Significance

Scientific Significance and Conceptual Advances:

Biologically, the ability to predict organoid outcomes early is quite significant. It means researchers can potentially identify when and which organoids will form a given tissue, allowing them to harvest samples at the right moment for molecular assays or to exclude organoids that will not form the desired structure. The manuscript's results indicate that RPE and lens fate decisions in retinal organoids are made much earlier than visible differentiation, with predictive signals detectable as early as ~11 hours for RPE and ~4-5 hours for lens. This suggests a surprising synchronization or early commitment in organoid development that was not previously appreciated. The authors' introduction of deep learning-derived determination windows refines the concept of a developmental "point of no return" for cell fate in organoids. Focusing on these windows could help in pinpointing the molecular triggers of these fate decisions. Another conceptual advance is demonstrating that non-invasive imaging data can serve a predictive role akin to (or better than) destructive molecular assays. The study highlights that classical morphology metrics and even expert eyes capture mainly recognition of emerging tissues, whereas the CNN detects subtler, non-intuitive features predictive of future development. This underlines the power of deep learning to uncover complex phenotypic patterns that elude human analysis, a concept that could be extended to other organoid systems and developmental biology contexts. In sum, the work not only provides a tool for prediction but also contributes conceptual insights into the timing of cell fate determination in organoids.

Strengths:

The combination of high-resolution time-lapse imaging with advanced deep learning is innovative. The authors effectively leverage AI to solve a biological uncertainty problem, moving beyond qualitative observations to quantitative predictions. The study uses a remarkably large dataset (1,000 organoids, >100k images), which is a strength as it captures variability and provides robust training data. This scale lends confidence that the model isn't overfit to a small sample. By comparing deep learning with classical machine learning and human predictions, the authors provide context for the model's performance. The CNN ensemble consistently outperforms both the classical algorithms and human experts, highlighting the value added by the new method. The deep learning model achieves high accuracy (F1 > 0.85) at impressively early time points. The fact that it can predict lens formation just ~4.5 hours into development with confidence is striking. Performance remained strong and exceeded human capability at all assessed times. Key experimental and analytical steps (segmentation, cross-validation between experiments, model calibration, use of appropriate metrics) are executed carefully. The manuscript is transparent about training procedures and even provides source code references, enhancing reproducibility. The manuscript is generally well-written with a logical flow from the problem (organoid heterogeneity) to the solution (predictive modeling) and clear figures referenced.

Weaknesses and Limitations:

Generalizability Across Batches/Conditions: One limitation is the variability in model performance on organoids from independent experiments. The CNN did slightly worse on a validation set from a separate experiment, indicating that differences in the experimental batch (e.g., slight protocol or environmental variations) can affect accuracy. This raises the question of how well the model would generalize to organoids generated under different protocols or by other labs. While the authors do employ an experiment-wise cross-validation, true external validation (on a totally independent dataset or a different organoid system) would further strengthen the claim of general applicability.

Interpretability of the Predictions: Despite using relevance backpropagation, the authors were unable to pinpoint clear human-interpretable image features that drive the predictions. In other words, the deep learning model remains somewhat of a "black box" in terms of what subtle cues it uses at early time points. This limits the biological insight that can be directly extracted regarding early morphological indicators of RPE or lens fate. It would be ideal if the study could highlight specific morphological differences (even if minor) correlated with fate outcomes, but currently those remain elusive.

Scope of Outcomes: The study focuses on two particular tissues (RPE and lens) as the outcomes of interest. These were well-chosen as examples (one induced, one spontaneous), but they do not encompass the full range of retinal organoid fates (e.g., neural retina layers). It's not a flaw per se, but it means the platform as presented is specialized. The method might need adaptation to predict more complex or multiple tissue outcomes simultaneously.

Requirement of Large Data and Annotations: Practically, the approach required a very large imaging dataset and extensive manual annotation; each organoid's RPE and lens outcome, plus manual masking for training the segmentation model. This is a substantial effort that may be challenging to reproduce widely. The authors suggest that perhaps ~500 organoids might suffice to achieve similar results, but the data requirement is still high. Smaller labs or studies with fewer organoids might not immediately reap the full benefits of this approach without access to such imaging throughput.

Medaka Fish vs. Other Systems: The retinal organoids in this study appear to be from medaka fish, whereas much organoid research uses human iPSC-derived organoids. It's not fully clear in the manuscript as to how the findings translate to mammalian or human organoids. If there are species-specific differences, the applicability to human retinal organoids (which are important for disease modeling) might need discussion. This is a minor point if the biology is conserved, but worth noting as a potential limitation.

Predicting Tissue Size is Harder: The model's accuracy in predicting how much tissue (relative area) an organoid will form, while good, is notably lower than for simply predicting presence/absence. Final F1 scores for size classes (~0.7) indicate moderate success. This implies that quantitatively predicting organoid phenotypic severity or extent is more challenging, perhaps due to more continuous variation in size. The authors do acknowledge the lower accuracy for size and treat it carefully.

Latency vs. Determination: While the authors narrow down the time window of fate determination, it remains somewhat unclear whether the times at which the model reaches high confidence truly correspond to the biological "decision point" or are just the earliest detection of its consequences. The manuscript discusses this caveat, but it's an inherent limitation that the predictive time point might lag the actual internal commitment event. Further work might be needed to link these predictions to molecular events of commitment.

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Referee #2

Evidence, reproducibility and clarity

Summary: Afting et al. present a computational pipeline for analyzing timelapse brightfield images of retinal organoids derived from Medaka fish. Their pipeline processes images along two paths: 1) morphometrics (based on computer vision features from skimage) and 2) deep learning. They discovered, through extensive manual annotation of ground truth, that their deep learning method could predict retinal pigmented epithelium and lens tissue emergence in time points earlier than either morphometrics or expert predictions. Our review is formatted based on the review commons recommendation.

Major comments:

Are the key conclusions convincing?

Yes, the key conclusion that deep learning outperforms morphometric approaches is convincing. However, several methodological details require clarification. For instance, were the data splitting procedures conducted in the same manner for both approaches? Additionally, the authors note in the methods: "The validation data were scaled to the same range as the training data using the fitted scalers obtained from the training data." This represents a classic case of data leakage, which could artificially inflate performance metrics in traditional machine learning models. It is unclear whether the deep learning model was subject to the same issue. Furthermore, the convolutional neural network was trained with random augmentations, effectively increasing the diversity of the training data. Would the performance advantage still hold if the sample size had not been artificially expanded through augmentation?

Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Their claims are currently preliminary, pending increased clarity and additional computational experiments described below.

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

• The authors discretize continuous variables into four bins for classification. However, a regression framework may be more appropriate for preserving the full resolution of the data. At a minimum, the authors should provide a stronger justification for this binning strategy and include an analysis of bin performance. For example, do samples near bin boundaries perform comparably to those near the bin centers? This would help determine whether the discretization introduces artifacts or obscures signals.
• The relevance backpropagation interpretation analysis is not convincing. The authors argue that the model's use of pixels across the entire image (rather than just the RPE region) indicates that the deep learning approach captures holistic information. However, only three example images are shown out of hundreds, with no explanation for their selection, limiting the generalizability of the interpretation. Additionally, it is unclear how this interpretability approach would work at all in earlier time points, particularly before the model begins making confident predictions around the 8-hour mark. It is also not specified whether the input used for GradSHAP matches the input used during CNN training. The authors should consider expanding this analysis by quantifying pixel importance inside versus outside annotated regions over time. Lastly, Figure 4C is missing a scale bar, which would aid in interpretability.
• The authors claim that they removed technical artifacts to the best of their ability, but it is unclear if the authors performed any adjustment beyond manual quality checks for contamination. Did the authors observe any illumination artifacts (either within a single image or over time)? Any other artifacts or procedures to adjust?
• In line 434-436 the authors state "In this work, we used 1,000 organoids in total, to achieve the reported prediction accuracies. Yet, we suspect that as little as ~500 organoids are sufficient to reliably recapitulate our findings." It is unclear what evidence the authors use to support this claim? The authors could perform a downsampling analysis to determine tradeoff between performance and sample size.

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

Yes, we believe all experiments are realistic in terms of time and resources. We estimate all experiments could be completed in 3-6 months.

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

No, the code is not currently available. We were not able to review the source code.

Are the experiments adequately replicated and statistical analysis adequate?

• The experiments are adequately replicated.
• The statistical analysis (deep learning) is lacking a negative control baseline, which would be helpful to observe if performance is inflated.

Minor comments:

Specific experimental issues that are easily addressable.

Are prior studies referenced appropriately?

Yes.

Are the text and figures clear and accurate?

The authors must improve clarity on terminology. For example, they should define a comprehensive dataset, significant, and provide clarity on their morphometrics feature space. They should elaborate on what they mean by "confounding factor of heterogeneity".

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

• Figure 2C describes a distance between what? The y axis is likely too simple. Same confusion over Figure 2D. Was distance computed based on tsne coordinates?
• The authors perform a Herculean analysis comparing dozens of different machine learning classifiers. They select two, but they should provide justification for this decision.
• It would be good to get a sense for how these retinal organoids grow - are they moving all over the place? They are in Matrigel so maybe not, but are they rotating? Can the author's approach predict an entire non-emergence experiment? The authors tried to standardize protocol, but ultimately if It's deriving this much heterogeneity, then how well it will actually generalize to a different lab is a limitation.
• The authors should dampen claims throughout. For example, in the abstract they state, "by combining expert annotations with advanced image analysis". The image analysis pipelines use common approaches.
• The authors state: "the presence of RPE and lenses were disagreed upon by the two independently annotating experts in a considerable fraction of organoids (3.9 % for RPE, 2.9% for lenses).", but it is unclear why there were two independently annotating experts. The supplements say images were split between nine experts for annotation.
• Details on the image analysis pipeline would be helpful to clarify. For example, why did they choose to measure these 165 morphology features? Which descriptors were used to quantify blur? Did the authors apply blur metrics per FOV or per segmented organoid?
• The description of the number of images is confusing and distracts from the number of organoids. The number of organoids and number of timepoints used would provide a better description of the data with more value. For example, does this image count include all five z slices?
• The authors should consider applying a maximum projection across the five z slices (rather than the middle z) as this is a common procedure in image analysis. Why not analyze three-dimensional morphometrics or deep learning features? Might this improve performance further?
• There is a lot of manual annotation performed in this work, the authors could speculate how this could be streamlined for future studies. How does the approach presented enable streamlining?

Significance

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

The paper's advance is technical (providing new methods for organoid quality control) and conceptual (providing proof of concept that earlier time points contain information to predict specific future outcomes in retinal organoids)

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

• The authors do a good job of placing their work in context in the introduction.
• The work presents a simple image analysis pipeline (using only the middle z slice) to process timelapse organoid images. So not a 4D pipeline (time and space), just 3D (time). It is likely that more and more of these approaches will be developed over time, and this article is one of the early attempts.
• The work uses standard convolutional neural networks.

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

• Data scientists performing image-based profiling for time lapse imaging of organoids.
• Retinal organoid biologists
• Other organoid biologists who may have long growth times with indeterminate outcomes.

Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

• Image-based profiling/morphometrics
• Organoid image analysis
• Computational biology
• Cell biology
• Data science/machine learning
• Software

This is a signed review: Gregory P. Way, PhD Erik Serrano Jenna Tomkinson Michael J. Lippincott Cameron Mattson Department of Biomedical Informatics, University of Colorado

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Referee #1

Evidence, reproducibility and clarity

This study presents predictive modeling for developmental outcome in retinal organoids based on high-content imaging. Specifically, it compares the predictive performance of an ensemble of deep learning models with classical machine learning based on morphometric image features and predictions from human experts for four different task: prediction of RPE presence and lense presence (at the end of development) as well as the respective sizes. It finds that the DL model outperforms the other approaches and is predictive from early timepoints on, strongly indicating a time-frame for important decision steps in the developmental trajectory.

Major comments: I find the paper over-all well written and easy to understand. The findings are relevant (see significance statement for details) and well supported. However, I have some remarks on the description and details of the experimental set-up, the data availability and reproducibility / re-usability of the data.

1. Some details about the experimental set-up are unclear to me. In particular, it seems like there is a single organoid per well, as the manuscript does not mention any need for instance segmentation or tracking to distinguish organoids in the images and associate them over time. Is that correct? If yes, it should be explicitly stated so. Are there any specific steps in the organoid preparation necessary to avoid multiple organoids per well? Having multiple organoids per well would require the aforementioned image analysis steps (instance segmentation and tracking) and potentially add significant complexity to the analysis procedure, so this information is important to estimate the effort for setting up a similar approach in other organoid cultures (for example cancer organoids, where multiple organoids per well are common / may not be preventable in certain experimental settings).
2. The terminology used with respect to the test and validation set is contrary to the field, and reporting the results on the test set (should be called validation set), should be avoided since it is used to select models. In more detail: the terms "test set" and "validation set" (introduced in 213-221) are used with the opposite meaning to their typical use in the deep learning literature. Typically, the validation set refers to a separate split that is used to monitor convergence / avoid overfitting during training, and the test set refers to an external set that is used to evaluate the performance of trained models. The study uses these terms in an opposite manner, which becomes apparent from line 624: "best performing model ... judged by the loss of the test set.". Please exchange this terminology, it is confusing to a machine learning domain expert. Furthermore, the performance on the test set (should be called validation set) is typically not reported in graphs, as this data was used for model selection, and thus does not provide an unbiased estimate of model performance. I would remove the respective curves from Figures 3 and 4.
3. The experimental set-up for the human expert baseline is quite different to the evaluation of the machine learning models. The former is based on the annotation of 4,000 images by seven expert, the latter based on a cross-validation experiments on a larger dataset. First of all, the details on the human expert labeling procedure is very sparse, I could only find a very short description in the paragraph 136-144, but did not find any further details in the methods section. Please add a methods section paragraph that explains in more detail how the images were chosen, how they were assigned to annotators, and if there was any redundancy in annotation, and if yes how this was resolved / evaluated. Second, the fact that the set-up for human experts and ML models is quite different means that these values are not quite comparable in a statistical sense. Ideally, human estimators would follow the same set-up as in ML (as in, evaluate the same test sets). However, this would likely prohibitive in the required effort, so I think it's enough to state this fact clearly, for example by adding a comment on this to the captions of Figure 3 and 4.
4. It is unclear to me where the theoretical time window for the Latent Determination Horizon in Figure 5 (also mentioned in line 350) comes from? Please explain this in more detail and provide a citation for it.
5. The intepretability analysis (Figure 4, 634-639) based on relevance backpropagation was performed based on DenseNet121 only. Why did you choose this model and not the ResNet / MobileNet? I think it is quite crucial to see if there are any differences between these model, as this would show how much weight can be put on the evidence from this analysis and I would suggest to add an additional experiment and supplementary figure on this.
6. The code referenced in the code availability statement is not yet present. Please make it available and ensure a good documentation for reproducibility. Similarly, it is unclear to me what is meant by "The data that supports the findings will be made available on HeiDoc". Does this only refer to the intermediate results used for statistical analysis? I would also recommend to make the image data of this study available. This could for example be done through a dedicated data deposition service such as BioImageArchive or BioStudies, or with less effort via zenodo. This would ensure both reproducibility as well as potential re-use of the data. I think the latter point is quite interesting in this context; as the authors state themselves it is unclear if prediction of the TOIs isn't even possible at an earlier point that could be achieved through model advances, which could be studied by making this data available.

Minor comments:

Line 315: Please add a citation for relevance backpropagation here.

Line 591: There seems to be typo: "[...] classification of binary classification [...]"

Line 608: "[...] where the images of individual organoids served as groups [...]" It is unclear to me what this means.

Significance

General assessment: This study demonstrates that (retinal) organoid development can be predicted from early timepoints with deep learning, where these cannot be discerned by human experts or simpler machine learning models. This fact is very interesting in itself due to its implication for organoid development, and could provide a valuable tool for molecular analysis of different organoid populations, as outlined by the authors. The contribution could be strengthened by providing a more thorough investigation of what features in the image are predictive at early timepoints, using a more sophisticated approach than relevance backprop, e.g. Discover (https://www.nature.com/articles/s41467-024-51136-9). This could provide further biological insight into the underlying developmental processes and enhance the understanding of retinal organoid development.

Advance: similar studies that predict developmental outcome based on image data, for example cell proliferation or developmental outcome exist. However, to the best of my knowledge, this study is the first to apply such a methodology to organoids and convincingly shows is efficacy and argues is potential practical benefits. It thus constitutes a solid technical advance, that could be especially impactful if it could be translated to other organoid systems in the future.

Audience: This research is of interest to a technical audience. It will be of immediate interest to researchers working on retinal organoids, who could adapt and use the proposed system to support experiments by better distinguishing organoids during development. To enable this application, code and data availability should be ensured (see above comments on reproducibility). It is also of interest to researchers in other organoid systems, who may be able to adapt the methodology to different developmental outcome predictions. Finally, it may also be of interest to image analysis / deep learning researchers as a dataset to improve architectures for predictive time series modeling.

My research background: I am an expert in computer vision and deep learning for biomedical imaging, especially in microscopy. I have some experience developing image analysis for (cancer) organoids. I don't have any experience on the wet lab side of this work.

Constantin Pape

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

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Reply to the reviewers

Manuscript number: RC-2024-02830

Corresponding author(s): Julien, Sage

1. General Statements

We thank the Reviewers for a fair review of our work and helpful suggestions. We have significantly revised the manuscript in response to these suggestions. We provide a point-by-point response to the Reviewers below but wanted to highlight in our response a recurring concern related to the strong cell cycle arrest observed upon the acute FAM53C knock-down being different than the limited phenotypes in other contexts, including the knockout mice and DepMap data.

First, we now show that we can recapitulate the strong G1 arrest resulting from the FAM53C knock-down using two independent siRNAs in RPE-1 cells, supporting the specificity of the effects.

Second, the G1 arrest that results from the FAM53C knock-down is also observed in cells with inactive p53, suggesting it is not due to a non-specific stress response due to “toxic” siRNAs. In addition, the arrest is dependent on RB, which fits with the genetic and biochemical data placing FAM53C upstream of RB, further supporting a specific phenotype.

Third, we have performed experiments in other human cells, including cancer cell lines. As would be expected for cancer cells, the G1 arrest is less pronounced but is still significant, indicating that the G1 arrest is not unique to RPE-1 cells.

Fourth, it is not unexpected that compensatory mechanisms would be activated upon loss of FAM53C during development or in cancer – which may explain the lack of phenotypes in vivo or upon long-term knockout. This has been true for many cell cycle regulators, either because of compensation by other family members that have overlapping functions, or by a larger scale rewiring of signaling pathways.

2. Point-by-point description of the revisions

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

Summary:

Taylar Hammond and colleagues identified new regulators of the G1/S transition of the cell cycle. They did so by screening public available data from the Cancer Dependency Map, and identified FAM53C as a positive regulator of the G1/S transition. Using biochemical assays they then show that FAM53 interacts with the DYRK1A kinase to inhibit its function. DYRK1A in its is known to induce degradation of cyclin D, leading the authors to propose a model in which DYRK1A-dependent cyclin D degradation is inhibited by FAM53C to permit S-phase entry. Finally the authors assess the effect of FAM53C deletion in a cortical organoid model, and in Fam53c knockout mice. Whereas proliferation of the organoids is indeed inhibited, mice show virtually no phenotype.

Major comments:

The authors show convincing evidence that FAM53C loss can reduce S-phase entry in cell cultures, and that it can bind to DYRK1A. However, FAM53 has multiple other binding partners and I am not entirely convinced that negative regulation of DYRK1A is the predominant mechanism to explain its effects on S-phase entry. Some of the claims that are made based on the biochemical assays, and on the physiological effects of FAM53C are overstated. In addition, some choices made methodology and data representation need further attention.

1. The authors do note that P21 levels increase upon FAM53C. They show convincing evidence that this is not a P53-dependent response. But the claim that " p21 upregulation alone cannot explain the G1 arrest in FAM53C-deficient cells (line 138-139) is misleading. A p53-independent p21 response could still be highly relevant. The authors could test if FAM53C knockdown inhibits proliferation after p21 knockdown or p21 deletion in RPE1 cells. The Reviewer raises a great point. Our initial statement needed to be clarified and also need more experimental support. We have performed experiments where we knocked down FAM53C and p21 individually, as well as in combination, in RPE-1 cells. These experiment show that p21 knock-down is not sufficient to negate the cell cycle arrest resulting from the FAM53C knock-down in RPE-1 cells (Figure 4B,C and Figure S4C,D).

We now extended these experiments to conditions where we inhibited DYRK1A, and we also compared these data to experiments in p53-null RPE-1 cells. Altogether, these experiments point to activation of p53 downstream of DYRK1A activation upon FAM53C knock-down, and indicate that p21 is not the only critical p53 target in the cell cycle arrest observed in FAM53C knock-down cells (Figure 4 and Figure S4).

The authors do not convincingly show that FAM53C acts as a DYRK1A inhibitor in cells. Figures 4B+C and S4B+C show extremely faint P-CycD1 bands, and tiny differences in ratios. The P values are hovering around the 0.05, so n=3 is clearly underpowered here. Total CycD1 levels also correlate with FAM53C levels, which seems to affect the ratios more than the tiny pCycD1 bands. Why is there still a pCycD1 band visible in 4B in the GFP + BTZ + DYRK1Ai condition? And if I look at the data points I honestly don't understand how the authors can conclude from S4C that knockdown of siFAM53C increases (DYRK1A dependent) increases in pCycD1 (relative to total CycD1). In figure 5C, no blot scans are even shown, and again the differences look tiny. So the authors should either find a way to make these assays more robust, or alter their claims appropriately.

We appreciate these comments from the Reviewer and have significantly revised the manuscript to address them.

The analysis of Cyclin D phosphorylation and stability are complicated by the upregulation of p21 upon FAM53C knock-down, in particular because p21 can be part of Cyclin D complexes, which may affect its protein levels in cells (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). Instead of focusing on Cyclin D levels and stability, we refocused the manuscript on RB and p53 downstream of FAM53C loss.

We removed previous panel 4B from the revised manuscript. For panels 4E and S4B (now panels S3J and S3K)), we used a true “immunoassay” (as indicated in the legend – not an immunoblot), which is much more quantitative and avoids error-prone steps in standard immunoblots (“Western blots”). Briefly, this system was developed by ProteinSimple. It uses capillary transfer of proteins and ELISA-like quantification with up to 6 logs of dynamic range (see their web site https://www.proteinsimple.com/wes.html). The “bands” we show are just a representation of the luminescence signals in capillaries. We made sure to further clarify the figure legends in the revised manuscript.

The representative Western blot images for 5C-D (now 5F-G) in the original submission are shown in Figure 5E, we apologize if this was not clear. The differences are small, which we acknowledge in the revised manuscript. Note that several factors can affect Cyclin D levels in cells, including the growth rate and the stage of the cell cycle. Our FACS analysis shows that normal organoids have ~63% of cells in G1 and ~13% in S phase; the overall lower proportion of S-phase cells in organoids may make the immunoblot difference appear smaller, with fewer cycling cells resulting in decreased Cyclin D phosphorylation.

Nevertheless, the Reviewer brings up a good point and comments from this Reviewer and the others made us re-think how to best interpret our results. As discussed above, we re-read carefully the Meyer paper and think that FAM53C’s role and DYRK1A activity in cells may be understood when considering levels of both CycD and p21 at the same time in a continuum. While our genetic and biochemical data support a role for FAM53C in DYRK1A inhibition, it is likely that the regulation of cell cycle progression by FAM53C is not exclusively due to this inhibition. As discussed above and below, we noted an upregulation of p21 upon FAM53C knock-down, and activation of p53 and its targets likely contributes significantly to the phenotypes observed. We added new experiments to support this more complex model (Figure 4 and Figure S4, with new model in S4L).

The experiments to test if DYRK1A inhibition could rescue the G1 arrest observed upon FAM53C knockdown are not entirely convincing either. It would be much more convincing if they also perform cell counting experiments as they have done in Figures 1F and 1G, to complement the flow cytometry assays. I suggest that the authors do these cell counting experiments in RPE1 +/- P53 cells as well as HCT116 cells. In addition, did the authors test if P21 is induced by DYRK1Ai in HCT116 cells?

We repeated the experiments with the DYRK1A inhibitor and counted the cells. In p53-null RPE-1 cells, we found that cell numbers do not increase in these conditions where we had observed a cell cycle re-entry (Fig. 4E), which was accompanied by apoptotic cell death (Fig. S4I). Thus, cells re-enter the cell cycle but die as they progress through S-phase and G2/M. We note that inhibition of DYRK1A has been shown to decrease expression of G2/M regulators (PMID: 38839871), which may contribute to the inability of cells treated to DYRK1Ai to divide. Because our data in RPE-1 cells showed that p21 knock-down was not sufficient to allow the FAM53C knock-down cells to re-enter the cell cycle, we did not further analyze p21 in HCT-116 cells.

The data in Figure 5C and 5D are identical, although they are supposed to represent either pCycD1 ratios or p21 levels. This is a problem because at least one of the two cannot be true. Please provide the proper data and show (representative) images of both data types.

We apologize for these duplicated panels in the original submission. We now replaced the wrong panel with the correct data (Fig. 5F,G).

Line 246: "Fam53c knockout mice display developmental and behavioral defects." I don't agree with this claim. The mutant mice are born at almost the expected Mendelian ratios, the body weight development is not consistently altered. But more importantly, no differences in adult survival or microscopic pathology were seen. The authors put strong emphasis on the IMPC behavioral analysis, but they should be more cautious. The IMPC mouse cohorts are tested for many other phenotypes related to behavior and neurological symptoms and apparently none of these other traits were changed in the IMPC Famc53c-/- cohort. Thus, the decreased exploration in a new environment could very well be a chance finding. The authors need to take away claims about developmental and behavioral defects from the abstract, results and discussion sections; the data are just too weak to justify this.

We agree with the Reviewer that, although we observed significant p-values, this original statement may not be appropriate in the biological sense. We made sure in the revised manuscript to carefully present these data.

Minor comments:

Can the authors provide a rationale for each of the proteins they chose to generate the list of the 38 proteins in the DepMap analysis? I looked at the list and it seems to me that they do not all have described functions in the G1/S transition. The analysis may thus be biased.

To address this point, we updated Table S1 (2nd tab) to provide a better rationale for the 38 factors chosen. Our focus was on the canonical RB pathway and we included RB binding proteins whose function had suggested they may also be playing a role in the G1/S transition. We do agree that there is some bias in this selection (e.g., there are more RB binding factors described) but we hope the Reviewer will agree with us that this list and the subsequent analysis identified expected factors, including FAM53C. Future studies using this approach and others will certainly identify new regulators of cell cycle progression.

Figure 1B is confusing to me. Are these just some (arbitrarily) chosen examples? Consider leaving this heatmap out altogether, of explain in more detail.

We agree with the Reviewer that this panel was not necessarily useful and possibly in the wrong place, and we removed it from the manuscript. We replaced it with a cartoon of top hits in the screen.

The y-axes in Figures 2C, 2D, 2E, and 4D are misleading because they do not start at 0. Please let the axis start at 0, or make axis breaks.

We re-graphed these panels.

Line 229: " Consequences ... brain development." This subheader is misleading, because the in vitro cortical organoid system is a rather simplistic model for brain development, and far away from physiological brain development. Please alter the header.

We changed the header to “Consequences of FAM53C inactivation in human cortical organoids in culture”.

Figure S5F: the gating strategy is not clear to me. In particular, how do the authors know the difference between subG1 and G1 DAPI signals? Do they interpret the subG1 as apoptotic cells? If yes, why are there so many? Are the culturing or harvesting conditions of these organoids suboptimal? Perhaps the authors could consider doing IF stainings on EdU or BrdU on paraffin sections of organoids to obtain cleaner data?

Thank you for your feedback. The subG1 population in the original Figure S5F represents cells that died during the dissociation step of the organoids for FACS analysis. To address this point, we performed live & dead staining to exclude dead cells and provide clearer data. We refined gating strategy for better clarity in the new S5F panel.

Figure S6A; the labeling seems incorrect. I would think that red is heterozygous here, and grey mutant.

We fixed this mistake, thank you.

__Reviewer #1 (Significance (Required)): __

The finding that the poorly studied gene FAM53C controls the G1/S transition in cell lines is novel and interesting for the cell cycle field. However, the lack of phenotypes in Famc53-/- mice makes this finding less interesting for a broader audience. Furthermore, the mechanisms are incompletely dissected. The importance of a p53-indepent induction of p21 is not ruled out. And while the direct inhibitory interaction between FAM53C and DYRK1A is convincing (and also reported by others; PMID: 37802655), the authors do not (yet) convincingly show that DYRK1A inhibition can rescue a cell proliferation defect in FAM53C-deficient cells.

Altogether, this study can be of interest to basic researchers in the cell cycle field.

I am a cell biologist studying cell cycle fate decisions, and adaptation of cancer cells & stem cells to (drug-induced) stress. My technical expertise aligns well with the work presented throughout this paper, although I am not familiar with biolayer interferometry.

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

Summary

In this study Hammond et al. investigated the role of Dual-specificity Tyrosine Phosphorylation regulated Kinase 1A (DYRK1) in G1/S transition. By exploiting Dependency Map portal, they identified a previously unexplored protein FAM53C as potential regulator of G1/S transition. Using RNAi, they confirmed that depletion of FAM53C suppressed proliferation of human RPE1 cells and that this phenotype was dependent on the presence protein RB. In addition, they noted increased level of CDKN1A transcript and p21 protein that could explain G1 arrest of FAM53C-depleted cells but surprisingly, they did not observe activation of other p53 target genes. Proteomic analysis identified DYRK1 as one of the main interactors of FAM53C and the interaction was confirmed in vitro. Further, they showed that purified FAM53C blocked the ability of DYRK1 to phosphorylate cyclin D in vitro although the activity of DYRK1 was likely not inhibited (judging from the modification of FAM53C itself). Instead, it seems more likely that FAM53C competes with cyclin D in this assay. Authors claim that the G1 arrest caused by depletion of FAM53C was rescued by inhibition of DYRK1 but this was true only in cells lacking functional p53. This is quite confusing as DYRK1 inhibition reduced the fraction of G1 cells in p53 wild type cells as well as in p53 knock-outs, suggesting that FAM53C may not be required for regulation of DYRK1 function. Instead of focusing on the impact of FAM53C on cell cycle progression, authors moved towards investigating its potential (and perhaps more complex) roles in differentiation of IPSCs into cortical organoids and in mice. They observed a lower level of proliferating cells in the organoids but if that reflects an increased activity of DYRK1 or if it is just an off target effect of the genetic manipulation remains unclear. Even less clear is the phenotype in FAM53C knock-out mice. Authors did not observe any significant changes in survival nor in organ development but they noted some behavioral differences. Weather and how these are connected to the rate of cellular proliferation was not explored. In the summary, the study identified previously unknown role of FAM53C in proliferation but failed to explain the mechanism and its physiological relevance at the level of tissues and organism. Although some of the data might be of interest, in current form the data is too preliminary to justify publication.

Major points

1. Whole study is based on one siRNA to Fam53C and its specificity was not validated. Level of the knock down was shown only in the first figure and not in the other experiments. The observed phenotypes in the cell cycle progression may be affected by variable knock-down efficiency and/or potential off target effects. We thank the Reviewer for raising this important point. First, we need to clarify that our experiments were performed with a pool of siRNAs (not one siRNA). Second, commercial antibodies against FAM53C are not of the best quality and it has been challenging to detect FAM53C using these antibodies in our hands – the results are often variable. In addition, to better address the Reviewer’s point and control for the phenotypes we have observed, we performed two additional series of experiments: first, we have confirmed G1 arrest in RPE-1 cells with individual siRNAs, providing more confidence for the specificity of this arrest (Fig. S1B); second, we have new data indicating that other cell lines arrest in G1 upon FAM53C knock-down (Fig. S1E,F and Fig. 4F).

Experiments focusing on the cell cycle progression were done in a single cell line RPE1 that showed a strong sensitivity to FAM53C depletion. In contrast, phenotypes in IPSCs and in mice were only mild suggesting that there might be large differences across various cell types in the expression and function of FAM53C. Therefore, it is important to reproduce the observations in other cell types.

As mentioned above, we have new data indicating that other cell lines arrest in G1 upon FAM53C knock-down (three cancer cell lines) (Fig. S1E,F and Fig. 4F).

Authors state that FAM53C is a direct inhibitor of DYRK1A kinase activity (Line 203), however this model is not supported by the data in Fig 4A. FAM53C seems to be a good substrate of DYRK1 even at high concentrations when phosphorylations of cyclin D is reduced. It rather suggests that DYRK1 is not inhibited by FAM53C but perhaps FAM53C competes with cyclin D. Further, authors should address if the phosphorylation of cyclin D is responsible for the observed cell cycle phenotype. Is this Cyclin D-Thr286 phosphorylation, or are there other sites involved?

We revised the text of the manuscript to include the possibility that FAM53C could act as a competitive substrate and/or an inhibitor.

We removed most of the Cyclin D phosphorylation/stability data from the revised manuscript. As the Reviewers pointed out, some of these data were statistically significant but the biological effects were small. As discussed above in our response to Reviewer #1, the analysis of Cyclin D phosphorylation and stability are complicated by the upregulation of p21 upon FAM53C knock-down, in particular because p21 can be part of Cyclin D complexes, which may affect its protein levels in cells (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). Instead of focusing on Cyclin D levels and stability, we refocused the manuscript on RB and p53 downstream of FAM53C loss.

We note, however, that we used specific Thr286 phospho-antibodies, which have been used extensively in the field. Our data in Figure 1 with palbociclib place FAM53C upstream of Cyclin D/CDK4,6. We performed Cyclin D overexpression experiments but RPE-1 cells did not tolerate high expression of Cyclin D1 (T286A mutant) and we have not been able to conduct more ‘genetic’ studies.

At many places, information on statistical tests is missing and SDs are not shown in the plots. For instance, what statistics was used in Fig 4C? Impact of FAM53C on cyclin D phosphorylation does not seem to be significant. In the same experiment, does DYRK1 inhibitor prevent modification of cyclin D?

As discussed above, we removed some of these data and re-focused the manuscript on p53-p21 as a second pathway activated by loss of FAM53C.

Validation of SM13797 compound in terms of specificity to DYRK1 was not performed.

This is an important point. We had cited an abstract from the company (Biosplice) but we agree that providing data is critical. We have now revised the manuscript with a new analysis of the compound’s specificity using kinase assays. These data are shown in Fig. S3F-H.

A fraction of cells in G1 is a very easy readout but it does not measure progression through the G1 phase. Extension of the S phase or G2 delay would indirectly also result in reduction of the G1 fraction. Instead, authors could measure the dynamics of entry to S phase in cells released from a G1 block or from mitotic shake off.

The Reviewer made a good point. As discussed in our response to Reviewer #1, with p53-null RPE-1 cells, we found that cell numbers do not increase in these conditions where we had observed a cell cycle re-entry (Fig. 4E), which was accompanied by apoptotic cell death (Fig. S4I). Thus, cells re-enter the cell cycle but die as they progress through S-phase and G2/M. We note that inhibition of DYRK1A has been shown to decrease expression of G2/M regulators (PMID: 38839871), which may contribute to the inability of cells treated to DYRK1Ai to divide. Because our data in RPE-1 cells showed that p21 knock-down was not sufficient to allow the FAM53C knock-down cells to re-enter the cell cycle, we did not further analyze p21 in HCT-116 cells. These data indicate that G1 entry by flow cytometry will not always translate into proliferation.

Other points:

Fig. 2C, 2D, 2E graphs should begin with 0

We remade these graphs.

Fig. 5D shows that the difference in p21 levels is not significant in FAM53C-KO cells but difference is mentioned in the text.

We replaced the panel by the correct panel; we apologize for this error.

Fig. 6D comparison of datasets of extremely different sizes does not seem to be appropriate

We agree and revised the text. We hope that the Reviewer will agree with us that it is worth showing these data, which are clearly preliminary but provide evidence of a possible role for FAM53C in the brain.

Could there be alternative splicing in mice generating a partially functional protein without exon 4? Did authors confirm that the animal model does not express FAM53C?

We performed RNA sequencing of mouse embryonic fibroblasts derived from control and mutant mice. We clearly identified fewer reads in exon 4 in the knockout cells, and no other obvious change in the transcript (data not shown). However, immunoblot with mouse cells for FAM53C never worked well in our hands. We made sure to add this caveat to the revised manuscript.

__Reviewer #2 (Significance (Required)): __

Main problem of this study is that the advanced experimental models in IPSCs and mice did not confirm the observations in the cell lines and thus the whole manuscript does not hold together. Although I acknowledge the effort the authors invested in these experiments, the data do not contribute to the main conclusion of the paper that FAM53C/DYRK1 regulates G1/S transition.

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

This paper identifies FAM53C as a novel regulator of cell cycle progression, particularly at the G1/S transition, by inhibiting DYRK1A. Using data from the Cancer Dependency Map, the authors suggest that FAM53C acts upstream of the Cyclin D-CDK4/6-RB axis by inhibiting DYRK1A.

Specifically, their experiments suggest that FAM53C Knockdown induces G1 arrest in cells, reducing proliferation without triggering apoptosis. DYRK1A Inhibition rescues G1 arrest in P53KO cells, suggesting FAM53C normally suppresses DYRK1A activity. Mass Spectrometry and biochemical assays confirm that FAM53C directly interacts with and inhibits DYRK1A. FAM53C Knockout in Human Cortical Organoids and Mice leads to cell cycle defects, growth impairments, and behavioral changes, reinforcing its biological importance.

Strength of the paper:

The study introduces a novel cell cycle control signalling module upstream of CDK4/6 in G1/S regulation which could have significant impact. The identification of FAM53C using a depmap correlation analysis is a nice example of the power of this dataset. The experiments are carried out mostly in a convincing manner and support the conclusions of the manuscript.

Critique:

1) The experiments rely heavily on siRNA transfections without the appropriate controls. There are so many cases of off-target effects of siRNA in the literature, and specifically for a strong phenotype on S-phase as described here, I would expect to see solid results by additional experiments. This is especially important since the ko mice do not show any significant developmental cell cycle phenotypes. Moreover, FAM53C does not show a strong fitness effect in the depmap dataset, suggesting that it is largely non-essential in most cancer cell lines. For this paper to reach publication in a high-standard journal, I would expect that the authors show a rescue of the S-phase phenotype using an siRNA-resistant cDNA, and show similar S-phase defects using an acute knock out approach with lentiviral gRNA/Cas9 delivery.

We thank the Reviewer for this comment. Please refer to the initial response to the three Reviewers, where we discuss our use of single siRNAs and our results in multiple cell lines. Briefly, we can recapitulate the G1 arrest upon FAM53C knock-down using two independent siRNAs in RPE-1 cells. We also observe the same G1 arrest in p53 knockout cells, suggesting it is not due to a non-specific stress response. In addition, the arrest is dependent on RB, which fits with the genetic and biochemical data placing FAM53C upstream of RB, further supporting a specific phenotype. Human cancer cell lines also arrest in G1 upon FAM53C knock-down, not just RPE-1 cells. Finally, we hope the Reviewer will agree with us that compensatory mechanisms are very common in the cell cycle – which may explain the lack of phenotypes in vivo or upon long-term knockout of FAM53C.

2) The S-phase phenotype following FAM53C should be demonstrated in a larger variety of TP53WT and mutant cell lines. Given that this paper introduces a new G1/S control element, I think this is important for credibility. Ideally, this should be done with acute gRNA/Cas9 gene deletion using a lentiviral delivery system; but if the siRNA rescue experiments work and validate an on-target effect, siRNA would be an appropriate alternative.

We now show data with three cancer cell lines (U2OS, A549, and HCT-116 – Fig. S1E,F and Fig. 4F), in addition to our results in RPE-1 cells and in human cortical organoids. We note that the knock-down experiments are complemented by overexpression data (Fig. 1G-I), by genetic data (our original DepMap screen), and our biochemical data (showing direct binding of FAM53C to DYRK1A).

3) The western blot images shown in the MS appear heavily over-processed and saturated (See for example S4B, 4A, B, and E). Perhaps the authors should provide the original un-processed data of the entire gels?

For several of our panels (e.g., 4E and S4B, now panels S3J and S3K)), we used a true “immunoassay” (as indicated in the legend – not an immunoblot), which is much more quantitative and avoids error-prone steps in standard immunoblots (“Western blots”). Briefly, this system was developed by ProteinSimple. It uses capillary transfer of proteins and ELISA-like quantification with up to 6 logs of dynamic range (see their web site https://www.proteinsimple.com/wes.html). The “bands” we show are just a representation of the luminescence signals in capillaries. We made sure to further clarify the figure legends in the revised manuscript.

Data in 4A are also not a western blot but a radiograph.

For immunoblots, we will provide all the source data with uncropped blots with the final submission.

4) A critical experiment for the proposed mechanism is the rescue of the FAM53C S-phase reduction using DYRK1A inhibition shown in Figure 4. The legend here states that the data were extracted from BrdU incorporation assays, but in Figure S4D only the PI histograms are shown, and the S-phase population is not quantified. The authors should show the BrdU scatterplot and quantify the phenotype using the S-phase population in these plots. G1 measurements from PI histograms are not precise enough to allow for conclusions. Also, why are the intensities of the PI peaks so variable in these plots? Compare, for example, the HCT116 upper and lower panels where the siRNA appears to have caused an increase in ploidy.

We apologize for the confusion and we fixed these errors, for most of the analyses, we used PI to measure G1 and S-phase entry. We added relevant flow cytometry plots to supplemental figures (Fig. S1G, H, I, as well as Fig. S4E and S4K, and Fig. S5F).

5) There's an apparent contradiction in how RB deletion rescues the G1 arrest (Figure 2) while p21 seems to maintain the arrest even when DYRK1A is inhibited. Is p21 not induced when FAM53C is depleted in RB ko cells? This should be measured and discussed.

This comment and comments from the two other Reviewers made us reconsider our model. We re-read carefully the Meyer paper and think that DYRK1A activity may be understood when considering levels of both CycD and p21 at the same time in a continuum (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). While our genetic and biochemical data support a role for FAM53C in DYRK1A inhibition, it is obvious that the regulation of cell cycle progression by FAM53C is not exclusively due to this inhibition. As discussed above and below, we noted an upregulation of p21 upon FAM53C knock-down, and activation of p53 and its targets likely contributes significantly to the phenotypes observed. We added new experiments to support this more complex model (Figure 4 and Figure S4, with new model in S4L).

__Reviewer #3 (Significance (Required)): __

In conclusion, I believe that this MS could potentially be important for the cell cycle field and also provide a new target pathway that could be relevant for cancer therapy. However, the paper has quite a few gaps and inconsistencies that need to be addressed with further experiments. My main worry is that the acute depletion phenotypes appear so strong, while the gene is non-essential in mice and shows only a minor fitness effect in the depmap screens. More convincing controls are necessary to rule out experimental artefacts that misguide the interpretation of the results.

We appreciate this comment and hope that the Reviewer will agree it is still important to share our data with the field, even if the phenotypes in mice are modest.

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Referee #3

Evidence, reproducibility and clarity

This paper identifies FAM53C as a novel regulator of cell cycle progression, particularly at the G1/S transition, by inhibiting DYRK1A. Using data from the Cancer Dependency Map, the authors suggest that FAM53C acts upstream of the Cyclin D-CDK4/6-RB axis by inhibiting DYRK1A.

Specifically, their experiments suggest that FAM53C Knockdown induces G1 arrest in cells, reducing proliferation without triggering apoptosis. DYRK1A Inhibition rescues G1 arrest in P53KO cells, suggesting FAM53C normally suppresses DYRK1A activity. Mass Spectrometry and biochemical assays confirm that FAM53C directly interacts with and inhibits DYRK1A. FAM53C Knockout in Human Cortical Organoids and Mice leads to cell cycle defects, growth impairments, and behavioral changes, reinforcing its biological importance.

Strength of the paper:

The study introduces a novel cell cycle control signalling module upstream of CDK4/6 in G1/S regulation which could have significant impact. The identification of FAM53C using a depmap correlation analysis is a nice example of the power of this dataset. The experiments are carried out mostly in a convincing manner and support the conclusions of the manuscript.

Critique:

1. The experiments rely heavily on siRNA transfections without the appropriate controls. There are so many cases of off-target effects of siRNA in the literature, and specifically for a strong phenotype on S-phase as described here, I would expect to see solid results by additional experiments. This is especially important since the ko mice do not show any significant developmental cell cycle phenotypes. Moreover, FAM53C does not show a strong fitness effect in the depmap dataset, suggesting that it is largely non-essential in most cancer cell lines. For this paper to reach publication in a high-standard journal, I would expect that the authors show a rescue of the S-phase phenotype using an siRNA-resistant cDNA, and show similar S-phase defects using an acute knock out approach with lentiviral gRNA/Cas9 delivery.
2. The S-phase phenotype following FAM53C should be demonstrated in a larger variety of TP53WT and mutant cell lines. Given that this paper introduces a new G1/S control element, I think this is important for credibility. Ideally, this should be done with acute gRNA/Cas9 gene deletion using a lentiviral delivery system; but if the siRNA rescue experiments work and validate an on-target effect, siRNA would be an appropriate alternative.
3. The western blot images shown in the MS appear heavily over-processed and saturated (See for example S4B, 4A, B, and E). Perhaps the authors should provide the original un-processed data of the entire gels?
4. A critical experiment for the proposed mechanism is the rescue of the FAM53C S-phase reduction using DYRK1A inhibition shown in Figure 4. The legend here states that the data were extracted from Brad incorporation assays, but in Figure S4D only the PI histograms are shown, and the S-phase population is not quantified. The authors should show the Brad scatterplot and quantify the phenotype using the S-phase population in these plots. G1 measurements from PI histograms are not precise enough to allow for conclusions. Also, why are the intensities of the PI peaks so variable in these plots? Compare, for example, the HCT116 upper and lower panels where the siRNA appears to have caused an increase in ploidy.
5. There's an apparent contradiction in how RB deletion rescues the G1 arrest (Figure 2) while p21 seems to maintain the arrest even when DYRK1A is inhibited. Is p21 not induced when FAM53C is depleted in RB ko cells? This should be measured and discussed.

Significance

In conclusion, I believe that this MS could potentially be important for the cell cycle field and also provide a new target pathway that could be relevant for cancer therapy. However, the paper has quite a few gaps and inconsistencies that need to be addressed with further experiments. My main worry is that the acute depletion phenotypes appear so strong, while the gene is non-essential in mice and shows only a minor fitness effect in the depmap screens. More convincing controls are necessary to rukle out experimental artefacts that misguide the interpretation of the results.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this study Hammond et al. investigated the role of Dual-specificity Tyrosine Phosphorylation regulated Kinase 1A (DYRK1) in G1/S transition. By exploiting Dependency Map portal, they identified a previously unexplored protein FAM53C as potential regulator of G1/S transition. Using RNAi, they confirmed that depletion of FAM53C suppressed proliferation of human RPE1 cells and that this phenotype was dependent on the presence protein RB. In addition, they noted increased level of CDKN1A transcript and p21 protein that could explain G1 arrest of FAM53C-depleted cells but surprisingly, they did not observe activation of other p53 target genes. Proteomic analysis identified DYRK1 as one of the main interactors of FAM53C and the interaction was confirmed in vitro. Further, they showed that purified FAM53C blocked the ability of DYRK1 to phosphorylate cyclin D in vitro although the activity of DYRK1 was likely not inhibited (judging from the modification of FAM53C itself). Instead, it seems more likely that FAM53C competes with cyclin D in this assay. Authors claim that the G1 arrest caused by depletion of FAM53C was rescued by inhibition of DYRK1 but this was true only in cells lacking functional p53. This is quite confusing as DYRK1 inhibition reduced the fraction of G1 cells in p53 wild type cells as well as in p53 knock-outs, suggesting that FAM53C may not be required for regulation of DYRK1 function. Instead of focusing on the impact of FAM53C on cell cycle progression, authors moved towards investigating its potential (and perhaps more complex) roles in differentiation of IPSCs into cortical organoids and in mice. They observed a lower level of proliferating cells in the organoids but if that reflects an increased activity of DYRK1 or if it is just an off target effect of the genetic manipulation remains unclear. Even less clear is the phenotype in FAM53C knock-out mice. Authors did not observe any significant changes in survival nor in organ development but they noted some behavioral differences. Weather and how these are connected to the rate of cellular proliferation was not explored. In the summary, the study identified previously unknown role of FAM53C in proliferation but failed to explain the mechanism and its physiological relevance at the level of tissues and organism. Although some of the data might be of interest, in current form the data is too preliminary to justify publication.

Major points

1. Whole study is based on one siRNA to Fam53C and its specificity was not validated. Level of the knock down was shown only in the first figure and not in the other experiments. The observed phenotypes in the cell cycle progression may be affected by variable knock-down efficiency and/or potential off target effects.
2. Experiments focusing on the cell cycle progression were done in a single cell line RPE1 that showed a strong sensitivity to FAM53C depletion. In contrast, phenotypes in IPSCs and in mice were only mild suggesting that there might be large differences across various cell types in the expression and function of FAM53C. Therefore, it is important to reproduce the observations in other cell types.
3. Authors state that FAM53C is a direct inhibitor of DYRK1A kinase activity (Line 203), however this model is not supported by the data in Fig 4A. FAM53C seems to be a good substrate of DYRK1 even at high concentrations when phosphorylations of cyclin D is reduced. It rather suggests that DYRK1 is not inhibited by FAM53C but perhaps FAM53C competes with cyclin D. Further, authors should address if the phosphorylation of cyclin D is responsible for the observed cell cycle phenotype. Is this Cyclin D-Thr286 phosphorylation, or are there other sites involved?
4. At many places, information on statistical tests is missing and SDs are not shown in the plots. For instance, what statistics was used in Fig 4C? Impact of FAM53C on cyclin D phosphorylation does not seem to be significant. IN the same experiment, does DYRK1 inhibitor prevent modification of cyclin D?
5. Validation of SM13797 compound in terms of specificity to DYRK1 was not performed.
6. A fraction of cells in G1 is a very easy readout but it does not measure progression through the G1 phase. Extension of the S phase or G2 delay would indirectly also result in reduction of the G1 fraction. Instead, authors could measure the dynamics of entry to S phase in cells released from a G1 block or from mitotic shake off.

Other points

1. Fig. 2C, 2D, 2E graphs should begin with 0
2. Fig. 5D shows that the difference in p21 levels is not significant in FAM53C-KO cells but difference is mentioned in the text.
3. Fig. 6D comparison of datasets of extremely different sizes does not seem to be appropriate
4. Could there be alternative splicing in mice generating a partially functional protein without exon 4? Did authors confirm that the animal model does not express FAM53C?

Significance

Main problem of this study is that the advanced experimental models in IPSCs and mice did not confirm the observations in the cell lines and thus the whole manuscript does not hold together. Although I acknowledge the effort the authors invested in these experiments, the data do not contribute to the main conclusion of the paper that FAM53C/DYRK1 regulates G1/S transition.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Taylar Hammond and colleagues identified new regulators of the G1/S transition of the cell cycle. They did so by screening public available data from the Cancer Dependency Map, and identified FAM53C as a positive regulator of the G1/S transition. Using biochemical assays they then show that FAM53 interacts with the DYRK1A kinase to inhibit its function. DYRK1A in its is known to induce degradation of cyclin D, leading the authors to propose a model in which DYRK1A-dependent cyclin D degradation is inhibited by FAM53C to permit S-phase entry. Finally the authors assess the effect of FAM53C deletion in a cortical organoid model, and in Fam53c knockout mice. Whereas proliferation of the organoids is indeed inhibited, mice show virtually no phenotype.

Major comments:

The authors show convincing evidence that FAM53C loss can reduce S-phase entry in cell cultures, and that it can bind to DYRK1A. However, FAM53 has multiple other binding partners and I am not entirely convinced that negative regulation of DYRK1A is the predominant mechanism to explain its effects on S-phase entry. Some of the claims that are made based on the biochemical assays, and on the physiological effects of FAM53C are overstated. IN addition, some choices made methodology and data representation need further attention.

1. The authors do note that P21 levels increase upon FAM53C. They show convincing evidence that this is not a P53-dependent response. But the claim that " p21 upregulation alone cannot explain the G1 arrest in FAM53C-deficient cells (line 138-139) is misleading. A p53-independent p21 response could still be highly relevant. The authors could test if FAM53C knockdown inhibits proliferation after p21 knockdown or p21 deletion in RPE1 cells.
2. The authors do not convincingly show that FAM53C acts a DYRK1A inhibitor in cells. Figures 4B+C and S4B+C show extremely faint P-CycD1 bands, and tiny differences in ratios. The P values are hovering around the 0.05, so n=3 is clearly underpowered here. Total CycD1 levels also correlate with FAM53C levels, which seems to affect the ratios more than the tiny pCycD1 bands. Why is there still a pCycD1 band visible in 4B in the GFP + BTZ + DYRK1Ai condition? And if I look at the data points I honestly don't understand how the authors can conclude from S4C that knockdown of siFAM53C increases (DYRK1A dependent) increases in pCycD1 (relative to total CycD1). In figure 5C, no blot scans are even shown, and again the differences look tiny. So the authors should either find a way to make these assays more robust, or alter their claims appropriately.
3. The experiments to test if DYRK1A inhibition could rescue the G1 arrest observed upon FAM53C knockdown are not entirely convincing either. It would be much more convincing if they also perform cell counting experiments as they have done in Figures 1F and 1G, to complement the flow cytometry assays. I suggest that the authors do these cell counting experiments in RPE1 +/- P53 cells as well as HCT116 cells. In addition, did the authors test if P21 is induced by DYRK1Ai in HCT116 cells?
4. The data in Figure 5C and 5D are identical, although they are supposed to represent either pCycD1 ratios or p21 levels. This is a problem because at least one of the two cannot be true. Please provide the proper data and show (representative) images of both data types.
5. Line 246: "Fam53c knockout mice display developmental and behavioral defects." I don't agree with this claim. The mutant mice are born at almost the expected Mendelian ratios, the body weight development is not consistently altered. But more importantly, no differences in adult survival or microscopic pathology were seen. The authors put strong emphasis on the IMPC behavioral analysis, but they should be more cautious. The IMPC mouse cohorts are tested for many other phenotypes related to behavior and neurological symptoms and apparently none of these other traits were changed in the IMPC Famc53c-/- cohort. Thus, the decreased exploration in a new environment could very well be a chance finding. The authors need to take away claims about developmental and behavioral defects from the abstract, results and discussion sections; the data are just too weak to justify this.

Minor comments:

1. Can the authors provide a rationale for each of the proteins they chose to generate the list of the 38 proteins in the DepMap analysis? I looked at the list and it seems to me that they do not all have described functions in the G1/S transition. The analysis may thus be biased.
2. Figure 1B is confusing to me. Are these just some (arbitrarily) chosen examples? Consider leaving this heatmap out altogether, of explain in more detail.
3. The y-axes in Figures 2C, 2D, 2E, and 4D are misleading because they do not start at 0. Please let the axis start at 0, or make axis breaks.
4. Line 229: " Consequences ... brain development." This subheader is misleading, because the in vitro cortical organoid system is a rather simplistic model for brain development, and far away from physiological brain development. Please alter the header.
5. Figure S5F: the gating strategy is not clear to me. In particular, how do the authors know the difference between subG1 and G1 DAPI signals? Do they interpret the subG1 as apoptotic cells? If yes, why are there so many? Are the culturing or harvesting conditions of these organoids suboptimal? Perhaps the authors could consider doing IF stainings on EdU or BrdU on paraffin sections of organoids to obtain cleaner data?
6. Figure S6A; the labeling seems incorrect. I would think that red is heterozygous here, and grey mutant.

Significance

The finding that the poorly studied gene FAM53C controls the G1/S transition in cell lines is novel and interesting for the cell cycle field. However, the lack of phenotypes in Famc53-/- mice makes this finding less interesting for a broader audience. Furthermore, the mechanisms are incompletely dissected. The importance of a p53-indepent induction of p21 is not ruled out. And while the direct inhibitory interaction between FAM53C and DYRK1A is convincing (and also reported by others; PMID: 37802655), the authors do not (yet) convincingly show that DYRK1A inhibition can rescue a cell proliferation defect in FAM53C-deficient cells.

Altogether, this study can be of interest to basic researchers in the cell cycle field.

I am a cell biologist studying cell cycle fate decisions, and adaptation of cancer cells & stem cells to (drug-induced) stress. My technical expertise aligns well with the work presented throughout this paper, although I am not familiar with biolayer interferometry.

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Reply to the reviewers

Since we are at the stage of simply proposing a Revision Plan to an affiliate journal, there is not a revised version of the manuscript yet. But we honestly thank the three reviewers for their important input, which we are taken into consideration very seriously.

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Referee #3

Evidence, reproducibility and clarity

Major Comments:

It is interesting case study but the main problem with the study is the use of an unsuitable tardigrade model species. It was shown in the past that Hypsibius exemplaris is not a good model species to test tardigrade survival under extreme stress. Of course, results of Hypsibius exemplaris can be published but from the entire manuscript all general comments that tardigrades react in this or in different way need to be removed. This is characteristic only to Hypsibius exemplaris species which is a poor model for studies focused on environmental stressTo present general conclusions use few different tardigrade species or at least a correct tardigrade species with confirmed high resilience for different kind of stress like Milnesium, Ramazzottius, Paramacrobiotus or similar must be tested. Based on present study I can only propose to publish this manuscript as a case study for one poorly stress resistant eutardigrade species, without any general conclusions about other tardigrades. See: Poprawa, I., Bartylak, T., Kulpla, A., Erdmann, W., Roszkowska, M., Chajec, Ł., Kaczmarek, Ł., Karachitos, A. & Kmita, H. (2022) Verification of Hypsibius exemplaris Gąsiorek et al., 2018 (Eutardigrada; Hypsibiidae) application in anhydrobiosis research. PLoS ONE 17(3): e0261485.

Minor comments:

1. General comment to entire manuscript. Please do not start sentences with abbreviations, i.e. The DNA instead of DNA, Caenorhabditis instead of C. etc. In bibliography many doin numbers for publications are lacking, you have a different styles of citations, do not use capital letters for words inside the article title e.g. "Tardigrades as a Potential Model Organism in Space Research.", change it to "Tardigrades as a potential model organism in space research." Or use capital letters in all citations. Use italics for Latin names of the species and genera. On figures please try to put all of them like this that specimens ill be situated horizontally and in the middle of figure.
2. Introduction, Lines 80-96: I do not understand why this section is in Introduction. This is description of the results of the studies could be minimal and details could be moved to proper chapters.
3. Results: In this section are mixed results with methods. Please put all parts to the correct chapters.
4. Line 227 and 235: Based on what you interpreted: "fully-grown adults" and "juveniles" that they were adult and fully grown? Please explain in the text.
5. Line 315: You wrote "These findings demonstrate that even a transient exposure to zeocin causes irreversible DNA damage, leading to delayed mortality." but not to all specimens as you marked above.
6. Line 461-462: You wrote: "In this study, we probed why tardigrades-despite their impressive DNA repair capacity and extremotolerance-still succumb to genotoxic stress." But only one tardigrade species with poor resilience to stress conditions has been tested in this study. What if more repair mechanisms are activated in tardigrades when tardigrades leaving the state of anhydrobiosis? Authors tested only active animals and in such mechanisms maybe not activated or are activated on lower level. What is even more problematic, and what I marked this in one of the first comments, the species used in study is incorrect because is not very resilient to extreme conditions. This species is also a poor anhydrobiotic species with almost zero ability to anhydrobiosis (during which repair mechanisms are activated).
7. Line 609: "..actively searching for food.." - How you know that they were looking for food? What was a difference between normal crawling around and looking for food?
8. Line 635: "In sum, tardigrades illustrate that..." - Only in case of Hypsibius. This is not characteristic for tardigrades. See my previous comments. This conclusion is too strong without adequate proof.
9. Lines 666-667: "Adults measured {greater than or equal to}240 μm in length, while juveniles ranged between 120-180 μm." - Why such measurements? It was connected with something or is it arbitrary? Please explain.
10. Lines: 673-677: "For each timepoint, fertility was calculated by dividing the total number of eggs laid by the number of live animals at that time (using the last recorded number of live animals when all animals had died). In Fig. 5A-B, fertility is presented as the mean cumulative number of eggs laid per animal over time; in Fig. S9, it is shown as the mean number of eggs laid per animal at each timepoint." - This method of calculating fertility may be valid only if you know that all the females laid the same number of eggs. It is obvious that some females produced less and some others more eggs. Hence, fertility can not be accurately calculated in this way.

Significance

Studies described in the manuscript are very interesting for many potential readers, however manuscript need to be modified as case study for one tardigrades species without generalization of the results for all tardigrades. It is very important to not suggest that all tardigrades react in the same way especially that species used is not a good candidate for this type of studies (see my major comments).

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Referee #2

Evidence, reproducibility and clarity

Summary:

This manuscript studies the effects of genotoxic stress using zeocin, a bleomycin-family drug, in the tardigrade species H. exemplaris. In a first experimental set, the authors evaluate the survival of the organisms as well as the levels of DNA damage.

A RT-qPCR analysis of a set of DNA repair genes identified in a previous study by another group (Clark-Hachtel, Courtney M. et al.; Curr Biol, Vol. 34, Issue 9, 1819-1830.e6) and a comet assay reveal the damage observed during treatment.

Experiments on fasting animals show variations in animal size that overlap with those seen in groups of animals treated with the genotoxic drug. Physiological variations are also observed, such as lipid loss and cuticle alteration.

In a subsequent experimental set, the authors indicate that the genotoxic drug blocks DNA replication and activates DNA repair systems in various tissues, particularly the digestive tissue, which appears to be specifically targeted in terms of its replicative capacity following DNA damage caused by the drug. A sensitivity study of tardigrade embryo development then shows that their proliferative capacity, which is highly dependent on replication, mobilizes different sets of DNA repair genes that may be more closely associated with replication than in adults.

Finally, a comparative study of the development of two organisms (C. elegans and planarian) also shows sensitivity to drugs that disrupt the replication process during development.

The authors conclude from all of this work that the cells of the animals' intestines are the main target of the genotoxic stress induced by the drug. The effects of disruption of the normal replication process in intestinal cells are thought to be the cause of the observed loss of tissue homeostasis (loss of lipids and tissue renewal capacity).

Major comments:

1. Zeocin is a drug derived from bleomycin but has not yet been extensively studied. Could you give examples of the use/validation of zeocin as a radiomimetic in other biological systems?

2. Similarities in transcriptional responses between UV and dehydration genotoxic stresses have already been observed (Yoshida et al., 2022; BMC Genomics 23, 405) in a tardigrade species closely related to H. exemplaris (R. varieornatus). However, no correlation in transcriptional responses could be observed after treating H. exemplaris with genotoxic stresses such as desiccation and 500 Gy gamma ray irradiation (Clark-Hachtel, Courtney M. et al.; Curr Biol, Vol 34, Issue 9, 1819 - 1830.e6). These results indicate that, depending on the type of genotoxic stress, transcriptomic responses can appear to be very different and sometimes uncorrelated, particularly in the species H. exemplaris. Bleomycin has been studied in previous reports (refs Yoshida Y, et al. Proc Jpn Acad Ser B Phys Biol Sci. 2024 100(7):414-428; Clark-Hachtel, Courtney M. et al.; Curr Biol, Vol 34, Issue 9, 1819 - 1830.e6; Marwan Anoud et al., 2024, eLife 13:RP92621), which used a transcriptomic study to confirm that it behaves as a radiomimetic for the species H. exemplaris.

On the other hand, since zeocin is a bleomycin-family drug, it is possible that its effects may differ slightly from those of bleomycin, exhibiting specific effects as observed by comparison of chemical radiomimetic and radiation treatments.

A control experiment comparing the effects of bleomycin and zeocin using RNAseq would validate that their use is equivalent.

1. A major conclusion of the manuscript is that DNA damage induced by the genotoxic drug disrupts replication mechanisms and leads to the observed effects. Are RT-qPCR analyses on a subset of drug-induced repair genes induced solely by the drug itself or by its indirect effect on replication?

It would be interesting to block replication in embryos and assess whether the same sets of DNA repair genes are induced when compared with treatment with zeocin only. Additionally, it will be interesting to redo the same DNA replication block experiments with additional treatment to compare the induced sets of DNA reparation genes. This will help to understand the true effect that will be directly imputable to zeocin.

Minor comments:

The data are well presented, and the experiments are well described for general understanding. Previous studies in this field have been well referenced. However, the link between DNA damage caused by the drug and its impact on replication needs to be better explained.

Finally, the use of the drug zeocin should be validated in this system by comparison with bleomycin.

Significance

This study evaluates the resistance of a species of tardigrades to genotoxic stress. Several previous studies have conducted this type of experiment using the same species with consistent results and using the same type of genotoxic chemical drug : bleomycin. In this study, a new genotoxic drug is evaluated for its effects on DNA damage as well as on the survival of organisms and their embryonic development. Definitive validation experiments of this new genotoxic chemical tool are necessary to determine its similarities with drugs already known for their effects in the literature.

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Referee #1

Evidence, reproducibility and clarity

This manuscript concerns tardigrade sensitivity to genotoxic stress. Using the radiomimetic drug Zeocin to induce DNA breaks, authors show that continuous exposure progressively kills tardigrades, accompanied by striking body shrinkage and lipid depletion. Authors show that germ cells and embryos, with their high proliferation rates, show heightened sensitivity. To resume, their findings pinpoint DNA replication as an Achilles' heel of organismal survival under genotoxic stress.

Major comments:

The claims and conclusions in this article are not sufficiently supported by the data. They require additional experiments or analyses.

The fundamental problem with this paper is the use of a single molecule, Zeocin, as a radiomimetic. It is absolutely essential to compare the results obtained with radiation. In the bibliography, researchers compare a drug with radiation. Bob Goldstein, for example, in his 2024 Current Biology paper uses radiation and bleomycin. The same is true for Concordet in his 2024 elife paper. Zeocin has been used very little on tardigrades. It cannot be used alone to draw conclusions from this study.

Additionally, at the beginning of the paper, the authors tested different concentrations of Zeocin. They showed results at two concentrations : 100ug/ml and 1mg/ml. In the remainder of the paper, only the latter concentration is used. This is not sufficient. The analyses should have been conducted in parallel on several concentrations in order to compare and analyze a potential dose-dependent effect.

Finally, the authors focused on two types of cells that have the particularity of replicating themselves: gut cells and storage cells. It would have been necessary to work on other cell types to compare the results.

The realization of these additional experiences are completely realistic.

The data and methods are presented in a reproducible manner. But experiments sometimes lack independent replicates and need to be reproduced.

The legend to Figure 1, for example, indicates that the experiment was conducted with 3 to 7 biological replicates and 60 to 120 animals. These are still very different numbers. And this can lead to significant bias.

For the other figures, no biological replicates were indicated and the numbers « n » are sometimes very different, as in Figure 4 with n=107 and n=166. A little more homogenization allows for better robustness of the results. And biological replicates are essential.

Sometimes there are some unclear elements in the figures. In Figure 3, if I understand correctly, A and B show the gut cells (adult) and C and D the storage cells (juvenile). The size difference is not very clear in this image. How old is the juvenile compared to this adult?

Significance

This study, if confirmed by additional experiments that are absolutely essential to validate these conclusions, will be interesting for the community of researchers working on tardigrades, even if the effects of genotoxic stress on tardigrades are already widely studied.

This study is relatively complete on only one molecule, Zeocin, at a concentration of 1 mg/ml. To be relevant, another genotoxic stress should be included in the study. And the study should also be conducted at the concentration of 100 ug/ml, which did show effects but was abandoned for the rest of the study. Similarly, only storage cells and gut cells were studied given their replication capacity. Other cell types should have been included in the study for comparison.

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Reply to the reviewers

We would like to thank all the reviewers for their valuable comments and criticisms. We have thoroughly revised the manuscript and the resource to address all the points raised by the reviewers. Below, we provide a point-by-point response for the sake of clarity.

Reviewer #1

__Evidence, reproducibility and clarity __

Summary: This manuscript, "MAVISp: A Modular Structure-Based Framework for Protein Variant Effects," presents a significant new resource for the scientific community, particularly in the interpretation and characterization of genomic variants. The authors have developed a comprehensive and modular computational framework that integrates various structural and biophysical analyses, alongside existing pathogenicity predictors, to provide crucial mechanistic insights into how variants affect protein structure and function. Importantly, MAVISp is open-source and designed to be extensible, facilitating reuse and adaptation by the broader community.

Major comments: - While the manuscript is formally well-structured (with clear Introduction, Results, Conclusions, and Methods sections), I found it challenging to follow in some parts. In particular, the Introduction is relatively short and lacks a deeper discussion of the state-of-the-art in protein variant effect prediction. Several methods are cited but not sufficiently described, as if prior knowledge were assumed. OPTIONAL: Extend the Introduction to better contextualize existing approaches (e.g., AlphaMissense, EVE, ESM-based predictors) and clarify what MAVISp adds compared to each.

We have expanded the introduction on the state-of-the-art of protein variant effects predictors, explaining how MAVISp departs from them.

- The workflow is summarized in Figure 1(b), which is visually informative. However, the narrative description of the pipeline is somewhat fragmented. It would be helpful to describe in more detail the available modules in MAVISp, and which of them are used in the examples provided. Since different use cases highlight different aspects of the pipeline, it would be useful to emphasize what is done step-by-step in each.

We have added a concise, narrative description of the data flow for MAVISp, as well as improved the description of modules in the main text. We will integrate the results section with a more comprehensive description of the available modules, and then clarify in the case studies which modules were applied to achieve specific results.

OPTIONAL: Consider adding a table or a supplementary figure mapping each use case to the corresponding pipeline steps and modules used.

We have added a supplementary table (Table S2) to guide the reader on the modules and workflows applied for each case study

We also added Table S1 to map the toolkit used by MAVISp to collect the data that are imported and aggregated in the webserver for further guidance.

- The text contains numerous acronyms, some of which are not defined upon first use or are only mentioned in passing. This affects readability. OPTIONAL: Define acronyms upon first appearance, and consider moving less critical technical details (e.g., database names or data formats) to the Methods or Supplementary Information. This would greatly enhance readability.

We revised the usage of acronyms following the reviewer’s directions of defying them at first appearance.

• The code and trained models are publicly available, which is excellent. The modular design and use of widely adopted frameworks (PyTorch and PyTorch Geometric) are also strong points. However, the Methods section could benefit from additional detail regarding feature extraction and preprocessing steps, especially the structural features derived from AlphaFold2 models. OPTIONAL: Include a schematic or a table summarizing all feature types, their dimensionality, and how they are computed.

We thank the reviewer for noticing and praising the availability of the tools of MAVISp. Our MAVISp framework utilizes methods and scores that incorporate machine learning features (such as EVE or RaSP), but does not employ machine learning itself. Specifically, we do not use PyTorch and do not utilize features in a machine learning sense. We do extract some information from the AlphaFold2 models that we use (such as the pLDDT score and their secondary structure content, as calculated by DSSP), and those are available in the MAVISp aggregated csv files for each protein entry and detailed in the Documentation section of the MAVISp website.

• The section on transcription factors is relatively underdeveloped compared to other use cases and lacks sufficient depth or demonstration of its practical utility. OPTIONAL: Consider either expanding this section with additional validation or removing/postponing it to a future manuscript, as it currently seems preliminary.

We have removed this section and included a mention in the conclusions as part of the future directions.

Minor comments: - Most relevant recent works are cited, including EVE, ESM-1v, and AlphaFold-based predictors. However, recent methods like AlphaMissense (Cheng et al., 2023) could be discussed more thoroughly in the comparison.

We have revised the introduction to accommodate the proper space for this comparison.

• Figures are generally clear, though some (e.g., performance barplots) are quite dense. Consider enlarging font sizes and annotating key results directly on the plots.

We have revised Figure 2 and presented only one case study to simplify its readability. We have also changed Figure 3, whereas retained the other previous figures since they seemed less problematic.

• Minor typographic errors are present. A careful proofreading is highly recommended. Below are some of the issues I identified: Page 3, line 46: "MAVISp perform" -> "MAVISp performs" Page 3, line 56: "automatically as embedded" -> "automatically embedded" Page 3, line 57: "along with to enhance" -> unclear; please revise Page 4, line 96: "web app interfaces with the database and present" -> "presents" Page 6, line 210: "to investigate wheatear" -> "whether" Page 6, lines 215-216: "We have in queue for processing with MAVISp proteins from datasets relevant to the benchmark of the PTM module." -> unclear sentence; please clarify Page 15, line 446: "Both the approaches" -> "Both approaches" Page 20, line 704: "advantage of multi-core system" -> "multi-core systems"

We have done a proofreading of the entire article, including the points above

Significance

General assessment: the strongest aspects of the study are the modularity, open-source implementation, and the integration of structural information through graph neural networks. MAVISp appears to be one of the few publicly available frameworks that can easily incorporate AlphaFold2-based features in a flexible way, lowering the barrier for developing custom predictors. Its reproducibility and transparency make it a valuable resource. However, while the technical foundation is solid and the effort substantial, the scientific narrative and presentation could be significantly improved. The manuscript is dense and hard to follow in places, with a heavy use of acronyms and insufficient explanation of key design choices. Improving the descriptive clarity, especially in the early sections, would greatly enhance the impact of this work.

Advance

to the best of my knowledge, this is one of the first modular platforms for protein variant effect prediction that integrates structural data from AlphaFold2 with bioinformatic annotations and even clinical data in an extensible fashion. While similar efforts exist (e.g., ESMfold, AlphaMissense), MAVISp distinguishes itself through openness and design for reusability. The novelty is primarily technical and practical rather than conceptual.

Audience

this study will be of strong interest to researchers in computational biology, structural bioinformatics, and genomics, particularly those developing variant effect predictors or analyzing the impact of mutations in clinical or functional genomics contexts. The audience is primarily specialized, but the open-source nature of the tool may diffuse its use among more applied or translational users, including those working in precision medicine or protein engineering.

Reviewer expertise: my expertise is in computational structural biology, molecular modeling, and (rather weak) machine learning applications in bioinformatics. I am familiar with graph-based representations of proteins, AlphaFold2, and variant effects based on Molecular Dynamics simulations. I do not have any direct expertise in clinical variant annotation pipelines.

Reviewer #2

__Evidence, reproducibility and clarity __

Summary: The authors present a pipeline and platform, MAVISp, for aggregating, displaying and analysis of variant effects with a focus on reclassification of variants of uncertain clinical significance and uncovering the molecular mechanisms underlying the mutations.

Major comments: - On testing the platform, I was unable to look-up a specific variant in ADCK1 (rs200211943, R115Q). I found that despite stating that the mapped refseq ID was NP_001136017 in the HGVSp column, it was actually mapped to the canonical UniProt sequence (Q86TW2-1). NP_001136017 actually maps to Q86TW2-3, which is missing residues 74-148 compared to the -1 isoform. The Uniprot canonical sequence has no exact RefSeq mapping, so the HGVSp column is incorrect in this instance. This mapping issue may also affect other proteins and result in incorrect HGVSp identifiers for variants.

We would like to thank the reviewer for pointing out these inconsistencies. We have revised all the entries and corrected them. If needed, the history of the cases that have been corrected can be found in the closed issues of the GitHub repository that we use for communication between biocurators and data managers (https://github.com/ELELAB/mavisp_data_collection). We have also revised the protocol we follow in this regard and the MAVISp toolkit to include better support for isoform matching in our pipelines for future entries, as well as for the revision/monitoring of existing ones, as detailed in the Method Section. In particular, we introduced a tool, uniprot2refseq, which aids the biocurator in identifying the correct match in terms of sequence length and sequence identity between RefSeq and UniProt. More details are included in the Method Section of the paper. The two relevant scripts for this step are available at: https://github.com/ELELAB/mavisp_accessory_tools/

- The paper lacks a section on how to properly interpret the results of the MAVISp platform (the case-studies are helpful, but don't lay down any global rules for interpreting the results). For example: How should a variant with conflicts between the variant impact predictors be interpreted? Are specific indicators considered more 'reliable' than others?

We have added a section in Results to clarify how to interpret results from MAVISp in the most common use cases.

• In the Methods section, GEMME is stated as being rank-normalised with 0.5 as a threshold for damaging variants. On checking the data downloaded from the site, GEMME was not rank-normalised but rather min-max normalised. Furthermore, Supplementary text S4 conflicts with the methods section over how GEMME scores are classified, S4 states that a raw-value threshold of -3 is used.

We thank the reviewer for spotting this inconsistency. This part in the main text was left over from a previous and preliminary version of the pre-print, we have revised the main text. Supplementary Text S4 includes the correct reference for the value in light of the benchmarking therewithin.

• Note. This is a major comment as one of the claims is that the associated web-tool is user-friendly. While functional, the web app is very awkward to use for analysis on any more than a few variants at once. The fixed window size of the protein table necessitates excessive scrolling to reach your protein-of-interest. This will also get worse as more proteins are added. Suggestion: add a search/filter bar. The same applies to the dataset window.

We have changed the structure of the webserver in such a way that now the whole website opens as its own separate window, instead of being confined within the size permitted by the website at DTU. This solves the fixed window size issue. Hopefully, this will improve the user experience.

We have refactored the web app by adding filtering functionality, both for the main protein table (that can now be filtered by UniProt AC, gene name or RefSeq ID) and the mutations table. Doing this required a general overhaul of the table infrastructure (we changed the underlying engine that renders the tables).

• You are unable to copy anything out of the tables.
• Hyperlinks in the tables only seem to work if you open them in a new tab or window.

The table overhauls fixed both of these issues

• All entries in the reference column point to the MAVISp preprint even when data from other sources is displayed (e.g. MAVE studies).

We clarified the meaning of the reference column in the Documentation on the MAVISp website, as we realized it had confused the reviewer. The reference column is meant to cite the papers where the computationally-generated MAVISp data are used, not external sources. Since we also have the experimental data module in the most recent release, we have also refactored the MAVISp website by adding a “Datasets and metadata” page, which details metadata for key modules. These include references to data from external sources that we include in MAVISp on a case-by-case basis (for example the results of a MAVE experiment). Additionally, we have verified that the papers using MAVISp data are updated in https://elelab.gitbook.io/mavisp/overview/publications-that-used-mavisp-data and in the csv file of the interested proteins.

Here below the current references that have been included in terms of publications using MAVISp data:

SMPD1

ASM variants in the spotlight: A structure-based atlas for unraveling pathogenic mechanisms in lysosomal acid sphingomyelinase

Biochim Biophys Acta Mol Basis Dis

38782304

https://doi.org/10.1016/j.bbadis.2024.167260

TRAP1

Point mutations of the mitochondrial chaperone TRAP1 affect its functions and pro-neoplastic activity

Cell Death & Disease

40074754

https://doi.org/10.1038/s41419-025-07467-6

BRCA2

Saturation genome editing-based clinical classification of BRCA2 variants

Nature

39779848

0.1038/s41586-024-08349-1

TP53, GRIN2A, CBFB, CALR, EGFR

TRAP1 S-nitrosylation as a model of population-shift mechanism to study the effects of nitric oxide on redox-sensitive oncoproteins

Cell Death & Disease

37085483

10.1038/s41419-023-05780-6

KIF5A, CFAP410, PILRA, CYP2R1

Computational analysis of five neurodegenerative diseases reveals shared and specific genetic loci

Computational and Structural Biotechnology Journal

38022694

https://doi.org/10.1016/j.csbj.2023.10.031

KRAS

Combining evolution and protein language models for an interpretable cancer driver mutation prediction with D2Deep

Brief Bioinform

39708841

https://doi.org/10.1093/bib/bbae664

OPTN

Decoding phospho-regulation and flanking regions in autophagy-associated short linear motifs

Communications Biology

40835742

10.1038/s42003-025-08399-9

DLG4,GRB2,SMPD1

Deciphering long-range effects of mutations: an integrated approach using elastic network models and protein structure networks

JMB

40738203

doi: 10.1016/j.jmb.2025.169359

Entering multiple mutants in the "mutations to be displayed" window is time-consuming for more than a handful of mutants. Suggestion: Add a box where multiple mutants can be pasted in at once from an external document.

During the table overhaul, we have revised the user interface to add a text box that allows free copy-pasting of mutation lists. While we understand having a single input box would have been ideal, the former selection interface (which is also still available) doesn’t allow copy-paste. This is a known limitation in Streamlit.

Minor comments

• Grammar. I appreciate that this manuscript may have been compiled by a non-native English speaker, but I would be remiss not to point out that there are numerous grammar errors throughout, usually sentence order issues or non-pluralisation. The meaning of the authors is mostly clear, but I recommend very thoroughly proof-reading the final version.

We have done proofreading on the final version of the manuscript

• There are numerous proteins that I know have high-quality MAVE datasets that are absent in the database e.g. BRCA1, HRAS and PPARG.

Yes, we are aware of this. It is far from trivial to properly import the datasets from multiplex assays. They often need to be treated on a case-by-case basis. We are in the process of carefully compiling locally all the MAVE data before releasing it within the public version of the database, so this is why they are missing. We are giving priorities to the ones that can be correlated with our predictions on changes in structural stability and then we will also cover the rest of the datasets handling them in batches. Having said this, we have checked the dataset for BRCA1, HRAS, and PPARG. We have imported the ones for PPARG and BRCA1 from ProtGym, referring to the studies published in 10.1038/ng.3700 and 10.1038/s41586-018-0461-z, respectively. Whereas for HRAS, checking in details both the available data and literature, while we did identify a suitable dataset (10.7554/eLife.27810), we struggled to understand what a sensible cut-off for discriminating between pathogenic and non-pathogenic variants would be, and so ended up not including it in the MAVISp dataset for now. We will contact the authors to clarify which thresholds to apply before importing the data.

• Checking one of the existing MAVE datasets (KRAS), I found that the variants were annotated as damaging, neutral or given a positive score (these appear to stand-in for gain-of-function variants). For better correspondence with the other columns, those with positive scores could be labelled as 'ambiguous' or 'uncertain'.

In the KRAS case study presented in MAVISP, we utilized the protein abundance dataset reported in (http://dx.doi.org/10.1038/s41586-023-06954-0) and made available in the ProteinGym repository (specifically referenced at https://github.com/OATML-Markslab/ProteinGym/blob/main/reference_files/DMS_substitutions.csv#L153). We adopted the precalculated thresholds as provided by the ProteinGym authors. In this regard, we are not really sure the reviewer is referring to this dataset or another one on KRAS.

• Numerous thresholds are defined for stabilizing / destabilizing / neutral variants in both the STABILITY and the LOCAL_INTERACTION modules. How were these thresholds determined? I note that (PMC9795540) uses a ΔΔG threshold of 1/-1 for defining stabilizing and destabilizing variants, which is relatively standard (though they also say that 2-3 would likely be better for pinpointing pathogenic variants).

We improved the description of our classification strategies for both modules in the Documentation page of our website. Also, we explained more clearly the possible sources of ‘uncertain’ annotations for the two modules in both the web app (Documentation page) and main text. Briefly, in the STABILITY module, we consider FoldX and either Rosetta or RaSP to achieve a final classification. We first classify one and the other independently, according to the following strategy:

If DDG ≥ 3, the mutation is Destabilizing If DDG ≤ −3, the mutation is Stabilizing If −2 We then compare the classifications obtained by the two methods: if they agree, then that is the final classification, if they disagree, then the final classification is Uncertain. The thresholds were selected based on a previous study, in which variants with changes in stability below 3 kcal/mol were not featuring a markedly different abundance at cellular level [10.1371/journal.pgen.1006739, 10.7554/eLife.49138]

Regarding the LOCAL_INTERACTION module, it works similarly as for the Stability module, in that Rosetta and FoldX are considered independently, and an implicit classification is performed for each, according to the rules (values in kcal/mol)

If DDG > 1, the mutation is Destabilizing. If DDG Each mutation is therefore classified for both methods. If the methods agree (i.e., if they classify the mutation in the same way), their consensus is the final classification for the mutation; if they do not agree, the final classification will be Uncertain.

If a mutation does not have an associated free energy value, the relative solvent accessible area is used to classify it: if SAS > 20%, the mutation is classified as Uncertain, otherwise it is not classified.

Thresholds here were selected according to best practices followed by the tool authors and more in general in the literature, as the reviewer also noticed.

• "Overall, with the examples in this section, we illustrate different applications of the MAVISp results, spanning from benchmarking purposes, using the experimental data to link predicted functional effects with structural mechanisms or using experimental data to validate the predictions from the MAVISp modules."

The last of these points is not an application of MAVISp, but rather a way in which external data can help validate MAVISp results. Furthermore, none of the examples given demonstrate an application in benchmarking (what is being benchmarked?).

We have revised the statements to avoid this confusion in the reader.

• Transcription factors section. This section describes an intended future expansion to MAVISp, not a current feature, and presents no results. As such, it should be moved to the conclusions/future directions section.

We have removed this section and included a mention in the conclusions as part of the future directions.

• Figures. The dot-plots generated by the web app, and in Figures 4, 5 and 6 have 2 legends. After looking at a few, it is clear that the lower legend refers to the colour of the variant on the X-axis - most likely referencing the ClinVar effect category. This is not, however, made clear either on the figures or in the app.

The reviewer’s interpretation on the second legend is correct - it does refer to the ClinVar classification. Nonetheless, we understand the positioning of the legend makes understanding what the legend refers to not obvious. We also revised the captions of the figures in the main text. On the web app, we have changed the location of the figure legend for the ClinVar effect category and added a label to make it clear what the classification refers to.

• "We identified ten variants reported in ClinVar as VUS (E102K, H86D, T29I, V91I, P2R, L44P, L44F, D56G, R11L, and E25Q, Fig.5a)" E25Q is benign in ClinVar and has had that status since first submitted.

We have corrected this in the text and the statements related to it.

Significance

Platforms that aggregate predictors of variant effect are not a new concept, for example dbNSFP is a database of SNV predictions from variant effect predictors and conservation predictors over the whole human proteome. Predictors such as CADD and PolyPhen-2 will often provide a summary of other predictions (their features) when using their platforms. MAVISp's unique angle on the problem is in the inclusion of diverse predictors from each of its different moules, giving a much wider perspective on variants and potentially allowing the user to identify the mechanistic cause of pathogenicity. The visualisation aspect of the web app is also a useful addition, although the user interface is somewhat awkward. Potentially the most valuable aspect of this study is the associated gitbook resource containing reports from biocurators for proteins that link relevant literature and analyse ClinVar variants. Unfortunately, these are only currently available for a small minority of the total proteins in the database with such reports. For improvement, I think that the paper should focus more on the precise utility of the web app / gitbook reports and how to interpret the results rather than going into detail about the underlying pipeline.

We appreciate the interest in the gitbook resource that we also see as very valuable and one of the strengths of our work. We have now implemented a new strategy based on a Python script introduced in the mavisp toolkit to generate a template Markdown file of the report that can be further customized and imported into GitBook directly (​​https://github.com/ELELAB/mavisp_accessory_tools/). This should allow us to streamline the production of more reports. We are currently assigning proteins in batches for reporting to biocurator through the mavisp_data_collection GitHub to expand their coverage. Also, we revised the text and added a section on the interpretation of results from MAVISp. with a focus on the utility of the web-app and reports.

In terms of audience, the fast look-up and visualisation aspects of the web-platform are likely to be of interest to clinicians in the interpretation of variants of unknown clinical significance. The ability to download the fully processed dataset on a per-protein database would be of more interest to researchers focusing on specific proteins or those taking a broader view over multiple proteins (although a facility to download the whole database would be more useful for this final group).

While our website only displays the dataset per protein, the whole dataset, including all the MAVISp entries, is available at our OSF repository (https://osf.io/ufpzm/), which is cited in the paper and linked on the MAVISp website. We have further modified the MAVISp database to add a link to the repository in the modes page, so that it is more visible.

My expertise. - I am a protein bioinformatician with a background in variant effect prediction and large-scale data analysis.

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

Evidence, reproducibility and clarity:

Summary:

The authors present MAVISp, a tool for viewing protein variants heavily based on protein structure information. The authors have done a very impressive amount of curation on various protein targets, and should be commended for their efforts. The tool includes a diverse array of experimental, clinical, and computational data sources that provides value to potential users interested in a given target.

Major comments:

Unfortunately I was not able to get the website to work correctly. When selecting a protein target in simple mode, I was greeted with a completely blank page in the app window. In ensemble mode, there was no transition away from the list of targets at all. I'm using Firefox 140.0.2 (64-bit) on Ubuntu 22.04. I would like to explore the data myself and provide feedback on the user experience and utility.

We have tried reproducing the issue mentioned by the reviewer, using the exact same Ubuntu and Firefox versions, but unfortunately failed to produce it. The website worked fine for us under such an environment. The issue experienced by the reviewer may have been due to either a temporary issue with the web server or a problem with the specific browser environment they were working in, which we are unable to reproduce. It would be useful to know the date that this happened to verify if it was a downtime on the DTU IT services side that made the webserver inaccessible.

I have some serious concerns about the sustainability of the project and think that additional clarifications in the text could help. Currently is there a way to easily update a dataset to add, remove, or update a component (for example, if a new predictor is published, an error is found in a predictor dataset, or a predictor is updated)? If it requires a new round of manual curation for each protein to do this, I am worried that this will not scale and will leave the project with many out of date entries. The diversity of software tools (e.g., three different pipeline frameworks) also seems quite challenging to maintain.

We appreciate the reviewer’s concerns about long-term sustainability. It is a fair point that we consider within our steering group, who oversee and plans the activities and meet monthly. Adding entries to MAVISp is moving more and more towards automation as we grow. We aim to minimize the manual work where applicable. Still, an expert-based intervention is really needed in some of the steps, and we do not want to renounce it. We intend to keep working on MAVISp to make the process of adding and updating entries as automated as possible, and to streamline the process when manual intervention is necessary. From the point of view of the biocurators, they have three core workflows to use for the default modules, which also automatically cover the source of annotations. We are currently working to streamline the procedures behind LOCAL_INTERACTION, which is the most challenging one. On the data manager and maintainers' side, we have workflows and protocols that help us in terms of automation, quality control, etc, and we keep working to improve them. Among these, we have workflows to use for the old entries updates. As an example, the update of erroneously attributed RefSeq data (pointed out by reviewer 2) took us only one week overall (from assigning revisions and importing to the database) because we have a reduced version of Snakemake for automation that can act on only the affected modules. Also, another point is that we have streamlined the generation of the templates for the gitbook reports (see also answer to reviewer 2).

The update of old entries is planned and made regularly. We also deposit the old datasets on OSF for transparency, in case someone needs to navigate and explore the changes. We have activities planned between May and August every year to update the old entries in relation to changes of protocols in the modules, updates in the core databases that we interact with (COSMIC, Clinvar etc). In case of major changes, the activities for updates continue in the Fall. Other revisions can happen outside these time windows if an entry is needed or a specific research project and needs updates too.

Furthermore, the community of people contributing to MAVISp as biocurators or developers is growing and we have scientists contributing from other groups in relation to their research interest. We envision that for this resource to scale up, our team cannot be the only one producing data and depositing it to the database. To facilitate this we launched a pilot for a training event online (see Event page on the website) and we will repeat it once per year. We also organize regular meetings with all the active curators and developers to plan the activities in a sustainable manner and address the challenges we encounter.

As stated in the manuscript, currently with the team of people involved, automatization and resources that we have gathered around this initiative we can provide updates to the public database every third month and we have been regularly satisfied with them. Additionally, we are capable of processing from 20 to 40 proteins every month depending also on the needs of revision or expansion of analyses on existing proteins. We also depend on these data for our own research projects and we are fully committed to it.

Additionally, we are planning future activities in these directions to improve scale up and sustainability:

• Streamlining manual steps so that they are as convenient as fast as possible for our curators, e.g. by providing custom pages on the MAVISp website
• Streamline and automatize the generation of useful output, for instance the reports, by using a combination of simple automation and large language models
• Implement ways to share our software and scripts with third parties, for instance by providing ready made (or close to) containers or virtual machines
• For a future version 2 if the database grows in a direction that is not compatible with Streamlit, the web data science framework we are currently using, we will rewrite the website using a framework that would allow better flexibility and performance, for instance using Django and a proper database backend. On the same theme, according to the GitHub repository, the program relies on Python 3.9, which reaches end of life in October 2025. It has been tested against Ubuntu 18.04, which left standard support in May 2023. The authors should update the software to more modern versions of Python to promote the long-term health and maintainability of the project.

We thank the reviewer for this comment - we are aware of the upcoming EOL of Python 3.9. We tested MAVISp, both software package and web server, using Python 3.10 (which is the minimum supported version going forward) and Python 3.13 (which is the latest stable release at the time of writing) and updated the instructions in the README file on the MAVISp GitHub repository accordingly.

We plan on keeping track of Python and library versions during our testing and updating them when necessary. In the future, we also plan to deploy Continuous Integration with automated testing for our repository, making this process easier and more standardized.

I appreciate that the authors have made their code and data available. These artifacts should also be versioned and archived in a service like Zenodo, so that researchers who rely on or want to refer to specific versions can do so in their own future publications.

Since 2024, we have been reporting all previous versions of the dataset on OSF, the repository linked to the MAVISp website, at https://osf.io/ufpzm/files/osfstorage (folder: previous_releases). We prefer to keep everything under OSF, as we also use it to deposit, for example, the MD trajectory data.

Additionally, in this GitHub page that we use as a space to interact between biocurators, developers, and data managers within the MAVISp community, we also report all the changes in the NEWS space: https://github.com/ELELAB/mavisp_data_collection

Finally, the individual tools are all available in our GitHub repository, where version control is in place (see Table S1, where we now mapped all the resources used in the framework)

In the introduction of the paper, the authors conflate the clinical challenges of variant classification with evidence generation and it's quite muddled together. They should strongly consider splitting the first paragraph into two paragraphs - one about challenges in variant classification/clinical genetics/precision oncology and another about variant effect prediction and experimental methods. The authors should also note that they are many predictors other than AlphaMissense, and may want to cite the ClinGen recommendations (PMID: 36413997) in the intro instead.

We revised the introduction in light of these suggestions. We have split the paragraph as recommended and added a longer second paragraph about VEPs and using structural data in the context of VEPs. We have also added the citation that the reviewer kindly recommended.

Also in the introduction on lines 21-22 the authors assert that "a mechanistic understanding of variant effects is essential knowledge" for a variety of clinical outcomes. While this is nice, it is clearly not the case as we can classify variants according to the ACMG/AMP guidelines without any notion of specific mechanism (for example, by combining population frequency data, in silico predictor data, and functional assay data). The authors should revise the statement so that it's clear that mechanistic understanding is a worthy aspiration rather than a prerequisite.

We revised the statement in light of this comment from the reviewer

In the structural analysis section (page 5, lines 154-155 and elsewhere), the authors define cutoffs with convenient round numbers. Is there a citation for these values or were these arbitrarily chosen by the authors? I would have liked to see some justification that these assignments are reasonable. Also there seems to be an error in the text where values between -2 and -3 kcal/mol are not assigned to a bin (I assume they should also be uncertain). There are other similar seemingly-arbitrary cutoffs later in the section that should also be explained.

We have revised the text making the two intervals explicit, for better clarity.

On page 9, lines 294-298 the authors talk about using the PTEN data from ProteinGym, rather than the actual cutoffs from the paper. They get to the latter later on, but I'm not sure why this isn't first? The ProteinGym cutoffs are somewhat arbitrarily based on the median rather than expert evaluation of the dataset, and I'm not sure why it's even worth mentioning them when proper classifications are available. Regarding PTEN, it would be quite interesting to see a comparison of the VAMP-seq PTEN data and the Mighell phosphatase assay, which is cited on page 9 line 288 but is not actually a VAMP-seq dataset. I think this section could be interesting but it requires some additional attention.

We have included the data from Mighell’s phosphatase assay as provided by MAVEdb in the MAVISp database, within the experimental_data module for PTEN, and we have revised the case study, including them and explaining better the decision of supporting both the ProteinGym and MAVEdb classification in MAVISp (when available). See revised Figure3, Table 1 and corresponding text.

The authors mention "pathogenicity predictors" and otherwise use pathogenicity incorrectly throughout the manuscript. Pathogenicity is a classification for a variant after it has been curated according to a framework like the ACMG/AMP guidelines (Richards 2015 and amendments). A single tool cannot predict or assign pathogenicity - the AlphaMissense paper was wrong to use this nomenclature and these authors should not compound this mistake. These predictors should be referred to as "variant effect predictors" or similar, and they are able to produce evidence towards pathogenicity or benignity but not make pathogenicity calls themselves. For example, in Figure 4e, the terms "pathogenic" and "benign" should only be used here if these are the classifications the authors have derived from ClinVar or a similar source of clinically classified variants.

The reviewer is correct, we have revised the terminology we used in the manuscript and refers to VEPs (Variant Effect Predictors)

Minor comments:

The target selection table on the website needs some kind of text filtering option. It's very tedious to have to find a protein by scrolling through the table rather than typing in the symbol. This will only get worse as more datasets are added.

We have revised the website, adding a filtering option. In detail, we have refactored the web app by adding filtering functionality, both for the main protein table (that can now be filtered by UniProt AC, gene name, or RefSeq ID) and the mutations table. Doing this required a general overhaul of the table infrastructure (we changed the underlying engine that renders the tables).

The data sources listed on the data usage section of the website are not concordant with what is in the paper. For example, MaveDB is not listed.

We have revised and updated the data sources on the website, adding a metadata section with relevant information, including MaveDB references where applicable.

Figure 2 is somewhat confusing, as it partially interleaves results from two different proteins. This would be nicer as two separate figures, one on each protein, or just of a single protein.

As suggested by the reviewer, we have now revised the figure and corresponding legends and text, focusing only on one of the two proteins.

Figure 3 panel b is distractingly large and I wonder if the authors could do a little bit more with this visualization.

We have revised Figure 3 to solve these issues and integrating new data from the comparison with the phosphatase assay

Capitalization is inconsistent throughout the manuscript. For example, page 9 line 288 refers to VampSEQ instead of VAMP-seq (although this is correct elsewhere). MaveDB is referred to as MAVEdb or MAVEDB in various places. AlphaMissense is referred to as Alphamissense in the Figure 5 legend. The authors should make a careful pass through the manuscript to address this kind of issues.

We have carefully proofread the paper for these inconsistencies

MaveDB has a more recent paper (PMID: 39838450) that should be cited instead of/in addition to Esposito et al.

We have added the reference that the reviewer recommended

On page 11, lines 338-339 the authors mention some interesting proteins including BLC2, which has base editor data available (PMID: 35288574). Are there plans to incorporate this type of functional assay data into MAVISp?

The assay mentioned in the paper refers to an experimental setup designed to investigate mutations that may confer resistance to the drug venetoclax. We started the first steps to implement a MAVISp module aimed at evaluating the impact of mutations on drug binding using alchemical free energy perturbations (ensemble mode) but we are far from having it complete. We expect to import these data when the module will be finalized since they can be used to benchmark it and BCL2 is one of the proteins that we are using to develop and test the new module.

Reviewer #3 (Significance (Required)):

Significance:

General assessment:

This is a nice resource and the authors have clearly put a lot of effort in. They should be celebrated for their achievments in curating the diverse datasets, and the GitBooks are a nice approach. However, I wasn't able to get the website to work and I have raised several issues with the paper itself that I think should be addressed.

Advance:

New ways to explore and integrate complex data like protein structures and variant effects are always interesting and welcome. I appreciate the effort towards manual curation of datasets. This work is very similar in theme to existing tools like Genomics 2 Proteins portal (PMID: 38260256) and ProtVar (PMID: 38769064). Unfortunately as I wasn't able to use the site I can't comment further on MAVISp's position in the landscape.

We have expanded the conclusions section to add a comparison and cite previously published work, and linked to a review we published last year that frames MAVISp in the context of computational frameworks for the prediction of variant effects. In brief, the Genomics 2 Proteins portal (G2P) includes data from several sources, including some overlapping with MAVISp such as Phosphosite or MAVEdb, as well as features calculated on the protein structure. ProtVar also aggregates mutations from different sources and includes both variant effect predictors and predictions of changes in stability upon mutation, as well as predictions of complex structures. These approaches are only partially overlapping with MAVISp. G2P is primarily focused on structural and other annotations of the effect of a mutation; it doesn’t include features about changes of stability, binding, or long-range effects, and doesn’t attempt to classify the impact of a mutation according to its measurements. It also doesn’t include information on protein dynamics. Similarly, ProtVar does include information on binding free energies, long effects, or dynamical information.

Audience:

MAVISp could appeal to a diverse group of researchers who are interested in the biology or biochemistry of proteins that are included, or are interested in protein variants in general either from a computational/machine learning perspective or from a genetics/genomics perspective.

My expertise:

I am an expert in high-throughput functional genomics experiments and am an experienced computational biologist with software engineering experience.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors present MAVISp, a tool for viewing protein variants heavily based on protein structure information. The authors have done a very impressive amount of curation on various protein targets, and should be commended for their efforts. The tool includes a diverse array of experimental, clinical, and computational data sources that provides value to potential users interested in a given target.

Major comments:

Unfortunately I was not able to get the website to work properly. When selecting a protein target in simple mode, I was greeted with a completely blank page in the app window, and in ensemble mode, there was no transition away from the list of targets at all. I'm using Firefox 140.0.2 (64-bit) on Ubuntu 22.04. I would have liked to be able to explore the data myself and provide feedback on the user experience and utility.

I have some serious concerns about the sustainability of the project and think that additional clarifications in the text could help. Currently is there a way to easily update a dataset to add, remove, or update a component (for example, if a new predictor is published, an error is found in a predictor dataset, or a predictor is updated)? If it requires a new round of manual curation for each protein to do this, I am worried that this will not scale and will leave the project with many out of date entries. The diversity of software tools (e.g., three different pipeline frameworks) also seems quite challenging to maintain.

On the same theme, according to the GitHub repository, the program relies on Python 3.9, which reaches end of life in October 2025. It has been tested against Ubuntu 18.04, which left standard support in May 2023. The authors should update the software to more modern versions of Python to promote the long-term health and maintainability of the project.

I appreciate that the authors have made their code and data available. These artifacts should also be versioned and archived in a service like Zenodo, so that researchers who rely on or want to refer to specific versions can do so in their own future publications.

In the introduction of the paper, the authors conflate the clinical challenges of variant classification with evidence generation and it's quite muddled together. The y should strongly consider splitting the first paragraph into two paragraphs - one about challenges in variant classification/clinical genetics/precision oncology and another about variant effect prediction and experimental methods. The authors should also note that they are many predictors other than AlphaMissense, and may want to cite the ClinGen recommendations (PMID: 36413997) in the intro instead.

Also in the introduction on lines 21-22 the authors assert that "a mechanistic understanding of variant effects is essential knowledge" for a variety of clinical outcomes. While this is nice, it is clearly not the case as we are able to classify variants according to the ACMG/AMP guidelines without any notion of specific mechanism (for example, by combining population frequency data, in silico predictor data, and functional assay data). The authors should revise the statement so that it's clear that mechanistic understanding is a worthy aspiration rather than a prerequisite.

In the structural analysis section (page 5, lines 154-155 and elsewhere), the authors define cutoffs with convenient round numbers. Is there a citation for these values or were these arbitrarily chosen by the authors? I would have liked to see some justification that these assignments are reasonable. Also there seems to be an error in the text where values between -2 and -3 kcal/mol are not assigned to a bin (I assume they should also be uncertain). There are other similar seemingly-arbitrary cutoffs later in the section that should also be explained.

On page 9, lines 294-298 the authors talk about using the PTEN data from ProteinGym, rather than the actual cutoffs from the paper. They get to the latter later on, but I'm not sure why this isn't first? The ProteinGym cutoffs are somewhat arbitrarily based on the median rather than expert evaluation of the dataset and I'm not sure why it's even worth mentioning them when proper classifications are available. Regarding PTEN, it would be quite interesting to see a comparison of the VAMP-seq PTEN data and the Mighell phosphatase assay, which is cited on page 9 line 288 but is not actually a VAMP-seq dataset. I think this section could be interesting but it requires some additional attention.

The authors mention "pathogenicity predictors" and otherwise use pathogenicity incorrectly throughout the manuscript. Pathogenicity is a classification for a variant after it has been curated according to a framework like the ACMG/AMP guidelines (Richards 2015 and amendments). A single tool cannot predict or assign pathogenicity - the AlphaMissense paper was wrong to use this nomenclature and these authors should not compound this mistake. These predictors should be referred to as "variant effect predictors" or similar, and they are able to produce evidence towards pathogenicity or benignity but not make pathogenicity calls themselves. For example, in Figure 4e, the terms "pathogenic" and "benign" should only be used here if these are the classifications the authors have derived from ClinVar or a similar source of clinically classified variants.

Minor comments:

The target selection table on the website needs some kind of text filtering option. It's very tedious to have to find a protein by scrolling through the table rather than typing in the symbol. This will only get worse as more datasets are added.

The data sources listed on the data usage section of the website are not concordant with what is in the paper. For example, MaveDB is not listed.

I found Figure 2 to be a bit confusing in that it partially interleaves results from two different proteins. I think this would be nicer as two separate figures, one on each protein, or just of a single protein.

Figure 3 panel b is distractingly large and I wonder if the authors could do a little bit more with this visualization.

Capitalization is inconsistent throughout the manuscript. For example, page 9 line 288 refers to VampSEQ instead of VAMP-seq (although this is correct elsewhere). MaveDB is referred to as MAVEdb or MAVEDB in various places. AlphaMissense is referred to as Alphamissense in the Figure 5 legend. The authors should make a careful pass through the manuscript to address this kind of issues.

MaveDB has a more recent paper (PMID: 39838450) that should be cited instead of/in addition to Esposito et al.

On page 11, lines 338-339 the authors mention some interesting proteins including BLC2, which has base editor data available (PMID: 35288574). Are there plans to incorporate this type of functional assay data into MAVISp?

Significance

General assessment:

This is a nice resource and the authors have clearly put a lot of effort in. They should be celebrated for their achievments in curating the diverse datasets, and the GitBooks are a nice approach. However, I wasn't able to get the website to work and I have raised several issues with the paper itself that I think should be addressed.

Advance:

New ways to explore and integrate complex data like protein structures and variant effects are always interesting and welcome. I appreciate the effort towards manual curation of datasets. This work is very similar in theme to existing tools like Genomics 2 Proteins portal (PMID: 38260256) and ProtVar (PMID: 38769064). Unfortunately as I wasn't able to use the site I can't comment further on MAVISp's position in the landscape.

Audience:

MAVISp could appeal to a diverse group of researchers who are interested in the biology or biochemistry of proteins that are included, or are interested in protein variants in general either from a computational/machine learning perspective or from a genetics/genomics perspective.

My expertise:

I am an expert in high-throughput functional genomics experiments and am an experienced computational biologist with software engineering experience.

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors present a pipeline and platform, MAVISp, for aggregating, displaying and analysis of variant effects with a focus on reclassification of variants of uncertain clinical significance and uncovering the molecular mechanisms underlying the mutations.

Major comments:

• On testing the platform, I was unable to look-up a specific variant in ADCK1 (rs200211943, R115Q). I found that despite stating that the mapped refseq ID was NP_001136017 in the HGVSp column, it was actually mapped to the canonical UniProt sequence (Q86TW2-1). NP_001136017 actually maps to Q86TW2-3, which is missing residues 74-148 compared to the -1 isoform. The Uniprot canonical sequence has no exact RefSeq mapping, so the HGVSp column is incorrect in this instance. This mapping issue may also affect other proteins and result in incorrect HGVSp identifiers for variants.
• The paper lacks a section on how to properly interpret the results of the MAVISp platform (the case-studies are useful, but don't lay down any global rules for interpreting the results). For example: How should a variant with conflicts between the variant impact predictors be interpreted? Are certain indicators considered more 'reliable' than others?
• In the Methods section, GEMME is stated as being rank-normalised with 0.5 as a threshold for damaging variants. On checking the data downloaded from the site, GEMME was not rank-normalised but rather min-max normalised. Furthermore, Supplementary text S4 conflicts with the methods section over how GEMME scores are classified, S4 states that a raw-value threshold of -3 is used.
• Note. This is a major comment as one of the claims is that the associated web-tool is user-friendly. While functional, the web app is very awkward to use for analysis on any more than a few variants at once.
  • The fixed window size of the protein table necessitates excessive scrolling to reach your protein-of-interest. This will also get worse as more proteins are added. Suggestion: add a search/filter bar.
  • The same applies to the dataset window.
  • You are unable to copy anything out of the tables.
  • Hyperlinks in the tables only seem to work if you open them in a new tab or window.
  • All entries in the reference column point to the MAVISp preprint even when data from other sources is displayed (e.g. MAVE studies).
  • Entering multiple mutants in the "mutations to be displayed" window is time-consuming for more than a handful of mutants. Suggestion: Add a box where multiple mutants can be pasted in at once from an external document.

Minor comments

• Grammar. I appreciate that this manuscript may have been compiled by a non-native English speaker, but I would be remiss not to point out that there are numerous grammar errors throughout, usually sentence order issues or non-pluralisation. The meaning of the authors is mostly clear, but I recommend very thoroughly proof-reading the final version.
• There are numerous proteins that I know have high-quality MAVE datasets that are absent in the database e.g. BRCA1, HRAS and PPARG.
• Checking one of the existing MAVE datasets (KRAS), I found that the variants were annotated as damaging, neutral or given a positive score (these appear to stand-in for gain-of-function variants). For better correspondence with the other columns, those with positive scores could be labelled as 'ambiguous' or 'uncertain'.
• Numerous thresholds are defined for stabilizing / destabilizing / neutral variants in both the STABILITY and the LOCAL_INTERACTION modules. How were these thresholds determined? I note that (PMC9795540) uses a ΔΔG threshold of 1/-1 for defining stabilizing and destabilizing variants, which is relatively standard (though they also say that 2-3 would likely be better for pinpointing pathogenic variants).
• "Overall, with the examples in this section, we illustrate different applications of the MAVISp results, spanning from benchmarking purposes, using the experimental data to link predicted functional effects with structural mechanisms or using experimental data to validate the predictions from the MAVISp modules."

The last of these points is not an application of MAVISp, but rather a way in which external data can help validate MAVISp results. Furthermore, none of the examples given demonstrate an application in benchmarking (what is being benchmarked?). - Transcription factors section. This section describes an intended future expansion to MAVISp, not a current feature, and presents no results. As such, it should probably be moved to the conclusions/future directions section. - Figures. The dot-plots generated by the web app, and in Figures 4, 5 and 6 have 2 legends. After looking at a few, it is clear that the lower legend refers to the colour of the variant on the X-axis - most likely referencing the ClinVar effect category. This is not, however, made clear either on the figures or in the app. - "We identified ten variants reported in ClinVar as VUS (E102K, H86D, T29I, V91I, P2R, L44P, L44F, D56G, R11L, and E25Q, Fig.5a)"

E25Q is benign in ClinVar and has had that status since first submitted.

Significance

Platforms that aggregate predictors of variant effect are not a new concept, for example dbNSFP is a database of SNV predictions from variant effect predictors and conservation predictors over the whole human proteome. Predictors such as CADD and PolyPhen-2 will often provide a summary of other predictions (their features) when using their platforms. MAVISp's unique angle on the problem is in the inclusion of diverse predictors from each of its different moules, giving a much wider perspective on variants and potentially allowing the user to identify the mechanistic cause of pathogenicity. The visualisation aspect of the web app is also a useful addition, although the user interface is somewhat awkward. Potentially the most valuable aspect of this study is the associated gitbook resource containing reports from biocurators for proteins that link relevant literature and analyse ClinVar variants. Unfortunately, these are only currently available for a small minority of the total proteins in the database with such reports.

For improvement, I think that the paper should focus more on the precise utility of the web app / gitbook reports and how to interpret the results rather than going into detail about the underlying pipeline.

In terms of audience, the fast look-up and visualisation aspects of the web-platform are likely to be of interest to clinicians in the interpretation of variants of unknown clinical significance. The ability to download the fully processed dataset on a per-protein database would be of more interest to researchers focusing on specific proteins or those taking a broader view over multiple proteins (although a facility to download the whole database would be more useful for this final group).

My expertise.

• I am a protein bioinformatician with a background in variant effect prediction and large-scale data analysis.

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Referee #1

Evidence, reproducibility and clarity

Summary: This manuscript, "MAVISp: A Modular Structure-Based Framework for Protein Variant Effects," presents a significant new resource for the scientific community, particularly in the interpretation and characterization of genomic variants. The authors have developed a comprehensive and modular computational framework that integrates various structural and biophysical analyses, alongside existing pathogenicity predictors, to provide crucial mechanistic insights into how variants affect protein structure and function. Importantly, MAVISp is open-source and designed to be extensible, facilitating reuse and adaptation by the broader community.

Major comments:

• While the manuscript is formally well-structured (with clear Introduction, Results, Conclusions, and Methods sections), I found it challenging to follow in some parts. In particular, the Introduction is relatively short and lacks a deeper discussion of the state-of-the-art in protein variant effect prediction. Several methods are cited but not sufficiently described, as if prior knowledge were assumed. OPTIONAL: Extend the Introduction to better contextualize existing approaches (e.g., AlphaMissense, EVE, ESM-based predictors) and clarify what MAVISp adds compared to each.
• The workflow is summarized in Figure 1(b), which is visually informative. However, the narrative description of the pipeline is somewhat fragmented. It would be helpful to describe in more detail the available modules in MAVISp, and which of them are used in the examples provided. Since different use cases highlight different aspects of the pipeline, it would be useful to emphasize what is done step-by-step in each. OPTIONAL: Consider adding a table or a supplementary figure mapping each use case to the corresponding pipeline steps and modules used.
• The text contains numerous acronyms, some of which are not defined upon first use or are only mentioned in passing. This affects readability. OPTIONAL: Define acronyms upon first appearance, and consider moving less critical technical details (e.g., database names or data formats) to the Methods or Supplementary Information. This would greatly enhance readability.
• The code and trained models are publicly available, which is excellent. The modular design and use of widely adopted frameworks (PyTorch and PyTorch Geometric) are also strong points. However, the Methods section could benefit from additional detail regarding feature extraction and preprocessing steps, especially the structural features derived from AlphaFold2 models. OPTIONAL: Include a schematic or a table summarizing all feature types, their dimensionality, and how they are computed.
• The section on transcription factors is relatively underdeveloped compared to other use cases and lacks sufficient depth or demonstration of its practical utility. OPTIONAL: Consider either expanding this section with additional validation or removing/postponing it to a future manuscript, as it currently seems preliminary.

Minor comments:

• Most relevant recent works are cited, including EVE, ESM-1v, and AlphaFold-based predictors. However, recent methods like AlphaMissense (Cheng et al., 2023) could be discussed more thoroughly in the comparison.
• Figures are generally clear, though some (e.g., performance barplots) are quite dense. Consider enlarging font sizes and annotating key results directly on the plots.
• Minor typographic errors are present. A careful proofreading is highly recommended. Below are some of the issues I identified:

Page 3, line 46: "MAVISp perform" -> "MAVISp performs"

Page 3, line 56: "automatically as embedded" -> "automatically embedded"

Page 3, line 57: "along with to enhance" -> unclear; please revise

Page 4, line 96: "web app interfaces with the database and present" -> "presents"

Page 6, line 210: "to investigate wheatear" -> "whether"

Page 6, lines 215-216: "We have in queue for processing with MAVISp proteins from datasets relevant to the benchmark of the PTM module." -> unclear sentence; please clarify

Page 15, line 446: "Both the approaches" -> "Both approaches"

Page 20, line 704: "advantage of multi-core system" -> "multi-core systems"

Significance

General assessment: the strongest aspects of the study are the modularity, open-source implementation, and the integration of structural information through graph neural networks. MAVISp appears to be one of the few publicly available frameworks that can easily incorporate AlphaFold2-based features in a flexible way, lowering the barrier for developing custom predictors. Its reproducibility and transparency make it a valuable resource. However, while the technical foundation is solid and the effort substantial, the scientific narrative and presentation could be significantly improved. The manuscript is dense and hard to follow in places, with a heavy use of acronyms and insufficient explanation of key design choices. Improving the descriptive clarity, especially in the early sections, would greatly enhance the impact of this work.

Advance: to the best of my knowledge, this is one of the first modular platforms for protein variant effect prediction that integrates structural data from AlphaFold2 with bioinformatic annotations and even clinical data in an extensible fashion. While similar efforts exist (e.g., ESMfold, AlphaMissense), MAVISp distinguishes itself through openness and design for reusability. The novelty is primarily technical and practical rather than conceptual.

Audience: this study will be of strong interest to researchers in computational biology, structural bioinformatics, and genomics, particularly those developing variant effect predictors or analyzing the impact of mutations in clinical or functional genomics contexts. The audience is primarily specialized, but the open-source nature of the tool may diffuse its use among more applied or translational users, including those working in precision medicine or protein engineering.

Reviewer expertise: my expertise is in computational structural biology, molecular modeling, and (rather weak) machine learning applications in bioinformatics. I am familiar with graph-based representations of proteins, AlphaFold2, and variant effects based on Molecular Dynamics simulations. I do not have any direct expertise in clinical variant annotation pipelines.

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Reply to the reviewers

Reviewer #1

Summary:

Miyamoto et al. report that importin α1 is highly enriched in a subfraction of micronuclei (about 40%), which exhibit defective nuclear envelopes and compromised accessibility of factors essential for the damage response associated with homologous recombination DNA repair. The authors suggest that the unequal localization and abnormal distribution of importin α1 within these micronuclei contribute to the genomic instability observed in cancer.

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Major comments:

1.) It is crucial to quantitatively assess the localization of importin α1 in micronuclei (MN) across non-transformed MCM10A cells compared to transformed cell lines (MC7, HeLa, and MDA-MB-231). This analysis would help determine whether the localization of importin α1 in MN correlates with genomic stability in human cancer cells

We appreciate the reviewer's thoughtful suggestion to compare non-transformed and transformed cell lines to evaluate importin α1 localization in MN. Given that HeLa cells are derived from cervical cancer rather than the mammary epithelium, we considered it inappropriate to directly compare them with non-transformed mammary epithelial MCF10A cells. Therefore, HeLa cells were analyzed separately to assess the effects of reversine treatment on importin α1 localization. The results indicated no significant difference between the treated and untreated HeLa cells. (Supplemental Fig. S2F in the revised manuscript). Regarding the comparison between MCF10A and the two cancer cell lines, MCF7 and MDA-MB-231, the proportion of importin α1-positive MN did not significantly differ across the cell lines, regardless of reversine treatment (Supplemental Fig. S3B, Untreated: p = 0.9850 and 0.5533; Reversine: p = 0.2218 and 0.9392). These results suggest that there is no clear difference in the localization of importin α1 in MN between the transformed and non-transformed cell lines tested. However, we acknowledge that this does not exclude the possibility that importin α1 localization to MN is linked to genomic instability under specific conditions.

2.) While the authors provide some evidence indicating partial disruption of nuclear envelopes in MN (Figures 3 and S4), it is noteworthy that this phenomenon also occurs in importin α1-negative MN. Furthermore, according to the figure legends, the data presented in both figures stem from a single experiment. Current literature suggests that compromised nuclear envelope integrity is one of the major contributors to genomic instability, mediated through mechanisms such as chromothripsis and cGAS-STING-mediated inflammation arising from MN. Therefore, a more comprehensive quantification of nuclear envelope integrity-ideally comparing non-transformed MCM10A cells with transformed cell lines (MC7, HeLa, and MDA-MB-231)-is necessary to substantiate the connection between aberrant importin α1 behavior in MN and chromothripsis processes, as well as regulation of the cGAS-STING pathway linked to genomic instability in cancer cells.

We thank the reviewer for the constructive suggestion to quantify nuclear envelope integrity more comprehensively. In response, we compared laminB1 localization at the MN membrane between importin α1-positive and -negative MN in MCF10A, MCF7, MDA-MB-231, and HeLa cells, and included these results in the revised manuscript (Fig. 4C). For each cell, the laminB1 intensity in the MN was normalized to that of the primary nucleus (PN). This analysis showed that laminB1 intensity was significantly lower in importin α1-positive MN across all cell lines, including non-transformed MCF10A cells. These findings support a close association between aberrant importin α1 accumulation and compromised nuclear envelope integrity, a key factor potentially linking MN to chromothripsis and cGAS-STING-mediated genomic instability.

3.) The schematic illustration presented in Figure 8 does not adequately summarize all findings from this study nor does it clarify how the localization of importin α1 within MN might hypothetically influence genome stability. Although it is reasonable to propose that "importin α can serve as a molecular marker for characterizing the dynamics of MN" (Line 344), the authors assert (Line 325) that their findings, along with others, have "potential implications for the induction of chromothripsis processes and regulation of the cGAS-STING pathway in cancer cells." However, they fail to provide a clear or even hypothetical explanation regarding how their findings contribute to these molecular events. To address this gap, it would be essential for them to contextualize their results within existing literature that explores and links structural integrity deficits or aberrant DNA replication/damage responses in MN with chromothripsis and inflammation (e.g., PMID: 32601372; PMID: 32494070; PMID: 27918550; PMID: 28738408; PMID: 28759889).

We agree that the previous schematic illustration (former Fig. 8) did not adequately summarize our findings and may have overstated our conclusions. Accordingly, we have removed this figure from the revised manuscript.

To address the reviewer's concern, we performed additional analyses and included the results in the new Figure 8. These data show that, in addition to RAD51, both RPA2 and cGAS display mutually exclusive localization with importin α1 in MN. RPA2, a single-stranded DNA-binding protein, stabilizes damaged DNA and enables RAD51 filament assembly during homologous recombination repair. Previous studies have demonstrated that RPA2 accumulates in ruptured MN in a CHMP4B-dependent manner (PMID: 32601372). Likewise, cGAS is a cytosolic DNA sensor that localizes to ruptured MN and activates innate immune signaling through the cGAS-STING pathway, as widely reported (PMID: 28738408; 28759889; see also PMID: 32494070; 27918550).

Our findings suggest an alternative scenario: even when nuclear envelope rupture occurs, importin α1-positive MN may remain inaccessible to DNA repair and sensing factors such as RPA2 and cGAS. This supports the view that importin α1 defines a distinct MN subset, separate from those characterized by the canonical DNA damage response or innate immune signaling factors. Furthermore, our overexpression experiments with EGFP-importin α1 (Fig. 7G, 7H) raises the possibility that importin α1 enrichment may impede the recruitment of DNA-binding proteins.

Taken together, these results support the conclusion that importin α1 marks a unique MN state and provides a molecular framework for distinguishing between different MN environments. At the reviewer's suggestion, we have cited all the recommended references (PMID: 32601372, 32494070, 27918550, 28738408, and 28759889) in the revised manuscript to better contextualize our findings. We are grateful for the reviewer's thoughtful suggestions and literature recommendations, which helped us clarify the implications of our findings within the broader context of chromothripsis and cGAS-STING-mediated genomic instability.

4.) Fig. 4D does not support the idea that importin α1 is euchromatin enriched: H3K9me3, H3K4me3 and H3K37me3 seem to be all deeply blue.

We sincerely thank the reviewer for pointing out the important limitations of the original version of Fig. 4D, as also raised in minor comment #5. As the reviewer correctly noted, this figure was intended to demonstrate that importin-α1 preferentially localizes to euchromatin regions (H3K4me3 and H3K36me3) rather than heterochromatin (H3K9me3 and H3K27me3). However, we acknowledge that in the original figure, the predominantly blue tone of the heatmap made this interpretation unclear and that the Spearman's correlation coefficient for H3K36me3 was missing. In response, we have substantially revised the figure (now shown as Fig. 5E in the revised manuscript). Specifically, we improved the color scale for better visual distinction, added the missing Spearman's coefficients for H3K36me3, and strengthened the analysis by incorporating ChIP-seq data obtained with two independent antibodies against importin α1 (Ab1 and Ab2). We believe that these revisions provide a clear and more accurate representation of euchromatin enrichment of importin-α1, as originally intended.

Indeed, the data presented by the authors do not adequately support a direct link between the presence of importin α1 in MN and genomic instability in human cancer cells. While the experimental correlations provided may not substantiate this connection definitively, they do lay a foundation for a grounded hypothesis and suggest the need for further research to explore this topic in greater depth. Additionally, it is worth noting that the evidence contributes to the growing list of nuclear proteins exhibiting abnormal behavior in micronuclei (MN). This highlights the significance of studying such proteins to understand their roles in genomic stability and cancer progression.

Following the reviewer's suggestion, we carefully revised the manuscript to ensure that our statements are consistent with the scope of the data and do not overstate our conclusions. As part of this effort, we removed the schematic illustration (former Fig. 8), which might have overstated our findings, and refined the relevant text to prevent overinterpretation.

To our knowledge, this study is the first to report the specific accumulation of importin α in MN. Our results suggest a previously unrecognized function of importin α beyond its canonical transport role and add to the growing list of nuclear proteins that exhibit abnormal behavior in MN. We hope that these findings will provide a conceptual and experimental basis for future studies aimed at clarifying the biological significance of MN heterogeneity and quality control in cancer biology.

Additional experiments are necessary to quantitatively assess the localization of importin α1 in micronuclei (MN) across non-transformed MCM10A cells and transformed cell lines (MC7, HeLa, MDA-MB-231). This analysis would help determine whether the localization of importin α1 in MN correlates with genomic stability in human cancer cells.

As part of our response to Major Comment 1, we conducted additional experiments to quantitatively compare importin α1 localization in MN between non-transformed MCF10A cells, breast cancer cell lines (MCF7 and MDA-MB-231), and HeLa cells. These results have been included in the revised manuscript (Supplemental Fig. S2F and Fig. S3B). The analyses showed no significant differences in the proportion of importin α1-positive MN among these cell lines, consistent with the reviewer's request for a more comprehensive evaluation.

The authors claim that importin α1 preferentially localizes to euchromatic areas rather than heterochromatic regions within MN. While this assertion is supported by the immunofluorescence (IF) images presented in Figures 4A/B and S5A/B, it remains less clear for Figure S5C/B. To strengthen this claim, providing averages of IF distributions from multiple cells across independent experiments would be beneficial to draw more robust conclusions.

We have quantified the co-localization of importin α1 with the euchromatin marker H3K4me3 and the heterochromatin marker H3K9me3 in micronuclei (MN) across four human cell lines (MCF10A, MCF7, MDA-MB-231, and HeLa). The results of this statistical analysis are included in the revised manuscript in Fig. 5C. These data provide quantitative evidence from independent experiments showing that importin α1 preferentially localizes to euchromatic regions within the MN, thereby supporting our initial observation.

Furthermore, ChIP-seq data are presented to support the idea that importin α1 preferentially distributes over euchromatin areas in MN. However, as described, the epigenetic chromatin status indicated by these ChIP-seq experiments reflects that of the principal nucleus (PN), not specifically the status within MN in MCF7 cells. Given that MN represent only a small fraction of the cell population under normal culture conditions-likely less than 5% for HeLa cells as shown in Figure S2D-the relevance of this data is limited. Additionally, according to data presented in Figure 1B, importin α1 does not localize or distribute within the PN as it does in MN in MCF7 cells. Therefore, further experiments should be conducted to substantiate that importin α1 preferentially targets euchromatin areas within MN and to compare this distribution with that observed in the principal nucleus. Such studies could reveal potential abnormalities regarding the correlation between epigenetic chromatin status and importin α distribution in MN.

As noted, these experiments were performed on whole-cell populations of MCF7 cells and therefore reflect the overall chromatin landscape, not specifically that of the MN. We fully acknowledge that MN constitute only a small fraction of the cell population under standard culture conditions (Supplemental Fig. S2D), and thus, the relevance of ChIP-seq data to MN must be interpreted with caution.

Nevertheless, our intention in presenting these data was to illustrate that importin α1 preferentially associates with euchromatin regions marked by H3K4me3. To examine this more directly, we analyzed importin α1 localization in MN using immunofluorescence with histone modification markers across multiple cell lines. These analyses, together with the quantitative results now included in the revised manuscript (Fig. 5C), confirming that importin α1 preferentially localizes to euchromatic regions within MN.

Taken together, although the ChIP-seq data were derived from whole-cell populations, the combined results from IF imaging and quantitative analysis support our interpretation that importin α1 retains its euchromatin-associating property within MN. We hope that these additional data will address the reviewer's concerns.

To support the hypothesis that importin α1 inhibits RAD51 accessibility within MN, Figures 7D and E should be supplemented with thorough quantification and statistical analysis based on at least three independent experiments. This additional data would enhance confidence in their findings regarding RAD51 accessibility inhibition by importin α1.

Following the reviewer's suggestion, we have added a new graph (Fig. 7F) in the revised manuscript. This figure presents the quantified frequency of RAD51-positive MN among importin α1-negative and importin α1-positive MN, analyzed across six microscopy fields (n = 6) from three independent experiments.

To improve clarity and consistency, we reorganized the panels: representative RAD51 images are now shown in Fig. 7B, and the Cell #1 (low RAD51) vs. Cell #2 (high RAD51) classification with etoposide responsiveness is summarized in Fig. 7C. As illustrated in Figs. 7D and 7E, importin α1 and RAD51 exhibit mutually exclusive localization in MN. Fig. 7F provides a unified statistical summary at the population level.

The results showed that the proportion of RAD51-positive MN was significantly lower among importin α1-positive MN than among importin α1-negative MN, providing robust quantitative support for the proposed mutual exclusivity between importin α1 localization and RAD51 accessibility in MN.

We are grateful to the reviewer for this constructive suggestion, which helped us clarify and better support the central message of our study.

The additional experiments proposed are controls and direct comparisons using the same techniques and experimental designs used by the authors, so it is reasonable that the authors can carry them out within a realistic timeframe.

We appreciate the reviewer's thoughtful consideration of the feasibility of the additional experiments.

Given the importance of reproducibility and the need to evaluate results based on imaging and quantitation, I strongly recommend that the authors include a detailed description of the optical microscopy procedures utilized in their study. This should encompass imaging conditions, acquisition settings, and the specific equipment used. Providing this information will enhance transparency and facilitate reproducibility. For reference, some valuable guidance on essential parameters for reproducibility can be found in Heddleston et al. (2021) (doi:10.1242/jcs.254144). Incorporating these details will not only strengthen the manuscript but also support other researchers in reproducing the findings accurately.

Following the reviewer's suggestion, we have substantially revised the Materials and Methods sections in the main and supplemental manuscripts to provide detailed descriptions of the optical microscopy procedures, including the specifications of the imaging equipment, acquisition settings, and image processing parameters. These revisions follow the best practices recommended by Heddleston et al. (2021, J. Cell Sci., doi:10.1242/jcs.254144).

We have also expanded the description of our quantitative image analysis using ImageJ, providing details on the parameters for MN identification and the measurement of colocalization rates between importin α and histone modifications. These additions ensured reproducibility and clarity.

We believe that these modifications will enhance the reproducibility of our results and increase the value of our study for the research community. We sincerely appreciate the reviewer's helpful suggestions.

Many of the plots and values in the manuscript lack appropriate statistical analysis, including p-values, which are not detailed in the figures or their legends. Furthermore, the Statistical Analysis section does not provide adequate information regarding the specific statistical tests employed or the criteria used to determine which analyses were applied in each case. To enhance the rigor and clarity of the study, it is essential that these issues be addressed prior to publication. A comprehensive presentation of statistical analysis will improve the reliability of the findings and allow readers to better understand the significance of the results. I recommend that the authors revise this section to include detailed explanations of all statistical methods used, along with corresponding p-values for all relevant comparisons.

We sincerely appreciate the reviewer's constructive comments highlighting the importance of transparent and rigorous statistical analyses. In response, we have carefully revised all figure panels, figure legends, and the Materials and Methods (Statistical Analysis) section in both the main and the supplementary manuscripts.

In the revised figure legends, we now provide the number of independent experiments and sample sizes (n), statistical tests applied (e.g., unpaired or paired two-tailed t-test, one-way ANOVA with Tukey's post-hoc test, two-way ANOVA with Sidak's multiple comparisons), data presentation format (mean {plus minus} SD), and corresponding p-values or significance indicators (*, **, ***). The Statistical Analysis section was also expanded to explain the rationale for selecting each statistical test, the criteria for significance, and the reporting of the replicates. These revisions ensure clarity, reproducibility, and transparency throughout the manuscript, directly addressing the reviewers' concerns. We are grateful for this valuable suggestion, which has significantly improved the rigor of our study.

Minor comments:

The authors claim that importin α1 exhibits remarkably low mobility in the micronuclei (MN) compared to its mobility in the principal nucleus (PN), as illustrated in Figure 1. However, based on the experimental design, this conclusion may not be appropriate. In the current setup, the FRAP experiment conducted in the PN measures the mobility of importin α1 molecules within the cell nucleus, where the influence of nuclear transport is likely negligible. Conversely, in the MN experiments shown, all molecules of importin α1 are bleached within a given MN. Consequently, what is being measured here primarily reflects the effects of nuclear transport rather than intrinsic molecular mobility. To accurately compare kinetics of nuclear transport, it would be essential to completely bleach the entire PN. If measuring molecular mobility between MN and PN is desired, only a small fraction of either MN or PN area/volume should be bleached during FRAP analysis. Additionally, it would be beneficial to include measurements of mobility for other canonical nuclear transport factors (e.g., RAN, CAS, RCC1) for comparative purposes. This broader context would allow for a more comprehensive understanding of importin α1 behavior relative to other factors involved in nuclear transport. Finally, utilizing cells that exhibit importin α1 signals in both PN and MN could further strengthen comparisons and provide more robust conclusions regarding its mobility dynamics.

We thank the reviewer for their constructive suggestions regarding our FRAP analysis. To address the concern that the original comparison between PN and the micronuclei (MN) might have been biased by differences in bleaching areas, we performed new experiments in which both PN and MN were fully bleached within the same cells (Fig. 3A, and 3C). This approach allowed for a more direct comparison of importin α1 dynamics under equivalent conditions.

These experiments revealed a markedly slower fluorescence recovery in MN than in PN, indicating reduced nuclear import and/or recycling efficiency of importin α1 in MN. In addition, we retained our original analysis to further characterize the heterogeneous mobility patterns of importin α1 in MN, identifying three distinct mobility classes: high, intermediate, and low (Fig. 3B, and 3D). Together, these results support our observation that importin α1 mobility is restricted in MN, likely due to altered nuclear transport dynamics.

As suggested by the reviewer, we attempted partial bleaching of MN to assess intranuclear mobility. However, owing to the small size of MN, partial bleaching is technically challenging and inconsistent, with some MN recovering even during the bleaching process. Therefore, reliable quantification was not possible. For transparency, these data are provided as a Reviewer-only Figure but were not included in the revised manuscript.

Finally, while we agree that examining other nuclear transport factors (e.g., RAN, CAS, RCC1) would be informative, our study focused on importin α1 dynamics. We consider these additional factors to be important directions for future investigations.

Prior studies are referenced appropriately in general, but the authors missed some references (PMID: 32601372; PMID: 32494070; PMID: 27918550; PMID: 28738408; PMID: 28759889) that I consider key to put the present findings in frame with previous works which link the lack of structural integrity and/or aberrant DNA replication/damage responses in MN with Cchromothripsis and inflammation.

We thank the reviewer for carefully pointing out the key references that are highly relevant to framing our findings in the context of previous studies on micronuclear instability, chromothripsis and inflammation. We fully agree with this suggestion.

In the revised manuscript, we have cited these studies in both the Introduction and Discussion sections. Specifically, we incorporated these studies when discussing the structural fragility of MN, aberrant DNA replication, and the exposure of micronuclear DNA to cytoplasmic sensors, which mechanistically link MN rupture to chromothripsis and cGAS-STING-mediated immune activation. For example, we now refer to the study demonstrating RPA2 recruitment to ruptured MN in a CHMP4B-dependent manner (PMID: 32601372), reports showing defective replication and DNA damage responses in MN (PMID: 32494070; 27918550), and seminal studies establishing cGAS localization to ruptured MN and activation of innate immune signaling (PMID: 28738408; 28759889).

By incorporating these references, we more clearly position our findings that importin α1 defines a distinct subset of MN lacking access to DNA repair and sensing factors such as RAD51, RPA2, and cGAS. This contextualization emphasizes that our data add to and extend the established view that compromised MN integrity underlies chromothripsis and inflammation by identifying importin α1 as a novel marker of an alternative MN microenvironment. We are grateful for this constructive recommendation, which has allowed us to strengthen the framing of our study in the existing literature.

The figures presented in the manuscript are clear; however, where plots are included, they require appropriate statistical analysis. It is essential to display p-values on the plots or within their legends to provide readers with information regarding the significance of the results. Including this statistical information will enhance the interpretability of the data and strengthen the overall findings of the study. I recommend that the authors revise these sections accordingly before publication.

In response, we have revised the relevant figure panels and their legends to clearly display the statistical significance, including p-values, where appropriate. Specifically, we added statistical annotations (p-values or significance markers such as asterisks) directly on the plots or in the corresponding legends, and clarified the number of replicates, statistical tests used, and definitions of error bars (mean {plus minus} SD). We believe that these revisions improve the interpretability and transparency of our results and strengthen the overall presentation of the data.

__ 1.) In lines 134-135, it is stated that "up to 40% of the MN showed importin α1 accumulation under both standard culture conditions and the reversine treatment (Fig. S2F)." However, Figure S2F only displays percentages for reversine-treated cells, and there is no mention in the text or figures regarding the percentage of importin α1-positive MN determined by immunofluorescence (IF) under standard culture conditions. This discrepancy should be addressed.__

Following the reviewer's comments, we revised Supplemental Fig. S2F shows a direct comparison of the proportion of importin α1-positive MN between untreated and reversine-treated HeLa cells based on indirect IF analysis. The Results section was updated accordingly (page 8, Lines 148-150): "We then examined whether reversine treatment affected the proportion of importin α1-positive MN. The results revealed that the MN formation rate for either untreated or treated cells was 36.2% {plus minus} 7.8 or 38.3% {plus minus} 8.8, respectively, with no significant difference (Fig. S2F). "

We believe that this revision addresses the reviewer's concern by providing relevant quantitative data for the untreated condition.

2.) In line 170, the authors state that "Cells in which overexpressed EGFP-importin α1 localized only in PN were excluded from the analysis (see Fig. 1E, top panels)." It is unclear why this exclusion was made. The authors should clarify whether they are referring to all constructs or only to the wild-type (WT) construct when mentioning EGFP-importin α1 localization solely in PN. This clarification is important as it may affect the results highlighted in line 173.

In this section, we aimed to clarify that the quantitative analysis focused exclusively on cells harboring MN, as the purpose of the analysis was to compare the localization of EGFP-importin α1 between MN and PN. We excluded cells that contained no MN and showed EGFP-importin α1 localization only in the PN. This criterion was consistently applied to both wild-type and mutant constructs. To avoid confusion, we have removed the sentence "Cells in which overexpressed EGFP-importin α1 localized only in PN were excluded from the analysis (see Fig. 1E, top panels)." from the revised manuscript.

3.) The statement in line 191 ("However, this antibody could not be further used in this context due to cross-reactivity with highly concentrated importin α1 in MN (Fig. S4)") is somewhat misleading. While it hints at a technical issue, it does not provide additional relevant information for understanding its implications for the rationale of the research. Moreover, Figure S4 is referenced but appears to refer specifically to panels S4D and E, which are not mentioned in the text. I recommend clarifying this point or removing it altogether.

We agree with the reviewer that the statement "However, this antibody could not be further used in this context due to cross-reactivity with highly concentrated importin α1 in MN (Fig. S4)" was not essential for understanding the rationale of our study and could be misleading. In response, we have removed this sentence from the revised manuscript, along with the corresponding Supplementary Fig. S4.

4.) Lines 197-199 contain a sentence that could be misleading and would benefit from clearer explanation. Although Figure 3D provides some clarity on this matter, no statistical analysis is included-only a bar plot is presented. A proper statistical analysis should be provided here to enhance understanding.

In the revised manuscript, we performed one-way ANOVA followed by Holm-Sidak's multiple comparisons test to evaluate the MN localization ratio of EGFP-NES between Imp-α1-negative and Imp-α1-positive MN. This analysis revealed a statistically significant difference (**p

5.) In lines 218-221, it states that importin α1 associates with euchromatin regions characterized by H3K4me3 and H3K36me3; however, Figure 4D lacks the Spearman's correlation coefficient value for H3K36me3 within the matrix. This omission needs correction.

We thank the reviewer for this insightful comment. As addressed in response to Major comment #4, we have substantially revised Fig. 5 and added the missing Spearman's correlation coefficient value for H3K36me3 (now shown in Fig. 5E). These revisions, together with the overall improvements to the figure, more clearly illustrate the euchromatin enrichment of importin-α1.

6.) For consistency in the experimental design aimed at identifying potential importin α1-interacting proteins, it would be more appropriate for Figures 5C/D to show IF data from MCF7 cells rather than HeLa cells.

We sincerely apologize for the misstatements in the legends of the original Fig. 5C. The correct description is that this experiment was performed using MCF7 cells, and we have revised the legend accordingly in the revised manuscript (now Fig. 6C). In addition, because the original data in Fig. 5D were obtained from HeLa cells, we repeated this experiment using MCF7 cells and replaced the panel with new data (now Fig. 6D).

7.) To substantiate claims that importin α1 inhibits RAD51 accessibility within MN, Figures 7D and E should include thorough quantitation and statistical analysis based on at least three independent experiments.

As described above, we addressed this point by adding a new quantification and statistical analysis in Fig. 7F, based on six microscopy fields across three independent experiments. This analysis directly supports our claim that importin α1 inhibits RAD51 accessibility in the MN.

We would also like to clarify that although the reviewer referred to Figs 7D and 7E, these two panels were designed to illustrate the same phenomenon-the mutually exclusive localization of importin α1 and RAD51 to distinct MN-shown in different contexts. Specifically, Fig. 7D presents examples from separate cells, each with MN containing either importin α1 or RAD51, while Fig. 7E shows a single cell containing two distinct MN, one enriched with importin α1 and the other with RAD51. Because both panels serve as illustrative examples of the same phenomenon, it would not be meaningful to quantify them independently as parallel datasets. Instead, we integrated the statistical analysis into a unified graph (Fig. 7F), which summarizes the frequency of RAD51-positive MN in relation to importin α1 status across the cell population, thereby supporting our interpretation that importin α1-positive MN represent a distinct subset that is less accessible to RAD51.

8.) The meaning of lines 336-338-"Therefore, the enrichment of importin α1 in MN, along with its interaction with chromatin, may regulate the accessibility of RAD51 to DNA/chromatin fibers in MN and protect its activity"-is unclear. I suggest rephrasing this sentence for improved clarity and comprehension.

We appreciate the reviewer's comment regarding the clarity of our statement in the Discussion (former lines 336-338). We agree that the original phrasing is ambiguous. To improve clarity and align with our results, we revised this section to emphasize that importin α1-positive MN represent a restricted environment from which DNA repair and sensing factors are excluded. Specifically, RAD51, RPA2, and cGAS showed mutually exclusive localization with importin α1, indicating that these MN are largely inaccessible to DNA-binding proteins (pages 20-21). This rephrasing removes the unclear phrase "protect its activity" and directly reflects our experimental findings, presenting a clearer interpretation that is consistent with the Results.

9.) Fig. 1D: Numbers on the y-axis are missing, x-axis labeling is too small

We appreciate the reviewer's careful examination of the figure. In the revised manuscript, we added numerical tick labels to both the x- and y-axes and increased the label font size to ensure clear readability, as shown in Fig. 1D. We also applied the same improvements to other fluorescence intensity plots, including Figs. 4A, 4B, 5A, 5B, 7H, and Supplemental Fig. S4C and S5A-S5F to ensure consistency in readability across the manuscript. We thank the reviewer for helping us improve the clarity and accuracy of our figure presentations.

10.) Fig. 1F: As the PN/MN values of the three experiments are seemingly identical (third column) the distribution of the three individual data of the PN (first column) should mirror the distribution of the three individual data of the MN (second column). The authors might want to check why this is not the case.

Upon re-examination of the source data, we identified and corrected a minor calculation error in one subset and regenerated the panel. After correction, the three independent PN/MN ratios were 3.1%, 2.9%, and 2.6%, rather than being identical. These corrected values were proportional to the corresponding PN and MN measurements and preserved the expected relationship between their distributions. Although the numerical differences were small, they demonstrated high reproducibility across independent experiments. These corrections do not alter the interpretation of Fig. 1F, and the distribution of PN/MN values is now consistent with the paired PN and MN data presented in the revised manuscript.

Significance Micronuclei (MN) primarily arise from defects in mitotic progression and chromatin segregation, often associated with chromatin bridges and/or lagging chromosomes. MN frequently exhibit DNA replication defects and possess a rupture-prone nuclear envelope, which has been linked to genomic instability. The nuclear envelope of MN is notably deficient in crucial factors such as lamin B and nuclear pore complexes (NPCs). This deficiency may be attributed to the influence of microtubules and the gradient of Aurora B activity at the mitotic midzone, which inhibits the recruitment of proper nuclear envelope components. Additionally, several other factors may contribute to this process: for instance, PLK1 controls the assembly of NPC components onto lagging chromosomes; chromosome size and gene density positively correlate with the membrane stability of MN; and abnormal accumulation of the ESCRT complex on MN exacerbates DNA damage within these structures, triggering pro-inflammatory pathways.

The work presented by Dr. Miyamoto and colleagues reveals the abnormal behavior of importin α1 in MN during interphase. According to their findings, it is reasonable to consider importin α1 as a molecular marker for characterizing MN dynamics. Furthermore, it could serve as a potential clinical marker if the authors provide additional experiments demonstrating significantly different localization patterns of importin α1 in transformed cells (e.g., MC7, HeLa, MDA-MB-231) compared to non-transformed cells (e.g., MCM10A).

While the authors present some evidence indicating partial disruption of nuclear envelopes in MN (Figures 3 and S4), it is noteworthy that this phenomenon also occurs in importin α1-negative MN. Moreover, according to the figure legends, data for both figures originate from a single experiment. As such, convincing evidence linking the aberrant behavior of importin α1 in MN with chromothripsis processes or regulation of the cGAS-STING pathway-and its implications for genomic instability in cancer cells-remains lacking.

Overall, it is not entirely clear what significance this advance holds for the field; while there are conceptual contributions made by this work, they do not appear sufficiently robust at this time. Further research is needed to clarify these connections and strengthen their conclusions regarding importin α1's role in MN dynamics and genomic instability.

We sincerely appreciate the reviewer's thoughtful and constructive evaluation of the significance of our study. We agree that in the original submission, the conceptual contribution was not fully supported by sufficient evidence. In the revised manuscript, we have substantially strengthened our findings by incorporating new data on RPA2 and cGAS, in addition to RAD51. These results consistently show that importin α1-positive MN are largely inaccessible to multiple DNA-recognizing proteins-including DNA repair factors (RAD51 and RPA2) and the innate immune sensor cGAS-whereas importin α1-negative MN readily recruit these proteins. This broader dataset reinforces the concept that importin α defines a distinct and restricted MN subset, extending beyond our initial observation of RAD51 exclusion.

By framing importin α as a molecular marker that discriminates between functionally distinct MN environments, our study conceptually advances the understanding of MN heterogeneity. This adds to the prior literature showing that defective nuclear envelope integrity underlies chromothripsis and cGAS-STING activation and positions importin α as a new marker for identifying MN that are refractory to these DNA repair and sensing pathways. While we agree that further work is necessary to directly link importin α enrichment to downstream genomic instability or inflammation in cancer, we believe that our revised data now provide a robust foundation for future investigations.

Taken together, the revised manuscript presents a clearer and more comprehensive conceptual advance: importin α-positive MN represents a previously unrecognized molecular environment distinct from MN characterized by canonical DNA repair or sensing factors. We are grateful to the reviewer, whose constructive comments greatly improved the clarity, robustness, and overall impact of our study. We believe that these findings will be of particular interest to researchers studying the mechanisms of genomic instability, chromothripsis, and cancer biology.

Reviewer #2

Summary:

The authors have shown that Importin α1, a nuclear transport factor, is enriched in subsets of micronuclei (MN) of cancer cells (MCF7 and HeLa) and, using FRAP, has an altered dynamics in MN. Moreover, the authors have shown that these levels of Importin α1 in the MN are likely not due to its traditional role for signal-dependent protein transport, as suggested by immunofluorescence of other factors important for this function. Additionally, cargo dynamics carrying NLS or NES signals were disrupted in Importin α1-positive micronuclei. Importin α1-positive micronuclei also appear to have a disrupted nuclear envelope, potentially explaining some of these cargo disruptions. The authors also demonstrated that Importin α colocalizes with proteins important for DNA replication, and p53 signaling using RIME, followed by immunofluorescence. Lastly, the authors show that Importin α and RAD51 have mutual exclusivity in the micronuclei.

Major comments:

1) A key issue is there are very few statistical tests used in this study. It is crucial to the interpretation of the data. We strongly urge the authors to re-analyze the data using appropriate statistical analyses. Along those lines, in many figures 1 or 2 images are shown without stating how many biological or technical replicates this is representative of or showing quantification of the anlyses. In general, the authors' statements would be strengthened by showing more examples and/or stating "N" in the figure legends or supplement.

We sincerely thank the reviewer for emphasizing the importance of including sufficient statistical analyses and replication information. As noted in our response to Reviewer #1, we have carefully revised the manuscript to enhance statistical rigor and transparency throughout. Specifically, we expanded the Statistical Analysis section in the Materials and Methods section to provide a clear description of the statistical approaches used. In addition, all figure legends have been revised to explicitly state the number of biological replicates, sample sizes, statistical tests applied, and corresponding p-values or significance indicators. Representative images are consistently accompanied by quantitative analyses derived from multiple independent experiments.

We believe that these comprehensive revisions directly address the reviewer's concerns and substantially improve the rigor, clarity, and interpretability of our manuscript.

2) Using RIME and immunofluorescence, the authors identify factors that co-localize with Importin α1 in subsets of micronuclei (Figure 5), which is interesting, but there is no functional data associated with this result. Are the authors stating that these differences account for altered DNA damage or replication? It is unclear what the conclusion is beyond "some MN are different than others." Could the authors knockdown/knockout these factors to determine if they recruit Importin α1 into MN or the reciprocal? For many of these factors, they appear to be broadly present throughout the entire primary nucleus as well, indicating there is nothing unique about their MN localization.

We agree that our original RIME and indirect IF analyses were primarily descriptive and lacked functional validation. To strengthen this aspect, we added new IF and quantification data (now presented in Fig. 8) showing that importin α1-positive MN are largely mutually exclusive with DNA repair and sensing factors such as RAD51, RPA2, and cGAS, whereas importin α1 frequently co-localizes with chromatin regulators identified by RIME, such as PARP1 and SUPT16H/FACT. These findings indicate that importin α1-positive MN define a distinct molecular environment enriched in replication- and chromatin-associated regulators but inaccessible to canonical DNA repair and sensing proteins.

This combination of mutual exclusivity with DNA repair/sensing factors and frequent co-localization with chromatin regulators underscores the biological significance of importin α1 localization in MN, as it may contribute to localized chromatin stabilization through association with chromatin regulators while simultaneously restricting access to DNA repair and sensing factors. Thus, importin α1-positive MN represent a restricted subset with potential implications for genome stability and immune signaling, going beyond the descriptive notion that "some MN are different than others."

Moreover, many chromatin regulators identified by RIME contain classical nuclear localization signals (NLSs), raising the possibility that importin α1 interacts with these proteins via their NLS sequences. We fully agree with the reviewer that knockdown or knockout experiments would be highly valuable to clarify whether such interactions actively recruit importin α1 into MN or occur reciprocally, and we regard this as an important direction for future investigations.

3) In line 274, the authors state that MN highly enriched for Importin α1 inhibits RAD51 accessibility but this is an overstatement of the data. Instead, the authors show that RAD51 and importin α1 do not colocalize in micronuclei, albeit without quantification which weakens their argument. Also, the consequence of this "mutual exclusivity" is unclear. Can the authors inhibit or knockdown Importin α1 and show that RAD51 goes to all micronuclei? And how is this different than the data shown for factors in Figure 5? Some of those show colocalization with Importin α1-positive micronuclei and others do not. Could you perform live imaging of labeled Importin a1 and RAD51 and show that as Importin α1 accumulates in MN that RAD51 or other DNA repair factors are exported? An alternative experiment would be to show that the C-mutant, which is defective in nuclear export, now colocalizes with RAD51 in MN. Please reconcile this or show experiments to prove the statement above.

We agree that our original wording "inhibits RAD51 accessibility" was not sufficiently supported by direct evidence, as it was based solely on the immunofluorescence data. Therefore, we have removed this statement from the Results section of the revised manuscript. To strengthen this point, we added a quantitative analysis (Fig. 7F) showing that RAD51 signals were significantly reduced in importin α1-enriched MN.

Regarding the suggestion to perform knockdown experiments, we note that the depletion of KPNA2 (gene name of importin α1) has been reported to cause severe cell-cycle arrest (Martinez-Olivera et al, 2018; Wang et al, 2012). Consistent with these reports, we also found that siRNA-mediated knockdown of KPNA2 in our system strongly reduced MN induction upon reversine treatment, making it technically unfeasible to analyze RAD51 localization under these conditions. We also sincerely thank the reviewer for suggesting the live imaging experiments. We fully agree that such experiments would provide valuable mechanistic insights, and we regard this as an important direction for future research.

In addition, to address the reviewer's concern about other DNA repair factors, we added new data (Fig. 8) showing that importin α1-positive MN are mutually exclusive with RPA2 and cGAS. RPA2 is a canonical single-strand DNA (ssDNA)-binding protein that stabilizes exposed ssDNA and facilitates RAD51 recruitment. It has been reported to accumulate in ruptured MN in a CHMP4B-dependent manner (Vietri et al, 2020). cGAS is a cytosolic DNA sensor that detects ruptured MN and activates innate immune signaling via the cGAS-STING pathway. Together with our RAD51 results, these data show that importin α1-positive MN are consistently segregated from multiple DNA-recognizing factors, including RAD51. Simultaneously, importin α1 co-localizes with chromatin regulators identified by RIME, such as PARP1 and SUPT16H/FACT. These findings support the view that importin α1-positive MN define a distinct molecular environment enriched in chromatin regulators but largely inaccessible to DNA repair and sensing factors. While the precise mechanism remains unclear, one possibility is that importin α1-associated chromatin interactions limit the access of DNA repair and sensing proteins. However, this interpretation is speculative and requires further investigation.

4) In the Discussion, line 343-344 states that "importin α1 is uniquely distributed and alters the nuclear/chromatin status when enriched in MN," however this is not currently supported by the present data. The data presented shows correlation (albeit weak) between euchromatic modifications and Importin α1, and it does not definitively show that importin α1 is sufficient to alter the nuclear-chromatin status when enriched in the MN. More substantial experiments would be required to show whether Importin α1 plays an active role in these modifications.

Following the reviewer's suggestion, in the revised manuscript, we removed this overstatement and rephrased the relevant sections of the Discussion. Rather than implying a causal role, we now describe the mutually exclusive localization of importin α1 with DNA repair and sensing factors (RAD51, RPA2, and cGAS), emphasize its preferential association with euchromatin regions marked by H3K4me3, and note its frequent co-localization with chromatin regulators identified by RIME, such as PARP1 and SUPT16H/FACT. These findings suggest that importin α1-positive MN define a distinct subset characterized by limited accessibility to DNA repair and sensing proteins, whereas cGAS-positive ruptured MN exemplify a state in which these proteins can accumulate.

We also added a concluding statement that frames importin α1 as defining a previously unrecognized MN subset that is distinct from conventional ruptured MN. This revision provides a more accurate and appropriately cautious interpretation of our data while underscoring the conceptual advance of our study by clarifying how importin α1 localization reveals MN heterogeneity.

Minor Comments

1) Summary statement (page 3 Line 40): The use of "their" is confusing. Whose microenvironment are you referring to?

We have rephrased the sentence as follows: The accumulation of importin α in micronuclei, followed by modulation of the microenvironment of the micronuclei, suggests the non-canonical function of importin α in genomic instability and cancer development. Thank you for this useful suggestion.

2) In Abstract and introduction (page 4, Line 44 and page 5, line 59) it states that MN are membrane enclosed structures, but this is not always the case (see https://doi.org/10.1038/nature23449 as one example).

While MN are typically surrounded by a nuclear envelope at the time of their formation during mitosis, we agree that this envelope can later rupture or fail to assemble completely, thereby exposing micronuclear DNA to the cytoplasm. To clarify this point, we revised the Introduction to explicitly acknowledge that MN may lose nuclear envelope integrity, which can have important consequences for genomic instability and immune activation inflammation. Specifically, we have added the following sentence to the Introduction (page 4, lines 77-80): "The nuclear envelope of MN can be partially or completely disrupted, allowing cytoplasmic DNA sensors, such as cyclic GMP-AMP synthase (cGAS), to access micronuclear DNA and trigger innate immune responses via the cGAS-STING pathway (Harding et al, 2017; Li & Chen, 2018; Mackenzie et al, 2017). "

We hope this addition appropriately addresses the concerns raised by Reviewer #2 while incorporating the valuable suggestions from Reviewer #1 without altering the overall structure and flow of the manuscript.

3) Given the fact that the RIME result identified proteins involved in DNA replication to be enriched with Importin α1, are these MN enriched in factors described in Fig. 5 simply localizing to MN that are in S phase, as described previously (doi: 10.1038/nature10802)?

We sincerely thank the reviewer for raising this constructive perspective regarding the potential relationship between importin α1 enrichment in micronuclei (MN) and the S phase. Our RIME analysis identified chromatin-associated proteins, such as PARP1 and SUPT16H/FACT, which are often activated during replication stress and frequently function in the S phase. However, importin α1-positive MN were not exclusively associated with S-phase-specific molecules, and our data do not indicate that these MN are restricted to the S phase.

Previous studies [e.g., (Crasta et al, 2012)] have established that MN are prone to replication defects and represent hotspots of genomic instability. The recovery of replication stress-responsive molecules, such as PARP1 and FACT, by RIME is therefore consistent with the biology of MN. Based on this valuable suggestion, we have revised the Discussion (page 19) to explicitly mention the potential involvement of replication-related proteins in importin α1-positive MN, as well as the possibility that importin α1 accumulation may contribute to replication defects in these structures. We are grateful to the reviewer for raising this important perspective, which has enabled us to place our findings in a broader mechanistic context.

We are grateful to the reviewer for this important comment, which has allowed us to place our findings in a broader mechanistic context and outline directions for future research, including testing the relationship between importin α1-positive MN and established S-phase markers such as PCNA.

4) The FRAP data is not very compelling. While it is clear there are differences between the PN and MN dynamics, what is driving these differences? Are these differences meaningful to the biology of the MN or PN? It is unclear what this data is contributing to the conclusions of the paper. Also, if the mobility of the MN is plotted on the same graph as the PN, the differences in MN mobility might not look as compelling.

We respectfully emphasize that FRAP analysis is a key component of our study, as it provides important insights into the distinct dynamics of importin α1 in MN compared to PN.

In the revised manuscript, we included new experiments (now shown in Fig. 3A and 3C) that directly compare the recovery kinetics of importin α1 in PN and MN in the same cells. By plotting the PN and MN recovery curves side by side, we aimed to improve clarity and provide a direct visualization of the pronounced differences in importin α1 dynamics between these compartments.

Our FRAP results showed that importin α1 accumulated in both PN and MN but exhibited markedly reduced mobility in MN. These findings suggest that, unlike in the PN, canonical nucleocytoplasmic recycling of importin α1 is impaired in MN. Furthermore, the reduced mobility indicates that importin α1 is stably associated with chromatin or chromatin-associated factors in MN, consistent with our additional biochemical and imaging data showing preferential association with euchromatin (e.g., H3K4me3) and chromatin regulators.

Taken together, the FRAP data provide functional evidence that complements our structural and molecular analyses, supporting our central conclusion that importin α1 accumulation in MN defines a restricted chromatin environment that influences the accessibility of DNA repair and sensing factors.

5) In Results (line 117), you state that "the cytoplasm of those cell lines emitted quite strong signals" for Importin α1, but that phrasing is a little confusing. Yes, Importin α1 is in present the cytoplasm in most cells, but it appears you are referring to the enrichment in MN. I would recommend re-phrasing this statement to make your intent clearer.

As the reviewer rightly noted, the original phrasing, "the cytoplasm of those cell lines emitted quite strong signals," was misleading, as it could suggest a broad cytoplasmic distribution of importin α1. Our observations showed that importin α1 accumulated specifically in MN located within the cytoplasm, but not in the cytoplasmic regions. To clarify this, we revised the Results section (page 7, lines 125-127) to read: " Next, we performed indirect immunofluorescence (IF) analysis on human cancer cell lines, including MCF7 and HeLa cells. Notably, we found that importin α1 accumulated prominently in MN located within the cytoplasm (MCF7 cells, Fig. 1B; HeLa cells, Fig. 1C; yellow arrowhead). " .

We believe that this revised wording more accurately reflects our findings and addresses the reviewer's concerns.

6) In Results (line 135, Figure S2E,F), the ratio of high, low or no Importin α1 intensity is confusing. Is this percentage relative to the total number of MN? It Is unclear what is meant by "whole number" of MN. Is Importin α1 intensity quantified or is it subjective?

We apologize for the confusing terminology used in the original manuscript for Supplemental Fig. S2 and thank the reviewer for pointing it out. Although the reviewer did not specifically comment on the classification of importin α1 signal intensity as "high" or "low," we recognized that this approach relied on subjective visual assessment and lacked clearly defined thresholds. To improve clarity and objectivity, we have removed this classification and now analyze importin α1 localization in MN as simply positive or negative (revised Supplemental Fig. S2E). The previous graph (original Fig. S2F) was deleted. In addition, the frequency of Importin α1-positive MN has been reported in the Results section of the main text (page 8). We believe that these revisions have improved the clarity and reproducibility of our data presentation.

7) Figure 2C is confusing. Are you counting MN with co-localization of Importin α1 and these factors? Please clarify.

Figure 2C shows the percentage of importin α1-positive MN that displayed localization of importin β1, CAS, or Ran based on IF analysis. In other words, it represents the co-localization rates of these transport factors specifically within the subset of MN positive for importin α1. To improve clarity, we revised the y-axis label in Fig. 2C to "Localization in Impα1-positive MN (%)" and modified the figure legend accordingly. We have clarified this point in the Results section (page 9). We believe that these revisions resolve the confusion and clarify the scope of the analysis.

8) Figure S3D quantification is very confusing and unclear. Also, how is this normalized? Are you controlling for total signal in each cell? And can the results of this experiment give you any mechanistic insight as to what is regulating MN localization beyond the interpretation of "MN localization is distinct from PN localization"? The "C-mutant" appears quite a bit different than the others. What might that indicate about the role of CAS/CSE1L in MN enrichment?

We apologize for the confusion caused by the quantification in the Supplemental Fig. S3D (now revised as Fig. S4D). This figure shows the relative enrichment of EGFP-importin α1 in MN compared with that in PN for wild-type and mutant constructs. To control for nuclear size, fluorescence intensity was measured using a fixed circular ROI (1.5-2.0 µm in diameter) placed in both the MN and PN of the same cell, and MN/PN intensity ratios were directly plotted for individual cells (n = 8 per condition). This procedure is described in detail in the Results section (page 10).

Regarding the C-mutant, the reduced MN/PN ratio primarily reflects increased importin α1 accumulation in the PN rather than a reduced retention in the MN. As discussed in the revised manuscript (page 18), this suggests that CAS/CSE1L-mediated nuclear export is active in the PN but may be impaired or uncoupled in the MN, possibly due to differences in nuclear envelope integrity or chromatin context. We believe that this clarification addresses the reviewer's concerns and highlights the mechanistic implications of the C-mutant phenotype.

9) For Figures 3A,B and S4, are these images of single z-slices or projections? It would be helpful to clarify for your interpretations as to whether they are truly partial or diffuse or the membrane is in another z-plane. Also, how does the localization of Importin α1 different or similar to other factors that localize to MN with a compromised nuclear envelope, such as cGAS? If it is based on epigenetic marks, it should be different than cGAS, which primarily binds non-chromatinized DNA.

We thank the reviewer for this valuable suggestion. All images shown in Figs 3A, 3B, and S4 in the original manuscript (now revised as Fig. 4A and 4B, with the original Fig. S4 omitted) were derived from single optical sections rather than projections. We would like to emphasize that similar discontinuities in signals for lamin proteins (including laminB1 and laminA/C) were consistently observed across multiple cells and independent experiments, indicating that these observations are not due to an artifact of image acquisition or a missing z-plane, but rather reflect a genuine partial loss of the MN membrane.

In contrast to cGAS, which predominantly binds non-chromatinized DNA in ruptured MN, our data indicate that importin α1 preferentially localizes to MN regions enriched in euchromatin-associated histone modifications, such as H3K4me3. The new data presented in Fig. 8 further strengthen this point by directly comparing importin α1 with DNA-recognizing proteins such as cGAS and RPA2, which preferentially localize to MN lacking importin α1. Together, these results highlight that importin α1-positive MN constitute a distinct subset characterized by chromatin-associated localization and reduced accessibility to DNA repair and sensing proteins.

10) In Results, it is unclear how Fig. 7B was calculated. Are the authors qualitatively assessing if RAD51 is there or looking for MN enrichment relative to PN? Additionally, in Fig. 7C, RAD51 localization is diffuse. It should be enriched in foci. I would recommend the authors repeat this experiment using pre-extraction then quantify RAD51 foci number and/or intensity.

For the quantification shown in Fig. 7B of the original manuscript, we acquired images containing approximately 15-50 cells per condition and counted all the micronuclei (MN) in those fields. The percentage of RAD51-positive MN relative to the total MN was calculated. In the revised manuscript, we further refined this analysis by classifying RAD51-positive MN into two categories based on signal intensity: weak (Cell #1 type) and strong (Cell #2 type). For each condition, nine independent fields were analyzed (302 MN in untreated cells and 213 MN in etoposide-treated cells). This quantification revealed that etoposide treatment preferentially increased the proportion of MN with strong RAD51 accumulation (Fig. 7C, right panels), indicating enhanced DNA damage in MN. Thus, our analysis was quantitative rather than qualitative, based on systematic counting across multiple fields.

Regarding the reviewer's suggestion of pre-extraction, we believe that this approach is technically difficult because MN are structurally fragile. Importantly, in the subset of MN with strong RAD51 accumulation, RAD51 was clearly present in foci rather than diffuse signals, as shown in the high-magnification images (Fig. 7E).

Finally, in response to Reviewer #1, we performed a new quantitative analysis (Fig. 7F) focusing on the frequency of strongly RAD51-positive MN in relation to importin α1 status. This analysis confirmed the mutually exclusive relationship between RAD51 and importin α1 in MN and further strengthened our conclusions.

11) In line 264, "notably" is misspelled.

Thank you for pointing this out. We have corrected the spelling.

12) In line 303, "scenarios" should be changed to the singular form.

Thank you for this confirmation. We have corrected this to "scenario".

13) In Figure legend, line 571-582, H3K27me3 is shown in Figure 4D, but the written legend does not mention this mark.

We have added the marks in the legend for Fig. 5E.

Significance: Overall, this paper shows compelling evidence for micronuclear localization of regulators of nuclear export, notably Importin α1. Of note, this occurs in subsets of MN that lack an intact nuclear envelope. And while it has been appreciated that compromised micronuclear envelopes lead to genomic instability, this is one of the first that demonstrate alteration in the nuclear envelope may disrupt import or export of nuclear proteins into micronuclei.

A limitation of the study is that much of the work is based on immunofluorescence and lacks mechanism. While there is much correlative data showing that Importin α1 localizes to micronuclei with compromised envelopes, it is unclear whether Importin α1 drives micronuclear collapse or it is downstream of this process. Additionally, Importin α1 micronuclear localization anti-correlates with RAD51 but does colocalize with other DNA replication factors, yet it is unclear whether their localization is dependent on Importin α1 or its role in nuclear export. Currently, the audience for this manuscript would be focused to those interested in micronuclei. If these concerns about an active role for Importin α1 in micronuclear export are resolved, it would greatly increase the impact of this manuscript to those interested more broadly in genomic instability, DNA repair, and cancer.

We thank the reviewer for positively evaluating our study and highlighting the importance of defining the biological significance of our findings. In the revised manuscript, we incorporated new data (Fig. 8) demonstrating that importin α1-positive MN are mutually exclusive not only with RAD51 but also with RPA2 and cGAS. These results clearly establish importin α1-positive MN as a distinct subset, defined by the enrichment of chromatin-associated proteins, while being largely inaccessible to canonical DNA repair and DNA-sensing factors.

Consistent with this, our FRAP experiments and analysis of the CAS/CSE1L-binding mutant (C-mut) further indicated that the recycling dynamics of importin α1 were altered in MN compared to PN. In addition, importin α1 was enriched in lamin-deficient areas of MN, where electron microscopy revealed a fragile nuclear envelope morphology. Together with prior evidence, as discussed in the revised manuscript that recombinant importin α can inhibit nuclear envelope assembly in Xenopus egg extracts (Hachet et al, 2004), these findings raise the possibility that high local concentrations of importin α1 may actively contribute to impaired nuclear envelope formation or stability in MN.

Such a distinct MN state may have important biological consequences. By limiting the access of DNA repair and DNA-sensing proteins, importin α1 accumulation may influence chromothripsis and immune activation, which, in turn, could play a role in tumor progression and genome instability. We believe that the identification of importin α1 as a marker defining such a restricted MN environment represents a conceptual advance that extends the relevance of our study beyond the MN field to the broader areas of genome instability, DNA repair, and cancer biology. We are grateful to the reviewer for encouraging us to strengthen the framing of our work, which has helped us clarify the novelty and impact of our findings.

Reviewer #3

Summary:

This study reports that importin alpha isoforms enrich strongly in a subset of micronuclei in cancer cells and uses mutagenesis and immunostaining to define how this localization relates to importin alpha's nuclear transport function. This enrichment occurs even though importin-alpha-positive micronuclei also contain Ran and the importin alpha export factor CSE1L, indicating that importin a enrichment is not simply a consequence of the absence of components of the nuclear transport machinery that control its localization. Mutagenesis of importin a indicates that Mn enrichment persists even when the importin beta binding and NLS binding capacities of imp a are impaired. Potential importin alpha interacting proteins are identified by proteomics, although the relationship of these potential binding partners to micronucleus localization is unclear.

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1. In Figure S3, the authors show that mutagenesis of importin alpha's CSE1L binding domain decreases the ratiometric enrichment in Mn vs. Pn. However, is this effect occurring because th CSE1L binding mutant decreases Mn enrichment, or increases Pn enrichment? It seems that the latter is possible based on the images shown. If the Pn specifically becomes brighter on average in cells expressing the C-mut, while Mn remain similar in fluorescence intensity, that might suggest that CSE1L has less of an effect on importin alpha export in Mn compared to Pn.

We appreciate the reviewer's insightful observations. In the revised analysis (now presented in Supplemental Fig. S4D), we quantified EGFP-importin α1 intensities in both PN and MN using fixed circular regions of interest. This revealed that the reduced MN/PN ratio observed in the CSE1L-binding mutant (C-mut) was mainly due to an increase in the PN signal rather than a decrease in the MN signal. These results are consistent with the reviewer's suggestion and indicate that CSE1L-mediated nuclear export is functional in PN but has a limited impact on MN.

Importantly, this interpretation is supported by our FRAP experiments (Fig. 3), which show that importin α1 recycles normally in the PN but exhibits markedly reduced mobility in the MN. Together with our proteomic and colocalization analyses (Fig. 6), which identified importin α1 association with chromatin regulators such as PARP1 and SUPT16H/FACT, these findings suggest that importin α1 accumulates in MN not only because the recycling machinery is uncoupled but also because it forms stable interactions with chromatin-associated proteins. As discussed in the revised manuscript, this dual mechanism provides a plausible explanation for the persistent retention of importin α1 in MN and its role in defining a distinct MN environment.

It is unclear from the text or the methods whether RIME identification of importin-alpha binding partners is performed in reversine-treated cells, which would increase the proportion of importin alpha in Mn, or in untreated cells. In either case, it seems likely that the majority of interactors identified would be cargoes that rely on importin alpha for import into the Pn. The rationale for linking these potential interactions to the Mn is unclear. While some of these factors are indeed shown enriched in Mn in Figure 5, the significance of this is also unclear. These points should be clarified.

We thank the reviewer for raising this important point. The RIME assay was performed using whole-cell extracts from untreated wild-type MCF7 cells, which primarily identified importin α1-associated nuclear cargo proteins. To assess their potential relevance to MN, we screened the RIME candidates using immunofluorescence data provided by the Human Protein Atlas database and experimentally validated those showing clear MN localization by colocalization with importin α1. This two-step approach enabled us to highlight importin α1 interactors that are functionally relevant to MN biology rather than general nuclear cargoes.

In response to the reviewer's concerns, we revised the Results section to clarify this rationale. Specifically, we added the explanation that "As importin α1 interactors are typically nuclear proteins, it is plausible that they reside not only in the primary nucleus but also in the MN. To test this possibility, we screened the identified candidates for MN localization using immunofluorescence images provided by the Human Protein Atlas (HPA) database (Pontén et al, 2008; Thul et al, 2017)." (page 14, lines 294-297).

This is consistent with the idea that a wide range of nuclear proteins carrying NLS motifs can recruit importin α1 into the micronuclei, where they reside. This protein-driven enrichment of importin α1 may create a restricted microenvironment in which canonical DNA repair and sensing proteins, including RAD51, RPA2, and cGAS, are excluded, thereby defining a distinct subset of micronuclei with limited genome surveillance capacity.

In Figure 6, the authors perform FRAP of importin alpha in Mn and show that it recovers much more slowly in Mn than in Pn. However, it appears from the images shown that the entire Mn was photobleached in each FRAP experiment. It thus is unclear whether the slow FRAP recovery is limited by slow diffusion of importin alpha within Mn/on Mn chromatin or impaired trafficking of importin alpha into and out of Mn. These distinct outcomes have distinct implications: either importin alpha is immobilized on Mn (eu)chromatin, or alternatively importin alpha is poorly transported into / out of Mn. This ambiguity could be resolved by bleaching a portion of a Mn and testing whether importin alpha diffuses within a single Mn.

We thank the reviewer for this insightful comment regarding the interpretation of FRAP data. As the reviewer rightly pointed out, the original FRAP design-where the entire MN was photobleached-does not allow for a clear discrimination between the intranuclear immobilization of importin α1 and impaired trafficking into or out of the MN.

In line with a similar suggestion from Reviewer #1, we attempted partial photobleaching of MN to evaluate whether importin α1 can diffuse within MN independently of nucleocytoplasmic transport. However, due to the small size of MN, precise targeting is technically challenging and recovery is often unreliable, with some MN even exhibiting partial recovery during the bleaching process itself. These data were not included in the revised figures; however, we provide representative examples as reviewer-only figures to illustrate these technical limitations.

To further clarify the nuclear transport dynamics of importin α1, we redesigned our FRAP experiments to fully photobleach both the PN and MN within the same cells under identical conditions. These results, presented in revised Fig. 3A and 3C, demonstrate a markedly slower recovery of importin α1 in MN compared to PN, strongly suggesting that nucleocytoplasmic recycling of importin α1 is impaired in MN. Moreover, the reduced mobility of importin α1 in the MN is consistent with stable chromatin binding, limiting its ability to diffuse freely within the nuclear space.

We believe that this additional analysis, prompted by the reviewer's comment, significantly strengthens the mechanistic interpretation of our FRAP data.

References

Crasta K, Ganem NJ, Dagher R, Lantermann AB, Ivanova EV, Pan Y, Nezi L, Protopopov A, Chowdhury D, Pellman D (2012) DNA breaks and chromosome pulverization from errors in mitosis. Nature 482: 53-58

Hachet V, Kocher T, Wilm M, Mattaj IW (2004) Importin α associates with membranes and participates in nuclear envelope assembly in vitro. EMBO J 23: 1526-1535

Martinez-Olivera R, Datsi A, Stallkamp M, Köller M, Kohtz I, Pintea B, Gousias K (2018) Silencing of the nucleocytoplasmic shuttling protein karyopherin a2 promotes cell-cycle arrest and apoptosis in glioblastoma multiforme. Oncotarget 9: 33471-33481

Vietri M, Schultz SW, Bellanger A, Jones CM, Petersen LI, Raiborg C, Skarpen E, Pedurupillay CRJ, Kjos I, Kip E, Timmer R, Jain A, Collas P, Knorr RL, Grellscheid SN, Kusumaatmaja H, Brech A, Micci F, Stenmark H, Campsteijn C (2020) Unrestrained ESCRT-III drives micronuclear catastrophe and chromosome fragmentation. Nat Cell Biol 22: 856-867

Wang CI, Chien KY, Wang CL, Liu HP, Cheng CC, Chang YS, Yu JS, Yu CJ (2012) Quantitative proteomics reveals regulation of karyopherin subunit alpha-2 (KPNA2) and its potential novel cargo proteins in nonsmall cell lung cancer. Mol Cell Proteomics 11: 1105-1122

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Referee #3

Evidence, reproducibility and clarity

This study reports that importin alpha isoforms enrich strongly in a subset of micronuclei in cancer cells and uses mutagenesis and immunostaining to define how this localization relates to importin alpha's nuclear transport function. This enrichment occurs even though importin-alpha-positive micronuclei also contain Ran and the importin alpha export factor CSE1L, indicating that importin a enrichment is not simply a consequence of the absence of components of the nuclear transport machinery that control its localization. Mutagenesis of importin a indicates that Mn enrichment persists even when the importin beta binding and NLS binding capacities of imp a are impaired. Potential importin alpha interacting proteins are identified by proteomics, although the relationship of these potential binding partners to micronucleus localization is unclear.

Significance

1. In Figure S3, the authors show that mutagenesis of importin alpha's CSE1L binding domain decreases the ratiometric enrichment in Mn vs. Pn. However, is this effect occurring because th CSE1L binding mutant decreases Mn enrichment, or increases Pn enrichment? It seems that the latter is possible based on the images shown. If the Pn specifically becomes brighter on average in cells expressing the C-mut, while Mn remain similar in fluorescence intensity, that might suggest that CSE1L has less of an effect on importin alpha export in Mn compared to Pn.
2. It is unclear from the text or the methods whether RIME identification of importin-alpha binding partners is performed in reversine-treated cells, which would increase the proportion of importin alpha in Mn, or in untreated cells. In either case, it seems likely that the majority of interactors identified would be cargoes that rely on importin alpha for import into the Pn. The rationale for linking these potential interactions to the Mn is unclear. While some of these factors are indeed shown enriched in Mn in Figure 5, the significance of this is also unclear. These points should be clarified.
3. In Figure 6, the authors perform FRAP of importin alpha in Mn and show that it recovers much more slowly in Mn than in Pn. However, it appears from the images shown that the entire Mn was photobleached in each FRAP experiment. It thus is unclear whether the slow FRAP recovery is limited by slow diffusion of importin alpha within Mn/on Mn chromatin or impaired trafficking of importin alpha into and out of Mn. These distinct outcomes have distinct implications: either importin alpha is immobilized on Mn (eu)chromatin, or alternatively importin alpha is poorly transported into / out of Mn. This ambiguity could be resolved by bleaching a portion of a Mn and testing whether importin alpha diffuses within a single Mn.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors have shown that Importin α1, a nuclear transport factor, is enriched in subsets of micronuclei (MN) of cancer cells (MCF7 and HeLa) and, using FRAP, has an altered dynamics in MN. Moreover, the authors have shown that these levels of Importin α1 in the MN are likely not due to its traditional role for signal-dependent protein transport, as suggested by immunofluorescence of other factors important for this function. Additionally, cargo dynamics carrying NLS or NES signals were disrupted in Importin α1-positive micronuclei. Importin α1-positive micronuclei also appear to have a disrupted nuclear envelope, potentially explaining some of these cargo disruptions. The authors also demonstrated that Importin α colocalizes with proteins important for DNA replication, and p53 signaling using RIME, followed by immunofluorescence. Lastly, the authors show that Importin α and RAD51 have mutual exclusivity in the micronuclei.

Major comments:

1. A key issue is there are very few statistical tests used in this study. It is crucial to the interpretation of the data. We strongly urge the authors to re-analyze the data using appropriate statistical analyses. Along those lines, in many figures 1 or 2 images are shown without stating how many biological or technical replicates this is representative of or showing quantification of the anlyses. In general, the authors' statements would be strengthened by showing more examples and/or stating "N" in the figure legends or supplement.
2. Using RIME and immunofluorescence, the authors identify factors that co-localize with Importin α1 in subsets of micronuclei (Figure 5), which is interesting, but there is no functional data associated with this result. Are the authors stating that these differences account for altered DNA damage or replication? It is unclear what the conclusion is beyond "some MN are different than others." Could the authors knockdown/knockout these factors to determine if they recruit Importin α1 into MN or the reciprocal? For many of these factors, they appear to be broadly present throughout the entire primary nucleus as well, indicating there is nothing unique about their MN localization.
3. In line 274, the authors state that MN highly enriched for Importin α1 inhibits RAD51 accessibility but this is an overstatement of the data. Instead, the authors show that RAD51 and importin α1 do not colocalize in micronuclei, albeit without quantification which weakens their argument. Also, the consequence of this "mutual exclusivity" is unclear. Can the authors inhibit or knockdown Importin α1 and show that RAD51 goes to all micronuclei? And how is this different than the data shown for factors in Figure 5? Some of those show colocalization with Importin α1-positive micronuclei and others do not. Could you perform live imaging of labeled Importin a1 and RAD51 and show that as Importin α1 accumulates in MN that RAD51 or other DNA repair factors are exported? An alternative experiment would be to show that the C-mutant, which is defective in nuclear export, now colocalizes with RAD51 in MN. Please reconcile this or show experiments to prove the statement above.
4. In the Discussion, line 343-344 states that "importin α1 is uniquely distributed and alters the nuclear/chromatin status when enriched in MN," however this is not currently supported by the present data. The data presented shows correlation (albeit weak) between euchromatic modifications and Importin α1, and it does not definitively show that importin α1 is sufficient to alter the nuclear-chromatin status when enriched in the MN. More substantial experiments would be required to show whether Importin α1 plays an active role in these modifications.

Minor Comments

1. Summary statement (page 3 Line 40): The use of "their" is confusing. Whose microenvironment are you referring to?
2. In Abstract and introduction (page 4, Line 44 and page 5, line 59) it states that MN are membrane enclosed structures, but this is not always the case (see https://doi.org/10.1038/nature23449 as one example).
3. Given the fact that the RIME result identified proteins involved in DNA replication to be enriched with Importin α1, are these MN enriched in factors described in Fig. 5 simply localizing to MN that are in S phase, as described previously (doi: 10.1038/nature10802)?
4. The FRAP data is not very compelling. While it is clear there are differences between the PN and MN dynamics, what is driving these differences? Are these differences meaningful to the biology of the MN or PN? It is unclear what this data is contributing to the conclusions of the paper. Also, if the mobility of the MN is plotted on the same graph as the PN, the differences in MN mobility might not look as compelling.
5. In Results (line 117), you state that "the cytoplasm of those cell lines emitted quite strong signals" for Importin α1, but that phrasing is a little confusing. Yes, Importin α1 is in present the cytoplasm in most cells, but it appears you are referring to the enrichment in MN. I would recommend re-phrasing this statement to make your intent clearer.
6. In Results (line 135, Figure S2E,F), the ratio of high, low or no Importin α1 intensity is confusing. Is this percentage relative to the total number of MN? It Is unclear what is meant by "whole number" of MN. Is Importin α1 intensity quantified or is it subjective?
7. Figure 2C is confusing. Are you counting MN with co-localization of Importin α1 and these factors? Please clarify.
8. Figure S3D quantification is very confusing and unclear. Also, how is this normalized? Are you controlling for total signal in each cell? And can the results of this experiment give you any mechanistic insight as to what is regulating MN localization beyond the interpretation of "MN localization is distinct from PN localization"? The "C-mutant" appears quite a bit different than the others. What might that indicate about the role of CAS/CSE1L in MN enrichment?
9. For Figures 3A,B and S4, are these images of single z-slices or projections? It would be helpful to clarify for your interpretations as to whether they are truly partial or diffuse or the membrane is in another z-plane. Also, how does the localization of Importin α1 different or similar to other factors that localize to MN with a compromised nuclear envelope, such as cGAS? If it is based on epigenetic marks, it should be different than cGAS, which primarily binds non-chromatinized DNA.
10. In Results, it is unclear how Fig. 7B was calculated. Are the authors qualitatively assessing if RAD51 is there or looking for MN enrichment relative to PN? Additionally, in Fig. 7C, RAD51 localization is diffuse. It should be enriched in foci. I would recommend the authors repeat this experiment using pre-extraction then quantify RAD51 foci number and/or intensity.
11. In line 264, "notably" is misspelled.
12. In line 303, "scenarios" should be changed to the singular form.
13. In Figure legend, line 571-582, H3K27me3 is shown in Figure 4D, but the written legend does not mention this mark.

Significance

Overall, this paper shows compelling evidence for micronuclear localization of regulators of nuclear export, notably Importin α1. Of note, this occurs in subsets of MN that lack an intact nuclear envelope. And while it has been appreciated that compromised micronuclear envelopes lead to genomic instability, this is one of the first that demonstrate alteration in the nuclear envelope may disrupt import or export of nuclear proteins into micronuclei.

A limitation of the study is that much of the work is based on immunofluorescence and lacks mechanism. While there is much correlative data showing that Importin α1 localizes to micronuclei with compromised envelopes, it is unclear whether Importin α1 drives micronuclear collapse or it is downstream of this process. Additionally, Importin α1 micronuclear localization anti-correlates with RAD51 but does colocalize with other DNA replication factors, yet it is unclear whether their localization is dependent on Importin α1 or its role in nuclear export. Currently, the audience for this manuscript would be focused to those interested in micronuclei. If these concerns about an active role for Importin α1 in micronuclear export are resolved, it would greatly increase the impact of this manuscript to those interested more broadly in genomic instability, DNA repair, and cancer.

Reviewer's areas of expertise: Genomic instability, cancer epigenetics, and mitosis

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Referee #1

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Miyamoto et al. report that importin α1 is highly enriched in a subfraction of micronuclei (about 40%), which exhibit defective nuclear envelopes and compromised accessibility of factors essential for the damage response associated with homologous recombination DNA repair. The authors suggest that the unequal localization and abnormal distribution of importin α1 within these micronuclei contribute to the genomic instability observed in cancer.

Major comments:

Are the key conclusions convincing?

The conclusions drawn by the authors would benefit from additional supportive experiments and a more detailed explanation. 1. It is crucial to quantitatively assess the localization of importin α1 in micronuclei (MN) across non-transformed MCM10A cells compared to transformed cell lines (MC7, HeLa, and MDA-MB-231). This analysis would help determine whether the localization of importin α1 in MN correlates with genomic stability in human cancer cells 2. While the authors provide some evidence indicating partial disruption of nuclear envelopes in MN (Figures 3 and S4), it is noteworthy that this phenomenon also occurs in importin α1-negative MN. Furthermore, according to the figure legends, the data presented in both figures stem from a single experiment. Current literature suggests that compromised nuclear envelope integrity is one of the major contributors to genomic instability, mediated through mechanisms such as chromothripsis and cGAS-STING-mediated inflammation arising from MN. Therefore, a more comprehensive quantification of nuclear envelope integrity-ideally comparing non-transformed MCM10A cells with transformed cell lines (MC7, HeLa, and MDA-MB-231)-is necessary to substantiate the connection between aberrant importin α1 behavior in MN and chromothripsis processes, as well as regulation of the cGAS-STING pathway linked to genomic instability in cancer cells. 3. The schematic illustration presented in Figure 8 does not adequately summarize all findings from this study nor does it clarify how the localization of importin α1 within MN might hypothetically influence genome stability. Although it is reasonable to propose that "importin α can serve as a molecular marker for characterizing the dynamics of MN" (Line 344), the authors assert (Line 325) that their findings, along with others, have "potential implications for the induction of chromothripsis processes and regulation of the cGAS-STING pathway in cancer cells." However, they fail to provide a clear or even hypothetical explanation regarding how their findings contribute to these molecular events. To address this gap, it would be essential for them to contextualize their results within existing literature that explores and links structural integrity deficits or aberrant DNA replication/damage responses in MN with chromothripsis and inflammation (e.g., PMID: 32601372; PMID: 32494070; PMID: 27918550; PMID: 28738408; PMID: 28759889). 4. Fig. 4D does not support the idea that importin α1 is euchromatin enriched: H3K9me3, H3K4me3 and H3K37me3 seem to be all deeply blue.

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

Indeed, the data presented by the authors do not adequately support a direct link between the presence of importin α1 in MN and genomic instability in human cancer cells. While the experimental correlations provided may not substantiate this connection definitively, they do lay a foundation for a grounded hypothesis and suggest the need for further research to explore this topic in greater depth. Additionally, it is worth noting that the evidence contributes to the growing list of nuclear proteins exhibiting abnormal behavior in micronuclei (MN). This highlights the significance of studying such proteins to understand their roles in genomic stability and cancer progression.

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

Additional experiments are necessary to quantitatively assess the localization of importin α1 in micronuclei (MN) across non-transformed MCM10A cells and transformed cell lines (MC7, HeLa, MDA-MB-231). This analysis would help determine whether the localization of importin α1 in MN correlates with genomic stability in human cancer cells. The authors claim that importin α1 preferentially localizes to euchromatic areas rather than heterochromatic regions within MN. While this assertion is supported by the immunofluorescence (IF) images presented in Figures 4A/B and S5A/B, it remains less clear for Figure S5C/B. To strengthen this claim, providing averages of IF distributions from multiple cells across independent experiments would be beneficial to draw more robust conclusions.

Furthermore, ChIP-seq data are presented to support the idea that importin α1 preferentially distributes over euchromatin areas in MN. However, as described, the epigenetic chromatin status indicated by these ChIP-seq experiments reflects that of the principal nucleus (PN), not specifically the status within MN in MCF7 cells. Given that MN represent only a small fraction of the cell population under normal culture conditions-likely less than 5% for HeLa cells as shown in Figure S2D-the relevance of this data is limited. Additionally, according to data presented in Figure 1B, importin α1 does not localize or distribute within the PN as it does in MN in MCF7 cells. Therefore, further experiments should be conducted to substantiate that importin α1 preferentially targets euchromatin areas within MN and to compare this distribution with that observed in the principal nucleus. Such studies could reveal potential abnormalities regarding the correlation between epigenetic chromatin status and importin α distribution in MN. To support the hypothesis that importin α1 inhibits RAD51 accessibility within MN, Figures 7D and E should be supplemented with thorough quantification and statistical analysis based on at least three independent experiments. This additional data would enhance confidence in their findings regarding RAD51 accessibility inhibition by importin α1.

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

The additional experiments proposed are controls and direct comparisons using the same techniques and experimental designs used by the authors, so it is reasonable that the authors can carry them out within a realistic timeframe.

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

Given the importance of reproducibility and the need to evaluate results based on imaging and quantitation, I strongly recommend that the authors include a detailed description of the optical microscopy procedures utilized in their study. This should encompass imaging conditions, acquisition settings, and the specific equipment used. Providing this information will enhance transparency and facilitate reproducibility. For reference, some valuable guidance on essential parameters for reproducibility can be found in Heddleston et al. (2021) (doi:10.1242/jcs.254144). Incorporating these details will not only strengthen the manuscript but also support other researchers in reproducing the findings accurately.

Are the experiments adequately replicated and statistical analysis adequate?

Many of the plots and values in the manuscript lack appropriate statistical analysis, including p-values, which are not detailed in the figures or their legends. Furthermore, the Statistical Analysis section does not provide adequate information regarding the specific statistical tests employed or the criteria used to determine which analyses were applied in each case. To enhance the rigor and clarity of the study, it is essential that these issues be addressed prior to publication. A comprehensive presentation of statistical analysis will improve the reliability of the findings and allow readers to better understand the significance of the results. I recommend that the authors revise this section to include detailed explanations of all statistical methods used, along with corresponding p-values for all relevant comparisons.

Minor comments:

Specific experimental issues that are easily addressable.

The authors claim that importin α1 exhibits remarkably low mobility in the micronuclei (MN) compared to its mobility in the principal nucleus (PN), as illustrated in Figure 1. However, based on the experimental design, this conclusion may not be appropriate. In the current setup, the FRAP experiment conducted in the PN measures the mobility of importin α1 molecules within the cell nucleus, where the influence of nuclear transport is likely negligible. Conversely, in the MN experiments shown, all molecules of importin α1 are bleached within a given MN. Consequently, what is being measured here primarily reflects the effects of nuclear transport rather than intrinsic molecular mobility. To accurately compare kinetics of nuclear transport, it would be essential to completely bleach the entire PN. If measuring molecular mobility between MN and PN is desired, only a small fraction of either MN or PN area/volume should be bleached during FRAP analysis. Additionally, it would be beneficial to include measurements of mobility for other canonical nuclear transport factors (e.g., RAN, CAS, RCC1) for comparative purposes. This broader context would allow for a more comprehensive understanding of importin α1 behavior relative to other factors involved in nuclear transport. Finally, utilizing cells that exhibit importin α1 signals in both PN and MN could further strengthen comparisons and provide more robust conclusions regarding its mobility dynamics.

Are prior studies referenced appropriately?

Prior studies are referenced appropriately in general, but the authors missed some references (PMID: 32601372; PMID: 32494070; PMID: 27918550; PMID: 28738408; PMID: 28759889) that I consider key to put the present findings in frame with previous works which link the lack of structural integrity and/or aberrant DNA replication/damage responses in MN with Cchromothripsis and inflammation.

Are the text and figures clear and accurate?

The figures presented in the manuscript are clear; however, where plots are included, they require appropriate statistical analysis. It is essential to display p-values on the plots or within their legends to provide readers with information regarding the significance of the results. Including this statistical information will enhance the interpretability of the data and strengthen the overall findings of the study. I recommend that the authors revise these sections accordingly before publication.

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

1. In lines 134-135, it is stated that "up to 40% of the MN showed importin α1 accumulation under both standard culture conditions and the reversine treatment (Fig. S2F)." However, Figure S2F only displays percentages for reversine-treated cells, and there is no mention in the text or figures regarding the percentage of importin α1-positive MN determined by immunofluorescence (IF) under standard culture conditions. This discrepancy should be addressed.
2. In line 170, the authors state that "Cells in which overexpressed EGFP-importin α1 localized only in PN were excluded from the analysis (see Fig. 1E, top panels)." It is unclear why this exclusion was made. The authors should clarify whether they are referring to all constructs or only to the wild-type (WT) construct when mentioning EGFP-importin α1 localization solely in PN. This clarification is important as it may affect the results highlighted in line 173.
3. The statement in line 191 ("However, this antibody could not be further used in this context due to cross-reactivity with highly concentrated importin α1 in MN (Fig. S4)") is somewhat misleading. While it hints at a technical issue, it does not provide additional relevant information for understanding its implications for the rationale of the research. Moreover, Figure S4 is referenced but appears to refer specifically to panels S4D and E, which are not mentioned in the text. I recommend clarifying this point or removing it altogether.
4. Lines 197-199 contain a sentence that could be misleading and would benefit from clearer explanation. Although Figure 3D provides some clarity on this matter, no statistical analysis is included-only a bar plot is presented. A proper statistical analysis should be provided here to enhance understanding.
5. In lines 218-221, it states that importin α1 associates with euchromatin regions characterized by H3K4me3 and H3K36me3; however, Figure 4D lacks the Spearman's correlation coefficient value for H3K36me3 within the matrix. This omission needs correction.
6. For consistency in the experimental design aimed at identifying potential importin α1-interacting proteins, it would be more appropriate for Figures 5C/D to show IF data from MCF7 cells rather than HeLa cells.
7. To substantiate claims that importin α1 inhibits RAD51 accessibility within MN, Figures 7D and E should include thorough quantitation and statistical analysis based on at least three independent experiments.
8. The meaning of lines 336-338-"Therefore, the enrichment of importin α1 in MN, along with its interaction with chromatin, may regulate the accessibility of RAD51 to DNA/chromatin fibers in MN and protect its activity"-is unclear. I suggest rephrasing this sentence for improved clarity and comprehension.
9. Fig. 1D: Numbers on the y-axis are missing, x-axis labeling is too small
10. Fig. 1F: As the PN/MN values of the three experiments are seemingly identical (third column) the distribution of the three individual data of the PN (first column) should mirror the distribution of the three individual data of the MN (second column). The authors might want to check why this is not the case.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
• Place the work in the context of the existing literature (provide references, where appropriate).

Micronuclei (MN) primarily arise from defects in mitotic progression and chromatin segregation, often associated with chromatin bridges and/or lagging chromosomes. MN frequently exhibit DNA replication defects and possess a rupture-prone nuclear envelope, which has been linked to genomic instability. The nuclear envelope of MN is notably deficient in crucial factors such as lamin B and nuclear pore complexes (NPCs). This deficiency may be attributed to the influence of microtubules and the gradient of Aurora B activity at the mitotic midzone, which inhibits the recruitment of proper nuclear envelope components. Additionally, several other factors may contribute to this process: for instance, PLK1 controls the assembly of NPC components onto lagging chromosomes; chromosome size and gene density positively correlate with the membrane stability of MN; and abnormal accumulation of the ESCRT complex on MN exacerbates DNA damage within these structures, triggering pro-inflammatory pathways. The work presented by Dr. Miyamoto and colleagues reveals the abnormal behavior of importin α1 in MN during interphase. According to their findings, it is reasonable to consider importin α1 as a molecular marker for characterizing MN dynamics. Furthermore, it could serve as a potential clinical marker if the authors provide additional experiments demonstrating significantly different localization patterns of importin α1 in transformed cells (e.g., MC7, HeLa, MDA-MB-231) compared to non-transformed cells (e.g., MCM10A). While the authors present some evidence indicating partial disruption of nuclear envelopes in MN (Figures 3 and S4), it is noteworthy that this phenomenon also occurs in importin α1-negative MN. Moreover, according to the figure legends, data for both figures originate from a single experiment. As such, convincing evidence linking the aberrant behavior of importin α1 in MN with chromothripsis processes or regulation of the cGAS-STING pathway-and its implications for genomic instability in cancer cells-remains lacking. Overall, it is not entirely clear what significance this advance holds for the field; while there are conceptual contributions made by this work, they do not appear sufficiently robust at this time. Further research is needed to clarify these connections and strengthen their conclusions regarding importin α1's role in MN dynamics and genomic instability. - State what audience might be interested in and influenced by the reported findings.

Scientist and health care professionals that research on mechanism of genomic instability and cancer - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Mitosis, mitotic chromatin decondensation, nuclear reformation, hematopoietic cancers, light microscopy, image analysis.

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Reply to the reviewers

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

This study explores chromatin organization around trans-splicing acceptor sites (TASs) in the trypanosomatid parasites Trypanosoma cruzi, T. brucei and Leishmania major. By systematically re-analyzing MNase-seq and MNase-ChIP-seq datasets, the authors conclude that TASs are protected by an MNase-sensitive complex that is, at least in part, histone-based, and that single-copy and multi-copy genes display differential chromatin accessibility. Altogether, the data suggest a common chromatin landscape at TASs and imply that chromatin may modulate transcript maturation, adding a new regulatory layer to an unusual gene-expression system.

I value integrative studies of this kind and appreciate the careful, consistent data analysis the authors implemented to extract novel insights. That said, several aspects require clarification or revision before the conclusions can be robustly supported. My main concerns are listed below, organized by topic/result section.

TAS prediction * Why were TAS predictions derived only from insect-stage RNA-seq data? Restricting TAS calls to one life stage risks biasing predictions toward transcripts that are highly expressed in that stage and may reduce annotation accuracy for lowly expressed or stage-specific genes. Please justify this choice and, if possible, evaluate TAS robustness using additional transcriptomes or explicitly state the limitation.

TAS predictions derived only from insect-stage RNA-seq data because in a previous study it was shown that there are no significant differences between stages in the 5’UTR procesing in T. cruzi life stages (https://doi.org/10.3389/fgene.2020.00166) We are not testing an additional transcriptome here, because the robustness of the software was already probed in the original article were UTRme was described (Radio S, 2018 doi:10.3389/fgene.2018.00671).

Results - "There is a distinctive average nucleosome arrangement at the TASs in TriTryps": * You state that "In the case of L. major the samples are less digested." However, Supplementary Fig. S1 suggests that replicate 1 of L. major is less digested than the T. brucei samples, while replicate 2 of L. major looks similarly digested. Please clarify which replicates you reference and correct the statement if needed.

The reviewer has a good point. We made our statement based on the value of the maximum peak of the sequenced DNA molecules, which in general is a good indicative of the extension of the digestion achieved by the sample (Cole H, NAR, 2011).

As the reviewer correctly points, we should have also considered the length of the DNA molecules in each percentile. However, in this case both, T. brucei’s and L major’s samples were gel purified before sequencing and it is hard to know exactly what fragments were left behind in each case. Therefore, it is better not to over conclude on that regard.

We have now comment on this in the main manuscript, and we have clarified in the figure legends which data set we used in each case.

* It appears you plot one replicate in Fig. 1b and the other in Suppl. Fig. S2. Please indicate explicitly which replicate is in each plot. For T. brucei, the NDR upstream of the TAS is clearer in Suppl. Fig. S2 while the TAS protection is less prominent; based on your digestion argument, this should correspond to the more-digested replicate. Please confirm.

The replicates used for the construction of each figure are explicitly indicated in Table S1. Although we have detailed in the table the original publication, the project and accession number for each data set, the reviewer is correct that in this case it was still not completely clear to which length distribution heatmap was each sample associated with. To avoid this confusion, we have now added the accession number for each data set to the figure legends and also clarified in Table S1. Regarding the reviewer’s comment on the correspondence between the observed TAS protection and the extent of samples digestion, he/she is correct that for a more digested sample we would expect a clearer NDR. In this case, the difference in the extent of digestion between these two samples is minor, as observed the length of the main peak in the length distribution histogram for sequenced DNA molecules is the same. These two samples GSM5363006, represented in Fig1 b, and GSM5363007, represented in S2, belong to the same original paper (Maree et al 2017), and both were gel purified before sequencing. Therefore, any difference between them could not only be the result of a minor difference in the digestion level achieved in each experiment but could be also biased by the fragments included or not during gel purification. Therefore, I would not over conclude about TAS protection from this comparison. We have now included a brief comment on this, in the figure discussion

* The protected region around the TAS appears centered on the TAS in T. brucei but upstream in L. major. This is an interesting difference. If it is technical (different digestion or TAS prediction offset), explain why; if likely biological, discuss possible mechanisms and implications.

We appreciate the reviewer suggestion. We cannot assure if it is due to technical or biological reasons, but there is evidence that L. major ‘s genome has a different dinucleotide content and it might have an impact on nucleosome assembly. We have now added a comment about this observation in the final discussion of the manuscript.

Results - "An MNase sensitive complex occupies the TASs in T. brucei": * The definition of "MNase activity" and the ordering of samples into Low/Intermediate/High digestion are unclear. Did you infer digestion levels from fragment distributions rather than from controlled experimental timepoints? In Suppl. Fig. S3a it is not obvious how "Low digestion" was defined; that sample's fragment distribution appears intermediate. Please provide objective metrics (e.g., median fragment length, fraction 120-180 bp) used to classify digestion levels.

As the reviewer suggests, the ideal experiment would be to perform a time course of MNase reaction with all the samples in parallel, or to work with a fixed time point adding increasing amounts of MNase. However, even when making controlled experimental timepoints, you need to check the length distribution histogram of sequenced DNA molecules to be sure which level of digestion you have achieved.

In this particular case, we used public available data sets to make this analysis. We made an arbitrary definition of low, intermediate and high level of digestion, not as an absolute level of digestion, but as a comparative output among the tested samples. We based our definition on the comparison of __the main peak in length distribution heatmaps because this parameter is the best metric to estimate the level of digestion of a given sample. It represents the percentage of the total DNA sequenced that contains the predominant length in the sample tested. __Hence, we considered:

low digestion: when the main peak is longer than the expected protection for a nucleosome (longer than 150 bp). We expect this sample to contain additional longer bands that correspond to less digested material.

intermediate digestion, when the main peak is the expected for the nucleosome core-protection (˜146-150bp).

high digestion, when the main peak is shorter than that (shorter than 146 bp). This case, is normally accompanied by a bigger dispersion in fragment sizes.

To do this analysis, we chose samples that render different MNase protection of the TAS when plotting all the sequenced DNA molecules relative to this point and we used this protection as a predictor of the extent of sample digestion (Figure 2). To corroborate our hypothesis, that the degree of TAS protection was indeed related to the extent of the MNase digestion of a given sample, we looked at the length distribution histogram of the sequenced DNA molecules in each case. It is the best measurement of the extent of the digestion achieved, especially, when sequencing the whole sample without any gel purification and representing all the reads in the analysis as we did. The only caveat is with the sample called “intermediate digestion 1” that belongs to the original work of Mareé 2017, since only this data set was gel purified.

Whether the sample used in Figure 1 (from Mareé 2017) is also from the same lab and is an MNase-seq. Strictly speaking, there is no methodological difference between MNase-seq and the input of a native MNase-ChIP-seq, since the input does not undergo the IP.

* Several fragment distributions show a sharp cutoff at ~100-125 bp. Was this due to gel purification or bioinformatic filtering? State this clearly in Methods. If gel purification occurred, that can explain why some datasets preserve the MNase-sensitive region.

The sharp cutoff is neither due to gel purification or bioinformatic filtering, it is just due to the length of the paired-end read used in each case. In earlier works the most common was to sequence only 50bp, with the improvement of technologies it went up to 75,100 or 125 bp. We have now clarified in Table S1 the length of the paired-reads used in each case when possible.

* Please reconcile cases where samples labeled as more-digested contain a larger proportion of >200 bp fragments than supposedly less-digested samples; this ordering affects the inference that digestion level determines the loss/preservation of TAS protection. Based on the distributions I see, "Intermediate digestion 1" appears most consistent with an expected MNase curve - please confirm and correct the manuscript accordingly.

As explained above, it's a common observation in MNase digestion of chromatin that more extensive digestion can still result in a broad range of fragment sizes, including some longer fragments. This seemingly counter-intuitive result is primarily due to the non-uniform accessibility of chromatin and the sequence preference of the MNase enzyme, which has a preference for AT reach sequences.

The rationale of this is as follows: when you digest chromatin with MNase and the objective is to map nucleosomes genome-wide, the ideal situation would be to get the whole material contained in the mononucleosome band. Given that MNase is less efficient to digest protected DNA but, if the reaction proceeds further, it always ends up destroying part of it, the result is always far from perfect. The better situation we can get, is to obtain samples were ˜80% of the material is contained in the mononucloesome band. __And here comes the main point: __even in the best scenario, you always get some additional longer bands, such as those for di or tri nucleosomes. If you keep digesting, you will get less than 80 % in the nucleosome band and, those remaining DNA fragments that use to contain di and tri nucleosomes start getting digested as well, originating a bigger dispersion in fragments sizes. How do we explain persistence of Long Fragments? The longest fragments (di-, tri-nucleosomes) that persist in a highly digested sample are the ones that were originally most highly protected by proteins or higher-order structure, or by containing a poor AT sequence content, making their linker DNA extremely resistant to initial cleavage. Once the majority of the genome is fragmented, these few resistant longer fragments become a more visible component of the remaining population, contributing to a broader size dispersion. Hence, you end up observing a bigger dispersion in length distributions in the final material. Bottom line, it is not a good practice to work with under or over digested samples. Our main point, is to emphasize that especially when comparing samples, it important to compare those with comparable levels of digestion. Otherwise, a different sampling of the genome will be represented in the remaining sequenced DNA.

Results - "The MNase sensitive complexes protecting the TASs in T. brucei and T. cruzi are at least partly composed of histones": * The evidence that histones are part of the MNase-sensitive complex relies on H3 MNase-ChIP signal in subnucleosomal fragment bins. This seems to conflict with the observation (Fig. 1) that fragments protecting TASs are often nucleosome-sized. Please reconcile these points: are H3 signals confined to subnucleosomal fragments flanking the TAS while the TAS itself is depleted of H3? Provide plots that compare MNase-seq and H3 ChIP signals stratified by consistent fragment-size bins to clarify this.

What we learned from other eukaryotic organisms that were deeply studied, such as yeast, is that NDRs are normally generated at regulatory points in the genome. In this sense, yeast tRNA genes have a complex with a bootprint smaller than a nucleosome formed by TFIIIC-TFIIB (Nagarajavel, doi: 10.1093/nar/gkt611). On the other hand, many promotor regions have an MNase-sensitive complex with a nucleosome-size footprint, but it does not contain histones (Chereji, et al 2017, doi:10.1016/j.molcel.2016.12.009). The reviewer is right that from Figure 1 and S2 we could observe that the footprint of whatever occupies the TAS region, especially in T. brucei, is nucleosome-size. However, it only shows the size, but it doesn’t prove the nature of its components. Nevertheless, those are only MNase-seq data sets. Since it does not include a precipitation with specific antibodies, we cannot confirm the protecting complex is made up by histones. In parallel, a complementary study by Wedel 2017, from Siegel’s lab, shows that using a properly digested sample and further immunoprecipitating with a-H3 antibody, the TAS is not protected by nucleosomes at least not when analyzing nucleosome size-DNA molecules. Besides, Briggs et. al 2018 (doi: 10.1093/nar/gky928) showed that at least at intergenic regions H3 occupancy goes down while R-loops accumulation increases. We have now added a supplemental figure associated to Figure 3 (new Suplemental 5) replotting R-loops and MNase-ChIP-seq for H3 relative to our predicted TAS showing this anti-correlation and how it partly correlates with MNase protection as well. As a control we show that Rpb9 trends resembles H3 as Siegel’s lab have shown in Wedel 2018.

* Please indicate which datasets are used for each panel in Suppl. Fig. S4 (e.g., Wedel et al., Maree et al.), and avoid calling data from different labs "replicates" unless they are true replicates.

In most of our analysis we used real replicated experiments. Such is the case MNase-seq data used in Figure 1, with the corresponding replicate experiments used in Figure S2; T. cruzi MNase-ChIP-seq data used in Figure 3b and 4a with the respective replicate used in Figures S4 and S5 (now S6 in the revised manuscript). The only case in which we used experiments coming from two different laboratories, is in the case of MNase-ChIP-seq for H3 from T. brucei. Unfortunately, there are only two public data sets coming each of them from different laboratories. The samples used in Fig 3 (from Siegel’s lab) whether the IP from H3 represented in S4 and S5 (S6 n the updated version) comes from another lab (Patterton’s). To be more rigorous, we now call them data 1 and 2 when comparing these particular case.

The reviewer is right that in this particular case one is native chromatin (Pattertons’) while the other one is crosslinked (Siegel’s). We have now clarified it in the main text that unfortunately we do not count on a replicate but even under both condition the result remains the same, and this is compatible with my own experience, were crosslinking does not affect the global nucleosome patterns (compared nucleosome organization from crosslinked chromatin MNAse-seq inputs Chereji, Mol Cell, 2017 doi: 10.1016/j.molcel.2016.12.009 and native MNase-seq from Ocampo, NAR, 2016 doi: 10.1093/nar/gkw068).

* Several datasets show a sharp lower bound on fragment size in the subnucleosomal range (e.g., ~80-100 bp). Is this a filtering artifact or a gel-size selection? Clarify in Methods and, if this is an artifact, consider replotting after removing the cutoff.

We have only filtered adapter dimmer or overrepresented sequences when needed. In Figures 2 and S3 we represented all the sequenced reads. In other figures when we sort fragments sizes in silico, such as nucleosome range, dinucleosome or subnucleosome size, we make a note in the figure legends. What the reviewer points is related to the length of the sequence DNA fragment in each experiment. As we explained above, the older data-sets were performed with 50 bp paired-end reads, the newer ones are 75, 100 or 125bp. This is information is now clarified in Table S1.

__Results - "The TASs of single and multi-copy genes are differentially protected by nucleosomes": __

__ __* Please include T. brucei RNA-seq data in Suppl. Fig. S5b as you did for T. cruzi.

We have shown chromatin organization for T. brucei in S5b to show that there is a similar trend. Unfortunately, we did not get a robust list of multi-copy genes for T. brucei as we did get for T. cruzi, therefore we do not want to over conclude showing the RNA-seq for these subsets of genes. The limitation is related to the fact that UTRme restrict the search and is extremely strict when calling sites at repetitive regions.

* Discuss how low or absent expression of multigene families affects TAS annotation (which relies on RNA-seq) and whether annotation inaccuracies could bias the observed chromatin differences.

The mapping of occurrence and annotations that belong to repetitive regions has great complexity. UTRme is specially designed to avoid overcalling those sites. In other words, there is a chance that we could be underestimating the number of predicted TASs at multi-copy genes. Regarding the impact on chromatin analysis, we cannot rule out that it might have an impact, but the observation favors our conclusion, since even when some TASs at multi-copy genes can remain elusive, we observe more nucleosome density at those places.

* The statement that multi-copy genes show an "oscillation" between AT and GC dinucleotides is not clearly supported: the multi-copy average appears noisier and is based on fewer loci. Please tone down this claim or provide statistical support that the pattern is periodic rather than noisy.

We have fixed this now in the preliminary revised version

* How were multi-copy genes defined in T. brucei? Include the classification method in Methods.

This classification was done the same way it was explained for T. cruzi

Genomes and annotations: * If transcriptomic data for the Y strain was used for T. cruzi, please explain why a Y strain genome was not used (e.g., Wang et al. 2021 GCA_015033655.1), or justify the choice. For T. brucei, consider the more recent Lister 427 assembly (Tb427_2018) from TriTrypDB. Use strain-matched genomes and transcriptomes when possible, or discuss limitations.

The most appropriate way to analyze high throughput data, is to aline it to the same genome were the experiments were conducted. This was clearly illustrated in a previous publication from our group were we explained how should be analyzed data from the hybrid CL Brener strain. A common practice in the past was to use only Esmeraldo-like genome for simplicity, but this resulted in output artifacts. Therefore, we aligned it to CL Brener genome, and then focused the main analysis on the Esmeraldo haplotype (Beati Plos ONE, 2023). Ideally, we should have counted on transcriptomic data for the same strain (CL Brener or Esmeraldo). Since this was not the case at that moment, we used data from Y strain that belongs to the same DTU with Esmeraldo.

In the case of T. brucei, when we started our analysis and the software code for UTRme was written, the previous version of the genome was available. Upon 2018 version came up, we checked chromatin parameters and observed that it did not change the main observations. Therefore, we continue working with our previous setups.

Reproducibility and broader integration: * Please share the full analysis pipeline (ideally on GitHub/Zenodo) so the results are reproducible from raw reads to plots.

We are preparing a full pipeline in GitHub. We will make it available before manuscript full revision

* As an optional but helpful expansion, consider including additional datasets (other life stages, BSF MNase-seq, ATAC-seq, DRIP-seq) where available to strengthen comparative claims.

We are now including a new suplemental figure including DRIP-seq and Rp9 ChIP-seq (revised S5). Additionally, we added a new panel c to figure 4, representing FAIRE-seq data for T. cruzi fore single and multi-copy genes

We are working on ATAC-seq analysis and BSF MNase-seq

Optional analyses that would strengthen the study: * Stratify single-copy genes by expression (high / medium / low) and examine average nucleosome occupancy at TASs for each group; a correlation between expression and NDR depth would strengthen the functional link to maturation.

We have now included a panel in suplemental figure 5 (now revised S6), showing the concordance for chromatin organization of stratified genes by RNA-seq levels relative to TAS.

__Minor / editorial comments: __ * In the Introduction, the sentence "transcription is initiated from dispersed promoters and in general they coincide with divergent strand switch regions" should be qualified: such initiation sites also include single transcription start regions.

We have clarified this in the preliminary revised version

* Define the dotted line in length distribution plots (if it is not the median, please clarify) and consider placing it at 147 bp across plots to ease comparison.

The dotted line is just to indicate where the maximum peak is located. It is now clarified in figure legends.

* In Suppl. Fig. 4b "Replicate2" the x-axis ticks are misaligned with labels - please fix.

We have now fixed the figure. Thanks for noticing this mistake.

* Typo in the Introduction: "remodellingremodeling" → "remodeling

Thanks for noticing this mistake, it is fixed in the current version of the manuscript

**Referee cross-commenting** Comment 1: I think Reviewer #2 and Reviewer #3 missed that they authors of this manuscript do cite and consider the results from Wedel at al. 2017. They even re-analysed their data (e.g. Figure 3a). I second Reviewer #2 comment indicating that the inclusion of a schematic figure to help readers visualize and better understand the findings would be an important addition.

Comment 2: I agree with Reviewer #3 that the use of different MNase digestion procedures in the different datasets have to be considered. On the other hand, I don't think there is a problem with figure 1 showing an MNase-protected TAS for T. brucei as it is based on MNase-seq data and reproduces the reported results (Maree et al. 2017). What the Siegel lab did in Wedel et al. 2017 was MNase-ChIPseq of H3 showing nucleosome depletion at TAS, but both results are not necessary contradictory: There could still be something else (which does not contain H3) sitting on the TAS protecting it from MNase digestion.

Reviewer #1 (Significance (Required)):

This study provides a systematic comparative analysis of chromatin landscapes at trans-splicing acceptor sites (TASs) in trypanosomatids, an area that has been relatively underexplored. By re-analyzing and harmonizing existing MNase-seq and MNase-ChIP-seq datasets, the authors highlight conserved and divergent features of nucleosome occupancy around TASs and propose that chromatin contributes to the fidelity of transcript maturation. The significance lies in three aspects: 1. Conceptual advance: It broadens our understanding of gene regulation in organisms where transcription initiation is unusual and largely constitutive, suggesting that chromatin can still modulate post-transcriptional processes such as trans-splicing. 2. Integrative perspective: Bringing together data from T. cruzi, T. brucei and L. major provides a comparative framework that may inspire further mechanistic studies across kinetoplastids. 3. Hypothesis generation: The findings open testable avenues about the role of chromatin in coordinating transcript maturation, the contribution of DNA sequence composition, and potential interactions with R-loops or RNA-binding proteins. Researchers in parasitology, chromatin biology, and RNA processing will find it a useful resource and a stimulus for targeted experimental follow-up.

My expertise is in gene regulation in eukaryotic parasites, with a focus on bioinformatic analysis of high-throughput sequencing data

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

Siri et al. perform a comparative analysis using publicly available MNase-seq data from three trypanosomatids (T. brucei, T. cruzi, and Leishmania), showing that a similar chromatin profile is observed at TAS (trans-splicing acceptor site) regions. The original studies had already demonstrated that the nucleosome profile at TAS differs from the rest of the genome; however, this work fills an important gap in the literature by providing the most reliable cross-species comparison of nucleosome profiles among the tritryps. To achieve this, the authors applied the same computational analysis pipeline and carefully evaluated MNase digestion levels, which are known to influence nucleosome profiling outcomes.

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. The manuscript could be improved with some clarifications and adjustments:

1. The authors state from the beginning that available MNase data indicate altered nucleosome occupancy around the TAS. However, they could also emphasize that the conclusions across the different trypanosomatids are inconsistent and even contradictory: NDR in T. cruzi versus protection-in different locations-in T. brucei and Leishmania.

We start our manuscript by referring to the first MNase-seq data sets publicly available for each TriTryp and we point that one of the main observations, in each of them, is the occurrence of a change in nucleosome density or occupancy at intergenic regions. In T. cruzi, in a previous publication from our group, we stablished that this intergenic drop in nucleosome density occurs near the trans-splicing acceptor site. In this work, we extend our study to the other members of TriTryps: T. brucei and L. major.

In T. brucei the papers from Patterton’s lab and Siegel’s lab came out almost simultaneously in 2017. Hence, they do not comment on each other’s work. The first one claims the presence of a well-positioned nucleosome at the TAS by using MNase-seq, while the second one, shows an NDR at the TAS by using MNase-ChIP-seq. However, we do not think they are contradictory, or they have inconsistency. We brought them together along the manuscript because we think these works can provide complementary information.

On one hand, we infer data from Pattertons lab is slightly less digested than the sample from Siegel’s lab. Therefore, we discuss that this moderate digestion must be the reason why they managed to detect an MNase protecting complex sitting at the TAS (Figure 1). On the other hand, Sigel’s lab includes an additional step by performing MNase-ChIP-seq, showing that when analyzing nucleosome size fragments, histones are not detected at the TAS. Here, we go further in this analysis on figure 3, showing that only when looking at subnucleosome-size fragments, we are able to detect histone H3. And this is also true for T. cruzi.

By integrating every analysis in this work and the previous ones, we propose that TASs are protected by an MNase-sensitive complex (probed in Figure 2). This complex most likely is only partly formed by histones, since only when analyzing sub-nucleosomes size DNA molecules we can detect histone H3 (Figure 3). To be absolutely sure that the complex is not entirely made up by histones, future studies should perform an MNse-ChIP-seq with less digested samples. However, it was previously shown that R-loops are enriched at those intergenic NDRs (Briggs, 2018 doi: 10.1093/nar/gky928) and that R-loops have plenty of interacting proteins (Girasol, 2023 10.1093/nar/gkad836). Therefore, most likely, this MNase-sensitive complexed have a hybrid nature made up by H3 and some other regulatory molecules, possibly involved in trans-splicing. We have now added a new figure S5 showing R-loop co-localization with the NDR.

Regarding the comparison between different organisms, after explaining the sensitivity to MNase of the TAS protecting complex, we discuss that when comparing equally digested samples T. cruzi and T. brucei display a similar chromatin landscape with a mild NDR at the TAS (See T. cruzi represented in Figure 1 compared to T. brucei represented in Intermediate digestion 2 in Figure 2, intermediate digestion in the revised manuscript). Unfortunately, we cannot make a good comparison with L. major, since we do not count on a similar level of digestion.

Another point that requires clarification concerns what the authors mean in the introduction and discussion when they write that trypanosomes have "...poorly organized chromatin with nucleosomes that are not strikingly positioned or phased." On the other hand, they also cite evidence of organization: "...well-positioned nucleosome at the spliced-out region.. in Leishmania (ref 34)"; "...a well-positioned nucleosome at the TASs for internal genes (ref37)"; "...a nucleosome depletion was observed upstream of every gene (ref 35)." Aren't these examples of organized chromatin with at least a few phased nucleosomes? In addition, in ref 37, figure 4 shows at least two (possibly three to four) nucleosomes that appear phased. In my opinion, the authors should first define more precisely what they mean by "poorly organized chromatin" and clarify that this interpretation does not contradict the findings highlighted in the cited literature.

For a better understanding of nucleosome positioning and phasing I recommend the review: Clark 2010 doi:10.1080/073911010010524945, Figure 4. Briefly, in a cell population there are different alternative positions that a given nucleosome can adopt. However, some are more favorable. When talking about favorable positions, we refer to the coordinates in the genome that are most likely covered by a nucleosome and are predominant in the cell population. Additionally, nucleosomes could be phased or not. This refers not only the position in the genome, but to the distance relative to a given point. In yeast, or in highly transcribed genes of more complex eukaryotes, nucleosomes are regularly spaced and phased relative to the transcription start site (TSS) or to the +1 nucleosome (Ocampo, NAR, 2016, doi:10.1093/nar/gkw068). In trypanosomes, nucleosomes have some regular distribution when making a browser inspection but, given that they are not properly phased with respect to any point, it is almost impossible to make a spacing estimation from paired-end data. This is also consistent with a chromatin that is transcribed in an almost constitutive manner.

As the reviewer mention, we do site evidence of organization. We think the original observations are correct, but we do not fully agree with some of the original statements. In this manuscript our aim is to take the best we learned from their original works and to make a constructive contribution adding to the original discussions. In this regard, in trypanosomes there are some conserved patterns in the chromatin landscape, but their nucleosomes are far from being well-positioned or phased. For a better understanding, compare the variations observed in the y axis when representing av. nucleosome occupancy in yeast with those observed in trypanosomes and you will see that the troughs and peaks are much more prominent in yeast than the ones observed in any TryTryp member.

Following the reviewer’s suggestion we have now clarified this in the main text

The paper would also benefit from the inclusion of a schematic figure to help readers visualize and better understand the findings. What is the biological impact of having nucleosomes, di-nucleosomes, or sub-nucleosomes at TAS? This is not obvious to readers outside the chromatin field. For example, the following statement is not intuitive: "We observed that, when analyzing nucleosome-size (120-180 bp) DNA molecules or longer fragments (180-300 bp), the TASs of either T. cruzi or T. brucei are mostly nucleosome-depleted. However, when representing fragments smaller than a nucleosome-size (50-120 bp) some histone protection is unmasked (Fig. 3 and Fig. S4). This observation suggests that the MNase sensitive complex sitting at the TASs is at least partly composed of histones." Please clarify.

We appreciate the reviewer’s suggestion to make a schematic figure. We are working on this and will be added to the manuscript upon final revision.

Regarding the biological impact of having mono, di or subnucleosome fragments, it is important to unveil the fragment size of the protected DNA to infer the nature of the protecting complex. In the case of tRNA genes in yeast, at pol III promoters they found footprints smaller than a nucleosome size that ended up being TFIIB-TFIIC (Nagarajavel, doi: 10.1093/nar/gkt611). Therefore, detecting something smaller than a nucleosome might suggest the binding of trans-acting factors different than histones or involving histones in a mixed complex. These mixed complexes are also observed, and that is the case of the centromeric nucleosome which has a very peculiar composition (Ocampo and Clark, Cells Reports, 2015). On the other hand, if instead we detect bigger fragments, it could be indicative of the presence of bigger protecting molecules or that those regions are part of higher order chromatin organization still inaccessible for MNase linker digestions.

Here we show on 2Dplots, that complex or components protecting the TAS have nucleosome size, but we cannot assure they are entirely made up by histones, since, only when looking at subnucleosome-size fragments, we are able to detect histone H3. We have now added part of this explanation to the discussion.

By integrating every analysis in this work and the previous ones, we propose that the TAS is protected by an MNase-sensitive complex (Figure 2). This complex most likely is only partly formed by histones, since only when analyzing sub-nucleosomes size DNA molecules we can detect histone H3 (Figure 3). As explained above, to be absolutely sure that the complex is not entirely made up by histones, future studies should perform an MNse-ChIP-seq with less digested samples. However, it was previously shown that R-loops are enriched at those intergenic NDRs (Briggs 2018) and that R-loops have plenty of interacting proteins (Girasol, 2023). Therefore, most likely, this MNase-sensitive complexed have a hybrid nature made up by H3 and some other regulatory molecules. We have now added a new S5 figure showing R-loop co-localization.

Some references are missing or incorrect:

we will make a thorough revision

"In trypanosomes, there are no canonical promoter regions." - please check Cordon-Obras et al. (Navarro's group). Thank you for the appropiate suggestion.

We have now added this reference

Please, cite the study by Wedel et al. (Siegel's group), which also performed MNase-seq analysis in T. brucei.

We understand that reviewer number 2# missed that we cited this reference and that we did used the raw data from the manuscript of Wedel et. al 2017 form Siegel’s group. We used the MNase-ChIP-seq data set of histone H3 in our analysis for Figures 3, S4b and S5b (S6c in the revised version), also detailed in table S1. To be even more explicit we have now included the accession number of each data set in the figure legend.

Figure-specific comments: Fig. S3: Why does the number of larger fragments increase with greater MNase digestion? Shouldn't the opposite be expected?

This a good observation. As we also explained to reviewer#1:

It's a common observation in MNase digestion of chromatin that more extensive digestion can still result in a broad range of fragment sizes, including some longer fragments. This seemingly counter-intuitive result is primarily due to the non-uniform accessibility of chromatin and the sequence preference of the MNase enzyme.

The rationale of this is as follows: when you digest chromatin with MNase and the objective is to map nucleosomes genome-wide, the ideal situation would to get the whole material contained in the mononucleosome band. Given that MNase is less efficient to digest protected DNA but, if the reaction proceeds further, it always ends up destroying part of it, the result is always far from perfect. The better situation we can get, is to obtain samples were ˜80% of the material is contained in the mononucloesome band. __And here comes the main point: __even in the best scenario, you always have some additional longer bands, such as those for di or tri nucleosomes. If you keep digesting, you will get less than 80 % in the nucleosome band and, those remaining DNA fragments that use to contain di and tri nucleosomes start getting digested as well originating a bigger dispersion in fragments sizes. How do we explain persistence of Long Fragments? The longest fragments (di-, tri-nucleosomes) that persist in a highly digested sample are the ones that were originally most highly protected by proteins or higher-order structure, making their linker DNA extremely resistant to initial cleavage. Once the majority of the genome is fragmented, these few resistant longer fragments become a more visible component of the remaining population, contributing to a broader size dispersion. Hence, there you end up having a bigger dispersion in length distributions in the final material. Bottom line, it is not a good practice to work with under or overdigested samples. Our main point is to emphasize that especially when comparing samples, it important to compare those with comparable levels of digestion. Otherwise, a different sampling of the genome will be represented in the remaining sequenced DNA Fig. S5B: Why not use MNase conditions under which T. cruzi and T. brucei display comparable profiles at TAS? This would facilitate interpretation.

The reviewer made a reasonable observation. The reason why we used MNase-ChIP_seq instead of just MNase to test occupancy at TAS at the subsets of genes, is because we intended to be more certain if we were talking about the presence of histones or something else. By using IP for histone H3 we can see that at multi-copy genes this protein is present when looking at nucleosome-size fragments. Additionally, as shown in figure S4b, length distribution histograms are also similar for the compared IPs.

Minor points:

There are several typos throughout the manuscript.

Thanks for the observation. We will check carefully.

Methods: "Dinucelotide frecuency calculation."

We will add a code in GitHub

Reviewer #2 (Significance (Required)):

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. Audience: basic science and specialized readers.

Expertise: epigenetics and gene expression in trypanosomatids.

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

The authors analysed publicly accessible MNase-seq data in TriTryps parasites, focusing on the chromatin structure around trans-splicing acceptor sites (TASs), which are vital for processing gene transcripts. They describe a mild nucleosome depletion at the TAS of T. cruzi and L. major, whereas a histone-containing complex protects the TASs of T. brucei. In the subsequent analysis of T. brucei, they suggest that a Mnase-sensitive complex is localised at the TASs. For single-copy versus multi-copy genes, the authors show different di-nucleotide patterns and chromatin structures. Accordingly, they propose this difference could be a novel mechanism to ensure the accuracy of trans-splicing in these parasites.

Before providing an in- depth review of the manuscript, I note that some missing information would have helped in assessing the study more thoroughly; however, in the light of the available information, I provide the following comments for consideration.

The numbering of the figures, including the figure legends, is missing in the PDF file. This is essential for assessing the provided information.

We apologized for not including the figure numbers in the main text, although they are located in the right place when called in the text. The omission was unwillingly made when figure legends were moved to the bottom of the main text. This is now fixed in the updated version of the manuscript.

The publicly available Mnase- seq data are manyfold, with multiple datasets available for T. cruzi, for example. It is unclear from the manuscript which dataset was used for which figure. This must be clarified.

This was detailed in Table S1. We have now replaced the table by an improved version, and we have also included the accession number of each data set used in the figure legends.

Why do the authors start in figure 1 with the description of an MNase- protected TAS for T.brucei, given that it has been clearly shown by the Siegel lab that there is a nucleosome depletion similar to other parasites?

We did not want to ignore the paper from Patterton’s lab because it was the first one to map nucleosomes genome-wide in T. brucei and the main finding of that paper claimed the existence of a well-positioned nucleosome at intergenic regions, what we though constitutes a point worth to be discussed. While Patterton’s work use MNase-seq from gel-purified samples and provides replicated experiments sequenced in really good depth; Siegel’s lab uses MNase-ChIP-seq of histone H3 but performs only one experiment and its input was not sequenced. So, each work has its own caveats and provides different information that together contributes to make a more comprehensive study. We think that bringing up both data sets to the discussion, as we have done in Figures 1 and 3, helps us and the community working in the field to enrich the discussion.

If the authors re- analyse the data, they should compare their pipeline to those used in the other studies, highlighting differences and potential improvements.

We are working on this point. We will provide a more detail description in the final revision.

Since many figures resemble those in already published studies, there seems little reason to repeat and compare without a detailed comparison of the pipelines and their differences.

Following the reviewer advice, we are now working on highlighting the main differences that justify analyzing the data the way we did and will be added in the finally revised method section.

At a first glance, some of the figures might look similar when looking at the original manuscripts comparing with ours. However, with a careful and detailed reading of our manuscripts you can notice that we have added several analyses that allow to unveil information that was not disclosed before.

First, we perform a systematic comparison analyzing every data set the same way from beginning to end, being the main difference with previous studies the thorough and precise prediction of TAS for the three organisms. Second, we represent the average chromatin organization relative to those predicted TASs for TriTryps and discuss their global patterns. Third, by representing the average chromatin into heatmaps, we show for the very first time, that those average nucleosome landscape are not just an average, they keep a similar organization in most of the genome. These was not done in any of the previous manuscripts except for our own (Beati, PLOS One 2023). Additionally, we introduce the discussion of how the extension of MNase reaction can affect the output of these experiments and we show 2D-plots and length distribution heatmaps to discuss this point (a point completely ignored in all the chromatin literature for trypanosomes). Furthermore, we made a far-reaching analysis by considering the contributions of each publish work even when addressed by different techniques. Finally, we discuss our findings in the context of a topic of current interest in the field, such as TriTryp’s genome compartmentalization.

Several previous Mnase- seq analysis studies addressing chromatin accessibility emphasized the importance of using varying degrees of chromatin digestion, from low to high digestion (30496478, 38959309, 27151365).

The reviewer is correct, and this point is exactly what we intended to illustrate in figure number 2. We appreciate he/she suggests these references that we are now citing in the final discussion. Just to clarify, using varying degrees of chromatin digestion is useful to make conclusions about a given organism but when comparing samples, strains, histone marks, etc. It is extremely important to do it upon selection of similar digested samples.

No information on the extent of DNA hydrolysis is provided in the original Mnase- seq studies. This key information can not be inferred from the length distribution of the sequenced reads.

The reviewer is correct that “No information on the extent of DNA hydrolysis is provided in the original Mnase-seq studies” and this is another reason why our analysis is so important to be published and discussed by the scientific community working in trypanosomes. We disagree with the reviewer in the second statement, since the level of digestion of a sequenced sample is actually tested by representing the length distribution of the total DNA sequenced. It is true that before sequencing you can, and should, check the level of digestion of the purified samples in an agarose gel and/or in a bioanalyzer. It could be also tested after library preparation, but before sequencing, expecting to observe the samples sizes incremented in size by the addition of the library adapters. But, the final test of success when working with MNase digested samples is to analyze length of DNA molecules by representing the histograms with length distribution of the sequenced DNA molecules. Remarkably, on occasions different samples might look very similar when run in a gel, but they render different length distribution histograms and this is because the nucleosome core could be intact but they might have suffered a differential trimming of the linker DNA associated to it or even be chewed inside (see Cole Hope 2011, section 5.2, doi: 10.1016/B978-0-12-391938-0.00006-9, for a detailed explanation).

As the input material are selected, in part gel- purified mono- nucleosomal DNA bands. Furthermore the datasets are not directly comparable, as some use native MNase, while others employ MNase after crosslinking; some involve short digestion times at 37 {degree sign} C, while others involve longer digestion at lower temperatures. Combining these datasets to support the idea of an MNase- sensitive complex at the TAS of T. brucei therefore may not be appropriate, and additional experiments using consistent methodologies would strengthen the study's conclusions.

In my opinion, describing an MNase- sensitive complex based solely on these data is not feasible. It requires specifically designed experiments using a consistent method and well- defined MNase digestion kinetics.

As the reviewer suggests, the ideal experiment would be to perform a time course of MNase reaction with all the samples in parallel, or to work with a fix time point adding increasing amounts of MNase. However, the information obtained from the detail analysis of the length distribution histogram of sequenced DNA molecules the best test of the real outcome. In fact, those samples with different digestion levels were probably not generated on purpose.

The only data sets that were gel purified are those from Mareé 2017 (Patterton’s lab), used in Figures 1, S1 and S2 and those from L. major shown in Fig 1. It was a common practice during those years, then we learned that is not necessary to gel purify, since we can sort fragment sizes later in silico when needed.

As we explained to reviewer #1, to avoid this conflict, we decided to remove this data from figures 2 and S3. In summary, the 3 remaining samples comes from the same lab, and belong to the same publication (Mareé 2022). These sample are the inputs of native MNase ChIp-seq, obtain the same way, totally comparable among each other.

Reviewer #3 (Significance (Required)):

Due to the lack of controlled MNase digestion, use of heterogeneous datasets, and absence of benchmarking against previous studies, the conclusions regarding MNase-sensitive complexes and their functional significance remain speculative. With standardized MNase digestion and clearly annotated datasets, this study could provide a valuable contribution to understanding chromatin regulation in TriTryps parasites.

As we have explained in the previous point our conclusions are valid since we do not compare in any figure samples coming from different treatments. The only exception to this comment could be in figure 3 when talking about MNase-ChIP-seq. We have now added a clear and explicit comment in the section and the discussion that despite having subtle differences in experimental procedures we arrive to the same results. This is the case for T. cruzi IP, run from crosslinked chromatin, compared to T. brucei’s IP, run from native chromatin.

Along the years it was observed in the chromatin field that nucleosomes are so tightly bound to DNA that crosslinking is not necessary. However, it is still a common practice specially when performing IPs. In our own hands, we did not observe any difference at the global level neither in T. cruzi or in my previous work with yeast.

...

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Referee #3

Evidence, reproducibility and clarity

The authors analysed publicly accessible MNase-seq data in TriTryps parasites, focusing on the chromatin structure around trans-splicing acceptor sites (TASs), which are vital for processing gene transcripts. They describe a mild nucleosome depletion at the TAS of T. cruzi and L. major, whereas a histone-containing complex protects the TASs of T. brucei. In the subsequent analysis of T. brucei, they suggest that a Mnase-sensitive complex is localised at the TASs. For single-copy versus multi-copy genes, the authors show different di-nucleotide patterns and chromatin structures. Accordingly, they propose this difference could be a novel mechanism to ensure the accuracy of trans-splicing in these parasites.

Before providing an in- depth review of the manuscript, I note that some missing information would have helped in assessing the study more thoroughly; however, in the light of the available information, I provide the following comments for consideration.

The numbering of the figures, including the figure legends, is missing in the PDF file. This is essential for assessing the provided information. The publicly available Mnase- seq data are manyfold, with multiple datasets available for T. cruzi, for example. It is unclear from the manuscript which dataset was used for which figure. This must be clarified. Why do the authors start in figure 1 with the description of an MNase- protected TAS for T.brucei, given that it has been clearly shown by the Siegel lab that there is a nucleosome depletion similar to other parasites? If the authors re- analyse the data, they should compare their pipeline to those used in the other studies, highlighting differences and potential improvements. Since many figures resemble those in already published studies, there seems little reason to repeat and compare without a detailed comparison of the pipelines and their differences. Several previous Mnase- seq analysis studies addressing chromatin accessibility emphasised the importance of using varying degrees of chromatin digestion, from low to high digestion (30496478, 38959309, 27151365). No information on the extent of DNA hydrolysis is provided in the original Mnase- seq studies. This key information can not be inferred from the length distribution of the sequenced reads. As the input material are selected, in part gel- purified mono- nucleosomal DNA bands. Furthermore the datasets are not directly comparable, as some use native MNase, while others employ MNase after crosslinking; some involve short digestion times at 37 {degree sign} C, while others involve longer digestion at lower temperatures. Combining these datasets to support the idea of an MNase- sensitive complex at the TAS of T. brucei therefore may not be appropriate, and additional experiments using consistent methodologies would strengthen the study's conclusions. In my opinion, describing an MNase- sensitive complex based solely on these data is not feasible. It requires specifically designed experiments using a consistent method and well- defined MNase digestion kinetics.

Significance

Due to the lack of controlled MNase digestion, use of heterogeneous datasets, and absence of benchmarking against previous studies, the conclusions regarding MNase-sensitive complexes and their functional significance remain speculative. With standardized MNase digestion and clearly annotated datasets, this study could provide a valuable contribution to understanding chromatin regulation in TriTryps parasites.

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Referee #2

Evidence, reproducibility and clarity

Siri et al. perform a comparative analysis using publicly available MNase-seq data from three trypanosomatids (T. brucei, T. cruzi, and Leishmania), showing that a similar chromatin profile is observed at TAS (trans-splicing acceptor site) regions. The original studies had already demonstrated that the nucleosome profile at TAS differs from the rest of the genome; however, this work fills an important gap in the literature by providing the most reliable cross-species comparison of nucleosome profiles among the tritryps. To achieve this, the authors applied the same computational analysis pipeline and carefully evaluated MNase digestion levels, which are known to influence nucleosome profiling outcomes.

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms. The manuscript could be improved with some clarifications and adjustments:

1. The authors state from the beginning that available MNase data indicate altered nucleosome occupancy around the TAS. However, they could also emphasize that the conclusions across the different trypanosomatids are inconsistent and even contradictory: NDR in T. cruzi versus protection-in different locations-in T. brucei and Leishmania.
2. Another point that requires clarification concerns what the authors mean in the introduction and discussion when they write that trypanosomes have "...poorly organized chromatin with nucleosomes that are not strikingly positioned or phased." On the other hand, they also cite evidence of organization: "...well-positioned nucleosome at the spliced-out region.. in Leishmania (ref 34)"; "...a well-positioned nucleosome at the TASs for internal genes (ref37)"; "...a nucleosome depletion was observed upstream of every gene (ref 35)." Aren't these examples of organized chromatin with at least a few phased nucleosomes? In addition, in ref 37, figure 4 shows at least two (possibly three to four) nucleosomes that appear phased. In my opinion, the authors should first define more precisely what they mean by "poorly organized chromatin" and clarify that this interpretation does not contradict the findings highlighted in the cited literature.
3. The paper would also benefit from the inclusion of a schematic figure to help readers visualize and better understand the findings. What is the biological impact of having nucleosomes, di-nucleosomes, or sub-nucleosomes at TAS? This is not obvious to readers outside the chromatin field. For example, the following statement is not intuitive: "We observed that, when analyzing nucleosome-size (120-180 bp) DNA molecules or longer fragments (180-300 bp), the TASs of either T. cruzi or T. brucei are mostly nucleosome-depleted. However, when representing fragments smaller than a nucleosome-size (50-120 bp) some histone protection is unmasked (Fig. 3 and Fig. S4). This observation suggests that the MNase sensitive complex sitting at the TASs is at least partly composed of histones." Please clarify. Some references are missing or incorrect:

"In trypanosomes, there are no canonical promoter regions." - please check Cordon-Obras et al. (Navarro's group).

Please, cite the study by Wedel et al. (Siegel's group), which also performed MNase-seq analysis in T. brucei.

Figure-specific comments:

Fig. S3: Why does the number of larger fragments increase with greater MNase digestion? Shouldn't the opposite be expected?

Fig. S5B: Why not use MNase conditions under which T. cruzi and T. brucei display comparable profiles at TAS? This would facilitate interpretation.

Minor points:

There are several typos throughout the manuscript.

Methods: "Dinucelotide frecuency calculation."

Significance

In my view, the main conclusion is that the profiles are indeed similar-even when comparing T. brucei and T. cruzi. This was not clear in previous studies (and even appeared contradictory, reporting nucleosome depletion versus enrichment) largely due to differences in chromatin digestion across these organisms.

Audience: basic science and specialized readers.

Expertise: epigenetics and gene expression in trypanosomatids.

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Referee #1

Evidence, reproducibility and clarity

This study explores chromatin organization around trans-splicing acceptor sites (TASs) in the trypanosomatid parasites Trypanosoma cruzi, T. brucei and Leishmania major. By systematically re-analyzing MNase-seq and MNase-ChIP-seq datasets, the authors conclude that TASs are protected by an MNase-sensitive complex that is, at least in part, histone-based, and that single-copy and multi-copy genes display differential chromatin accessibility. Altogether, the data suggest a common chromatin landscape at TASs and imply that chromatin may modulate transcript maturation, adding a new regulatory layer to an unusual gene-expression system.

I value integrative studies of this kind and appreciate the careful, consistent data analysis the authors implemented to extract novel insights. That said, several aspects require clarification or revision before the conclusions can be robustly supported. My main concerns are listed below, organized by topic/result section.

TAS prediction:

• Why were TAS predictions derived only from insect-stage RNA-seq data? Restricting TAS calls to one life stage risks biasing predictions toward transcripts that are highly expressed in that stage and may reduce annotation accuracy for lowly expressed or stage-specific genes. Please justify this choice and, if possible, evaluate TAS robustness using additional transcriptomes or explicitly state the limitation.

Results

• "There is a distinctive average nucleosome arrangement at the TASs in TriTryps":
• You state that "In the case of L. major the samples are less digested." However, Supplementary Fig. S1 suggests that replicate 1 of L. major is less digested than the T. brucei samples, while replicate 2 of L. major looks similarly digested. Please clarify which replicates you reference and correct the statement if needed.
• It appears you plot one replicate in Fig. 1b and the other in Suppl. Fig. S2. Please indicate explicitly which replicate is in each plot. For T. brucei, the NDR upstream of the TAS is clearer in Suppl. Fig. S2 while the TAS protection is less prominent; based on your digestion argument, this should correspond to the more-digested replicate. Please confirm. The protected region around the TAS appears centered on the TAS in T. brucei but upstream in L. major. This is an interesting difference. If it is technical (different digestion or TAS prediction offset), explain why; if likely biological, discuss possible mechanisms and implications.

Results

• "An MNase sensitive complex occupies the TASs in T. brucei":
• The definition of "MNase activity" and the ordering of samples into Low/Intermediate/High digestion are unclear. Did you infer digestion levels from fragment distributions rather than from controlled experimental timepoints? In Suppl. Fig. S3a it is not obvious how "Low digestion" was defined; that sample's fragment distribution appears intermediate. Please provide objective metrics (e.g., median fragment length, fraction 120-180 bp) used to classify digestion levels.
• Several fragment distributions show a sharp cutoff at ~100-125 bp. Was this due to gel purification or bioinformatic filtering? State this clearly in Methods. If gel purification occurred, that can explain why some datasets preserve the MNase-sensitive region.
• Please reconcile cases where samples labeled as more-digested contain a larger proportion of >200 bp fragments than supposedly less-digested samples; this ordering affects the inference that digestion level determines the loss/preservation of TAS protection. Based on the distributions I see, "Intermediate digestion 1" appears most consistent with an expected MNase curve - please confirm and correct the manuscript accordingly. Results - "The MNase sensitive complexes protecting the TASs in T. brucei and T. cruzi are at least partly composed of histones":
• The evidence that histones are part of the MNase-sensitive complex relies on H3 MNase-ChIP signal in subnucleosomal fragment bins. This seems to conflict with the observation (Fig. 1) that fragments protecting TASs are often nucleosome-sized. Please reconcile these points: are H3 signals confined to subnucleosomal fragments flanking the TAS while the TAS itself is depleted of H3? Provide plots that compare MNase-seq and H3 ChIP signals stratified by consistent fragment-size bins to clarify this.
• Please indicate which datasets are used for each panel in Suppl. Fig. S4 (e.g., Wedel et al., Maree et al.), and avoid calling data from different labs "replicates" unless they are true replicates.
• Several datasets show a sharp lower bound on fragment size in the subnucleosomal range (e.g., ~80-100 bp). Is this a filtering artifact or a gel-size selection? Clarify in Methods and, if this is an artifact, consider replotting after removing the cutoff. Results - "The TASs of single and multi-copy genes are differentially protected by nucleosomes":
• Please include T. brucei RNA-seq data in Suppl. Fig. S5b as you did for T. cruzi.
• Discuss how low or absent expression of multigene families affects TAS annotation (which relies on RNA-seq) and whether annotation inaccuracies could bias the observed chromatin differences.
• The statement that multi-copy genes show an "oscillation" between AT and GC dinucleotides is not clearly supported: the multi-copy average appears noisier and is based on fewer loci. Please tone down this claim or provide statistical support that the pattern is periodic rather than noisy.
• How were multi-copy genes defined in T. brucei? Include the classification method in Methods.

Genomes and annotations:

• If transcriptomic data for the Y strain was used for T. cruzi, please explain why a Y strain genome was not used (e.g., Wang et al. 2021 GCA_015033655.1), or justify the choice. For T. brucei, consider the more recent Lister 427 assembly (Tb427_2018) from TriTrypDB. Use strain-matched genomes and transcriptomes when possible, or discuss limitations.

Reproducibility and broader integration:

• Please share the full analysis pipeline (ideally on GitHub/Zenodo) so the results are reproducible from raw reads to plots.
• As an optional but helpful expansion, consider including additional datasets (other life stages, BSF MNase-seq, ATAC-seq, DRIP-seq) where available to strengthen comparative claims. Optional analyses that would strengthen the study:
• Stratify single-copy genes by expression (high / medium / low) and examine average nucleosome occupancy at TASs for each group; a correlation between expression and NDR depth would strengthen the functional link to maturation.

Minor / editorial comments:

• In the Introduction, the sentence "transcription is initiated from dispersed promoters and in general they coincide with divergent strand switch regions" should be qualified: such initiation sites also include single transcription start regions.
• Define the dotted line in length distribution plots (if it is not the median, please clarify) and consider placing it at 147 bp across plots to ease comparison.
• In Suppl. Fig. 4b "Replicate2" the x-axis ticks are misaligned with labels - please fix.
• Typo in the Introduction: "remodellingremodeling" → "remodeling."

Referee cross-commenting

Comment 1: I think Reviewer #2 and Reviewer #3 missed that they authors of this manuscript do cite and consider the results from Wedel at al. 2017. They even re-analysed their data (e.g. Figure 3a). I second Reviewer #2 comment indicating that the inclusion of a schematic figure to help readers visualize and better understand the findings would be an important addition.

Comment 2: I agree with Reviewer #3 that the use of different MNase digestion procedures in the different datasets have to be considered. On the other hand, I don't think there is a problem with figure 1 showing an MNase-protected TAS for T. brucei as it is based on MNase-seq data and reproduces the reported results (Maree et al. 2017). What the Siegel lab did in Wedel et al. 2017 was MNase-ChIPseq of H3 showing nucleosome depletion at TAS, but both results are not necessary contradictory: There could still be something else (which does not contain H3) sitting on the TAS protecting it from MNase digestion.

Significance

This study provides a systematic comparative analysis of chromatin landscapes at trans-splicing acceptor sites (TASs) in trypanosomatids, an area that has been relatively underexplored. By re-analyzing and harmonizing existing MNase-seq and MNase-ChIP-seq datasets, the authors highlight conserved and divergent features of nucleosome occupancy around TASs and propose that chromatin contributes to the fidelity of transcript maturation.

The significance lies in three aspects:

1. Conceptual advance: It broadens our understanding of gene regulation in organisms where transcription initiation is unusual and largely constitutive, suggesting that chromatin can still modulate post-transcriptional processes such as trans-splicing.
2. Integrative perspective: Bringing together data from T. cruzi, T. brucei and L. major provides a comparative framework that may inspire further mechanistic studies across kinetoplastids.
3. Hypothesis generation: The findings open testable avenues about the role of chromatin in coordinating transcript maturation, the contribution of DNA sequence composition, and potential interactions with R-loops or RNA-binding proteins. Researchers in parasitology, chromatin biology, and RNA processing will find it a useful resource and a stimulus for targeted experimental follow-up.

My expertise is in gene regulation in eukaryotic parasites, with a focus on bioinformatic analysis of high-throughput sequencing data

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Reply to the reviewers

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Reply to the Reviewers

We thank the reviewers for their positive assessments overall and for many helpful suggestions for clarification to make the manuscript more accessible to a broader audience. We made minor text changes and added more labels to the figures to address these comments.

• *

__Referee #1

__

Summary: In this study, the authors show a genetic interaction of the lipid receptors Lpr-1, Lpr-3 and Scav-2 in C. elegans. They show that Lpr-1 loss-of-function specifically affects aECM localization of Lpr-3 and attribute the lethality of Lpr-1 mutants to this phenotype. The authors performed a mutagenesis screen and identified a third lipid receptor, Scav-2, as a modulating factor: loss of scav-2 partially rescues the Lpr-1 phenotype. The authors created a variety of tools for this study, notably Crispr-Cas9-mediated knock-ins for endogenous tagging of the receptors.

Major comments:

1. while the authors provide a nice diagram showing the potential roles and interplay of lpr-1, lpr-3 and scav-2, it remains unclear what their respective cargo is. The nature of interaction between the proteins remains unclear from the data.

Response

• We agree that identifying the relevant cargo(s) will be key to understanding the detailed mechanisms involved and that the lack of such information is a limitation of our study. However, the impact of our study is to show that these lipid transporters functionally interact to affect aECM organization, a role that could be relevant to many systems, including humans.

As an optional (since time-consuming) experiment I would suggest trying more tissue-specific lipidomics.

Response

• This would be an interesting future experiment but is outside our current technical capabilities.

The lipidomics data should be presented in the figures, even if there were no significant changes. Importantly, show the lipid abundance at least of total lipids, better of individual classes, normalized to the material input (e.g. number of embryos, protein).

Response

• The reviewer is right to point out that lipid variations could occur at different levels, and that we should exercise caution. However, the unsupervised lipidomics analysis would have detected not only individual lipid variations, but also variations in the total or subgroup lipid content. Indeed, the eggs were weighed prior to extraction and each sample was extracted with the same precise volume of solvent before analysis. Furthermore, the LC-MS/MS injection sequence included blanks and quality control (QC) samples. The blanks were the extraction solvent, which allowed us to control for features unrelated to the biological samples. The QC sample was a mixture of all the samples included in the injection sequence, reflecting the central values of the model. If a subclass of samples, such as the lpr-1 mutant, had been characterized by a decrease in one lipid, a subgroup of lipids, or all lipids, it would have clustered separately. Instead, our PCA showed that the variation between samples of the same genotype (wild type, lpr-1 mutant, or lpr-1; scav-2) was similar to the variation between samples from two different genotypes. This means that we did not detect modifications to lipid quantity specifically or in total. A figure illustrating the lipid contents would show no difference between groups.

Figure 1g: I do not understand what the lpr3:gfp signal is: the punctae in the overview image? and where are they in the zoom image showing anulli and alae? Also, how where the anulli and alae structures labeled? please provide more information

Response

• All of the fluorescent signal shown in this figure panel corresponds to the indicated LPR fusion - no other labelling method was used. SfGFP::LPR-3 labels the matrix structures (alae and annuli) as well as some puncta – the ratio of matrix to puncta changes over developmental stages. We edited the figure legend to make this more clear.

One point that is not sufficiently adressed is that the authors deduce from the inability of the scav-2 gfp knock in to suppress lpr1 lethality that scav2 function is not impaired. This is quite indirect. Can the authors provide more convincing evidence that scav-2 ki has normal function?

Response

• Suppression of lpr-1 (or other aECM mutant) lethality is the only known phenotype caused by loss of scav-2 Therefore, this is the only phenotype for which we can do a rescue experiment to test functionality of the knock-in. The data presented do indicate that the knock-in fusion retains significant function.

In general, the data is clearly presented and the statistical analyses look sound.

Response

• Thank you

__Minor comments: __

Please provide page and line numbers!

Response:

• done

Avoid contractions like "don't" in both text and figure legends

Response:

• changed one instance of “don’t” to “do not”

Page 12: I do not understand the meaning of the sentence "This transgene also caused more modest lethality in a wild-type background"

Response:

• Wording changed to “This transgene caused very little lethality in a wild-type background (Fig. 6C), indicating it is not generally toxic.”

Figure 7: what is meant with "Dodt"?

Response:

• Dodt gradient contrast imaging is a method for transmitted light imaging similar to DIC and is used on some confocal microscopes. It is now explained in the Methods section. We removed the Dodt label from Figure 7 since it seems to be confusing and it is not really important whether the brightfield image is DIC or Dodt.

  Reviewer #1 (Significance (Required)):

  The study is experimentally sound and uses numerous novel tools, such as endogenously tagged lipid receptors. It is an interesting study for researchers in basic research studying lipid receptors and ECM biology. It provides insights on the genetic interaction of lipid receptors. My expertise is in lipid biochemistry, inter-organ lipid trafficking and imaging. I am not very familiar with C. elegans genetics.

__Referee #2 __ 1. The manuscript is very well written; the documentation is fine, but some more details are needed for better following the subject for readers not familiar with nematode anatomy.

For instance, while alae are somehow explained, annuli are not - structures that look abnormal in lpr1 and lpr1-scav2 mutants (Fig. 5B).

Response

• Apologies for this oversight. We added annuli labels to Figure 1 and Figure 5 panels and added descriptions of annuli to the Figure 1 legend and the Results text.

Moreover, the authors show in Fig. 1 the punctae etc in the epidermis, whereas in Fig. 2 the show Lpr3 accumulation or not in the duct and the pore (lpr1). How do they localize in the cells of these structures at high magnification? It is also important to see the Lpr3 localisation in lpr1 mutants shown in Fig. 2A with the quality of the images shown in Fig. 1F. This applies also to Figs. 4 and 5.

Responses:

• The embryonic duct and pore cells are very small and we have not reliably seen puncta within them. In Figs 2 and 5, we supplemented the duct and pore images with those from the epidermis, which is a much larger tissue, allowing us to resolve puncta and matrix structures with better resolution.
• The laser settings in Figs 2,4,5 (as opposed to Fig. 1) were chosen to avoid saturation of the matrix signal so that we could do accurate quantifications as shown. The images are unmodified with respect to brightness and therefore appear relatively dim – but we think they convey the observations very accurately.

I would like to see punctae in lpr1-scav2 doubles.

Response:

• Puncta in this genotype are shown for the epidermis in Figure 5. It has not been possible to see puncta specifically within the embryonic duct and pore.

Regarding the central mechanism, one possibility is - what the authors describe - that Lpr1 is needed for Lpr3 accumulation in ducts and tubes. Alternatively, Lpr1 is needed for duct and tube expansion, in lack of which Lpr3 is unable to reach its destination that is the lumina. Scav2, in this scenario, might be antagonist of tube and duct expansion, and thereby rescue the Lpr1 mutant phenotype independently. Admittedly, the non-accumulation of Lpr3 in scav2 mutants argues against a lpr1-independent function of scav2.

Responses:

• LPR-1 is indeed needed to maintain duct and pore tube integrity as the tubes grow, but in mutants the tubes appear to collapse at a later stage than we imaged here (Stone et al 2009). The ~normal accumulation of LET-4 and LET-653 further argues that the duct and pore tubes are still intact at the 1.5-to-2-fold stages. Therefore, we conclude that the defect in LPR-3 accumulation precedes duct and pore collapse.
• The changes we document in the epidermis also show that the lpr-1 mutant affects LPR-3 accumulation in another (non-tube) tissue.

In any case, to underline the aspect of Lpr1-Scav2 dosage relationship, the authors may also have a look at Lpr3 distribution in lpr1 heterozygous, and lpr1-scav2 double heterozygous worms. In this spirit, it would be interesting to see the semi-dominant effects of scav2 on Lpr3 localisation in lpr1 mutants by microscopy.

Response:

• Because of the hermaphroditism of C. elegans, it would be technically challenging to confidently identify heterozygous (vs. homozygous) embryos for confocal imaging. We do not think that the results would be informative enough to warrant the effort, given that we’ve already shown that scav-2 heterozygosity can partly suppress lpr-1 The expectation is that LPR-3 levels would be partially restored in the scav-2 het, but it might take a very large sample size to confidently assess that partial effect.

One word to the overexpression studies: it is surprising that the amounts of Scav2 delivered by the expression through the grl-2 promoter in the lpr1, scav2 background are almost matching those by the opposite effect of scav2 mutations on lpr1 dysfunction.

Response:

• The reviewer refers to the transgenic rescue experiment with the grl-2pro::SCAV-2 transgene. Because the scav-2 mutant phenotype being tested is suppression of lpr-1 lethality, the expected result from scav-2 rescue is to restore the lpr-1 lethal phenotype to the strain. This is exactly the result we see. We have revised the text to more clearly explain the logic.

One issue concerns the localization of scav2-gfp "rarely" in vesicles: what are these vesicles?

Response

• Only a handful of vesicles were seen across all the images we collected, and we have not yet identified them. They could be associated with either SCAV-2 delivery or removal from the plasma membrane, as now stated in the text. SCAV-2 trafficking would be an interesting area for further study but is beyond the scope of this paper.

One comment to the Let653 transgenes/knock-ins: the localization of transgenic Let653-gfp may be normal in lpr1 mutants because there are wild-type copies in the background.

Response

• There are wild type copies of LET-653 in the background, but no wild type copies of LPR-1. Even if the untagged LET-653 would be recruiting the tagged LET-653 as the reviewer suggests, we can still conclude that lpr-1 loss does not prevent the untagged LET-653 (and thus also the tagged LET-653) from accumulating in the duct lumen matrix.

One thought to the model: if Scav2 has a function in a lpr1 background, this means that yet another transporter X delivers the substrate for Scav2, isn't it?

Response

• Yes, we completely agree with this interpretation and have revised the discussion and Figure 8 legend to more explicitly make this point.

A word to the term haploinsifficient that is used in this study: scav2 mutants would be haploinsifficient if the heterozygous worms died in an otherwise wild-type background.

Response

• We disagree with this comment. The term “haploinsufficient” simply means that heterozygosity for a deletion or other loss of function allele can cause a mutant phenotype – the term is not restricted to lethal phenotypes.

  Reviewer #2 (Significance (Required)):

  Alexandra C.Belfi and colleagues wrote the manuscript entitled "Opposing roles for lipocalins and a CD36 family scavenger receptor in apical extracellular matrix-dependent protection of narrow tube integrity" in which they report on their findings on the genetic and cell-biological interaction between the lipid transporters Lpr1 and scav2 in the nematode C. elegans. In principle, these two proteins are involved in shaping the apical extracellular matrix (aECM) of ducts by regulating the amounts of Lpr3 in the extracellular space. While seems to act cell autonomously, Lpr1 has a non-cell autonomous effect on Lpr3.

---

__Referee #3 __ Summary: Using a powerful combination of genetic and quantitative imaging approaches, Belfi et al., describe novel findings on the roles of several lipocalins-secreted lipid carrier proteins-in the production and organization of the apical extracellular matrix (aECM) required for small diameter tube formation in C. elegans. The work comprises a substantial extension of previous studies carried out by the Sundaram lab, which has pioneered studies into the roles of aECM and accessory proteins in creating the duct-pore excretion tube and which also plays a role in patterning of the epidermal cuticle. One core finding is that the lipocalin LPR-1 does not stably associate with the aECM but is instead required for the incorporation of another lipocalin, LPR-3. A second major finding is that reduction of function in SCAV-2, a SCARB family membrane lipid transporter, suppresses lpr-1 mutant lethality along with associated duct-pore defects and mislocalization of LPR-3. Likewise loss of scav-2 partially suppresses defects in two other aECM proteins and restores defects in LPR-3 localization in one of them (let-653). Additional genetic and protein localization studies lead to the model that LPR-1 and SCAV-2 may antagonistically regulate one or more lipid or lipoprotein factors necessary for LPR-3 localization and duct-pore formation. A role for LPR-1 and LPR-3 at lysosomes is clearly implicated based on co-localization studies, although a specific role for lysosomes (or related organelles) is not defined. Finally, MS data suggests that neither LPR-1 or SCAV-2 grossly affect lipid composition in embryos, consistent with dietary interventions failing to affect mutant phenotypes. Ultimately, a plausible schematic model is presented to explain for much of the data.

__*Major comments:

*__

1. The studies are very thorough, convincing, and generally well described. Conclusions are logical and well grounded. Additional experiments are not required to support the authors major conclusions, and the data and methods are described in a sufficient detail to allow replication. As such my comments are minor and should be addressable at the author's discretion in writing.

Response

• Thank you for these positive comments

  __Minor comments: __2) In the abstract, "tissue-specific suppression" made me think that there was going to be a tissue-specific knockdown experiment, which was not the case. Rather scav-2 suppression is specific to the duct-pore, which corresponds to where scav-2 is expressed. Consider rewording this.

Response

• Wording was changed to “duct/pore-specific suppression”

  3) Page 5. Suggest wording change to, "Whereas LPR-3 incorporates stably into the precuticle, suggesting a structural role in matrix organization, LPR-1..."

Response

• Done

  4) LIMP-2 versus LIMP2. Both are used. Uniprot lists LIMP2, but some papers use LIMP-2. Choose one and be consistent.

Response

• Everything changed to LIMP2.

  5) Some of the data for S6 Fig wasn't referred to directly in the text. Namely results regarding pcyt-1 and pld-1. I'd suggest incorporating this into the results section possibly using, "As a control for our lipid supplementation experiments..."

Response

• These experiments are now described on page 11.

  6) Page 12 bottom. I understand the use of "oppose", but another way to put it is that SCAV-2 and LPR-1 (antagonistically or collectively) modulate aECM composition. Other terms that might confuse some readers is the use of upstream and downstream, although I OK with its use in the context of this work.

Response

• The genetics indicate that lpr-1 and scav-2 have opposite effects on tube shaping and LPR-3 localization, so they do function antagonistically rather than collectively/cooperatively; we decided to keep this terminology.

  7) Page 16. I understand the logic that SCAV-2 is unlikely to directly modulate LPR-3 given its presumed molecular function. But is it possible that LPR-3 levels are already maxed out in the aECM so that loss of SCAV-2 doesn't lead to any increase? Conversely, one could argue that even if acting indirectly, SCAV-2 could have led to increased LPR-3 levels, unless they were already maxed.

Response

• This is a good point and the possibility is now mentioned in the Results page 9. We also changed our wording in the Abstract and Discussion to acknowledge the possibility that LPR-3 could be the SCAV-2 cargo, though we still don’t favor this model.

  8) Figure legend 1. I did not see an asterisk in figure 1B.

Response

• thanks for catching this error, text removed

  9) Figure 1C. Might want to define the "degree" term in the legend for people outside the field.

Response

• We added an explanation to the figure legend.

  10) Fig 1 G. I was just wondering if cuticle autofluorescence was an issue for taking these images.

Response

• Cuticle auto fluorescence is generally quite dim in L4s with our settings, and it was not an issue at this mid/late L4 stage, which corresponds to when both LPR fusions are at their brightest. Note that both large panels are MAX projections and yet you can’t see any cuticle auto-fluorescence in the LPR-1 panel.

  11) Fig 2 and others. Please define error bars.

Response

• These correspond to the standard deviation; this information is now added to the Methods.

  12) Fig 5. From the images, it looks like lpr-1; scav-2 doubles might have a worse (pre)cuticle defect in LPR-3 localization than lpr-1 singles. If so that would be interesting and would suggest that their relationship with respect to the modulation of LPR-3 is context dependent. Admittedly, the lack of obvious scav-2 expression in the epidermis would not be consistent with an effect (positive or negative).

Response

• The lpr-1 scav-2 strain is certainly not improved over lpr-1 but we have not noted any consistent worsening of the phenotype either.

  13) Consider defining Dodt in the first figure legend where it appears.

Response

• Dodt gradient contrast imaging is a method of transmitted light imaging similar to DIC and is used on some confocal microscopes. It is now explained in the Methods section. We removed the term from Figure 7 since it seems to be confusing.

  14) For Mander's, is there a reason to report just one of the two findings (M1 or M2) versus both?

Response

• We now include the 2nd Manders value in the figure legend and note that value is much lower (0.25) because much of the red signal is lysosomes (where green would be quenched by acidity).

  15) Consider referring to specific panels (A, B...) within references to the supplemental files.

Response

• done

  16) Fig S6E. Neither "increasing nor increasing" to "increasing nor decreasing".

Response

• fixed

  **Referees cross-commenting**

  I thought that Reviewers 1 and 2 brought up some good points. My sense is that Belfi and colleagues can address most of these in writing, but are of course welcome to add new data as they see fit. I get that it's not a "perfect" paper where everything is explained fully or comes together, but I don't see that as a flaw that needs to be fixed. I think that the manuscript represents a good deal of work (as it is) and provides a sufficient advance while also suggesting an interesting link to disease. It will be up to individual journals to decide if the findings meets their criteria.

  Reviewer #3 (Significance (Required)):

  Significance: The work carried out in this paper, and more generally by the Sundaram lab, always has a ground-breaking element because very few labs in the field have studied in detail the developmental roles and regulation of the aECM, in large part because it can be challenging to dissect. The core findings in this study are rather novel and unexpected, namely the opposing roles of the paralogous LPR-1 and LPR-3 lipocalins and their functional interactions with SCAV-2. The study does stop short of finding specific molecules (lipid or lipoprotein) that would mediate the effects they report, and it wasn't yet clear how the lysosomal co-loc plays a role, but this is not a criticism of the work presented or the forward progress. I was particularly intrigued by the idea, presented in the discussion, that disruption of vascular aECM could potentially account for some of the (complex) observations regarding the role of lipocalins and SCARB proteins in human disease. This would represent a new avenue for researchers to consider and underscores the power of using non-biased approaches in model systems.

  As for all my reviews, this is signed by David Fay.

• *

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Referee #3

Evidence, reproducibility and clarity

Summary:

Using a powerful combination of genetic and quantitative imaging approaches, Belfi et al., describe novel findings on the roles of several lipocalins-secreted lipid carrier proteins-in the production and organization of the apical extracellular matrix (aECM) required for small diameter tube formation in C. elegans. The work comprises a substantial extension of previous studies carried out by the Sundaram lab, which has pioneered studies into the roles of aECM and accessory proteins in creating the duct-pore excretion tube and which also plays a role in patterning of the epidermal cuticle. One core finding is that the lipocalin LPR-1 does not stably associate with the aECM but is instead required for the incorporation of another lipocalin, LPR-3. A second major finding is that reduction of function in SCAV-2, a SCARB family membrane lipid transporter, suppresses lpr-1 mutant lethality along with associated duct-pore defects and mislocalization of LPR-3. Likewise loss of scav-2 partially suppresses defects in two other aECM proteins and restores defects in LPR-3 localization in one of them (let-653). Additional genetic and protein localization studies lead to the model that LPR-1 and SCAV-2 may antagonistically regulate one or more lipid or lipoprotein factors necessary for LPR-3 localization and duct-pore formation. A role for LPR-1 and LPR-3 at lysosomes is clearly implicated based on co-localization studies, although a specific role for lysosomes (or related organelles) is not defined. Finally, MS data suggests that neither LPR-1 or SCAV-2 grossly affect lipid composition in embryos, consistent with dietary interventions failing to affect mutant phenotypes. Ultimately, a plausible schematic model is presented to explain for much of the data.

Major comments:

The studies are very thorough, convincing, and generally well described. Conclusions are logical and well grounded. Additional experiments are not required to support the authors major conclusions, and the data and methods are described in a sufficient detail to allow replication. As such my comments are minor and should be addressable at the author's discretion in writing.

Minor comments:

1) In the abstract, "tissue-specific suppression" made me think that there was going to be a tissue-specific knockdown experiment, which was not the case. Rather scav-2 suppression is specific to the duct-pore, which corresponds to where scav-2 is expressed. Consider rewording this.

2) Page 5. Suggest wording change to, "Whereas LPR-3 incorporates stably into the precuticle, suggesting a structural role in matrix organization, LPR-1..."

3) LIMP-2 versus LIMP2. Both are used. Uniprot lists LIMP2, but some papers use LIMP-2. Choose one and be consistent.

4) Some of the data for S6 Fig wasn't referred to directly in the text. Namely results regarding pcyt-1 and pld-1. I'd suggest incorporating this into the results section possibly using, "As a control for our lipid supplementation experiments..."

5) Page 12 bottom. I understand the use of "oppose", but another way to put it is that SCAV-2 and LPR-1 (antagonistically or collectively) modulate aECM composition. Other terms that might confuse some readers is the use of upstream and downstream, although I OK with its use in the context of this work.

6) Page 16. I understand the logic that SCAV-2 is unlikely to directly modulate LPR-3 given its presumed molecular function. But is it possible that LPR-3 levels are already maxed out in the aECM so that loss of SCAV-2 doesn't lead to any increase? Conversely, one could argue that even if acting indirectly, SCAV-2 could have led to increased LPR-3 levels, unless they were already maxed.

7) Figure legend 1. I did not see an asterisk in figure 1B.

8) Figure 1C. Might want to define the "degree" term in the legend for people outside the field.

9) Fig 1 G. I was just wondering if cuticle autofluorescence was an issue for taking these images.

10) Fig 2 and others. Please define error bars.

11) Fig 5. From the images, it looks like lpr-1; scav-2 doubles might have a worse (pre)cuticle defect in LPR-3 localization than lpr-1 singles. If so that would be interesting and would suggest that their relationship with respect to the modulation of LPR-3 is context dependent. Admittedly, the lack of obvious scav-2 expression in the epidermis would not be consistent with an effect (positive or negative).

12) Consider defining Dodt in the first figure legend where it appears.

13) For Mander's, is there a reason to report just one of the two findings (M1 or M2) versus both?

14) Consider referring to specific panels (A, B...) within references to the supplemental files.

15) Fig S6E. Neither "increasing nor increasing" to "increasing nor decreasing".

As for all my reviews, this is signed by David Fay.

Referees cross-commenting

I thought that Reviewers 1 and 2 brought up some good points. My sense is that Belfi and colleagues can address most of these in writing, but are of course welcome to add new data as they see fit. I get that it's not a "perfect" paper where everything is explained fully or comes together, but I don't see that as a flaw that needs to be fixed. I think that the manuscript represents a good deal of work (as it is) and provides a sufficient advance while also suggesting an interesting link to disease. It will be up to individual journals to decide if the findings meets their criteria.

Significance

Significance:

The work carried out in this paper, and more generally by the Sundaram lab, always has a ground-breaking element because very few labs in the field have studied in detail the developmental roles and regulation of the aECM, in large part because it can be challenging to dissect. The core findings in this study are rather novel and unexpected, namely the opposing roles of the paralogous LPR-1 and LPR-3 lipocalins and their functional interactions with SCAV-2. The study does stop short of finding specific molecules (lipid or lipoprotein) that would mediate the effects they report, and it wasn't yet clear how the lysosomal co-loc plays a role, but this is not a criticism of the work presented or the forward progress. I was particularly intrigued by the idea, presented in the discussion, that disruption of vascular aECM could potentially account for some of the (complex) observations regarding the role of lipocalins and SCARB proteins in human disease. This would represent a new avenue for researchers to consider and underscores the power of using non-biased approaches in model systems.

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Referee #2

Evidence, reproducibility and clarity

The manuscript is very well written; the documentation is fine, but some more details are needed for better following the subject for readers not familiar with nematode anatomy. For instance, while alae are somehow explained, annuli are not - structures that look abnormal in lpr1 and lpr1-scav2 mutants (Fig. 5B). Moreover, the authors show in Fig. 1 the punctae etc in the epidermis, whereas in Fig. 2 the show Lpr3 accumulation or not in the duct and the pore (lpr1). How do they localize in the cells of these structures at high magnification? It is also important to see the Lpr3 localisation in lpr1 mutants shown in Fig. 2A with the quality of the images shown in Fig. 1F. This applies also to Figs. 4 and 5. I would like to see punctae in lpr1-scav2 doubles. Regarding the central mechanism, one possibility is - what the authors describe - that Lpr1 is needed for Lpr3 accumulation in ducts and tubes. Alternatively, Lpr1 is needed for duct and tube expansion, in lack of which Lpr3 is unable to reach its destination that is the lumina. Scav2, in this scenario, might be antagonist of tube and duct expansion, and thereby rescue the Lpr1 mutant phenotype independently. Admittedly, the non-accumulation of Lpr3 in scav2 mutants argues against a lpr1-independent function of scav2. In any case, to underline the aspect of Lpr1-Scav2 dosage relationship, the authors may also have a look at Lpr3 distribution in lpr1 heterozygous, and lpr1-scav2 double heterozygous worms. In this spirit, it would be interesting to see the semi-dominant effects of scav2 on Lpr3 localisation in lpr1 mutants by microscopy. One word to the overexpression studies: it is surprising that the amounts of Scav2 delivered by the expression through the grl-2 promoter in the lpr1, scav2 background are almost matching those by the opposite effect of scav2 mutations on lpr1 dysfunction.

One issue concerns the localization of scav2-gfp "rarely" in vesicles: what are these vesicles?

One comment to the Let653 transgenes/knock-ins: the localization of transgenic Let653-gfp may be normal in lpr1 mutants because there are wild-type copies in the background.

One thought to the model: if Scav2 has a function in a lpr1 background, this means that yet another transporter X delivers the substrate for Scav2, isn't it?

A word to the term haploinsifficient that is used in this study: scav2 mutants would be haploinsifficient if the heterozygous worms died in an otherwise wild-type background.

Significance

Alexandra C.Belfi and colleagues wrote the manuscript entitled "Opposing roles for lipocalins and a CD36 family scavenger receptor in apical extracellular matrix-dependent protection of narrow tube integrity" in which they report on their findings on the genetic and cell-biological interaction between the lipid transporters Lpr1 and scav2 in the nematode C. elegans. In principle, these two proteins are involved in shaping the apical extracellular matrix (aECM) of ducts by regulating the amounts of Lpr3 in the extracellular space. While seems to act cell autonomously, Lpr1 has a non-cell autonomous effect on Lpr3.

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Referee #1

Evidence, reproducibility and clarity

Summary: In this study, the authors show a genetic interaction of the lipid receptors Lpr-1, Lpr-3 and Scav-2 in C. elegans. They show that Lpr-1 loss-of-function specifically affects aECM localization of Lpr-3 and attribute the lethality of Lpr-1 mutants to this phenotype. The authors performed a mutagenesis screen and identified a third lipid receptor, Scav-2, as a modulating factor: loss of scav-2 partially rescues the Lpr-1 phenotype. The authors created a variety of tools for this study, notably Crispr-Cas9-mediated knock-ins for endogenous tagging of the receptors.

Major comments: while the authors provide a nice diagram showing the potential roles and interplay of lpr-1, lpr-3 and scav-2, it remains unclear what their respective cargo is. The nature of interaction between the proteins remains unclear from the data. As an optional (since time-consuming) experiment I would suggest trying more tissue-specific lipidomics. The lipidomics data should be presented in the figures, even if there were no significant changes. Importantly, show the lipid abundance at least of total lipids, better of individual classes, normalized to the material input (e.g. number of embryos, protein). Figure 1g: I do not understand what the lpr3:gfp signal is: the punctae in the overview image? and where are they in the zoom image showing anulli and alae? Also, how where the anulli and alae structures labeled? please provide more information One point that is not sufficiently adressed is that the authors deduce from the inability of the scav-2 gfp knock in to suppress lpr1 lethality that scav2 function is not impaired. This is quite indirect. Can the authors provide more convincing evidence that scav-2 ki has normal function? In general, the data is clearly presented and the statistical analyses look sound.

Minor comments: Please provide page and line numbers! Avoid contractions like "don't" in both text and figure legends Page 12: I do not understand the meaning of the sentence "This transgene also caused more modest lethality in a wild-type background" Figure 7: what is meant with "Dodt"?

Significance

The study is experimentally sound and uses numerous novel tools, such as endogenously tagged lipid receptors. It is an interesting study for researchers in basic research studying lipid receptors and ECM biology. It provides insights on the genetic interaction of lipid receptors.

My expertise is in lipid biochemistry, inter-organ lipid trafficking and imaging. I am not very familiar with C. elegans genetics.

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Reply to the reviewers

_Below we address all the comments by the reviewers. However, the figures that were used in our response are unfortunately not displayed in this format. _

Reviewer #1

Evidence, reproducibility and clarity

Thanks to the development of Ribo-Seq, translational buffering has been reported in the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. Although the authors' report provides a step forward in our understanding of translational buffering, this reviewer found a series of concerns in this paper. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

Major comments: 1. This paper heavily relies on the reference 18. However, this paper was not properly stated (no page or journal number); the study in Bioinformatics is nowhere to be found on the website, despite being out in 2024 apparently. Either title is wrong (yet a biorxiv can be found). This reviewer guessed that the reference 18 may be accepted. However, without a proper reference, this paper could not be judged since nearly all the parts of this work have been based on the reference 18. Also, the Ribobase data used in this manuscript comes from this reference, so it had better be well defined, especially when another Ribobase data set seems to be available online: http://www.bioinf.uni-freiburg.de/~ribobase/index.html

We apologize for the citation issue. This citation by Liu et al , 2024 (18) was a preprint from BioRxiv. This manuscript is now published in Nature Biotechnology. The reference has been updated in the revised version of the manuscript. The reference number in revised manuscript is Liu et al, 2025 (23).

In the Discussion, the authors mentioned "TE is based on a compositional regression model (18) rather than the commonly applied approach of using a logarithmic ratio of ribosome occupancy to mRNA abundance." This important information should be mentioned in the early section of the manuscript. Related to this, there are other published methods for exploring change in translation efficiency (e.g., 10.1093/bioinformatics/btw585; 10.1093/nar/gkz223) that could also be suitable in this context. It is not entirely clear if their approach is better than before. Again, the improper reference to 18 made our assessment of this work difficult.

We apologize and acknowledge the impact of the citation issue on this point. In Liu et al (2025), we have provided a comparison between our approach and the log-ratio strategy. We also agree that additional context was needed within the current study. Hence, we have now included more detailed information about the TE calculations in the initial results section (line 94).

As noted by the reviewer, several other methods have been developed previously for measuring changes in translation efficiency. These methods are designed to be used in cases of paired designs where there is a treatment or manipulation that is assayed along with controls. While these methods are highly valuable in assessing differential TE, they are unable to accommodate the type of meta-analyses described in our study. In particular, we do not report changes/differential TE with respect to a control sample but instead focus on the coordinated patterns of TE across experiments. We now note this important distinction in the manuscript in the discussion section (line 494).

The paper mainly relies on detecting a set of buffered genes using mRNA-TE correlation and MAD ratios (Ribo-Seq/RNA-Seq). While the concept seems sound, the authors should ensure that this method is reliable. Several controls could be used to confirm this. First, if any studies in humans or mice have described a set of genes as buffered, it would be worth checking for overlap between the authors' set of 'TB high' genes and the previously established list. Furthermore, the authors could use packages explicitly developed for translational buffering detection, such as annota2seq (https://academic.oup.com/nar/article/47/12/e70/5423604?login=true). Not all of the data used by the authors may be suitable for such packages, but the authors could at least partially use them on some of their datasets and see whether the buffered genes reported by these packages match their predictions.

We thank the reviewer for this constructive suggestion. To the best of our knowledge, no prior study in humans or mice has systematically analyzed translational buffering across a wide range of conditions. As a result, defining a gold-standard set for benchmarking is currently not feasible.

While packages such as anota2seq have proven highly valuable for identifying buffering effects in controlled experimental designs (e.g., comparing a treatment to a matched control), they are not readily applicable to the type of large-scale meta-analysis we present here.Our study integrates ribosome profiling and RNA-seq data across diverse datasets and conditions, which lies outside the design scope of such tools.

The most relevant point of comparison to our work is Wang et al. 2020 Nature, which examined a related but distinct form of translational buffering across species for a given tissue. We now present the overlap of genes identified as buffered in our study vs Wang et al. 2020. The details are presented in the reviewer's comment 5-2.

The threshold of 'TB high' or 'TB low' (top and bottom 250) is somewhat arbitrary. Why not top 100 or 500? The authors should provide a rationale for this choice. Also, they could include a numeric measure of buffering (the sum of the two rankings is probably suitable for this purpose). Several of the authors' explorations are suitable for numerical quantification (GO enrichment can be turned into GSEA, and the boxplot can be shown as correlations)

Thanks for these suggestions. We agree that the threshold used to define TB high and low are somewhat subjective. We ensure that changing this cutoff as suggested is easily achievable with the provided R script. These can be used to reproduce all of the reported analyses of translational buffering with different cutoffs.

To further assess whether our conclusions are robust to the selection of these thresholds, we tested several different values to define the TB high and TB low groups. As an example, we show here that the effect on protein variation and association of intrinsic features like the UTR lengths with the buffering potential of genes for different thresholds (i.e. if the TB high = top 100 or TB high = top 200) remain similar to the current cutoff of 250. However, if we increase the cutoff of TB high to 2000 and TB low to top 2000-4000 , the difference between the various features is diminished (Figure A& B). Further, protein variation (human cancer cell line and tissue) also becomes more similar across the three categories, possibly indicating a reduced regulatory potential of genes as their rank increases (Figure C& D).Our analyses reveal that highly ranked genes show associations with particular features, indicating an underlying hierarchy in translational buffering potential. This point is now discussed in the manuscript (line 177).

Legend: Effect of different thresholds on . A. Length features B. Median RNA expression C. Protein variation in human cancer cell line and D. on Primary human tissues

In response to the reviewer's suggestion of presenting data using numerical quantitation, we incorporated several additional inclusions in the manuscript.

1. We now report association of CDS / UTR length with translational buffering as a function of their translational buffering rank with highly ranked genes showing associations with particular features, indicating an underlying hierarchy in translational buffering potential (Sup Fig 3 A-B) Ii. We now include scatter plots which show that highly ranked genes have lower variation at the protein level in both cancer cell line and primary tissues (Sup Fig. 6 A-C).

Iii. We have now carried out modified GO enrichment analyses. Specifically, Gene Ontology enrichment analysis was performed for the TB high genes in humans and mouse using the clusterProfiler R package. Lists of TB high genes in human or mouse were analyzed against the Gene Ontology (GO) database using the enrichGO() function, with the organism-specific annotation database (org.Hs.eg.db for human or org.Mm.eg.db for mouse) as reference. Gene identifiers were supplied as gene symbols, and all genes in the current study were used as the background universe. Enrichment was carried out for the Biological Process (BP) ontology, with significance assessed by the hypergeometric test. P-values were adjusted for multiple testing using the Benjamini–Hochberg method, and terms with an adjusted p-value Legend: Gene Ontology (GO) enrichment analysis of the TB high gene set, performed with the clusterProfiler R package. Enriched GO Biological Process terms are shown after redundancy reduction using clusterProfiler::simplify. Each dot represents a GO term, with dot size indicating the number of genes associated with the term and color reflecting the adjusted p-value (Benjamini–Hochberg correction). Only the top non-redundant terms are displayed.

• *

Additionally, we performed Gene set enrichment analysis using the list of genes ordered according to their RNA-TE correlation. Hence lower ranks have lower RNA-TE correlations. The GSEA plots show significantly enriched Gene Ontology Biological Process (GO:BP) terms at the lower ranks of the ordered gene list. Together, these analyses further emphasize the observation that genes involved in macromolecular complexes are translationally buffered.

• *

Legend: Curves represent the enrichment score (ES) across the ranked gene list, with vertical bars indicating the positions of pathway-associated genes. The enrichment was identified using the gseGO() function from clusterProfiler.

Several of the statements of the authors in the Introduction or Discussion sections are not entirely true regarding the literature on the topics, or lack major papers on the topic, and therefore, they are a bit misleading. Among others, here are some:

We thank the reviewer for the suggestions and now have been incorporated in the revised manuscript, accordingly.

5-1 "In addition, genetic differences arising from aneuploidy, cell type differences or variability observed in the natural population can further determine the amplitude of variation (4-7). The effect of mRNA variation under these conditions is mostly reflected at the protein levels (2, 4-8).". Several recent or more ancient papers suggest that mRNA variation coming from aneuploidy, natural genetic variation, or CNV is buffered or not well reflected at the protein level: DOI: 10.1038/s41586-024-07442-9 DOI: 10.1073/pnas.2319211121 DOI: 10.1016/j.cels.2017.08.013 DOI: 10.15252/msb.20177548

We agree that mRNA variation coming from aneuploidy, natural genetic variation, or CNV is buffered or not well reflected at the protein level for some genes. This point has now been revised in the introduction. We have incorporated all the suggested literature into the revised manuscript (line 38).

5-2: The authors should also consider mentioning these studies and softening their initial statement. "Similarly, translational buffering of certain genes have been reported in mammalian cells, specifically under estrogen receptor alpha (ERα) depletion conditions (16).". Translational buffering has been deeply explored in mammalian tissues and even across several mammalian species in this study (DOI: 10.1038/s41586-020-2899-z). In this, the authors also provide a nice exploration of the gene characteristics that are associated with translational buffering. The authors should mention it and compare the study's findings to theirs ultimately.

We thank the reviewer for this suggestion. We have now cited the recommended study in the revised manuscript (line 65). Here, we provide a comparison of its findings with ours. While this related work offers important insights into translational buffering, its focus is on buffering across species within a given tissue, whereas our study emphasizes buffering across conditions, cell types, and treatments within a species. Despite this difference in focus, the comparison is highly informative, and we now highlight both the similarities and distinctions between the two studies in the relevant section of the revised manuscript.

Wang et al. calculate the variation at the transcriptome level vs at the translatome level and is represented as delta ∆ value for each gene. A lower value represents lower variation at the ribosome occupancy level than at the mRNA levels across various species. We classified the genes in the Wang et al study as TB high, TB low genes or others as identified in the current study while indicating the calculated delta ∆ from Wang et al. Many of the genes with a lower delta value (are delta ∆ Legend: A. Dot plot to highlight the delta value of all genes in the Wang et al study (also present in RiboBase) which are further grouped as TB high, low or others in (A) brain and (B) liver.

5-3: "Differences in species evaluated and statistical methods have resulted in conflicting interpretations (13, 28).". These conflicting results have been previously discussed in reviews on the topic that would be worth mentioning: DOI: 10.1016/j.cell.2016.03.014 DOI: 10.1038/s41576-020-0258-4

We have added these reviews at the appropriate location of the manuscript.

1. In addition to the p-values stated in the main text, the authors should annotate their plots when they find significant differences between groups to greatly facilitate the visual interpretation of the graphs.

We have now annotated many of the relevant graphs with p-values to facilitate visual interpretation, adding them where space and figure design allow.

Based on the data of Figure 4D, apparently, ribosome occupancy was not buffered even in high TB sets. The authors may argue that translational buffering may not cope with such a strong mRNA reduction. In that case, how big a difference in mRNA level does the buffering system adjust in protein synthesis? The authors should test gradual gene knockdown and/or overexpression and conduct Ribo-Seq/RNA-Seq to survey the buffering range.

We appreciate the reviewer’s suggestion regarding the experiment to determine the buffering range.To understand this for multiple genes, we attempted a series of knockdowns using CRISPR/gRNA approach using a MutiCas12a approach. We targeted 8 buffered and 2 non-buffered genes using a 10-plex crRNA along with 10-plex gRNA serving as a negative control (Figure below). The fold change at the mRNA level of the targeted gene was within the variation range observed in replicates for other non-targeted genes. The challenge in performing a gradual knockdown is the subtle changes in RNA expression falls within the margin of error of estimation, making it difficult to understand the clear implications of the mRNA levels on buffering. Hence, the precise experimental manipulation of mRNA expression levels that would be conducive to translational buffering remains highly technically challenging. As noted in our manuscript (Figure 4D), the conventional approaches for manipulation of transcript abundance lead to larger changes than typically observed as a result of natural variation.

*Legend: Validation of translational buffering by targeted knockdown of genes. A. The scatter plot shows the coefficient of variation of mRNA and ribosome occupancy between HEK293T cells targeted with sgRNA of different efficiencies. The genes indicated in blue are buffered and those in green are non buffered genes. B. The plot shows the fold change in mRNA abundance and ribosome occupancy as compared to cells that were infected with non-targeting crRNA array control (ratio of cpm in test vs control). Each color represents a gene and each point of a gene represents cells targeted by one of the four CRISPR arrays. *

"differential transcript accessibility model" could not be functional if mRNA is reduced beyond the accessible pool (i.e., less than the threshold, all the mRNAs are translated without buffering). The authors should carefully reconsider this model and the effective range of mRNAs.

We agree with the reviewer that according to the 'differential transcript accessibility model,' transcripts with abundances below a certain threshold should be completely accessible to the translational pool. Further, this could also be true for the other model, wherein initiation rate cannot increase beyond a particular threshold for transcripts of very low abundance. However, our observation from our haploinsufficiency analysis (Figure 4 B& C) and siRNA knockdown analysis from RiboBase (Figure 4 D) suggests that buffering might be possible within a given range of transcript abundance. Testing the buffering range by serial knockdowns might help in determining the threshold at which transcripts exhibit buffering. However, due to the challenges of serial knockdown as discussed above, makes this analysis difficult with Ribosome profiling and matched RNA-seq approach. An alternative approach could involve imaging translating and non-translating mRNA of buffered genes in different cells, which may help distinguish the two models. However, this falls outside the scope of the manuscript.

Minor comments:

1. Some figures are of poor quality as they seem to have points outside of the panel representations... Like Figure 3C, one point is out of the square, same for Figure 4E. Similarly, on figure 5F, some outliers seem to be clearly cut from the figure (maybe not, but then the author should put a larger space between the end of the figure and the max y points). Same for panel S2D and S6D, this does not sound so rigorous.

We agree and apologize for this issue. The axes of the figures have been annotated appropriately to indicate the presence of outliers in the figures.

1. There are several typos or weird sentences. Here are some (but maybe not all): 2-1: [...]with lower sums corresponding to higher final ranks. "two rankings". Based on these final ranks[...] 2-2: For each dataset, median absolute deviation (MAD) "i" protein abundance was calculated across samples 2-3: [...]neighbor method implemented in the MatchIT package (38) Differences in protein[...] a point is missing here. 2-4: Additionally a second dataset providing predictions of haploinsufficiency (pHaplo score) and triplosensitivity (pTriplo score) for all autosomal genes (25) was used to asses the distribution of these score"S" across buffered and non-buffered gene sets . There is a missing "s" at "score" and there is a space between the last word and the final point.

The necessary corrections have been incorporated in the revised version of the manuscript.

1. In the "Lymphoblastoid cell line data analysis:" section, this reviewer wonders why the authors used a different method to calculate buffering compared to before.

The main reason is the limited sample of the lymphoblastoid cell line data. In our larger analyses, we could use median absolute deviation as a robust metric of dispersion across heterogeneous samples. However, given the smaller dataset in that study we decided CV would be a better indicator of dispersion. To evaluate the potential for translational buffering of genes from RiboBase, we used two metrics. The first was the negative correlation between translation efficiency and RNA abundance across samples. The second metric relied on the ratio of variation in ribosome occupancy to variation in RNA levels. Given the limited sample size of the lymphoblastoid cell line dataset, we used the coefficient of variation (CV) instead of the median absolute deviation (MAD), as the data in this study were normalized using counts per million (CPM) rather than the centered log-ratio (clr) normalization used in RiboBase. This CV ratio allowed us to assess the effect of natural variation in RNA abundance on ribosome occupancy.

1. "Samples which had R2 less than 0.2 were removed as the residuals calculated for these samples could be unreliable". These samples for which the correspondence between RNA-Seq and Ribo-Seq is low wouldn't be the ones most impacted by translational buffering? Is it sure that the authors are not missing something here?

We agree with the reviewer that genes that show translational buffering may not conform to linear relationships between the two parameters. However, the proportion of genes exhibiting this buffering effect is not expected to significantly influence the overall regression fit. Instead, we hypothesized that low quality samples or truly different relationships between the two parameters can make this relationship nonlinear, rendering it unsuitable for linear regression analysis for calculation of TE.

To address these possibilities, we first analysed a commonly used proxy for data quality. Given the characteristic movement of ribosomes across mRNAs, periodicity of sequencing reads is a useful metric to assess whether reads are randomly fragmented, as in RNA-seq, or specifically represent ribosome-protected footprints. For this, we compared two groups: samples that were removed (~30) and those retained for analysis. We plotted the distribution of periodicity scores for all samples in both groups. For the calculation of periodicity scores, first the percentage of reads mapped to the dominant frame position across the dynamic ribosome footprint read length range was calculated for each sample. The periodicity score was calculated by taking the weighted sum of these dominant percentages, with weights based on the total read counts at each length.

The results indicate that the removed samples did not have lower periodicity scores, suggesting that their quality in terms of periodicity was comparable to the retained samples.

        To assess the second possibility, we checked if the study involved major perturbations, which may skew the relationship towards non linearity. The 30 samples that were removed came from 14 unique studies, 18 of which involved perturbation which possibly affected either of the two parameters. In addition to the genetic/pharmacological perturbations specific to the study, the overall conditions of the cells during an experiment could influence this relationship. Another point to note is that many of the filtered-out samples are HeLa and HEK293T cells, which show a normal relationship between ribosome occupancy and RNA abundance for the majority of cases.

        These considerations suggest that removing these samples is most appropriate, as their inclusion could bias the TE calculations.

For Figure 4B and 4C, the authors should provide statistical tests and p-values to confirm the observed trends.

The haploinsufficiency and triplosensitivity analyses are now supported by a chi-squared test. The details of the statistical test are now mentioned in the text and the p-values have been noted on the respective figures.

In Figure 2A, the "all genes" color doesn't correspond to the point color.

The color in the figure has been modified in the revised version of the manuscript.

1. "To understand if codon usage patterns are[...]". This comes slightly out of the blue. The authors could maybe explain why codon usage should be explored for translational buffering. The authors should cite recent key works in the fields: DOI: 10.1016/j.celrep.2023.113413 DOI: 10.1101/2023.11.27.568910

We would like to thank the reviewer for their suggestion. The references have been incorporated in the revised version of the manuscript. We have now explained why codon usage could be a contributor in determining the translational buffering potential (line 190).

"The change in each metric was calculated by subtracting the mean value in the control samples from that in the knockdown samples. This yielded the differential mRNA abundance and ribosome occupancy resulting from gene knockdown.". This looks statistically weak. The authors should consider using more robust methods like DESeq.

We thank the reviewer for the suggestion. We reanalyzed the selected studies using edgeR and the modified figure is included in the revised version of the manuscript (Figure 4D). The conclusion after this analysis remains essentially the same. In particular, translational buffering is ineffective when mRNA abundance is perturbed drastically. Additionally, the limited number of experiments with direct perturbation of buffered genes limit the generalizability of this observation. This limitation is included in the result section (line 342).

Legend: Scatter plot represents log2 fold change in RNA abundance and ribosome occupancy. Each point represents a gene and the fold change in its RNA and ribosome occupancy with respect to their controls. The line represents the line of equivalence. Buffered genes do not show less change in ribosome occupancy upon reduction in their RNA levels than other genes.

1. "Genes in the buffered gene set had a higher codon adaptation index than the non-buffered set, indicating that candidates in the buffered gene set are relatively well expressed due to the presence of a higher proportion of the codons observed in highly expressed genes". What do the authors mean by "relatively well expressed"? Abundantly expressed? This sentence and the causality under it is unclear and should be modified or better explained.

We thank the reviewer for pointing out the lack of clarity in the sentence. We have now quantitatively measured the CAI in the three categories and modified the sentence to better explain the rationale in the revised version (line 183). “To understand if codon usage patterns are associated with translational buffering, we next analyzed codon properties across buffered and non-buffered human gene sets. The codon adaptation index quantifies how closely a gene’s codon usage aligns with that of highly expressed genes. Genes in the buffered gene set had a higher codon adaptation index than the non-buffered set. Specifically, 28.4% of TB high genes, 14% of TB low genes and 9.3% of genes in the other category fall within the top decile (>90th percentile) of codon adaptation index.”

The panel 4D is unclear. Is one point associated with one gene? Or is it the average of several genes? If it's one point for one gene, it is important to clearly state it because the number of cases is therefore quite low, especially for the TB high and low.

Each point and line are associated with a single gene. This is now clarified in the legend of the figure (line 364). The number of genes in this analysis is limited to the available ribosome profiling data with gene knockdown experiments.

1. In Figure 2J, GGU (Gly), AAG (Lys), and ACU (Arg) provide negative effects on prediction, although these were enriched in the high TB set (Figure 2E). This contradiction should be explained.

While this appears to be a seeming contradiction, it is in line with what we expected. In particular, the objective of Figure 2J is to illustrate the features that predict the mRNA–TE correlation of genes, as identified using a LGBM model. The Spearman correlation shown reflects the relationship between each feature and the mRNA–TE correlation values. A negative correlation for codons such as GGU (Gly), AAG (Lys), and ACU (Thr) suggests that enrichment of these codons is associated with lower mRNA–TE correlation. This is in agreement with our observation in Figure 2E which suggests that high TB genes are enriched in these codons. In contrast, transcript size exhibits a positive correlation, indicating that shorter transcripts tend to have lower mRNA–TE correlation values.

Given that the choice of colors is a potential source of confusion, we have revised the text (line 230) and the figure (& legend) to try to clarify this relationship.

The subtitle of "Translationally buffered genes exhibit variable association kinetics with the translational machinery in response to mRNA variation" sounds unfair to this reviewer. Since the authors did not work on kinetics directly, the use of this word is misleading.

We agree and revised the subtitle to “The association of translationally buffered genes with the translational machinery varies in response to changes in mRNA abundance"

1. The explanation of Figure 5A "We next explored the potential mechanisms that may give rise to translational buffering. Specifically, we considered two non-mutually exclusive models by which mRNA abundance might be decoupled from ribosome occupancy. In the first, the "differential transcript accessibility model", mRNA abundance determines the fraction of transcripts that are accessible to the translational pool. In this scenario, an increase in mRNA abundance would be accompanied by a proportionally smaller increase in the fraction of transcripts entering the translating pool for buffered genes, compared to non-buffered genes. In the second, the "initiation rate model", the rate of translation initiation per transcript scales inversely with mRNA abundance. Under this model, the proportion of mRNA entering the translational pool would be comparable across buffered and non-buffered genes (Fig 5A)." is hard to understand. The authors should rewrite for a better understanding of the readers.

This section has been rewritten in the revised version of the manuscript. The text now reads as

“We next explored the potential mechanisms that may give rise to translational buffering. Specifically, we considered two non-mutually exclusive models by which mRNA abundance might be decoupled from ribosome occupancy. In the first, the “differential transcript accessibility model”, mRNA abundance determines the fraction of transcripts that are accessible to the translational pool. In this scenario, an increase in mRNA abundance would be accompanied by a proportionally smaller increase in the fraction of transcripts entering the translating pool for buffered genes, compared to non-buffered genes. In the second, the “initiation rate model”, the rate of translation initiation per transcript scales inversely with mRNA abundance. Under this model, as mRNA abundance increases, translation initiation on each transcript is reduced, thereby lowering the number of ribosomes per transcript. However, this mechanism allows a proportional increase in transcripts entering the translational pool for buffered genes, similar to non-buffered genes”

Significance

Thanks to the development of Ribo-Seq, translational buffering has been reported in various works. However, the systematic investigation has remained challenging. Employing the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. A group of mRNAs whose expression variance is buffered at the translation level was comprehensively surveyed in humans and mice. The authors found a series of features in the translationally buffered genes, including high GC contents in the 5′ UTR, optimal codon usage, and mRNA length. The depletion or increase of one allele of the genes in the group may be particularly detrimental to cells. The authors' report provides a step forward in our understanding of translational buffering, appealing to the broad scientific community in basic and applied biology. However, this reviewer found a series of concerns in this paper, including clarity in the methods, experimental validation, referring the earlier works, etc. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

We thank the reviewer for noting the significance of the work and for their constructive feedback.

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

In this manuscript, Rao and colleagues present a comprehensive analysis of translational buffering in human and mouse by mining 1515 matched ribosome profiling and RNAseq datasets from diverse tissues and cell lines. They define translational buffering as genes whose TE is negatively correlated with mRNA abundance across conditions, and further identify candidates by comparing median absolute deviations of ribosome occupancy versus mRNA levels. The authors find a conserved set of buffered genes enriched for components of multiprotein complexes, demonstrate that buffered genes exhibit lower protein variability and greater dosage sensitivity, and propose two non-mutually exclusive mechanistic models (differential accessibility and initiation rate modulation). Finally, they perform complementary fractionation experiments in HEK293T cells to support these models.

These findings propose a novel, conserved mechanism of translational buffering that tunes gene expression in mouse and human, showing how intrinsic sequence features and cellular context cooperate to stabilize protein output across diverse conditions. However, further evidence is required to fully support the authors conclusions, particularly direct validation of the proposed models of buffering.

We thank the reviewer for their positive assessment and thoughtful suggestions that we address below.

Below are my main concerns:

1. The choice of the top 250 genes by spearman correlation and MAD ratio as "TB high" seems arbitrary. The authors should justify these cut offs (via permutation analysis or FDR control) and show that conclusions are robust to different thresholds.

We agree that the threshold used to define TB high and TB low is somewhat subjective, and we now clearly acknowledge this in the discussion section (line 485). We now provide an R script that reproduces all analyses of translational buffering, where changing this cutoff to higher or lower values is straightforward.

To ensure the robustness of our conclusions, we evaluated several thresholds for defining TB high and TB low. We observed that the conclusions hold within a reasonable range of values (100-250). For example, the effects on protein variation and the association of intrinsic features such as UTR lengths with buffering potential remain consistent when TB high is defined as the top 100 or the top 200 genes, compared with the current cutoff of 250. In contrast, when we define TB high as the top 2000 and TB low as ranks 2000–4000, the difference between the various features is diminished (Figure A& B). Further, protein variation (human cancer cell line and tissue) also becomes more similar across the three categories, possibly indicating a reduced regulatory potential of genes as their rank increases (Figure C& D). Our results show that highly ranked genes consistently associate with specific features, suggesting an underlying hierarchy in translational buffering potential.

Legend: Effect of different thresholds on . A. Length features B. Median RNA expression C. Protein variation in human cancer cell line and D. on Primary human tissues

The modified compositional regression approach for TE and imputation of missing values are central to the study, but details are relegated to supplemental methods. The manuscript would benefit from a clear comparison of this method against standard log-ratio TE estimates, including sensitivity analyses to missing-data imputation strategies

We thank the reviewer for the feedback. We have now added further description of the modified compositional regression and the imputation strategy in the results section (line 94). Comparison to standard log-ratio TE estimates and their limitations has already been detailed in Liu et al. 2025, Nature Biotechnology. Therefore, in the current manuscript we specifically focus on the effect of the imputation strategy.

        Specifically, the modified imputation slightly improved concordance between the set of genes that are identified to be translationally buffered using the negative RNA-TE relationship or using RNA -Ribosome occupancy correlation (0.91 to 0.94). Further, we assessed the correlation between TE and protein abundance as measured by mass spectrometry from seven human cell lines (A549, HEK293, HeLa, HepG2, K562, MCF7 and U2OS). The protein measurements were obtained from PaxDb. The new imputation strategy slightly increased mean correlation between the TE and proteome abundance as compared to naive strategy. It specifically showed improved correlation for HepG2, A549 and HeLa cell lines. 3507 genes were used for this analysis that were common between PaxDb, Liu et al., 2005 and the current study.

Legend: Proteomics vs TE correlation of cell types without or with imputation strategy. Spearman correlation between compositional TE calculated as calculated by Liu et al., 2025 from 68 samples from 11 studies (HEK293), 86 samples from 10 studies (HeLa), 58 samples from four studies (U2OS), 29 samples from five studies (A549), five samples from two studies (MCF7), seven samples from two studies (K562) and 10 samples from two studies (HepG2) or from the current study. 57 samples from 10 studies (HEK293), 82 samples from 9 studies (HeLa), 58 samples from four studies (U2OS), 29 samples from five studies (A549), 5 samples from two studies (MCF7), one samples from one studies (K562) and 9 samples from two studies (HepG2) . 3507 genes were used for this analysis that were common between Paxdb, Liu et al., 2005 and the current study.

Human data are derived mainly from immortalized cell lines, whereas mouse data are from primary tissues. Pooling these heterogeneous sources may conflate cell type-specific regulation with intrinsic buffering. The authors should either stratify analyses by context or demonstrate buffering signatures remain consistent within more homogeneous subsets

We thank the reviewer for the suggestion and agree that heterogeneity could potentially mask cell type-specific buffering effects. The TB-high genes we report are those that show consistent and robust expression across diverse contexts. However, unlike RNA-seq datasets, the current number of ribosome profiling samples per cell type is still limited, and a more comprehensive assessment of context-specific buffering will require larger datasets that will accumulate over time.

Nonetheless, we have stratified the analysis by cellular context. Specifically, we grouped samples of the same cell-type and repeated the buffering analysis. We provide a new table listing TB-ranks of genes for the five cell types with the largest sample sizes as a table in github.

https://github.com/CenikLab/Translational-buffering/blob/Translational-Buffering/combined_tables.xlsx

As an additional control, we compared buffering patterns between related and unrelated cell lines. For example, the correlation of TB ranks between related cell lines HEK293T (n = 98) and HEK293 (n = 57) is higher (0.46) than between either and an unrelated cell line, HeLa (n = 82). Similarly, the correlation between two liver cell lines, Huh7 (n = 39) and HepG2 (n = 9), is higher (0.20) than between Huh7 and a similarly sampled but unrelated lymphoblastoid cell line (LCL, n = 9; correlation = 0.05). While these analyses suggest that cell type-specific patterns may exist, their exploration is currently limited by sample size, as detecting buffering requires substantial variability in mRNA expression. We now highlight this as a limitation in the Discussion section (line 573).

*Legend: Spearman correlation between TB ranks of different pairs of cell lines. The first set indicates comparison with HEK293T. The second set indicates comparison between liver cells (HepG2 and Huh 7). *

The HEK293T fractionation experiments offer preliminary support for both the "accessibility" and "initiation" models, but only slope analyses are shown. To validate these models, the authors should perform targeted reporter assays (dual luciferase constructs with 5′UTR swaps) or manipulations of initiation factors (eIF4E knockdown) to directly test how transcript abundance alters initiation rates versus pool entry

We thank the reviewer for suggesting experiments to validate the proposed models. In the luciferase reporter experiments, constructs bearing the endogenous UTRs from non-buffered genes would be expected to result in expression that is proportional to transcript abundance. In contrast, swapping a 5’ UTR from buffered genes would mitigate this effect of translation buffering via “initiation rate model” depending on the 5 UTR sequence of transcript. However, as outlined below, this experiment has important caveats:

1. Role of coding sequence: Such assays primarily test the contribution of the 5′UTR and do not address potential cooperative effects between the 5′UTR and the coding sequence (CDS). Thus, if 5′UTRs fails to recapitulate translational buffering, it would be unclear whether the buffering requires coordinated action of the 5′UTR and CDS or whether the gene in question simply does not conform to the initiation-rate model.
2. Sensitivity of measurements: Reporter-based measurements often rely on RT-qPCR to quantify expression changes. While suitable for large fold-changes, small shifts may fall within the assay’s technical margin of error, limiting the interpretability of the results. iii. Gene-to-gene variability: Buffered and non-buffered transcripts likely span a wide range of intrinsic initiation rates. Selecting only a few “representative” transcripts for 5′UTR swapping could yield results that are not broadly generalizable.

Similarly, knockdown of general initiation factors will likely impact on both buffered and non-buffered genes, which could limit the ability to distinguish the effect of transcript abundance on translational buffering via either of the proposed models. We envision an alternative future approach that would involve single molecule imaging translating and non-translating mRNAs of buffered and non-buffered genes under varying abundance conditions in a physiological context. Such experiments are likely the most suitable for disentangling the contributions of accessibility versus initiation. While we find this an exciting direction for future work, it lies beyond the scope of the present manuscript.

The conclusion that buffering reduces protein variability relies on mass-spec comparisons, but ribosome occupancy does not always reflect functional protein output (due to elongation stalling or co-translational degradation). Incorporating orthogonal measures, such as pulse-labeling or western blots for key buffered versus non-buffered genes, would strengthen the link between buffering and proteome stability

We agree with the reviewer’s concern and have been acknowledged as a limitation in the discussion section. To address this with orthogonal approaches, we carried out several additional experiments. Specifically, we identified a study from RiboBase (GSE132703) that exhibited significant variation in FUS transcript (a translationally buffered gene) abundance across conditions—namely HEK293T wild type, LARP1A single knockout (SKO), and LARP1A/B double knockout (DKO) using their RNA-seq data. We reached out to the authors of the study and obtained these knockout cell lines. We reanalyzed RNA abundance under the different conditions by RT-qPCR and assessed protein levels by Western blot. Despite observing differences in RNA abundance, FUS protein levels did not exhibit corresponding change at the protein level.

We also selected a non-buffered gene; DNAJC6, that also showed RNA-level differences. However, the change in RNA expression was not consistent at the protein level. Some caveats of Western blot is its limited sensitivity which may prevent detection of subtle changes and that the measurements are steady-state protein levels which cannot resolve whether differences arise from altered synthesis or degradation.

*Legend : Validation of buffering gene by western blot: A. Plot showing the RNA abundance and ribosome occupancy of buffered gene ; FUS and non buffered genes; DNAJC6 with variation in HEK293T-wild type, LARP1A single knockout and LARP1A/B double knockout. B. Validation of the RNA seq data by qPCR. C. Western Blot showing the FUS, DNAJC6 and Actin in wild type and different mutants. D. Bar plot showing the quantification of western blot. *

        In addition to this targeted analysis , we performed quantitative mass spectrometry to evaluate the effect of mRNA variation at the protein level at global scale.

LC MS/MS analysis was performed on the above samples in triplicates at the Proteomics facility of the University of Texas. A total of 4,048 proteins were identified using a peptide confidence threshold of 95% and a protein confidence threshold of 99%, with a minimum of two peptides required for identification. Total precursor intensities for all peptides of a protein was summed and was used for protein quantification using DEP (Differential Enrichment of Proteomics Analysis) Package, in Bioconductor, R (https://rdrr.io/bioc/DEP/man/DEP.html). DEP was used for variance normalization and statistical testing of differentially expressed proteins. As expected LARP1 protein was identified in the control cells but not in the single or double knockouts.

We then plotted the fold change in RNA as determined by edgeR analysis of RNA-seq from (Philippe et al. 2020) and the fold change in protein abundance from our mass spectrometry data. We observed that genes in the TB high group show reduced changes at the protein level compared to TB low or others as determined by the linear regression analysis in both single and double LARP1 KO mutants. This finding is consistent with our findings that buffered genes show lower variation in the protein abundance in response to change in mRNA expression.

Legend: Scatter plot showing the log2fold change in the RNA and protein levels as determined by RNA seq from (Philippe et al. 2020) or mass spectroscopy. Differential analysis of RNA was done using the edgeR package and the DEP (Differential Enrichment of Proteomics Analysis) Package *was used for mass spectrometry analysis. Only genes with an FDR We have not included this data in the manuscript given the deviation of the approach from our original analysis, but we are happy to reconsider the inclusion of this data to supplement our proteomic analysis.

While the LGBM modeling shows modest predictive power of sequence features alone, the manuscript stops short of exploring what cellular factors might drive context dependence. Integrating public datasets on RNA-binding protein expression or mTOR pathway activity across samples could illuminate trans-acting determinants of buffering and move beyond correlative sequence analyses,

We thank the reviewer for this suggestion. To investigate potential trans-acting determinants of buffering, we focused on 1,394 human RBPs as classified by Hentze et al. (2018), reasoning that some of these factors may facilitate translational buffering. Specifically, we examined correlations between the RNA expression of each RBP and the TE of all other genes across samples. p-values were corrected using the Bonferroni procedure. For each RBP, we then performed a Fisher’s exact test to assess whether the number of significant correlations was enriched among buffered versus non-buffered genes.

This analysis revealed that the expression levels of many RBPs are significantly enriched for either positive or negative correlations with the TE of buffered genes. In particular, we note that RNA expression of many buffered RBPs is enriched for negative correlations with the TE of other buffered transcripts. These results suggest that, rather than considering translational buffering in isolation for each transcript, buffering effects may be coordinated at the translational level and influenced by shared trans-acting factors such as RBPs. Network-based approaches have been valuable for RNA co-expression and are only now being applied to TE covariation. However, the correlative nature of these analyses limits causal inference. For example, although many ribosomal proteins appear to influence the buffering of other ribosomal proteins, they themselves may be regulated by a non-ribosomal RBP—so the apparent effects could reflect upstream regulatory influences. This analysis is now included as a supplementary figure (Sup. Fig. 5) of the revised manuscript.

Legend: A scatter plot of odds ratio log₂ of number of significant correlations (RNA abundance of RBPs ::TE of genes) and the p value from fisher test. The vertical dashed line represents the threshold odds ratio, above which RBPs exhibit a higher number of significant correlations with buffered genes. P values were corrected using Bonferroni procedure* and the horizontal dashed line represents the adjusted p value cutoff. *

Reviewer #2 (Significance (Required)):

Overall, this manuscript leverages an unprecedented compendium of matched ribosome profiling and RNAseq datasets across human cell lines and mouse tissues, combined with improved TE estimation, to robustly catalog genes exhibiting translational buffering, a clear methodological and conceptual strength. The main limitations stem from heterogeneous sample sources, largely correlative analyses, and a lack of targeted mechanistic validation. Compared to prior yeast focused studies, it fills a key gap by demonstrating conservation of buffering in mammals and linking it to dosage sensitivity and protein stability, representing a conceptual advance in understanding post-transcriptional homeostasis and a methodological step forward in TE analysis. This work will interest researchers in RNA biology, gene expression regulation, systems biology, and cancer proteomics, as well as those studying dosage-sensitive pathways and translational control. My expertise is on translational control in cancer.

We thank the reviewer for noting the broader significance of the work and for their constructive feedback.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Rao and colleagues present a comprehensive analysis of translational buffering in human and mouse by mining 1515 matched ribosome profiling and RNAseq datasets from diverse tissues and cell lines. They define translational buffering as genes whose TE is negatively correlated with mRNA abundance across conditions, and further identify candidates by comparing median absolute deviations of ribosome occupancy versus mRNA levels. The authors find a conserved set of buffered genes enriched for components of multiprotein complexes, demonstrate that buffered genes exhibit lower protein variability and greater dosage sensitivity, and propose two non-mutually exclusive mechanistic models (differential accessibility and initiation rate modulation). Finally, they perform complementary fractionation experiments in HEK293T cells to support these models.

These findings propose a novel, conserved mechanism of translational buffering that tunes gene expression in mouse and human, showing how intrinsic sequence features and cellular context cooperate to stabilize protein output across diverse conditions. However, further evidence is required to fully support the authors conclusions, particularly direct validation of the proposed models of buffering. Below are my main concerns:

1. The choice of the top 250 genes by spearman correlation and MAD ratio as "TB high" seems arbitrary. The authors should justify these cut offs (via permutation analysis or FDR control) and show that conclusions are robust to different thresholds
2. The modified compositional regression approach for TE and imputation of missing values are central to the study, but details are relegated to supplemental methods. The manuscript would benefit from a clear comparison of this method against standard log-ratio TE estimates, including sensitivity analyses to missing-data imputation strategies
3. Human data are derived mainly from immortalized cell lines, whereas mouse data are from primary tissues. Pooling these heterogeneous sources may conflate cell type-specific regulation with intrinsic buffering. The authors should either stratify analyses by context or demonstrate buffering signatures remain consistent within more homogeneous subsets
4. The HEK293T fractionation experiments offer preliminary support for both the "accessibility" and "initiation" models, but only slope analyses are shown. To validate these models, the authors should perform targeted reporter assays (dual luciferase constructs with 5′UTR swaps) or manipulations of initiation factors (eIF4E knockdown) to directly test how transcript abundance alters initiation rates versus pool entry
5. The conclusion that buffering reduces protein variability relies on mass-spec comparisons, but ribosome occupancy does not always reflect functional protein output (due to elongation stalling or co-translational degradation). Incorporating orthogonal measures, such as pulse-labeling or western blots for key buffered versus non-buffered genes, would strengthen the link between buffering and proteome stability
6. While the LGBM modeling shows modest predictive power of sequence features alone, the manuscript stops short of exploring what cellular factors might drive context dependence. Integrating public datasets on RNA-binding protein expression or mTOR pathway activity across samples could illuminate trans-acting determinants of buffering and move beyond correlative sequence analyses

Significance

Overall, this manuscript leverages an unprecedented compendium of matched ribosome profiling and RNAseq datasets across human cell lines and mouse tissues, combined with improved TE estimation, to robustly catalog genes exhibiting translational buffering, a clear methodological and conceptual strength. The main limitations stem from heterogeneous sample sources, largely correlative analyses, and a lack of targeted mechanistic validation. Compared to prior yeast focused studies, it fills a key gap by demonstrating conservation of buffering in mammals and linking it to dosage sensitivity and protein stability, representing a conceptual advance in understanding post-transcriptional homeostasis and a methodological step forward in TE analysis. This work will interest researchers in RNA biology, gene expression regulation, systems biology, and cancer proteomics, as well as those studying dosage-sensitive pathways and translational control. My expertise is on translational control in cancer.

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

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

Thanks to the development of Ribo-Seq, translational buffering has been reported in various works. However, the systematic investigation has remained challenging. Employing the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. Although the authors' report provides a step forward in our understanding of translational buffering, this reviewer found a series of concerns in this paper. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

Major comments:

1. This paper heavily relies on the reference 18. However, this paper was not properly stated (no page or journal number); the study in Bioinformatics is nowhere to be found on the website, despite being out in 2024 apparently. Either title is wrong (yet a biorxiv can be found). This reviewer guessed that the reference 18 may be accepted. However, without a proper reference, this paper could not be judged since nearly all the parts of this work have been based on the reference 18. Also, the Ribobase data used in this manuscript comes from this reference, so it had better be well defined, especially when another Ribobase data set seems to be available online: http://www.bioinf.uni-freiburg.de/~ribobase/index.html
2. In the Discussion, the authors mentioned "TE is based on a compositional regression model (18) rather than the commonly applied approach of using a logarithmic ratio of ribosome occupancy to mRNA abundance." This important information should be mentioned early section of the manuscript. Related to this, there are other published methods for exploring change in translation efficiency (e.g., 10.1093/bioinformatics/btw585; 10.1093/nar/gkz223) that could also be suitable in this context. It is not entirely clear if their approach is better than before. Again, the improper reference to 18 made our assessment of this work difficult.
3. The paper mainly relies on detecting a set of buffered genes using mRNA-TE correlation and MAD ratios (Ribo-Seq/RNA-Seq). While the concept seems sound, the authors should ensure that this method is reliable. Several controls could be used to confirm this. First, if any studies in humans or mice have described a set of genes as buffered, it would be worth checking for overlap between the authors' set of 'TB high' genes and the previously established list. Furthermore, the authors could use packages explicitly developed for translational buffering detection, such as annota2seq (https://academic.oup.com/nar/article/47/12/e70/5423604?login=true). Not all of the data used by the authors may be suitable for such packages, but the authors could at least partially use them on some of their datasets and see whether the buffered genes reported by these packages match their predictions.
4. The threshold of 'TB high' or 'TB low' (top and bottom 250) is somewhat arbitrary. Why not top 100 or 500? The authors should provide a rationale for this choice. Also, they could include a numeric measure of buffering (the sum of the two rankings is probably suitable for this purpose). Several of the authors' explorations are suitable for numerical quantification (GO enrichment can be turned into GSEA, and the boxplot can be shown as correlations)
5. Several of the statements of the authors in the Introduction or Discussion sections are not entirely true regarding the literature on the topics, or lack major papers on the topic, and therefore, they are a bit misleading. Among others, here are some:

5-1 "In addition, genetic differences arising from aneuploidy, cell type differences or variability observed in the natural population can further determine the amplitude of variation (4-7). The effect of mRNA variation under these conditions is mostly reflected at the protein levels (2, 4-8).". Several recent or more ancient papers suggest that mRNA variation coming from aneuploidy, natural genetic variation, or CNV is buffered or not well reflected at the protein level:

DOI: 10.1038/s41586-024-07442-9 DOI: 10.1073/pnas.2319211121 DOI: 10.1016/j.cels.2017.08.013 DOI: 10.15252/msb.20177548

5-2: The authors should also consider mentioning these studies and softening their initial statement. "Similarly, translational buffering of certain genes have been reported in mammalian cells, specifically under estrogen receptor alpha (ERα) depletion conditions (16).". Translational buffering has been deeply explored in mammalian tissues and even across several mammalian species in this study (DOI: 10.1038/s41586-020-2899-z). In this, the authors also provide a nice exploration of the gene characteristics that are associated with translational buffering. The authors should mention it and compare the study's findings to theirs ultimately.

5-3: "Differences in species evaluated and statistical methods have resulted in conflicting interpretations (13, 28).". These conflicting results have been previously discussed in reviews on the topic that would be worth mentioning: DOI: 10.1016/j.cell.2016.03.014 DOI: 10.1038/s41576-020-0258-4 6. In addition to the p-values stated in the main text, the authors should annotate their plots when they find significant differences between groups to greatly facilitate the visual interpretation of the graphs. 7. Based on the data of Figure 4D, apparently, ribosome occupancy was not buffered even in high TB sets. The authors may argue that translational buffering may not cope with such a strong mRNA reduction. In that case, how big a difference in mRNA level does the buffering system adjust in protein synthesis? The authors should test gradual gene knockdown and/or overexpression and conduct Ribo-Seq/RNA-Seq to survey the buffering range. 8. "differential transcript accessibility model" could not be functional if mRNA is reduced beyond the accessible pool (i.e., less than the threshold, all the mRNAs are translated without buffering). The authors should carefully reconsider this model and the effective range of mRNAs.

Minor comments:

1. Some figures are of poor quality as they seem to have points outside of the panel representations... Like Figure 3C, one point is out of the square, same for Figure 4E. Similarly, on figure 5F, some outliers seem to be clearly cut from the figure (maybe not, but then the author should put a larger space between the end of the figure and the max y points). Same for panel S2D and S6D, this does not sound so rigorous.
2. There are several typos or weird sentences. Here are some (but maybe not all):

2-1: [...]with lower sums corresponding to higher final ranks. "two rankings". Based on these final ranks[...]

2-2: For each dataset, median absolute deviation (MAD) "i" protein abundance was calculated across samples

2-3: [...]neighbor method implemented in the MatchIT package (38) Differences in protein[...] a point is missing here.

2-4: Additionally a second dataset providing predictions of haploinsufficiency (pHaplo score) and triplosensitivity (pTriplo score) for all autosomal genes (25) was used to asses the distribution of these score"S" across buffered and non-buffered gene sets . There is a missing "s" at "score" and there is a space between the last word and the final point. 3. In the "Lymphoblastoid cell line data analysis:" section, this reviewer wonders why the authors used a different method to calculate buffering compared to before. 4. "Samples which had R2 less than 0.2 were removed as the residuals calculated for these samples could be unreliable". These samples for which the correspondence between RNA-Seq and Ribo-Seq is low wouldn't be the ones most impacted by translational buffering? Is it sure that the authors are not missing something here? 5. For Figure 4B and 4C, the authors should provide statistical tests and p-values to confirm the observed trends. 6. In Figure 2A, the "all genes" color doesn't correspond to the point color. 7. "To understand if codon usage patterns are[...]". This comes slightly out of the blue. The authors could maybe explain why codon usage should be explored for translational buffering. The authors should cite recent key works in the fields: DOI: 10.1016/j.celrep.2023.113413 DOI: 10.1101/2023.11.27.568910 8. "The change in each metric was calculated by subtracting the mean value in the control samples from that in the knockdown samples. This yielded the differential mRNA abundance and ribosome occupancy resulting from gene knockdown.". This looks statistically weak. The authors should consider using more robust methods like DESeq. 9. "Genes in the buffered gene set had a higher codon adaptation index than the non-buffered set, indicating that candidates in the buffered gene set are relatively well expressed due to the presence of a higher proportion of the codons observed in highly expressed genes". What do the authors mean by "relatively well expressed"? Abundantly expressed? This sentence and the causality under it is unclear and should be modified or better explained. 10. The panel 4D is unclear. Is one point associated with one gene? Or is it the average of several genes? If it's one point for one gene, it is important to clearly state it because the number of cases is therefore quite low, especially for the TB high and low. 11. In Figure 2J, GGU (Gly), AAG (Lys), and ACU (Arg) provide negative effects on prediction, although these were enriched in the high TB set (Figure 2E). This contradiction should be explained. 12. The subtitle of "Translationally buffered genes exhibit variable association kinetics with the translational machinery in response to mRNA variation" sounds unfair to this reviewer. Since the authors did not work on kinetics directly, the use of this word is misleading. 13. The explanation of Figure 5A "We next explored the potential mechanisms that may give rise to translational buffering. Specifically, we considered two non-mutually exclusive models by which mRNA abundance might be decoupled from ribosome occupancy. In the first, the "differential transcript accessibility model", mRNA abundance determines the fraction of transcripts that are accessible to the translational pool. In this scenario, an increase in mRNA abundance would be accompanied by a proportionally smaller increase in the fraction of transcripts entering the translating pool for buffered genes, compared to non-buffered genes. In the second, the "initiation rate model", the rate of translation initiation per transcript scales inversely with mRNA abundance. Under this model, the proportion of mRNA entering the translational pool would be comparable across buffered and non-buffered genes (Fig 5A)." is hard to understand. The authors should rewrite for a better understanding of the readers.

Significance

Thanks to the development of Ribo-Seq, translational buffering has been reported in various works. However, the systematic investigation has remained challenging. Employing the database of published Ribo-Seq and matched RNA-Seq, Rao et al. attempt to understand the mechanism underlying translational buffering of mRNA variation across diverse materials. A group of mRNAs whose expression variance is buffered at the translation level was comprehensively surveyed in humans and mice. The authors found a series of features in the translationally buffered genes, including high GC contents in the 5′ UTR, optimal codon usage, and mRNA length. The depletion or increase of one allele of the genes in the group may be particularly detrimental to cells. The authors' report provides a step forward in our understanding of translational buffering, appealing to the broad scientific community in basic and applied biology. However, this reviewer found a series of concerns in this paper, including clarity in the methods, experimental validation, referring the earlier works, etc. These points could be tackled to improve the reliability of their findings, the strength of their main message, and the global understandability of the paper.

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Reply to the reviewers

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

SECTION A - Evidence, Reproducibility, and Clarity Summary The study investigates the neurodevelopmental impact of trisomy 21 on human cortical excitatory neurons derived from induced pluripotent stem cells (hiPSCs). Key findings include a modest reduction in spontaneous firing, a marked deficit in synchronized bursting, decreased neuronal connectivity, and altered ion channel expression-particularly a downregulation of voltage‐gated potassium channels and HCN1. These conclusions are supported by a combination of in vitro calcium imaging, electrophysiological recordings, viral monosynaptic tracing, RNA sequencing, and in vivo transplantation with two‐photon imaging.

Major Comments • Convincing Nature of Key Conclusions: The study's conclusions are generally well supported by a diverse set of experimental approaches. However, certain claims regarding the intrinsic properties of the excitatory network would benefit from further qualification. In particular, the assertion that reduced synchronization is solely attributable to altered ion channel expression might be considered somewhat preliminary without additional corroborative experiments.

1.1) We agree with the reviewer and now write in the abstract: 'Together, these findings demonstrate long-lasting impairments in human cortical excitatory neuron network function associated with Trisomy 21 .' And in the Introduction: 'Collectively, the observed changes in ion channel expression, neuronal connectivity, and network activity synchronization may contribute to functional differences relevant to the cognitive and intellectual features associated with Down syndrome.'

• One major limitation of the current experimental design is the reliance on predominantly excitatory neuronal cultures derived from hiPSCs. Although the authors convincingly demonstrate differences in network synchronization and connectivity between trisomic (TS21) and control neurons, the almost exclusive focus on excitatory cells limits the physiological relevance of the in vitro network. In the developing cortex, interneurons and astrocytes play crucial roles in modulating network excitability, synaptogenesis, and plasticity. Therefore, incorporating these cell types-either through co-culture systems or through directed differentiation protocols that yield a more heterogeneous neuronal population-could help to determine whether the observed deficits are intrinsic to excitatory neurons or are compounded by a lack of proper inhibitory regulation and glial support. 1.2) Thank you for this thoughtful comment. We agree that interneurons and astrocytes are crucial for network function. To clarify, astrocytes are generated in this culture system, as we previously reported in our characterisation of the timecourse of network development using this approach (Kirwan et al., Development 2025). However, our primary goal was to first isolate and define the cell-autonomous defects intrinsic to TS21 excitatory neurons, minimizing the complexity introduced by additional neuronal types. This focused approach was chosen also because engineering a stable co-culture system with reproducible excitatory/inhibitory (E/I) proportions is a significant undertaking that extends beyond the scope of this initial investigation, and has proven challenging to date for the field. By establishing this foundational phenotype, our work complements prior studies on interneuron and glial contributions. Future studies building on this work will be essential to dissect the more complex, non-cell-autonomous effects within a heterogeneous network. Importantly, since our initial submission, two highly relevant preprints have emerged-including a notable study from the Geschwind laboratory at UCLA (Vuong et al., bioRxiv, 2025; Risgaard et al., bioRxiv, 2025), as well as our own complementary study Lattke et al, under revision, that highlight widespread transcriptional changes in excitatory cells of the human fetal DS cortex, providing strong validation for our central findings. This convergence of results from multiple groups underscores the timeliness and importance of our work.

• Furthermore, the assessment of neuronal connectivity via pseudotyped rabies virus tracing, while innovative, has inherent limitations. The quantification of connectivity as a ratio of red-to-green fluorescence pixels may be influenced by differential viral infection efficiencies, variations in the expression levels of the TVA receptor, or even by the lower basal activity levels observed in TS21 cultures. Complementary approaches-such as electron microscopy for synaptic density analysis or functional connectivity measurements using multi-electrode arrays (MEAs)-could provide additional structural and functional insights that would validate the rabies tracing data. 1.3) Thank you for this constructive feedback. While we cannot formally exclude that TS21 cells might express the TVA receptor at lower levels due to generalized gene dysregulation, we infected all WT and TS21 cultures in parallel using identical virus preparations and titers to minimize technical variability. Crucially, we also addressed the potential confound of differential basal activity by performing the rabies tracing under TTX incubation (see Suppl. Fig. 7), which blocks network activity and ensures that viral spread reflects structural connectivity alone.

While complementary methods like EM or MEA could provide additional insight, they fall outside the scope of the current study. We are confident that our rigorous controls validate our use of the rabies tracing method to assess structural connectivity.

• Qualification of Claims: Some conclusions, particularly those linking specific ion channel dysregulation (e.g., HCN1 loss) directly to network deficits, might be better presented as preliminary. The authors could temper their language to indicate that while the evidence is suggestive, the mechanistic link remains to be fully established. 1.4) We have revised the text to more clearly indicate that the link between HCN1 dysregulation and network deficits is correlative and remains to be fully established. While our ex vivo recordings suggest altered Ih-like currents consistent with reduced HCN1 expression, we now present these findings as preliminary and hypothesis-generating, pending further functional validation. We write in the discussion: However, further targeted functional validation will be needed to confirm a causal link.

• Need for Additional Experiments: Additional experiments that could further consolidate the current findings include: o Inclusion of Inhibitory Neurons or Co-culture Systems: Incorporating interneurons or astrocytes would help determine whether the observed deficits are solely intrinsic to excitatory neurons. See 1.2 o Alternative Connectivity Assessments: Complementing the rabies virus tracing with electron microscopy or multi-electrode array (MEA) recordings would add structural and functional validation of the connectivity differences. See 1.3 o Extended Temporal Profiling: Monitoring network activity over a longer developmental window would clarify whether the observed deficits represent a delay or a permanent alteration in network maturation. 1.5) In vivo we were able to track the cells for up to five months post-transplantation supporting the interpretation of a permanent alteration.

• Reproducibility and Statistical Rigor: The methods and data presentation are largely clear, with adequate replication and appropriate statistical analyses. Nonetheless, a more detailed description of the experimental replicates, particularly regarding the viral tracing and in vivo transplantation studies, would enhance reproducibility. The availability of raw data and scripts for calcium imaging analysis would also further support independent verification. We thank the reviewer for these suggestions and we now provide a more detailed description of replicates. We also add the raw data.

Minor Comments • Experimental Details: Minor revisions could include clarifying the infection efficiency and expression levels of the viral constructs used in connectivity assays to rule out technical variability.

See 1.3

• Literature Context: The authors reference prior studies appropriately; however, integrating a brief discussion comparing their findings with alternative DS models (e.g., organoids or other hiPSC-derived systems) would improve contextual clarity. We thank the reviewer for this helpful suggestion. We have now added a brief discussion comparing our findings with those reported in alternative Down syndrome models, including brain organoids and other hiPSC-derived systems. This addition helps to contextualize our results within the broader field and highlights the unique strengths and limitations of our in vitro and in vivo xenograft approach. We write: 'Our findings align with and extend previous studies using alternative Down syndrome models, such as brain organoids and other hiPSC-derived systems. Organoid models have provided valuable insights into early neurodevelopmental phenotypes in DS, including altered interneuron proportions (Xu et al Cell Stem Cell 2019) but also suggest that variability across isogenic lines can overshadow subtle trisomy 21 neurodevelopmental phenotypes (Czerminski et al Front in Neurosci 2023). However, these systems often lack the structural complexity, vascularization, and long-term maturation achievable in vivo. By using a xenotransplantation model, we were able to assess the maturation and functional properties of human neurons within a physiologically relevant environment over extended time frames, offering complementary insights into DS-associated circuit dysfunction (Huo et al Stem Cell Reports 2018; Real et al., 2018).

• Presentation and Clarity: Figures are generally clear,.But the manuscript contains a minor labeling error. On page 13, the figure is erroneously labeled as "Fig6A", whereas, based on the context and corresponding data, it should be "Fig5A". I recommend that the authors correct this mistake to ensure consistency and avoid potential confusion for readers. Thank you for pointing this out. This has been corrected in the revised manuscript.

Reviewer #1 (Significance (Required)):

SECTION B - Significance • Nature and Significance of the Advance: The work offers a substantial conceptual advance by providing a mechanistic link between trisomy 21 and impaired neuronal network synchronization. Technically, the study integrates state-of-the-art imaging, electrophysiology, and transcriptomic profiling, thereby offering a multifaceted view of DS-related neural dysfunction. Clinically, the findings have the potential to inform future therapeutic strategies targeting network connectivity and ion channel function in Down syndrome.

We thank the reviewer for this very supportive comment.

• Context in the Existing Literature: The study builds on previous observations of altered network activity in DS patients and DS mouse models (e.g., altered EEG synchronization and reduced synaptic connectivity). It extends these findings to human-derived neuronal models, thus bridging a gap between clinical observations and molecular/cellular mechanisms. Relevant literature includes studies on DS neurodevelopment and the role of ion channels in synaptic maturation. • Target Audience: The reported findings will be of interest to researchers in neurodevelopmental disorders, Down syndrome, and ion channel physiology. Additionally, the study may attract the attention of those working on hiPSC-derived models of neurological diseases, as well as clinicians interested in the pathophysiology of DS. • Keywords and Field Contextualization: Keywords: Down syndrome, trisomy 21, neuronal connectivity, synchronized network activity, hiPSC-derived cortical neurons, ion channel dysregulation.

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

Summary The manuscript by Peter et al., reports on the neuronal activity and connectivity of iPSC-derived human cortical neurons from Down syndrome (DS) that is caused by caused by trisomy of the human chromosome 21 (TS21). Major points: Although the manuscript is potentially interesting, the results appear somehow preliminary and need to be corroborated by control experiments and quantifications of effects to fully sustain the conclusions. (1) The authors have not assessed the percentage of WT and TS21 cells that acquire a neuronal or glia identity in their cultures. Indeed, the origin of alterations in network activity and connectivity observed in TS21 neurons could simply derive from reduced number of neurons arising from TS21 iPSC. Alternatively, the same alteration in network activity and connectivity could derive from a multitude of other factors including deficits in neuronal development, neurite extension, or intrinsic electrophysiological properties. In the current version of the manuscript, none of these has been investigated. 2.1) We thank the reviewer for this thoughtful comment. In response, we included an in vivo characterization of cell-type proportions at the same time points where we observed network activity defects using in vivo calcium imaging (see Supplementary Fig. 6).

Previous work has identified several cellular and molecular phenotypes in human cells, postmortem tissue, and mouse models-including those mentioned by the reviewer. In this study, our focus was on investigating neural network activity, intrinsic electrophysiological properties both in vitro and in vivo, and preliminary bulk RNA sequencing. We have also independently measured cell proportions in the human fetal cortex and conducted a more extensive transcriptomic analysis of Ts21 versus control cells in a separate study (Lattke et al., under revision). We observed a reduction of RORB/FOXP1-expressing Layer 4 neurons in the human fetal cortex at midgestation, as well as increased GFAP+ cells, reduced progenitors and a non significant reduction of Cux2+ cells in late stage DS human cell transplants, along with a gene network dysregulation specifically affecting excitatory neurons (Lattke et al., under revision). Here, we provide complementary findings, demonstrating reduced excitatory neuron network connectivity in vitro and decreased neural network synchronised activity in both in vitro and in vivo models (see also 2.8). We agree with the reviewer that this could be for a number of reasons, both cell autonomous (channel expression and/or function) or non-autonomous (connectivity and/or network composition - as reflected in differences in proportions of SATB2+ neurons generated in TS21 cortical differentiations).

(2) Electrophysiological properties of TS21 and WT neurons at day 53/54 in vitro indicate an extremely immature stage of development (i.e. RMP between -36 and -27 mV with most of the cells firing a single action potential after current injection) in the utilized culture conditions: This is far from ideal for in vitro neuronal-network studies. Finally, reduced activity of HCN1 channels should be confirmed by specific recordings isolating or blocking the related current.

2.2) Thank you for this thoughtful comment. We have also conducted ex vivo electrophysiological recordings and found that the neurons exhibit relatively immature properties, consistent with the known slow developmental trajectory of human neuron cultures. In light of this and the absence of direct confirmatory evidence, we now refer to the observed reduction in HCN1 as preliminary.

Main points highlighting the preliminary character of the study. 1) In Figure 1 immunofluorescence images of the neuronal differentiation markers (Tbr1, Ctip2 and Tuj1) are showed. However, no quantification of the percentage of cells expressing these markers for WT and TS21 neurons is reported. On the other hand, simple inspection of the representative images clearly seams to indicate a difference between the two genotypes, with TS21 cultures showing lower number of cells expressing neuronal markers. This quantification should be corroborated by a similar staining for an astrocyte marker (GFAP, but not S100b since is triplicated in DS). This is an extremely important point since it is obvious that any change in the percentage of neurons (or the neuron/astrocyte ratio) in the cultures will strongly affect the resulting network activity (shown in Figure 2) and the connectivity (showed in Figure 4). Possibly, the quantification should be done at the same time points of the calcium imaging experiments.

2.3) See 2.1. We included an in vivo characterization of cell-type proportions at the same time points where we observed network activity defects using in vivo calcium imaging. (see Supplementary Fig. 6).

2) In Figure 2 the authors show some calcium imaging traces of WT and TS21 cultures at different time points. However, they again do not show any quantification of neuronal activity. A power spectra analysis is shown in Supplementary Figure 2, but only for WT cultures, while in Supplementary Figure 3 a comparison between WT and Ts21 power spectra is done, but only at the 50 day time point, while difference in synchrony are assessed at 60 days. At minimum, the author should include in main Figure 2 the quantification of the mean calcium event rate and mean event amplitude at the different time points and the power spectra analysis for both WT and TS21 cultures at the same timepoints.

2.4) We thank the reviewer for this comment. We now add the power spectra analysis in the main Figure 2 and quantification of the mean calcium burst rate and mean event amplitude in SuppFig. 4.

Of note, the synchronized neuronal activity is present in WT cultures at day 60, but totally lost at subsequent time-points (70 and 80 days). The results of this later time points are different from previous data from the same lab (Kirwan et al., 2015). How might these data be explained? It would be important to rule out any potential issues with the health of the culture that could explain the loss of neuronal activity.It would be beneficial to check cell viability at the different time points to exclude possible confounding factors ? A propidium staining or a MTT assay would strongly improve the soundness of the calcium data.

2.5) We thank the reviewer for this important observation. The difference from the findings reported in Kirwan et al., 2015 is due to the use of a different neuronal differentiation medium in the current study (BrainPhys versus N2B27). BrainPhys medium supports robust early network activity compared to N2B27 (onset before day 60 in BrainPhys, post-day 60 in N2B27), resulting in an earlier decline in synchrony at later stages (day 70-80 in BrainPhys, compared with day 90-100 in N2B27). Importantly, in our in vivo xenograft model, burst activity is sustained up to at least 5 months post-transplantation (mpt), indicating that the neurons retain the capacity for network activity over extended periods in a more physiological environment. We adapted the text accordingly.

3) In Figure 3 there is no quantification of the number and/or density of transplanted neurons for WT and TS21, but only representative images. As above, inspection of the representative images seems to show a decrease in cells labeled by the Tbr1 neuronal marker for TS21 cells. Moreover, the in vivo calcium imaging of transplanted WT and TS21 cells lacks most of the quantification normally done in calcium imaging experiments. Are the event rate and event amplitude different between WT and TS21 neurons ? The measure of neuronal synchrony by mean pixel correlation is not well explained, but it looks somehow simplistic. Neuronal synchrony can be more precisely measured by cross-correlation analysis or spike time tiling coefficients on the traces from single-neuron ROI rather than on all pixels in the field of view, as apparently was done here.

2.6) We thank the reviewer for these valuable points. We now include quantification of the number and density of transplanted neurons for both WT and Ts21 grafts in Extended Data Figure 5 (see 2.1).

Regarding the in vivo calcium imaging, we appreciate the reviewer's suggestion to include additional standard metrics. We have quantified the event rate in Real et al 2018. These analyses reveal that Ts21 neurons show a reduction in event rate.

We agree that our initial description of the synchrony analysis using mean pixel correlation was not sufficiently detailed. We have now clarified this in the Methods and Results, and we acknowledge its limitations. Importantly, we note that the reduced synchronisation is a highly consistent phenotype, observed across at least six independent donor pairs, different differentiation protocols, and both in vitro (and in two independent labs) and in vivo settings. As suggested, future studies using ROI-based approaches-such as cross-correlation or spike-time tiling coefficients-would provide a more refined characterization of synchrony at the single-neuron level (Sintes et al, in preparation). We now include this point in the discussion.

4) The results on reduced neuronal connectivity in Figure 3 look very striking. However, these results should be accompanied by control experiments to verify the number of neuronal cells and neurite extension in WT and Ts21 cultures. These two parameters could indeed strongly influence the results. As the cultures appear to grow in clusters, bright-field images and TuJ1 staining of the cultures will also greatly help to understand the degree of morphological interconnection between the clusters.

We now add Tuj1 staining in Supplementary figure 10.

5) The authors performed RNA-seq experiments on day 50 cultures. Why the authors do not show the complete differential gene expression analysis, but only a small subset of genes? A comprehensive volcano plot and the complete list of identified genes with logFC and FDR values would be helpful. If possible, comparison of the present data (particularly on KCN and HCN expression changes) with published and publicly available expression datasets of other human or human Down syndrome iPSC-derived neurons or human Down syndrome brains will greatly increase the soundness of the present findings. In addition, the gene ontology (GO) results are mentioned in the text, but are not presented. Showing the complete GO analysis for both up and downregulated genes will help the reader to better understand the RNA-seq results. Notably, the results shown in Supplementary Figure on GRIN2A and GRIN2B expression (with values of 300-700 counts versus 2000-4000 counts, respectively) clearly indicate that in both WT and TS21 cultures the NMDA developmental switch has not occurred yet at the 50 days timepoint.

We now show volcano plots in Supplementary Fig. 11.

6) The measure of hyperpolarization-activated currents shown in Figure 5 lack proper control experiments. First, the hyperpolarizing current in TS21 cells do not reach a steady-state as the controls. The two curves are therefore hard to compare. To exclude possible difference in kinetic activation, the authors should have prolonged the current injection period (1-2 seconds). Second, to ultimately prove that such currents are mediated by HCN channels in WT cells the authors should perform some control experiments with a specific HCN blocker. A good example of a suitable protocol, with also current blockers to exclude all other possible current contributions, is the one reported in Matt et al Cell. Mol. Life Sci. 68, 125-137 (2011).

2.7) We thank the reviewer for this detailed and helpful comment. We agree that to definitively identify the recorded currents as Ih, it would be necessary to isolate them pharmacologically using specific HCN channel blockers and appropriate controls, such as those described in Matt et al., Cell. Mol. Life Sci. Unfortunately, due to current constraints, we no longer have access to the animals used in this study and cannot allocate the necessary time or resources, we are unable to perform the additional experiments at this stage.

However, our goal here was to use electrophysiological recordings as an indication of altered HCN channel activity, which we then support with molecular evidence. We now emphasize this point more clearly in the revised manuscript.

7) The manuscript lacks information on the statistical analysis used. Also, the numerosity of samples is not clear. Were the dots shown in some graph technical replicates from a single neuronal induction or were all independent neuronal inductions or a mix of the two ? Please clarify.

We now clarify the numbers in the Figure legend.

8) The method section lacks important information to guarantee reproducibility. Just a few examples: • Only electrophysiology methods for slice are reported, but not for in vitro culture.

We now clarify these details in the methods.

• Details on Laminin coating is lacking. What concentration was used ? Was poly-ornithine or poly-lysine used before Laminin coating ? We now clarify these details in the methods.

• How long cells were switched to BrainPhys medium before calcium imaging ? We now clarify these details in the methods.

Minor point/typos etc.

Introduction • Page 4 line 6: in the line "Trisomy 21 in humans commonly results in a range in developmental and morphological changes in the forebrain ..." "in" could be replaced by "of". We have fixed this. • Page 5 line 2: please remove "an" before the word "another". We have fixed this. • Page 5 line 2: please replace "ecitatory" with "excitatory". We have fixed this typo.

Results • Page 10 line 25: The concept of "pixel-wise" appears for the first time in this section and could be better introduced to facilitate the understanding of the experiment. • In the "results" section, page 11 line 1 and 4, references are made to "Figure 4D" and "4F," but these figures do not appear to be present in the figure section. Upon reviewing the rest of the section, the data seem to refer to "Figure 3D" and "3E." We have fixed this. Discussion • Page 15 line 20: please replace "synchronised" with "synchronized". We have fixed this typo. • Page 16 line 11: please replace "T21" with "TS21". We have fixed this typo. Methods • Page 19 line 12: "Pens/Strep" has to be replaced by Pen/Strep. We have fixed this typo. • Page 20 line 20: "Tocris Biocience" has to be replaced by "Tocris Bioscience". We have fixed this typo. • Page 21 line 2: "Addegene" has to be replaced by "Addgene". We have fixed this typo. Figures • Figure 3: the schematic experimental design (Fig. 3A) could be enlarged to match the width of the images/graphs below. We have fixed this. • Figure 5: the reviewer suggests resizing/repositioning the graphs in Fig. 1A so that they match the width of those below. We have fixed this. • Figure S1D: In all the figures of the paper, the respective controls for the TS21 1 and TS21 2 lines are labelled as "WT1/WT2," while in these graphs, they are called "Ctrl1" and "Ctrl2." To ensure consistency throughout the paper, it is suggested to change the names in these graphs. We have fixed this. • Figure S4L: The graph is not very clear, especially regarding the significance reported at -50 pA, please modify the graphical visualization and/or add a legend in the caption. We have fixed this.

Reviewer #2 (Significance (Required)):

Nature and significance of the advance for the field. The results presented in the manuscript are potentially interesting and useful, but not completely novel (currents deregulation has already been highlighted in mouse models of Down Syndrome).

2.8) We thank the reviewer for this comment. While we agree that current deregulation has been observed in mouse models of Down syndrome, the novelty and significance of our study lie in demonstrating these alterations directly in human neurons using both in vitro and in vivo xenograft models.

This is a critical advance because the human cortex has distinct developmental and functional properties not fully recapitulated in mice. In fact, three recent studies have already highlighted significant defects mainly in excitatory neurons within the fetal human DS cortex (Vuong et al., bioRxiv, 2025; Risgaard et al., bioRxiv, 2025; Lattke et al, under revision). Our work builds directly on these observations by providing, for the first time, an electrophysiological and network-level characterization of these human-specific deficits.

Our findings thus provide translationally relevant insight that is not merely confirmatory but extends previous work by grounding it in a human cellular context.

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Referee #2

Evidence, reproducibility and clarity

Summary

The manuscript by Peter et al., reports on the neuronal activity and connectivity of iPSC-derived human cortical neurons from Down syndrome (DS) that is caused by caused by trisomy of the human chromosome 21 (TS21).

Major points:

Although the manuscript is potentially interesting, the results appear somehow preliminary and need to be corroborated by control experiments and quantifications of effects to fully sustain the conclusions.

(1) The authors have not assessed the percentage of WT and TS21 cells that acquire a neuronal or glia identity in their cultures. Indeed, the origin of alterations in network activity and connectivity observed in TS21 neurons could simply derive from reduced number of neurons arising from TS21 iPSC. Alternatively, the same alteration in network activity and connectivity could derive from a multitude of other factors including deficits in neuronal development, neurite extension, or intrinsic electrophysiological properties. In the current version of the manuscript, none of these has been investigated.

(2) Electrophysiological properties of TS21 and WT neurons at day 53/54 in vitro indicate an extremely immature stage of development (i.e. RMP between -36 and -27 mV with most of the cells firing a single action potential after current injection) in the utilized culture conditions: This is far from ideal for in vitro neuronal-network studies. Finally, reduced activity of HCN1 channels should be confirmed by specific recordings isolating or blocking the related current.

Main points highlighting the preliminary character of the study.

1) In Figure 1 immunofluorescence images of the neuronal differentiation markers (Tbr1, Ctip2 and Tuj1) are showed. However, no quantification of the percentage of cells expressing these markers for WT and TS21 neurons is reported. On the other hand, simple inspection of the representative images clearly seams to indicate a difference between the two genotypes, with TS21 cultures showing lower number of cells expressing neuronal markers. This quantification should be corroborated by a similar staining for an astrocyte marker (GFAP, but not S100b since is triplicated in DS). This is an extremely important point since it is obvious that any change in the percentage of neurons (or the neuron/astrocyte ratio) in the cultures will strongly affect the resulting network activity (shown in Figure 2) and the connectivity (showed in Figure 4). Possibly, the quantification should be done at the same time points of the calcium imaging experiments.

2) In Figure 2 the authors show some calcium imaging traces of WT and TS21 cultures at different time points. However, they again do not show any quantification of neuronal activity. A power spectra analysis is shown in Supplementary Figure 2, but only for WT cultures, while in Supplementary Figure 3 a comparison between WT and Ts21 power spectra is done, but only at the 50 day time point, while difference in synchrony are assessed at 60 days. At minimum, the author should include in main Figure 2 the quantification of the mean calcium event rate and mean event amplitude at the different time points and the power spectra analysis for both WT and TS21 cultures at the same timepoints.

Of note, the synchronized neuronal activity is present in WT cultures at day 60, but totally lost at subsequent time-points (70 and 80 days). The results of this later time points are different from previous data from the same lab (Kirwan et al., 2015). How might these data be explained? It would be important to rule out any potential issues with the health of the culture that could explain the loss of neuronal activity.It would be beneficial to check cell viability at the different time points to exclude possible confounding factors ? A propidium staining or a MTT assay would strongly improve the soundness of the calcium data.

3) In Figure 3 there is no quantification of the number and/or density of transplanted neurons for WT and TS21, but only representative images. As above, inspection of the representative images seems to show a decrease in cells labeled by the Tbr1 neuronal marker for TS21 cells. Moreover, the in vivo calcium imaging of transplanted WT and TS21 cells lacks most of the quantification normally done in calcium imaging experiments. Are the event rate and event amplitude different between WT and TS21 neurons ? The measure of neuronal synchrony by mean pixel correlation is not well explained, but it looks somehow simplistic. Neuronal synchrony can be more precisely measured by cross-correlation analysis or spike time tiling coefficients on the traces from single-neuron ROI rather than on all pixels in the field of view, as apparently was done here.

4) The results on reduced neuronal connectivity in Figure 3 look very striking. However, these results should be accompanied by control experiments to verify the number of neuronal cells and neurite extension in WT and Ts21 cultures. These two parameters could indeed strongly influence the results. As the cultures appear to grow in clusters, bright-field images and TuJ1 staining of the cultures will also greatly help to understand the degree of morphological interconnection between the clusters.

5) The authors performed RNA-seq experiments on day 50 cultures. Why the authors do not show the complete differential gene expression analysis, but only a small subset of genes? A comprehensive volcano plot and the complete list of identified genes with logFC and FDR values would be helpful. If possible, comparison of the present data (particularly on KCN and HCN expression changes) with published and publicly available expression datasets of other human or human Down syndrome iPSC-derived neurons or human Down syndrome brains will greatly increase the soundness of the present findings. In addition, the gene ontology (GO) results are mentioned in the text, but are not presented. Showing the complete GO analysis for both up and downregulated genes will help the reader to better understand the RNA-seq results. Notably, the results shown in Supplementary Figure on GRIN2A and GRIN2B expression (with values of 300-700 counts versus 2000-4000 counts, respectively) clearly indicate that in both WT and TS21 cultures the NMDA developmental switch has not occurred yet at the 50 days timepoint.

6) The measure of hyperpolarization-activated currents shown in Figure 5 lack proper control experiments. First, the hyperpolarizing current in TS21 cells do not reach a steady-state as the controls. The two curves are therefore hard to compare. To exclude possible difference in kinetic activation, the authors should have prolonged the current injection period (1-2 seconds). Second, to ultimately prove that such currents are mediated by HCN channels in WT cells the authors should perform some control experiments with a specific HCN blocker. A good example of a suitable protocol, with also current blockers to exclude all other possible current contributions, is the one reported in Matt et al Cell. Mol. Life Sci. 68, 125-137 (2011).

7) The manuscript lacks information on the statistical analysis used. Also, the numerosity of samples is not clear. Were the dots shown in some graph technical replicates from a single neuronal induction or were all independent neuronal inductions or a mix of the two ? Please clarify.

8) The method section lacks important information to guarantee reproducibility. Just a few examples: - Only electrophysiology methods for slice are reported, but not for in vitro culture. - Details on Laminin coating is lacking. What concentration was used ? Was poly-ornithine or poly-lysine used before Laminin coating ? - How long cells were switched to BrainPhys medium before calcium imaging ?

Minor point/typos etc.

Introduction

• Page 4 line 6: in the line "Trisomy 21 in humans commonly results in a range in developmental and morphological changes in the forebrain ..." "in" could be replaced by "of".
• Page 5 line 2: please remove "an" before the word "another".
• Page 5 line 2: please replace "ecitatory" with "excitatory"

Results

• Page 10 line 25: The concept of "pixel-wise" appears for the first time in this section and could be better introduced to facilitate the understanding of the experiment.
• In the "results" section, page 11 line 1 and 4, references are made to "Figure 4D" and "4F," but these figures do not appear to be present in the figure section. Upon reviewing the rest of the section, the data seem to refer to "Figure 3D" and "3E."

Discussion

• Page 15 line 20: please replace "synchronised" with "synchronized".
• Page 16 line 11: please replace "T21" with "TS21".

Methods

• Page 19 line 12: "Pens/Strep" has to be replaced by Pen/Strep.
• Page 20 line 20: "Tocris Biocience" has to be replaced by "Tocris Bioscience".
• Page 21 line 2: "Addegene" has to be replaced by "Addgene".

Figures

• Figure 3: the schematic experimental design (Fig. 3A) could be enlarged to match the width of the images/graphs below.
• Figure 5: the reviewer suggests resizing/repositioning the graphs in Fig. 1A so that they match the width of those below.
• Figure S1D: In all the figures of the paper, the respective controls for the TS21 1 and TS21 2 lines are labelled as "WT1/WT2," while in these graphs, they are called "Ctrl1" and "Ctrl2." To ensure consistency throughout the paper, it is suggested to change the names in these graphs.
• Figure S4L: The graph is not very clear, especially regarding the significance reported at -50 pA, please modify the graphical visualization and/or add a legend in the caption.

Significance

Nature and significance of the advance for the field. The results presented in the manuscript are potentially interesting and useful, but not completely novel (currents deregulation has already been highlighted in mouse models of Down Syndrome).

Work in the context of the existing literature. This work follows the line of evidence that characterizes Down Syndrome in human neurons (Huo, H.-Q. et al. Stem Cell Rep. 10, 1251-1266 (2018); Briggs, J. A. et al. Etiology. Stem Cells 31, 467-478 (2013)), both in vitro and in xenotransplanted mice, by corrborating some important findings already found in animal models (Stern, S., Segal, M. & Moses, E. EBioMedicine 2, 1048-1062 (2015); Cramer, N. P., Xu, X., F. Haydar, T. & Galdzicki, Z. Physiol. Rep. 3, e12655 (2015); Stern, S., Keren, R., Kim, Y. & Moses, E. http://biorxiv.org/lookup/doi/10.1101/467522 (2018) doi:10.1101/467522.

Audience. Scientists in the field of pre-clinical biomedical research, especially those working on neurodevelopmental disorders and iPSC-based non-animal models.

Field of expertise. In vitro electrophysiology, Neurodevelopmental disorders, Down Syndrome, ips cells.

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

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Referee #1

Evidence, reproducibility and clarity

Summary

The study investigates the neurodevelopmental impact of trisomy 21 on human cortical excitatory neurons derived from induced pluripotent stem cells (hiPSCs). Key findings include a modest reduction in spontaneous firing, a marked deficit in synchronized bursting, decreased neuronal connectivity, and altered ion channel expression-particularly a downregulation of voltage‐gated potassium channels and HCN1. These conclusions are supported by a combination of in vitro calcium imaging, electrophysiological recordings, viral monosynaptic tracing, RNA sequencing, and in vivo transplantation with two‐photon imaging.

Major Comments

• Convincing Nature of Key Conclusions: The study's conclusions are generally well supported by a diverse set of experimental approaches. However, certain claims regarding the intrinsic properties of the excitatory network would benefit from further qualification. In particular, the assertion that reduced synchronization is solely attributable to altered ion channel expression might be considered somewhat preliminary without additional corroborative experiments.
• One major limitation of the current experimental design is the reliance on predominantly excitatory neuronal cultures derived from hiPSCs. Although the authors convincingly demonstrate differences in network synchronization and connectivity between trisomic (TS21) and control neurons, the almost exclusive focus on excitatory cells limits the physiological relevance of the in vitro network. In the developing cortex, interneurons and astrocytes play crucial roles in modulating network excitability, synaptogenesis, and plasticity. Therefore, incorporating these cell types-either through co-culture systems or through directed differentiation protocols that yield a more heterogeneous neuronal population-could help to determine whether the observed deficits are intrinsic to excitatory neurons or are compounded by a lack of proper inhibitory regulation and glial support.
• Furthermore, the assessment of neuronal connectivity via pseudotyped rabies virus tracing, while innovative, has inherent limitations. The quantification of connectivity as a ratio of red-to-green fluorescence pixels may be influenced by differential viral infection efficiencies, variations in the expression levels of the TVA receptor, or even by the lower basal activity levels observed in TS21 cultures. Complementary approaches-such as electron microscopy for synaptic density analysis or functional connectivity measurements using multi-electrode arrays (MEAs)-could provide additional structural and functional insights that would validate the rabies tracing data.
• Qualification of Claims: Some conclusions, particularly those linking specific ion channel dysregulation (e.g., HCN1 loss) directly to network deficits, might be better presented as preliminary. The authors could temper their language to indicate that while the evidence is suggestive, the mechanistic link remains to be fully established.
• Need for Additional Experiments: Additional experiments that could further consolidate the current findings include:
  • Inclusion of Inhibitory Neurons or Co-culture Systems: Incorporating interneurons or astrocytes would help determine whether the observed deficits are solely intrinsic to excitatory neurons.
  • Alternative Connectivity Assessments: Complementing the rabies virus tracing with electron microscopy or multi-electrode array (MEA) recordings would add structural and functional validation of the connectivity differences.
  • Extended Temporal Profiling: Monitoring network activity over a longer developmental window would clarify whether the observed deficits represent a delay or a permanent alteration in network maturation.
• Reproducibility and Statistical Rigor: The methods and data presentation are largely clear, with adequate replication and appropriate statistical analyses. Nonetheless, a more detailed description of the experimental replicates, particularly regarding the viral tracing and in vivo transplantation studies, would enhance reproducibility. The availability of raw data and scripts for calcium imaging analysis would also further support independent verification.

Minor Comments

• Experimental Details:

Minor revisions could include clarifying the infection efficiency and expression levels of the viral constructs used in connectivity assays to rule out technical variability. - Literature Context:

The authors reference prior studies appropriately; however, integrating a brief discussion comparing their findings with alternative DS models (e.g., organoids or other hiPSC-derived systems) would improve contextual clarity. - Presentation and Clarity:

Figures are generally clear,.But the manuscript contains a minor labeling error. On page 13, the figure is erroneously labeled as "Fig6A", whereas, based on the context and corresponding data, it should be "Fig5A". I recommend that the authors correct this mistake to ensure consistency and avoid potential confusion for readers.

Significance

• Nature and Significance of the Advance:

The work offers a substantial conceptual advance by providing a mechanistic link between trisomy 21 and impaired neuronal network synchronization. Technically, the study integrates state-of-the-art imaging, electrophysiology, and transcriptomic profiling, thereby offering a multifaceted view of DS-related neural dysfunction. Clinically, the findings have the potential to inform future therapeutic strategies targeting network connectivity and ion channel function in Down syndrome. - Context in the Existing Literature:

The study builds on previous observations of altered network activity in DS patients and DS mouse models (e.g., altered EEG synchronization and reduced synaptic connectivity). It extends these findings to human-derived neuronal models, thus bridging a gap between clinical observations and molecular/cellular mechanisms. Relevant literature includes studies on DS neurodevelopment and the role of ion channels in synaptic maturation. - Target Audience:

The reported findings will be of interest to researchers in neurodevelopmental disorders, Down syndrome, and ion channel physiology. Additionally, the study may attract the attention of those working on hiPSC-derived models of neurological diseases, as well as clinicians interested in the pathophysiology of DS. - Keywords and Field Contextualization:

Keywords: Down syndrome, trisomy 21, neuronal connectivity, synchronized network activity, hiPSC-derived cortical neurons, ion channel dysregulation.

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Reply to the reviewers

We thank the referees for taking time to review our manuscript. These reviews are positive, highlighting the novelty of our findings. The majority of comments are cosmetic, and we have added data in response to some technical points. We feel that some of the additional experiments proposed would not add significant methodological depth, and cross-commenting suggests that our referees agree. At present we are attempting antibody staining to quantify Tk peptide retention in the midgut, as per suggestion by reviewer #2.

We enclose our point-by-point response to each referee's points, below.

__Reviewer #1 __

• Can the authors state in the figure legends the numbers of flies used for each lifespan and whether replicates have been done?

• We have incorporated the requested information into legends for lifespan experiments.

• Do the interventions shorten lifespan relative to the axenic cohort? Or do they prevent lifespan extension by axenic conditions? Both statements are valid, and the authors need to be consistent in which one they use to avoid confusing the reader.

• We read these statements differently. The only experiment in which a genetic intervention prevented lifespan extension by axenic conditions is neuronal TkR86C knockdown (Figure 6B-C). Otherwise, microbiota shortened lifespan relative to axenic conditions, and genetic knockdowns extend blocked this effect (e.g. see lines 131-133). We have ensured that the framing is consistent throughout, with text edited at lines 198-199, 298-299, 311-312, 345-347, 408-409, 424-425, 450, 497-503.

• TkRNAi consistently reduces lipid levels in axenic flies (Figs 2E, 3D), essentially phenocopying the loss of lipid stores seen in control conventionally reared (CR) flies relative to control axenic. This suggests that the previously reported role of Tk in lipid storage - demonstrated through increased lipid levels in TkRNAi flies (Song et al (2014) Cell Rep 9(1): 40) - is dependent on the microbiota. In the absence of the microbiota TkRNAi reduces lipid levels. The lack of acknowledgement of this in the text is confusing

• We have added text at lines 219-222 to address this point. We agree that this effect is hard to interpret biologically, since expressing RNAi in axenics has no additional effect on Tk expression (Figure S7). Consequently we can only interpret this unexpected effect as a possible off-target effect of RU feeding on TAG, specific to axenic flies. However, this possibility does not void our conclusion, because an off-target dimunition of TAG cannot explain why CR flies accumulate TAG following TkRNAi We hope that our added text clarifies.

• *I have struggled to follow the authors logic in ablating the IPCs and feel a clear statement on what they expected the outcome to be would help the reader. *

• We have added the requested statement at lines 423-424, explaining that we expected the IPC ablation to render flies constitutively long-lived and non-responsive to A pomorum.

• *Can the authors clarify their logic in concluding a role for insulin signalling, and qualify this conclusion with appropriate consideration of alternative hypotheses? *

• We have added our logic at lines 449-454. In brief, we conclude involvement for insulin signalling because FoxO mutant lifespan does not respond to TkRNAi, and diminishes the lifespan-shortening effect of * pomorum*. However, we cannot state that the effects are direct because we do not have data that mechanistically connects Tk/TkR99D signalling directly in insulin-producing cells. The current evidence is most consistent with insulin signalling priming responses to microbiota/Tk/TkR99D, as per the newly-added text.

• Typographical errors

• We have remedied the highlighted errors, at lines 128-140.

• I'd encourage the authors to provide lifespan plots that enable comparison between all conditions

• We have plotted our figures in faceted boxes, because the number of survival curves that would need to be presented on the same axis (e.g. 16 for Figure 5) would not be intellegible. However we have ensured that axes on faceted plots are equivalent and with grid lines for comparison. Moreover, our approach using statistical coefficients (EMMs) enables direct quantitative comparison of the differences among conditions.

Reviewer #2

• Not…essential for publication…is it possible to look at Tk protein levels?

• We have acquired a small amount of anti-TK antibody and we will attempt to immunostain guts associated with * pomorum and L. brevis*. We are also attempting the equivalent experiment in mouse colon reared with/without a defined microbiota. These experiments are ongoing, but we note that the referee feels that the manuscript is a publishable unit whether these stainings succeed or not.

• it would be good to show that the bacterial levels are not impacted [by TkRNAi]

• We have quantified CFUs in CR flies upon ubiquitous TkRNAi (Figure S5), finding that the RNAi does not affect bacterial load. New text at lines 138-139 articulates this point.

• The effect of Tk RNAi on TAG is opposite in CR and Ax or CR and Ap flies, and the knockdown shows an effect in either case (Figure 2E, Figure 3D). Why is this?

• As per response to Reviewer #1, we have added text at lines 219-222 to address this point.

• Is it possible to perform at least one lifespan repeat with the other Tk RNAi line mentioned?

• We have added another experiment showing longevity upon knockdown in conventional flies, using an independent TkRNAi line (Figure S3).

• Is it possible that this driver is simply not resulting in an efficient KD of the receptor? I would be inclined to check this

• This comment relates to Figure 7G. We do see an effect of the knockdown in this experiment, so we believe that the knockdown is effective. However the direction of response is not consistent with our hypothesis so the experiment is not informative about the role of these cells. We therefore feel there is little to be gained by testing efficacy of knockdown, which would also be technically challenging because the cells are a small population in a larger tissue which expresses the same transcripts elsewhere (i.e. necessitating FISH).

• Would it be possible to use antibodies for acetylated histones?

• The comment relates to Figure 4C-E. The proposed studies would be a significant amount of work because, to our knowledge, the specific histone marks which drive activation in TK+ cells remain unknown. On the other hand, we do not see how this information would enrich the present story, rather such experiments would appear to be the beginning of something new. We therefore agree with Reviewer #1 (in cross-commenting) that this additional work is not justified.

Reviewer #3

• *In Line243, the manuscript states that the reporter activity was not increased in the posterior midgut. However, based on the presented results in Fig4E, there is seemingly not apparent regional specificity. A more detailed explanation is necessary. *

• We thank the reviewer sincerely for their keen eye, which has highlighted an error in the previous version of the figure. In revisiting this figure we have noticed, to our dismay, that the figures for GFP quantification were actually re-plots of the figures for (ac)K quantification. This error led to the discrepancy between statistics and graphics, which thankfully the reviewer noticed. We have revised the figure to remedy our error, and the statistics now match the boxplots and results text.

• Fig1C uses Adh for normalization. Given the high variability of the result, the authors should (1) check whether Adh expression levels changed via bacterial association

• We selected Adh on the basis of our RNAseq analysis, which showed it was not different between AX and CV guts, whereas many commonly-used “housekeeping” genes were. We have now added a plot to demonstrate (Figure S2).

• The statement in Line 82 that EEs express 14 peptide hormones should be supported with an appropriate reference

• We have added the requested reference (Hung et al, 2020) at line 86.

• Tk+ EEC activity should be assessed directly, rather than relying solely on transcript levels. Approaches such as CaLexA or GCaMP could be used.

• We agree with reviewers 1-2 (in cross-commenting) that this proposal is non-trivial and not justified by the additional insight that would be gained. As described above, we are attempting to immunostain Tk, which if successful will provide a third line of evidence for regulation of Tk+ cells. However we note that we already have the strongest possible evidence for a role of these cells via genetic analysis (Figure 5).

• While the difficulty of maintaining lifelong axenic conditions is understandable, it may still be feasible to assess the induction of Tk (ie. Tk transcription or EE activity upregulation) by the microbiome on males.

• As the reviewer recognises, maintaining axenic experiments for months on end is not trivial. Given the tendency for males either to simply mirror female responses to lifespan-extending interventions, or to not respond at all, we made the decision in our work to only study females. We have instead emphasised in the manuscript that results are from female flies.

• TkR86C, in addition to TkR99D, may be involved in the A. pomorum-lifespan interaction. Consider revising the title to refer more generally to the "tachykinin receptor" rather than only TkR99D.

• We disagree with this interpretation: the results do not show that TkR86C-RNAi recapitulates the effect of enteric Tk-RNAi. A potentially interesting interaction is apparent, but the data do not support a causal role for TkR86C. A causal role is supported only for TkR99D, knockdown of which recapitulates the longevity of axenic flies and TkRNAi flies. Therefore we feel that our current title is therefore justified by the data, and a more generic version would misrepresent our findings.

• The difference between "aging" and "lifespan" should also be addressed.

• The smurf phenotype is a well-established metric of healthspan. Moreover, lifespan is the leading aggregate measure of ageing. We therefore feel that the use of “ageing” in the title is appropriate.

• If feasible, assessing foxo activation would add mechanistic depth. This could be done by monitoring foxo nuclear localization or measuring the expression levels of downstream target genes.

• Foxo nuclear localisation has already been shown in axenic flies (Shin et al, 2011). We have added text and citation at lines 402-403.

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Referee #3

Evidence, reproducibility and clarity

Summary

Marcu et al. demonstrate a gut-neuron axis that is required for the lifespan-shortening effects mediated by gut bacteria. They show that the presence of commensal bacteria-particularly Acetobacter pomorum-promotes Tk expression in the gut, which then binds to neuronal tachykinin receptors to shorten lifespan. Tk has also recently been reported to extend lifespan via adipokinetic hormone (Akh) signaling (Ahrentløv et al., Nat Metab 7, 2025), but the mechanism here appears distinct. The lifespan shortening by Ap via Tk seems to be partially dependent on foxo and independent of both insulin signaling and Akh-mediated lipid mobilization. Although the detailed mechanistic link to lifespan is not fully resolved, the experiment and its results clearly shows the involvement of the molecules tested. This work adds a valuable dimension to our growing understanding of how gut bacteria influence host longevity. However, there are some points that should be addressed.

1. Tk+ EEC activity should be assessed directly, rather than relying solely on transcript levels. Approaches such as CaLexA or GCaMP could be used.
2. In Line243, the manuscript states that the reporter activity was not increased in the posterior midgut. However, based on the presented results in Fig4E, there is seemingly not apparent regional specificity. A more detailed explanation is necessary.
3. If feasible, assessing foxo activation would add mechanistic depth. This could be done by monitoring foxo nuclear localization or measuring the expression levels of downstream target genes.
4. Fig1C uses Adh for normalization. Given the high variability of the result, the authors should (1) check whether Adh expression levels changed via bacterial association and/or (2) compare the results using different genes as internal standard.
5. While the difficulty of maintaining lifelong axenic conditions is understandable, it may still be feasible to assess the induction of Tk (ie. Tk transcription or EE activity upregulation) by the microbiome on males.
6. We also had some concerns regarding the wording of the title. Fig6B and C suggests that TkR86C, in addition to TkR99D, may be involved in the A. pomorum-lifespan interaction. Consider revising the title to refer more generally to the "tachykinin receptor" rather than only TkR99D. The difference between "aging" and "lifespan" should also be addressed. While the study shows a role for Tk in lifespan, assessment of aging phenotypes (eg. Climbing assay, ISC proliferation) beyond the smurf assay is required to make conclusions about aging.
7. The statement in Line 82 that EEs express 14 peptide hormones should be supported with an appropriate reference, if available.

Referees cross-commenting

I agree with the other reviewers that the study has been done very well and hence additional experiments are not mandatory to be published such as calcium imaging. However, I still believe that testing Tk's elevation by the Ap in males should greatly increase the generality of the finding, no matter what the outcome would be. Too many studies use only females.

Significance

General assessment

The main strength of this study is the careful and extensive lifespan analyses, which convincingly demonstrate the role of gut microbiota in regulating longevity. The authors clarify an important aspect of how microbial factors contribute to lifespan control. The main limitation is that the study primarily confirms the involvement of previously reported signaling pathways, without identifying novel molecular players or previously unrecognized mechanisms of lifespan regulation.

Advance

The lifespan-shortening effect of Acetobacter pomorum (Ap) has been reported previously, as has the lifespan-shortening effect of Tachykinin (Tk). However, this study is the first to link these two factors mechanistically, which represents a significant and original contribution to the field. The advance is primarily mechanistic, providing new insight into how microbial cues converge on host signaling pathways to influence ageing.

Audience

This work will be of particular interest to a specialized audience of basic researchers in ageing biology. It will also attract interest from microbiome researchers who are investigating host-microbe interactions and their physiological consequences. The findings will be useful as a conceptual framework for future mechanistic studies in this area.

Field of expertise

Drosophila ageing, lifespan, microbiome, metabolism

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Referee #2

Evidence, reproducibility and clarity

The main finding of this work is that microbiota impacts lifespan though regulating the expression of a gut hormone (Tk) which in turn acts on its receptor expressed on neurons. This conclusion is robust and based on a number of experimental observation, carefully using techniques in fly genetics and physiology: 1) microbiota regulates Tk expression, 2) lifespan reduction by microbiota is absent when Tk is knocked down in gut (specifically in the EEs), 3) Tk knockdown extends lifespan and this is recapitulated by knockdown of a Tk receptor in neurons. These key conclusions are very convincing. Additional data are presented detailing the relationship between Tk and insulin/IGF signalling and Akh in this context. These are two other important endocrine signalling pathways in flies. The presentation and analysis of the data are excellent.

There are only a few experiments or edits that I would suggest as important to confirm or refine the conclusions of this manuscript. These are:

1. When comparing the effects of microbiota (or single bacterial species) in different genetic backgrounds or experimental conditions, I think it would be good to show that the bacterial levels are not impacted by the other intervention(s). For example, the lifespan results observed in Figure 2A are consistent with Tk acting downstream of the microbes but also with Tk RNAi having an impact on the microbiota itself. I think this simple, additional control could be done for a few key experiments. Similarly, the authors could compare the two bacterial species to see if the differences in their effects come from different ability to colonise the flies.
2. The effect of Tk RNAi on TAG is opposite in CR and Ax or CR and Ap flies, and the knockdown shows an effect in either case (Figure 2E, Figure 3D). Why is this? Better clarification is required.
3. With respect to insulin signalling, all the experiments bar one indicate that insulin is mediating the effects of Tk. The one experiment that does not is using dilpGS to knock down TkR99D. Is it possible that this driver is simply not resulting in an efficient KD of the receptor? I would be inclined to check this, but as a minimum I would be a bit more cautious with the interpretation of these data.
4. Is it possible to perform at least one lifespan repeat with the other Tk RNAi line mentioned? This would further clarify that there are no off-target effects that can account for the phenotypes.

There are a few other experiments that I could suggest as I think they could enrich the current manuscript, but I do not believe they are essential for publication: 5. The manuscript could be extended with a little more biochemical/cell biology analysis. For example, is it possible to look at Tk protein levels, Tk levels in circulation, or even TkR receptor activation or activation of its downstream signalling pathways? Comparing Ax and CR or Ap and CR one would expect to find differences consistent with the model proposed. This would add depth to the genetic analysis already conducted. Similarly, for insulin signalling - would it be possible to use some readout of the pathway activity and compare between Ax and CR or Ap and CR? 6. The authors use a pan-acetyl-K antibody but are specifically interested in acetylated histones. Would it be possible to use antibodies for acetylated histones? This would have the added benefit that one can confirm the changes are not in the levels of histones themselves. 7. I think the presentation of the results could be tightened a bit, with fewer sections and one figure per section.

Referees cross-commenting

Reviewer 1

I generally agree with this reviewer but for

"I'm convinced by the data showing that FOXO is required for TkRNAi to prevent lifespan shortening by Ap, but FOXO doesn't only respond to insulin signalling and can't be taken by itself to indicate a role for insulin signalling which the authors appear to do here."

To the best of my knowledge, Foxo has only been shown to be required for lifespan extension/modulation by a reduction in insulin-like signalling. I.e. it does respond to other pathways but this is the only one where Foxo activity is known to modulate lifespan.

Reviewer 3

I agree with reviewer 1 that point raised under (1) does not appear strictly required for the conclusions of the manuscript.

Both reviewers 1 and 3:

I have a different take on the results of experiments where IPCs are manipulated. To me, Figure 7D and E show that ablating the IPCs removes the difference between Ax and Ap i.e. the IPCs are involved and insulin-like signalling is likely involved. The fact that RNAi against the TKR99D receptor does not have the same effect, does not matter (the sensing could happen in different neurons). Similarly, dilp expression is only a minor readout of what is happening with insulin-like signalling - dilps are controlled at the level of secretion.

However, I would be happy for the authors to present different arguments and make a reasonable conclusion, which may differ from mine. But I think the arguments I present above should be taken into account.

Significance

The main contribution of this manuscript is the identification of a mechanism that links the microbiota to lifespan. This is very exciting and topical for several reasons:

1) The microbiota is very important for overall health but it is still unclear how. Studying the interaction between microbiota and health is an emerging, growing field, and one that has attracted a lot of interest, but one that is often lacking in mechanistic insight. Identifying mechanisms provides opportunities for therapies. The main impact of this study comes from using the fruit fly to identify a mechanism.

2) It is very interesting that the authors focus on an endocrine mechanism, especially with the clear clinical relevance of gut hormones to human health recently demonstrated with new, effective therapies (e.g. Wegovy).

3) Tk is emerging as an important fly hormone and this study adds a new and interesting dimension by placing TK between microbiota and lifespan.

I think the manuscript will be of great interest to researchers in ageing, human and animal physiology and in gut endocrinology and gut function.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study the authors use a Drosophila model to demonstrate that Tachykinin (Tk) expression is regulated by the microbiota. In Drosophila conventionally reared (CR) flies are typically shorter lived than those raised without a microbiota (axenic). Here, knockdown of Tk expression is found to prevent lifespan shortening by the microbiota and the reduction of lipid stores typically seen in CR flies when compared to axenic counterparts. It does so without reducing food intake or fecundity which are often seen as necessary trade-offs for lifespan extension. Further, the strength of the interaction between Tk and the microbiota is found to be bacteria specific and is stronger in Acetobacter pomorum (Ap) monoassociated flies compared to Levilactobacillus brevis (Lb) monoassociation. The impact on lipid storage was also only apparent in Ap-flies. Building on these findings the authors show that gut specific knockdown is largely sufficient to explain these phenotypes. Knockdown of the Tk receptor, TkR99D, in neurons recapitulates the lifespan phenotype of intestinal Tk knockdown supporting a model whereby Tk from the gut signals to TkR99D expressing neurons to regulate lifespan. In addition, the authors show that FOXO may have a role in lifespan regulation by the Tk-microbiota interaction. However, they rule out a role for insulin producing cells or Akh-producing cells suggesting the microbiota-Tk interaction regulates lifespan through other, yet unidentified, mechanisms.

Major comments:

Overall, I find the key conclusions of the paper convincing. The authors present an extensive amount of experimental work, and their conclusions are well founded in the data. In particular, the impact of TkRNAi on lifespan and lipid levels, the central finding in this study, has been demonstrated multiple times in different experiments and using different genetic tools. As a result, I don't feel that additional experimental work is necessary to support the current conclusions. However, I find it hard to assess the robustness of the lifespan data from the other manipulations used (TkR99DRNAi, TkRNAi in dFoxo mutants etc.) because information on the population size and whether these experiments have been replicated is lacking. Can the authors state in the figure legends the numbers of flies used for each lifespan and whether replicates have been done? For all other data it is clear how many replicates have been done, and the methods give enough detail for all experiments to be reproduced.

Minor comments:

While I feel the conclusions of this study are well supported by the data I found this to be a complex read and in places hard to follow. I feel some work is necessary in the writing to help the reader follow the authors logic. Below I describe some of the issues that confused me and provide some suggestions that I hope the authors will find helpful.

Survival curves The authors state that the lifespan difference between CR and axenic flies disappears with TkRNAi because TkRNAi CR flies are longer lived, rather than because TkRNAi axenic flies are shorter lived. Is this consistent in every TkRNAi experiment? It's hard for the reader to assess this because the relevant lifespan curves are presented on separate plots. I'd encourage the authors to provide lifespan plots that enable comparison between all conditions. For example, in figures 2 and 6 the reader wants to directly compare between RU- and RU+ but can't easily do so. Additional plots could be made available in the supplementary figures showing the comparisons that are not easy to make on the main figures.

Consistent framing of the data Do the interventions shorten lifespan relative to the axenic cohort? Or do they prevent lifespan extension by axenic conditions? Both statements are valid, and the authors need to be consistent in which one they use to avoid confusing the reader. For example, line 325 says TkR86CRNAi prevents lifespan extension in axenic flies. Given the framing in the previous sections, it might be clearer to say that TkR86CRNAi shortens the lifespan of axenic flies to that of CR flies in contrast to TkRNAi and TkR99DRNAi which don't.

The impact of TkRNAi on lipid levels in axenic flies TkRNAi consistently reduces lipid levels in axenic flies (Figs 2E, 3D), essentially phenocopying the loss of lipid stores seen in control conventionally reared (CR) flies relative to control axenic. This suggests that the previously reported role of Tk in lipid storage - demonstrated through increased lipid levels in TkRNAi flies (Song et al (2014) Cell Rep 9(1): 40) - is dependent on the microbiota. In the absence of the microbiota TkRNAi reduces lipid levels. The lack of acknowledgement of this in the text is confusing for the reader because it is inconsistent with the microbiota driving both higher Tk expression and higher lipid storage. If the microbiota increases Tk expression and this results in reduced lipid storage, why does reduced Tk expression also result in reduced lipid storage in axenic flies? This could further highlight the unique impact that the interaction between TkRNAi and the microbiota has on lipid storage, given it reverses both the impact of the microbiota alone and TkRNAi alone. I feel this aspect of the data should be given more attention in the text both for clarity and because it may be telling us something important about the function of Tk. The current framing around pleiotropic effects is valid, and the impact of Tk on lipid storage is clearly independent of its impact on lifespan and so is not central to this study. However, I feel a short additional paragraph to acknowledge this nuance of the data is needed. It can be made clear in the text that further exploration is beyond the scope of the current study.

Role of insulin signalling and insulin producing cells I'm convinced by the data showing that FOXO is required for TkRNAi to prevent lifespan shortening by Ap, but FOXO doesn't only respond to insulin signalling and can't be taken by itself to indicate a role for insulin signalling which the authors appear to do here.

I would expect ablation of IPCs to have the opposite effect to foxo mutation and to increase FOXO activity throughout the organism due to a reduction in Dilp levels and so reduced insulin signalling. So, I have struggled to follow the authors logic in ablating the IPCs and feel a clear statement on what they expected the outcome to be would help the reader. They find that TkRNAi still prevents lifespan shortening by Ap when IPCs are ablated and that TkR99DRNAi in IPCs also doesn't block lifespan shortening by Ap despite reducing the expression of dilp3 and dilp5. To me these data rule out a role for insulin signalling despite the requirement for FOXO and yet the authors conclude that insulin signalling is involved in the response to Ap and TkRNAi, although not obligately (lines 420 - 422 and 511 - 512). Can the authors clarify their logic in concluding a role for insulin signalling, and qualify this conclusion with appropriate consideration of alternative hypotheses? The potential involvement of other signalling inputs to FOXO activity, e.g. immune signalling and JNK, should be acknowledged and warrants some discussion.

Typographical errors:

Incomplete sentence line 121 to 122 - starting "Cox proportional hazards.... and posthoc tests (Fig 2b).

Line 123 "EMMs" - define abbreviation on first use

References to Fig 2b (first given on line 122), should be capitalised to Fig 2B for consistency.

Lines 231 and 317 - the phrase "steady state (microbiota independent) expression" in reference to flyATLAS 2 data could be misleading. The term "microbiota independent" could suggest that expression levels have been shown not to be regulated by the microbiota and this is not the case. The authors should change this to simply state they are referring to steady state expression in conventionally reared flies.

Referees cross-commenting

Below are brief comments on the revision suggestions that reviewers 2 and 3 have requested.

Reviewer 2

1. I agree that confirmation that TkRNAi doesn't impact microbial levels could be helpful and would be straightforward for the authors to do. However, I don't feel it's essential to support the central claims of the paper.
2. I agree.
3. I don't feel that any of these experiments supports a role for insulin signalling, so I don't feel that this additional control is needed.
4. It would be a good addition to have lifespan data from a separate knockdown line for corroboration. However, this has already been done in several different genetic backgrounds through crosses with different driver lines in multiple tissues, so I feel it's unnecessary given the time and resources that lifespan experiments take. There's also the caveat that different RNAi lines can knockdown to different extents so that would have to be assessed as well and if there's a difference it may mean that ultimately not much can be concluded from this additional experiment.
5. A good suggestion, but not straightforward and depends on the availability of the necessary tools, or possibly the generation of new tools. One for a follow up study.
6. I feel this is not important enough to the central findings of the study to warrant the extra work.
7. I agree.

Reviewer 3 1. Imaging calcium signalling is not straightforward unless a lab already has the tools available and optimised. If Tk+ EEs show changes in calcium signalling I'm not convinced that this tells us anything specific to the Tk-microbiota interaction. The point is the role of Tk itself, not the broader activity of the cells that express it. 2. I agree this needs clarification. 3. I agree that this would add depth, if feasible, but feel it's not essential to support the current conclusions. 4. This is a minor point and given the RT-qPCR data and the RNAseq data corroborate each other I'm convinced that Tk levels are elevated. 5. I feel exploring this in males is opening an additional line of enquiry beyond the scope of the current study. Either the phenotypes are the same - in which case what is added? - or they are different but there's no scope to assess why. A good suggestion for a follow up study. 6. No comment. 7. Agreed.

One final comment. It's true that FOXO has only been shown to regulate lifespan in the context of insulin signalling. However, as far as I'm aware it hasn't been shown not to regulate lifespan downstream of it's other activators, this simply hasn't been explored due to the historical focus on insulin signalling in this field. In the context of host-microbiota interactions considering other pathways the activate FOXO, such as immune and JNK signals, would make sense.

Reviewed by Dr Rebecca Clark, Department of Biosciences, Durham University

Significance

Overall, I find the key conclusions of the paper convincing. The authors present an extensive amount of experimental work, and their conclusions are well founded in the data. We have known that the microbiota influence lifespan for some time but the mechanisms by which they do so have remained elusive. This study identifies one such mechanism and as a result opens several avenues for further research. The Tk-microbiota interaction is shown to be important for both lifespan and lipid homeostasis, although it's clear these are independent phenotypes. The fact that the outcome of the Tk-microbiota interaction depends on the bacterial species is of particular interest because it supports the idea that manipulation of the microbiota, or specific aspects of the host-microbiota interaction, may have therapeutic potential.<br /> These findings will be of interest to a broad readership spanning host-microbiota interactions and their influence on host health. They move forward the study of microbial regulation of host longevity and have relevance to our understanding of microbial regulation of host lipid homeostasis. They will also be of significant interest to those studying the mechanisms of action and physiological roles of Tachykinins.

Field of expertise: Drosophila, gut, ageing, microbiota, innate immunity

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Reply to the reviewers

1. General Statements

We thank the reviewers for providing thoughtful and constructive feedback, which will help us improve the clarity and rigor of the paper. On balance, the reviews were positive. Reviewer 1 mentioned that “This is a strong manuscript with few problems and all important findings well justified, indeed this is a nicely polished…..high-quality manuscript,” and that “this paper makes a major breakthrough, showing that cell autonomous defects in hTSCs are very likely at the heart of the pathology observed in GIN-prone murine mutants.” Reviewer 3 stated that “The study is well designed, and the manuscript is very well written. The conclusions are supported by the evidence presented.” Reviewer 2 was less enthusiastic, with main concerns being that “The paper is mostly descriptive and often quite confusing leaving one not much closer to understanding the mechanistic basis for the interesting sex-biased semi-lethal phenotype.” and felt that figure titles/section headers overstated the results, and finally recommended to improve some technical aspects and tempering conclusions. The proposed edits we think address most issues raised by the reviewers either with re-writing or adding data as described below.

In response to reviewer #1 comments:

Major comments:

• I am confused as to the basis of the sex-skewing phenomenon? Is the problem that lack of maternally loaded WT Mcm4 worsens the phenotype, or is the issue that Mcm4C3/C3 dams are less able to retain pregnancies, perhaps being a more inflammatory environment? Also, while there quite consistent evidence for reduced viability of Mcm4C3/C3McmGt/+ progeny, especially for female progeny, how confident can we be that the genotype of the dam vs. sire is important? Notably on a Ddx58 background, the progeny of the Mcm4C3/C3 sire included seven live male Mcm4C3/C3McmGt/+ but no female.

Regarding the first point (sex skewing only when female is C3/C3), we also suspected either: 1) the maternal uterine environment, or 2) reduced oocyte quality. Although not reported in this manuscript, we tested #1 by performing embryo transfer experiments. Transferring 2-cell stage embryos from sex-skewing mating to WT females did not rescue the sex-bias. We then examined oocytes from C3/C3 females. We found evidence for compromised mitochondria and transcriptome disruption. However, we are not sure why this happens (poor follicle support? Oocyte intrinsic phenomenon?). We are reserving these results and additional experiments for another paper, especially since this one mainly deals with GIN and placenta development. If the reviewers feel strongly that the embryo transfer data is crucial, we can include it.

Regarding how confident we are that the genotype of the dam vs. sire is important, this stems from our previous paper by McNairn et al 2019 (the percentage of female C3/C3 M2/+ from sex-skewing mating is 20% compared to 60% from the reciprocal mating), which was quite dramatic. Consistent with this, MCM levels were significantly reduced in the placentae only when the dam was C3/C3 and the sire C3/+ M2/+, but not in the reciprocal cross. The reviewer makes a good observation about the Ddx58 cross; we can only hypothesize that the mutation somehow sensitizes females in this scenario and will make mention of it in the revision. We also realize that we neglected to write in Methods that the Ddx58 allele was coisogenic in the C3H background.

• I'm not sure what Supplementary Figure 6 is showing (faster differentiation of C3 but less TGC?). Regardless, it's hard to draw too much conclusion from one not-very-pretty Western blot. This figure requires both additional replicates and a better explanation of how it fits with the other conclusions of the paper..

We hypothesized that the JZ defect observed in the semi-lethal genotype placentas could arise either from impaired maintenance of the progenitor pool or from reduced capacity of mutant trophoblast progenitors to differentiate into the JZ lineage. The blot in Supplementary Figure 6 was intended as a qualitative demonstration that mutant trophoblast stem cells can differentiate into JZ lineages. We recognize that the figure is not definitive and will revise the text to clarify its purpose. A replicate(s) of the Western will be performed as suggested.

• Supplementary Figure 7F-G is puzzling. Half of the mESCs have gamma-H2AX at all times, including most in S or G2 phase? In Figure S7E, do the quadrants correspond to being negative or positive for gamma-H2AX? At very least, IF images showing clear gamma-H2AX foci would be much more convincing.

The gates for γH2AX FACS analysis were established using negative controls lacking primary antibody. As reported previously, embryonic stem cells display high basal levels of γH2AX staining (Chuykin et al., Cell Cycle 2008; Turinetto et al., Stem Cells 2012; Ahuja et al., Nat Comm 2016), which likely explains the broad signal observed across cell cycle phases. Regardless, we will provide immunofluorescence staining of γH2Ax and foci count in our revision.

• The methods section is well detailed, but it would be ideal to clarify how many replicates each Western Blot or flow cytometry experiment is representative of.

Thanks for the suggestion. We will update this for Fig4 and Fig5.

Minor comments:

• Is it possible that cGAS-STING and RIG pathways act redundantly to cause inflammation and lethality, or that other innate immune components are involved? I don't expect the authors to make compound mutants to test this but at least this possibility should be discussed textually.

We appreciate the reviewer’s point, and had the same suspicion. Supporting this, we will add new RNA-seq analysis of Tmem173 KO placentas revealed elevated inflammatory gene expression compared to C3/C3 M2/+ controls, consistent with potential redundancy or feedback regulation. We will update in supplementary figures to reflect this.

In response to reviewer #2 comments:

Major comments:

A major concern throughout the paper is that conclusions are often overstating their data. The title of figure 2 is "placentae with replication stress have smaller junctional and labyrinth zones". However, there is no measure of replication stress in this figure, just a histological evaluation of the placentae from the different mutants. The title of figure 3 is "Impact of GIN on LZ is less than JZ," but there is no measure of GIN, but instead measurement of number of cells in cell cycle and some bulk RNA-seq analysis. Title of figure 4 is "TSCs with increased genomic instability exhibit abnormal phenotypes." Again there is no measure of GIN, but instead staining of derived TSCs for proliferation, cell death, and a TSC marker. Title of figure 5 is "DNA damage responses and G2/M checkpoint activation drive premature TSC differentiation." However, there does not appear to be a difference in gH2AX between the two mutant genotypes. Checkpoint proteins might be up, but need quantification and reproduction. > 4C is the only marker of differentiation. Importantly, all the analyses here are associations, not connections, so cannot use the word "drive". Similar issues can be raised with a number of the supplementary figures.

The Chaos3 (chromosome aberrations occurring spontaneously 3) model is a well-established system of intrinsic chronic replication stress and GIN. It is characterized by ~20 fold elevation of blood micronuclei (Shima et al., Nature 2007), a hallmark of GIN (Soxena et al., Mol Cell 2022); a destabilized MCM2-7 helicase prone to replication fork collapse (Bai et al., PLoS Genet 2016); and increased mitotic chromosome abnormalities and decreased dormant origins (Kawabata et al., Mol Cell 2011; Chuang et al., Nucleic Acid Res 2012) that are known to cause GIN and replication stress (Ibarra et al., PNAS 2008 ). Also, in our previous work (McNairn et al Nature 2019), we showed that placentae from C3/C3 dams exhibit significantly elevated γH2Ax as well as reduced MCM2 and MCM4 protein levels. In our current study, we also observe elevated γH2Ax in mutant TSCs (C3/C3 and C3/C3 M2/+), consistent with genomic instability. Nevertheless, we acknowledge that in TSCs, we did not formally demonstrate replications stress(RS), so where appropriate, we will advise figure titles, for example to say that “cells/placentae with a GIN or RS genotype.”

We acknowledge the reviewers concern regarding western blots. We will provide quantification and statistics in our revision.

1) A deeper analysis of the cell lines is likely to be the most fruitful path to reveal interesting mechanisms. It is very surprising that there is no phenotype in ESCs. Authors should check for increased apoptosis. Maybe the phenotypic cells are lost. Or do ESCs use different MCMs/mechanisms of DNA replication or are they better able to handle replication stress and GIN? How many passages were the TSCs and ESCs cultured for? Does GIN (i.e. aneuploidy, CNVs) develop in TSCs and ESCs with passaging? How do the MCM mutations impact the molecular identity of the ESC and TSC cells including their heterogeneity in the population.

We assessed apoptosis using cleaved caspase 3 flow cytometry in mutant ESCs and observed no difference compared to controls (we will add this data as Supplementary Fig. 7).

We believe there are intrinsic differences in TSCs and ESCs in their ability to respond to and counteract replication stress and DNA damage. ESCs are known to license more replication origins than somatic cells at a higher rate, which protects them from short G1-induced replication stress (Ahuja et al., Nat Comm 2016; Ge et al., Stem Cell Rep 2015; Matson et al., eLife 2017). Human placental cells physiologically exhibit high levels of mutation rate and chromosomal instability in vivo (Coorens et al., Nature 2021). Supporting this, Wang, D., et al (Nat Comm 2025) reported that several cell cycle and DDR regulators are differentially expressed in human TSCs vs human pluripotent stem cells. Whether such transcriptional differences directly contribute to functional outcomes remains to be determined.

All experiments in this study were conducted using early-passage ESCs and TSCs (i.e. Finally, we showed that close to 90% mutant ESCs are KLF4+ (a naive pluripotency marker) whereas EOMES+ cells were significantly reduced in TSCs carrying the GIN genotype (Fig. 4E–F and Supplementary Fig. 7), highlighting lineage-specific differences.

Minor Comments:

1) There is a lack of quantification and repeats for all Westerns. At minimum there should be three repeats for each experiment, quantification including normalization to a reference protein, and stats confirming any proposed differences between conditions.

We will update our revision with quantification and statistics for western blots.

2) I would recommend moving the results in supp table 1 to figure 1. While negative, they are the newer results. The results shown in current figure 1 are essentially a reproduction of their previous work.

The placental observations presented in Fig.1 are new. In particular, the placental and embryonic weight measurements graphed in Fig1B and C have not been published by our group. Fig1A reproduces our previous observation on embryo viability in GIN mutants (McNairn et al., Nature 2019), while the schematic was provided for better flow and readability given the complex mating schemes. We are agnostic on the Suppl Table 1. It could be changed to a new Table 1 in the main section depending on the journal.

In response to reviewer #3 comments:

Major Comments

While the inclusion of bulk RNAseq data of whole placental tissue is appreciated, the interpretation of the results is somewhat problematic, as it is acknowledged that the cell type composition of the placentas is drastically different between groups. Making conclusions based upon GSEA analysis of two different groups with drastically different cell type composition is somewhat misleading, as based on the results, it is a direct reflection of the cell types present. It would be more helpful to perform cell type deconvolution of the RNAseq data to estimate the proportion of each cell type within the bulk samples and compare that to what is seen histologically and not dive too deeply into the pathways since the results could just be a reflection of the cell types e.g. angiogenesis pathways from more endothelial cells. Additionally, the RNAseq data can be leveraged to look at expression of inflammatory genes by sex, which may show interesting patterns based on the other results.

We agree that the representation of cell types in the placenta is problematic especially for underrepresented genes. We propose to use the BayesPrism tool (Chu et al., Nat Cancer 2022) to deconvolute bulk RNA-seq for better representation of transcriptional changes in the placenta.

Section: GIN impairs trophoblast stem cell establishment and maintenance. To support the assertion in the first paragraph, beyond measuring apoptosis, it would be helpful at this stage to look at RNA expression levels indicative of the activation of DNA damage checkpoint genes

We have performed RNA-seq on mutant ESC and TSCs and are in the process of data analysis. We will update these results in the revision.

Please include additional methodological details in the methods section on the statistical analysis done for differential expression analysis. Specifically, what type of normalization was used, if lowly expressed genes were filtered out and at what cutoff, what statistical model was used (did you include covariates?), what comparisons were made? Did you stratify by sex? What cutoff was used for statistical significance? Did you perform multiple testing correction?

We will update RNA-Seq data analysis methods in our full revision.

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

Reviewer #1 comments:

• Supplementary Table 1. would be enhanced greatly showing comparable tables for Mcm4C3/C3 x Mcm4C3/+McmGt/+ in mice without the Tmem173 or Ddx58 mutations. It is fine to recycle data from McNairn 2019 here, as long as the source is indicated, but a comparison is needed.

Thanks for pointing this out. We have updated this suggestion in Supp table 1.

• In Figure S3E-F, is the box above each graph supposed to show the genotype of the dam?

Yes. Thanks for pointing this out. We have added a description in the figure legend to make it clear.

• "Indeed, the placenta and embryo weights of E13.5 Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ animals were significantly improved vs. Mcm4C3/C3 Mcm2Gt/+ animals, rendering them similar to Mcm4C3/C3 littermates (Fig. 6A-C). The JZ (but not LZ) area in Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ placentae also increased to the level of Mcm4C3/C3 littermates (Fig. 6D-H)." There are two problems here. First, the figure calls are wrong. Second, the description of the data is not quite right, it looks like the C3/C3 and C3/C3 M2/+ M3/+ LZs are a similar size to each and are statistically indistinguishable.

Thanks for catching this. We have updated these in the main text.

*Reviewer #2 comments: *

Minor comment

• Need to review citations to figures. For example, no citations are made to figure 4a and 4c.

Thanks for catching this. We have updated the text.

Reviewer #3 comments:

Define the first use of >4C DNA content to help readers understand this potentially unfamiliar term.

We have edited this part to indicate cells with more than 4C DNA content for better clarity.

iDEP tool - please include citation to manuscript instead of link

We have updated this citation.

Check citations. Some citations to BioRxiv that are now published e.g. 13.

We have updated this citation.

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

Reviewer 2

2) Along similar lines, most of the in vivo phenotypic analyses are performed at E13.5, long after defects are likely beginning to express themselves especially given that they see phenotypes in the TSCs, which represent the polar TE of a E4.5. To understand the primary defects of the in vivo phenotype, they should be looking much earlier. Supplemental figure 5 is a start but represents a rather superficial analysis.

The peri-implantation period, namely E4.5, represents a “black box” of embryonic development given that this is a critical stage for implantation. Aside from being an extremely difficult stage to analyze technically, we don’t think it is essential to the conclusions (or doable in a timely manner), especially given the use of TSCs. If we complete EdU studies on E6.5 embryos, we will include them.

3) Fig. 6 would benefit from evidence that MCM3 mutant is rescuing MCM4 levels in the chromatin fraction of cells and the DNA damage phenotype.

The genetic evidence presented is strong, and although we didn’t do the suggested experiment, we feel that our previous studies (McNairn et al., Nature 2019 and Chuang et al., PLoS Genet 2010) on the effects of MCM3 as a nuclear export factor (as it is in yeast (Liku et al., Mol Biol Cell 2005)) are a reasonable basis for not repeating such experiments. Furthermore, we are no longer maintaining the Mcm3 line and it would take over a year to reconstitute and rebreed triple mutants.

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Referee #3

Evidence, reproducibility and clarity

This manuscript examines chronic replication stress-mediated genomic instability in placental development and concludes that it disrupts placental development in mice. The study is well designed and the manuscript is very well written. The conclusions are supported by the evidence presented. The manuscript would be improved by addressing the comments below.

Major Comments:

• While the inclusion of bulk RNAseq data of whole placental tissue is appreciated, the interpretation of the results is somewhat problematic, as it is acknowledged that the cell type composition of the placentas is drastically different between groups. Making conclusions based upon GSEA analysis of two different groups with drastically different cell type composition is somewhat misleading, as based on the results, it is a direct reflection of the cell types present. It would be more helpful to perform cell type deconvolution of the RNAseq data to estimate the proportion of each cell type within the bulk samples and compare that to what is seen histologically and not dive too deeply into the pathways since the results could just be a reflection of the cell types e.g. angiogenesis pathways from more endothelial cells. Additionally, the RNAseq data can be leveraged to look at expression of inflammatory genes by sex, which may show interesting patterns based on the other results.

• Section: GIN impairs trophoblast stem cell establishment and maintenance. To support the assertion in the first paragraph, beyond measuring apoptosis, it would be helpful at this stage to look at RNA expression levels indicative of the activation of DNA damage checkpoint genes

Minor Comments:

• Define the first use of >4C DNA content to help readers understand this potentially unfamiliar term.

• Please include additional methodological details in the methods section on the statistical analysis done for differential expression analysis. Specifically, what type of normalization was used, if lowly expressed genes were filtered out and at what cutoff, what statistical model was used (did you include covariates?), what comparisons were made? Did you stratify by sex? What cutoff was used for statistical significance? Did you perform multiple testing correction?

• iDEP tool - please include citation to manuscript instead of link

• Check citations. Some citations to BioRxiv that are now published e.g. 13.

Significance

The manuscript concludes that replication-stress induced genomic instability impairs placental development in mice. This is a significant advance in the field, as it mechanistically links genomic instability to placental development with further study needed in human trophoblast to establish clinical relevance. Strengths of this manuscript include solid study design, interpretation and presentation (both writing and figures). Weakness of the manuscript reside primarily in the RNAseq analysis results, methods and interpretation. The manuscript is of interest to audiences with interests in genome maintenance, development and placental biology. To contextualize this reviewer's point of view, this review is based on expertise in genomics, computational biology and placental biology.

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Referee #2

Evidence, reproducibility and clarity

The manuscript, "Chronic replication stress-mediated genomic instability disrupts placenta development in mice" by Munisha et al follows up a 2019 paper in Nature by the same group where they show that mutations to the MCM genes lead to a sex-skewed semi-lethal phenotype starting after embryonic day 9.5 and extending to birth. In the paper, they hypothesized that the semi-lethality is secondary to genomic instability (GIN) driven inflammation due to activation of the innate immune pathways sensing cytoplasmic DNA. In this paper, they start by disproving that hypothesis and then go on to present data arguing lethality is due to a placental development defect rather than inflammation. The paper is mostly descriptive and often quite confusing leaving one not much closer to understanding the mechanistic basis for the interesting sex-biased semi-lethal phenotype that was described in their original paper. The most interesting aspect of the paper is the derivation of TSC and ESCs and initial analysis suggesting that the TSCs are more sensitive to the MCM mutations, but the analysis is rather shallow. Importantly it is unclear how the phenotype explains the sex-skewing of the phenotype. Are the TSC phenotypes sex-skewed and if so why? Also, why is the JZ and especially GlyTCs most effected?

A major concern throughout the paper is that conclusions are often overstating their data. The title of figure 2 is "placentae with replication stress have smaller junctional and labyrinth zones". However, there is no measure of replication stress in this figure, just a histological evaluation of the placentae from the different mutants. The title of figure 3 is "Impact of GIN on LZ is less than JZ," but there is no measure of GIN, but instead measurement of number of cells in cell cycle and some bulk RNA-seq analysis. Title of figure 4 is "TSCs with increased genomic instability exhibit abnormal phenotypes." Again there is no measure of GIN, but instead staining of derived TSCs for proliferation, cell death, and a TSC marker. Title of figure 5 is "DNA damage responses and G2/M checkpoint activation drive premature TSC differentiation." However, there does not appear to be a difference in gH2AX between the two mutant genotypes. Checkpoint proteins might be up, but need quantification and reproduction. > 4C is the only marker of differentiation. Importantly, all the analyses here are associations, not connections, so cannot use the word "drive". Similar issues can be raised with a number of the supplementary figures.

Major Comments:

1) A deeper analysis of the cell lines is likely to be the most fruitful path to reveal interesting mechanisms. It is very surprising that there is no phenotype in ESCs. Authors should check for increased apoptosis. Maybe the phenotypic cells are lost. Or do ESCs use different MCMs/mechanisms of DNA replication or are they better able to handle replication stress and GIN? How many passages were the TSCs and ESCs cultured for? Does GIN (i.e. aneuploidy, CNVs) develop in TSCs and ESCs with passaging? How do the MCM mutations impact the molecular identity of the ESC and TSC cells including their heterogeneity in the population.

2) Along similar lines, most of the in vivo phenotypic analyses are performed at E13.5, long after defects are likely beginning to express themselves especially given that they see phenotypes in the TSCs, which represent the polar TE of a E4.5. To understand the primary defects of the in vivo phenotype, they should be looking much earlier. Supplemental figure 5 is a start but represents a rather superficial analysis.

3) Fig. 6 would benefit from evidence that MCM3 mutant is rescuing MCM4 levels in the chromatin fraction of cells and the DNA damage phenotype.

Minor Comments:

1) There is a lack of quantification and repeats for all Westerns. At minimum there should be three repeats for each experiment, quantification including normalization to a reference protein, and stats confirming any proposed differences between conditions.

2) I would recommend moving the results in supp table 1 to figure 1. While negative, they are the newer results. The results shown in current figure 1 are essentially a reproduction of their previous work.

3) Need to review citations to figures. For example, no citations are made to figure 4a and 4c.

Significance

As is, the study does not provide much new insight or understanding of how the MCM mutants are driving the sex-skewed semi-lethal phenotype. It would likely take much effort (months) to reach such a goal. However, without such effort, it is unclear what the significance of the story is. It does make the observation that the placenta appears to be impacted more severely and earlier than then the embryo, and that within the placenta, certain zones and cell types are more vulnerable. The reasons for these differential impacts are unclear though.

If the authors choose not to dig deeper as suggested in the major comments, then at a minimum it would be important to soften their conclusions as raised in the summary and at least perform experiments/edits proposed in minor comments.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In a previous paper (McNairn et al. 2019 "Female-biased embryonic death from inflammation induced by genomic instability" Science), the Schimenti lab demonstrated that mouse embryos with hypomorphic mutations of the heterohexameric minichromosome maintenance complex, mutations that cause increased genomic instability (GIN), show reduced embryonic viability, with greater loss of female embryos and some parent-of-origin effect. Treatment with immunosuppressants, including ibuprofen and testosterone, partially rescued the observed lethality.

In this new manuscript, the Schimenti lab demonstrates that these GIN-prone mutants feature smaller placentas with fewer cells. Mutations that interfere with the ability of the innate immune system to respond to micronuclei (a consequence of GIN) have no protective effect. Munisha and colleagues then demonstrate that MCM-mutant TSCs are harder to derive and show elevated apoptosis and a greater propensity for differentiation. The mutant TSCs show CHK1 phosphorylation, P53 phosphorylation and higher P21 levels, all consistent with a response to DNA damage. Downstream of this, they also show loss and inhibition of CDK1, which is already established to cause G2/M arrest (generally) and endoreduplication (specifically in trophoblast). The authors advance a model in which GIN results in loss of the TSC pool by apoptosis, cell cycle arrest and premature differentiation, resulting in smaller placentas and particularly fewer junctional zone cells. How this causes inflammation is less clear, but inflammation appears to be a downstream effect rather than cause of poor placentation.

Major comments:

This is a strong manuscript with few problems and all important findings well justified, indeed this is a nicely polished manuscript for something just entering peer review. There are a few unclear points textually and a couple places in the supplementary figures where better data quality would help, but generally it is a high-quality manuscript.

• I am confused as to the basis of the sex-skewing phenomenon? Is the problem that lack of maternally loaded WT Mcm4 worsens the phenotype, or is the issue that Mcm4C3/C3 dams are less able to retain pregnancies, perhaps being a more inflammatory environment? Also, while there quite consistent evidence for reduced viability of Mcm4C3/C3McmGt/+ progeny, especially for female progeny, how confident can we be that the genotype of the dam vs. sire is important? Notably on a Ddx58 background, the progeny of the Mcm4C3/C3 sire included seven live male Mcm4C3/C3McmGt/+ but no female.

• I'm not sure what Supplementary Figure 6 is showing (faster differentiation of C3 but less TGC?). Regardless, it's hard to draw too much conclusion from one not-very-pretty Western blot. This figure requires both additional replicates and a better explanation of how it fits with the other conclusions of the paper..

• Supplementary Figure 7F-G is puzzling. Half of the mESCs have gamma-H2AX at all times, including most in S or G2 phase? In Figure S7E, do the quadrants correspond to being negative or positive for gamma-H2AX? At very least, IF images showing clear gamma-H2AX foci would be much more convincing.

• The methods section is well detailed, but it would be ideal to clarify how many replicates each Western Blot or flow cytometry experiment is representative of.

The required additional experiments re: Supplementary Figure 6 and 7 could be conducted in a couple of months.

Minor comments:

• Supplementary Table 1. would be enhanced greatly showing comparable tables for Mcm4C3/C3 x Mcm4C3/+McmGt/+ in mice without the Tmem173 or Ddx58 mutations. It is fine to recycle data from McNairn 2019 here, as long as the source is indicated, but a comparison is needed.

• Is it possible that cGAS-STING and RIG pathways act redundantly to cause inflammation and lethality, or that other innate immune components are involved? I don't expect the authors to make compound mutants to test this but at least this possibility should be discussed textually.

• In Figure S3E-F, is the box above each graph supposed to show the genotype of the dam?

• "Indeed, the placenta and embryo weights of E13.5 Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ animals were significantly improved vs. Mcm4C3/C3 Mcm2Gt/+ animals, rendering them similar to Mcm4C3/C3 littermates (Fig. 6A-C). The JZ (but not LZ) area in Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ placentae also increased to the level of Mcm4C3/C3 littermates (Fig. 6D-H)." There are two problems here. First, the figure calls are wrong. Second, the description of the data is not quite right, it looks like the C3/C3 and C3/C3 M2/+ M3/+ LZs are a similar size to each and are statistically indistinguishable.

Significance

I partially discussed the above in the summary, but this paper makes a major breakthrough, showing that cell autonomous defects in hTSCs are very likely at the heart of the pathology observed in GIN-prone murine mutants.

Some questions go unsolved. Why are TSCs more prone to die in response to GIN than mESCs, particularly in light of the general observation that karyotypic abnormality is more common in placental lineage? How does the placental abnormality give rise to inflammation? No manuscript can answer every question, and I think this is a mature manuscript that can be published in a good journal with limited modifications.

I am an expert on gene regulation in placental development, with somewhat less expertise in the DNA damage field. The placenta field will find this paper interesting, as will the DNA damage field. There are also ramifications for cancer research. The question of why some cells tolerate high levels of DNA damage and others die is very relevant to cancer.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

SUMMARY

In this study, Fernandes and colleagues addressed the question of the role of micro-RNAs in regulating the coupling between organ growth and developmental timing. Using Drosophila, they identified the conserved micro-RNA miR-184 as a regulator of the developmental transition between juvenile larval stages and metamorphosis. This transition is under the control of the steroid hormone Ecdysone, and has been shown to be modulated in case of abnormal tissue growth to adjust the duration of larval growth in response to developmental perturbations. The relaxin-like hormone Dilp8 has been identified as a key secreted factor involved in this coupling. Here, the authors show that miR-184 is involved in the regulation of Dilp8 expression both in physiological conditions and upon growth perturbation. They propose that this function is carried out in imaginal tissues, where miR-184 levels are modulated by tissue stress. While several factors have already been involved in triggering sharp dilp8 induction at the transcriptional level, this study adds another level of complexity to the regulation of Dilp8 by proposing that its expression is fine-tunned post-transcriptionally through repression by miR-184.

__MAJOR COMMENTS______

Overall, the manuscript is well organized, and the logics of the experimental plan well presented. The results are clear, and I appreciate the quality of the pupariation curves. However, I believe that two main conclusions of the paper are not fully supported by the results presented in the figures: the direct regulation of dilp8 3'UTR by miR-184, and the specificity of this regulation in imaginal discs. Here I develop in more details these two aspects.

Comment 1) The strategy of the 3'UTR sensor is not fully optimized. Indeed, in most experiments, qRT-PCR is used to assess dilp8 expression levels, although it reflects both transcriptional and post-transcriptional. Importantly, to show that post-transcriptional regulation is involved in the response to tissue damage, the levels of the 3'UTR sensor should be analyzed in discs expressing RAcs (showing at the same time that the response is cell-autonomous in the discs). The expected upregulation of the sensor should be prevented by simultaneous expression of miR-184. This approach would shed light on the relative contribution of transcriptional versus post-transcriptional regulation of dilp8 in response to growth perturbation.

Response: We thank the reviewer for this comment. We agree that qRT-PCRs do not distinguish between transcriptional and post-transcriptional changes of dilp8 levels, in response to changes in miR-184 levels and tissue damage. In addition to the qRT-PCR data we have looked at dilp8-3’UTR-GFP reporter in response to overexpression of miR-184 in the wingdisc using patched-Gal4 driver, which show downregulation of the GFP reporter in the ptc domain (Fig 4C-D’). This suggests that dilp8 mRNA is a direct target of miR-184 by post-transcriptional regulation through its 3’UTR. Further, to confirm the specificity of the effect of miR-184 on dilp8-3’UTR, we generated a dilp8-3’UTR mutant in which the single target site for miR-184 was mutated. We show that the mutated dilp8-3’UTR reporter doesn’t show any regulation in response to miR-184 overexpression in the ptc domain of the wingdisc (Fig. 4E, E’, F, F’). This experiment confirms the specificity of the dilp8-3’UTR regulation by miR-184.

As suggested by the reviewer we analysed dilp8-3’UTR-GFP reporter expression by overexpressing RicinA using ptcGAL4 driver in the wing imaginal disc (Fig. S6F-G’). We observed a slight but consistent increase in the dilp8-3’UTR-GFP reporter expression, indicating post-transcriptional regulation of dilp8 expression in response to tissue damage. However, the increase of reporter GFP levels observed in this experiment in response to tissue damage is mild (Fig. S6F-G’) than expected based on the qRT-PCR results (Fig S6A and B). We have added this new data to the manuscript (Fig. S6F-G’).

We propose the following reasons to explain this result:

a) both transcriptional and post-transcriptional regulation of dilp8 mRNA in response to developmental perturbations

b) the data on 3’UTR reporter GFP is specifically from the ptc domain expression of RicinA, whereas for dilp8 transcript levels we have expressed RicinA in all larval imaginal tissues, or in the entire wing imaginal disc, which could be one of the reasons for the stronger effect seen on dilp8 mRNA levels

c) we are not certain if the tubulin-promoter driven dilp8-3’UTR GFP reporter reflects post-transcriptional regulation of dilp8 by miR-184 efficiently in comparison to qRT-PCR. This is especially as the reporter-GFP-3’UTR will be expressed at very high levels due to the tubulin promoter, a majority of this reporter-GFP mRNA may not be relieved from degradation due to the moderate suppression of miR-184 in response to RicinA overexpression.

Thus, our experiments suggest that dilp8 levels are regulated post-transcriptionally by miR-184 which contributes to pupariation delays in response to tissue damage. In support of this, we could rescue pupariation delays and dilp8 induction caused by RicinA expression using overexpression of miR-184 (Figs 5B, C). Thus, we confirm that the effect of post-transcriptional regulation by miR-184 during developmental perturbations also contributes to dilp8 induction and pupariation delays. Unfortunately, due to experimental limitations we could not perform simultaneous expression of RicinA and miR-184 to evaluate the rescue of dilp8-3’UTR-GFP sensor expression. The levels of dilp8-3’UTR sensor GFP is reduced efficiently by miR-184 overexpression (Fig 4D), which prevented us from attempting the rescue of the moderate increase of dilp8-3’UTR GFP levels in response to RicinA.

Comment 2) In my opinion, the use of a 3'UTR sensor is not sufficient to conclude that the regulation by miR-184 is direct, as miR-184 could also regulate an intermediate factor that acts on dilp8 post-transcriptional regulation. To solve this issue, a common strategy is to generate a 3'UTR sensor with mutated binding sites that should abolish the regulation by miR-184. This mutated 3'UTR might also respond differently to tissue damage, which would strongly support the conclusions of the study.

Response: We couldn’t agree more with the reviewer, this comment is addressed in the response to comment 1. We have confirmed the specificity of regulation of dilp8-3’UTR by miR-184 using target site mutated dilp8-3’UTR (new figures added to the manuscript Fig. 4E, E’, F, F’). We tested if the changes in dilp8 mRNA levels in response to tissue damage is post-transcriptional mediated by miR-184. We observe that there is a slight, but consistent increase of dilp8-3’UTR GFP reporter levels in the ptc domain of wingdisc in response to RicinA expression, suggesting a role for miR-184 mediated post-translational regulation of dilp8. However, we have not yet tested the mutated dilp8-3’UTR GFP reporter in response to tissue damage.

Comment 3) Concerning the tissue-specific regulation of Dilp8 by miR-184, these results need to be strengthened. Indeed, this comes mostly from phenotypes observed with rn-GAL4. Although this is a classical tool for driving expression in imaginal discs, rn-GAL4 also drives strong expression in other tissues that could contribute to triggering a delay, such as the CNS and part of the gut (proventriculus). In our hands, some growth phenotypes in the wing obtained with rn-GAL4 could be fully reverted by blocking GAL4 in the CNS indicating that the phenotype was not wing-specific. Importantly, miR-184 seems to be highly expressed in the CNS according to FlyBase, reinforcing the possibility that it plays a role in this organ. Here I propose approaches to confirm that miR-184 mediated regulation of dilp8 and developmental timing indeed occur in the discs:

- Another driver with less secondary expression sites could be used (pdmR11F02-GAL4), or rn-GAL4 could be combined with an elav-GAL80 to prevent expression in most neurons. - The authors could identify the source of Dilp8 upregulation in miR-184 mutants using tissue-specific qRT-PCR instead of whole larvae expression like in Fig 4A-B. - This tissue-specific upregulation could be functionally tested using a rescue experiment, in which the delay observed in miR-184 mutants could be rescued by disc-specific downregulation of Dilp8 (using pdm2-GAL4 for instance).

Response: We are thankful to the reviewer, and agree that it is important to show that the effects that we see using rn-Gal4 are specific to imaginal discs, and not due to an effect in CNS. We tested this by expressing miR-184 sponge in the CNS. Though miR-184 is highly expressed in the larval CNS, downregulation of miR-184 specifically in the pan-neuronal background using elav-GAL4 led to no effects on pupariation timepoint. We have added this as supplementary data Figure S4. Therefore, we believe that the miR-184 downregulation phenotype in the rnGAL4 background can be mainly attributed to its role in the imaginal discs. In addition, as suggested by the reviewer we have also demonstrated that downregulation of miR-184 in the imaginal discs using rnGAL4 driver leads to an increase in dilp8 expression (Fig S5B). Thus confirming that dilp8 mRNA is enhanced in the imaginal discs by blocking miR-184.

OPTIONAL: Because it is known that dilp8 is strongly regulated at the transcriptional level, the relative input from post-transcriptional upregulation is an important question arising from this study. Although it might be a more long-term approach, I believe that generating a Dilp8 mutant lacking its 3'UTR or, even better, with mutated miR-184 binding sites, would shed light on the role of this regulation for the response to growth perturbation and/or developmental stability (fluctuating asymmetry).

Response: We thank the reviewer for the suggestion. This would have been an interesting experiment to carry out especially in the context of fluctuating asymmetry.

MINOR COMMENTS

1. __ I think that a number of results could be moved to SI as they are either controls, or reproduce published data without bringing novelty. For instance, results in Fig 5A-D are similar to data published by Sanchez et al, as stated in the text. Fig6A as well.__

__Response: __We thank the reviewer for this suggestion, Fig. 5A-D, and F has been moved to Fig. S6A-E. We have also moved data from Fig. 6 to Fig. 5, as a result Fig 6 A-D has become Fig. 5 B-D.

__ Fig 6D is quite mysterious, as it suggests that basal JNK activation regulates miR-184, which is different from a context of tissue damage. I think that this result could be removed. Alternatively, if the authors want to dig in that direction, more experiments should be provided, such as bskDN expression in an RAcs context and the effects on miR-184 levels and the 3'UTR sensor (since transcript levels are already published).__

Response: We would like to clarify that our experiments suggest that endogenous JNK signalling negatively regulates miR-184, as blocking basal JNK signalling using bskDN increased the levels of miR-184 (changed to Fig 5D). Enhanced JNK signalling has been reported to be involved in tissue damage responses, and we propose that RicinA mediated increase in JNK signalling leads to the reduction of miR-184 (changed to Fig 5A, S6D-E). However, we are not strongly implying this as we did not co-express RicinA and bskDN to show that JNK signalling is responsible for the drop in miR-184 levels in response to tissue damage. We thank the reviewer for seeking this explanation, we have rewritten the results section to improve clarity.

__ The references related to Dilp8 should be checked more in detail in the intro and discussion. About Dilp8 and developmental stability: remove the ref to Colombani et al 2012, instead put Boone et al 2016 and add Blanco-Obregon et al 2022 (in addition to Garelli et al 2012 who initially identified this phenotype. About Lgr3 as the receptor for Dilp8: add Colombani et al, Current Biology 2015, and cite here Vallejo et al 2015, Garelli et al 2015. Among the important transcriptional regulators of Dilp8, Xrp1 could be mentioned (Boulan et al 2019, Destefanis et al 2022) as it plays a complementary function to JNK depending on the type of tissue stress.__

__Response: __We are really sorry for the glaring errors in citing appropriate references. We thank the reviewer for correcting this for us. We have made necessary changes to the text.

Significance

GENERAL ASSESSMENT This study provides convincing data showing that the conserved microRNA miR-184 plays a role in regulating developmental timing in Drosophila through modulating the levels of Dilp8, a key factor in the coupling between tissue growth and developmental transitions. The results are convincing, but the general conclusions of the paper need to be strengthened regarding the direct regulation of dilp8 by miR-184 and the tissue-specificity of this interaction.

ADVANCE Dilp8 is a key factor that modulates growth and timing in response to developmental perturbations and contributes to developmental precision in physiological conditions. As such, its regulation has been studied by different groups in the last decade, leading to the identification of several inputs for its transcriptional regulation. Here, the authors uncover a post-transcriptional regulation by miR-184, adding another level of regulation of Dilp8 that contribute to ensuring proper regulation of developmental timing, and opening the possibility that miR-184 might play similar roles in other species.

AUDIENCE This study is of interest for researchers in the field of basic science, with a focus on developmental timing, tissue damage and biological function of microRNAs.

REVIEWER EXPERTISE Drosophila, growth control, developmental timing, Dilp8.

Reviewer #2

Evidence, reproducibility and clarity

Drosophila has helped to characterize the mechanisms that coordinate tissue growth with developmental timing. The insulin/relaxin-like peptide Dilp8 has been identified as a key factor that communicates the abnormal growth status of larval imaginal discs to neuroendocrine neurons responsible for regulating the timing of metamorphosis. Dilp8, derived from imaginal discs, targets four Lgr3-positive neurons in the central nervous system, activating cyclic-AMP signaling in an Lgr3-dependent manner. This signaling pathway reduces the production of the molting hormone, ecdysone, delaying the onset of metamorphosis. Simultaneously, the growth rates of healthy imaginal tissues slow down, enabling the development of proportionate individuals.

In this manuscript "miR-184 modulates dilp8 to control developmental timing during normal growth conditions and in response to developmental perturbations" by Dr. Varghese and colleagues, the authors identify a new post transcriptional regulator of Dilp8. The authors show that miR-184 plays a pivotal role in tissue damage responses by inducing dilp8 expression, which in turn delays pupariation to allow sufficient time for damage repair mechanisms to take effect.

Major points:

Comment 1) In most of the experiments for percentage of pupariation, the 50% pupariation in control is around 110 hours AED in figures 1, 2 and 3. In figures 5 and 6 using the UAS Ricin, the controls are more around 90 hours AED. Why this discrepancy?

Response: We thank the reviewer for asking for this clarification. The former experiments for Figs 1-3 were carried out at 25oC while the latter experiments with a cold sensitive version of RicinA (UAS-RAcs), Figs 5 and 6 (now changed to Figs. 5 and S6 as suggested by reviewer #1) were carried out at 29oC (permissive temperature). This difference in temperature has led to alterations in pupariation timing. We apologise for not having mentioned this in the text, now we have made necessary corrections to the methods section clearly indicating this.

Comment 2) What is the mechanism behind the expression of miR-184 in stress conditions? Is miR-184 also implicated in other conditions giving rise to a developmental delay (X-rays irradiation or animal bearing rasV12, scrib-/- tumors)?

Response: We thank the reviewer for these questions.

a) In response to developmental perturbations by RicinA, we believe that activation of JNK signalling controls miR-184 expression. We propose this as our experiments show that imaginal disc damage leads to enhancement of JNK signalling and increase in dilp8 mRNA levels (as reported earlier by Colombani et al 2012; Sánchez et al 2019), and a simultaneous reduction of miR-184 (Figs. S6A, D, E). We also have performed new experiments to show that in response to RicinA expression in the wingdisc there is moderate increase in the dilp8-3’UTR-GFP sensor expression (Figs. S6F-G’), indicating a post-transcriptional regulation of dilp8 expression in response to tissue stress. We also show that RicinA induced dilp8 expression and pupariation delay can be rescued by increasing miR-184 levels (Fig 5B and C), suggesting that the reduction of miR-184 in response to tissue damage contributes to the damage responses. In a separate experiment we show that blocking the endogenous JNK pathway by the expression of bskDN enhances miR-184 levels, suggesting that miR-184 is under the regulation of JNK signalling (Fig 5D). Hence, we speculate that during tissue stress, activation of JNK signalling leads to a reduction of miR-184 levels which contributes to regulating the levels of dilp8 post-transcriptionally and resulting in pupariation delays. The text has been modified to explain this better.

b) In a previous paper by Shu et al., 2017 (https://doi.org/10.18632/oncotarget.22226) decreased expression of miR-184 was observed in a lglRNAi; RasV12 tumor background. Apart from this various studies have shown that dilp8 levels increase in response to tumour, radiation stress, apoptosis, and tissue damage (Yeom et al 2021, Ray et al 2019, Demay et al 2014, Katsuyama et al 2015, Colombani et al 2012, Garelli et al 2012). Whether the regulation of dilp8 by miR-184, occurs in these backgrounds is yet to be tested. We have now discussed this possibility in the manuscript.

Comment 3) dilp8 mutant animals have also been shown to be more resistant to starvation or desiccation (https://doi.org/10.3389/fendo.2020.00461). Is miR-184 implicated in this answer?

Response: We thank the reviewer for this question. In our earlier experiments miR-184 has been demonstrated to be regulated by nutrition in the larval stages and lack of miR-184 led to enhanced larval death in response to diet restriction (Fernandes et al., 2022). miR-184 was also demonstrated to play a role in the insulin producing cells (IPCs) in regulating lifespan (Fernandes & Varghese., 2022). In the current work, we propose miR-184 to act upstream of dilp8 in response to stress stimuli. Hence, it is possible that miR-184 might be involved in responses to starvation and desiccation stress in the adult female flies, by regulating dilp8 levels post-transcriptionally. However, it has not been tested yet if the miR-184 regulation of dilp8 plays a role in resistance to starvation or desiccation in adult females, as this was not within the scope of the current study. We have now added this reference in the discussion section.

Comment 4) dilp8 expression has been also shown to be regulated by Xrp1 in response to ribosome stress (https://doi.org/10.1016/j.devcel.2019.03.016). This paper should be included in the manuscript. Is it possible that the expression levels of miR184 are regulated by Xrp1?

Response: We thank the reviewer for the suggestion and have incorporated the reference into the paper. During ribosome stress in the larval imaginal discs the stress-response transcription factor Xrp1 acts through dilp8 in regulating systemic growth. We agree with the reviewer, it is possible that expression of miR-184 is regulated by Xrp1. Currently we have not explored this possibility. We have now added this to the discussion section.

Minor points:

1. __ Does the overexpression of miR184 induce an increased fluctuating asymmetry?__

Response: We thank the reviewer for asking this question. The role of dilp8 in the fluctuation asymmetry is only observed in the dilp8 hypomorphic mutant background. To replicate this we would have to overexpress miR-184 in either the whole larvae or in the wing discs. Unfortunately overexpression of miR-184 in the wing discs (using rnGAL4) leads to pupal lethality while as overexpression of miR-184 in the whole larvae leads to embryonic lethality and therefore we were not be able to conclude from our experiments if miR-184 overexpression induces increased fluctuating asymmetry.

2. There are 2 references Colombani et al. (2012 for Dilp8 and 2015 for Lgr3). Can you double check that they are used accordingly

Response: We thank the reviewer for pointing these errors out and we have incorporated these changes into the paper.

Significance

Altogether, the paper present compiling lines of evidence supporting the proposed model. The experiments are well designed and are convincing. The papers is interesting and relevant for a broad audience.

__Reviewer #3 __

Evidence, reproducibility and clarity (Required):

This is an interesting study demonstrating an interaction between miR-184 and the Drosophila insulin-like peptide 8 (dilp8) in the tissue damage response. The authors show that Dilp8 activity is negatively regulated by miR-184, apparently through direct interaction between miR-184 and the dilp8-3'UTR, which leads to lower dilp8 mRNA transcript levels, via an undetermined mechanism, supposedly its degradation? Furthermore, the authors show that during aberrant tissue growth, miR-184 levels are very slightly downregulated (see comment below), and based on other experiments, imply causation of this with the increased dilp8 mRNA levels that occur in these tissues, again via an unclear mechanism: upregulation or stabilization of dilp8 mRNA. The authors present evidence that the JNK pathway, which had been known to be critical for dilp8 mRNA upregulation upon tissue damage, does so via miR-184.

Major Comments:

__Comment 1: The data showing the direct regulation of dilp8-3'UTR by miR-184 are not very strong and would require more controls to strengthen the claim, as described below. __

Response: We have performed new experiments to validate that dilp8-3’UTR is regulated by miR-184. Please see the detailed responses to comments 10-12 below.

__Comment 2: The miR-184 effects are also very small (less than 2-fold reduction with tissue damage; or less than 2-fold induction with JNK-pathway inhibition via bskDN). These two points are the weakest part of the manuscript and model. __

Response: We agree with the reviewers on this point. The reduction in miR-184 levels in response to RicinA expression is modest (25–30%), and the induction of miR-184 in response to bskDN expression is less than two-fold (Figs. 5A and D). In contrast, dilp8 transcript levels increase several-fold in response to RicinA expression (Fig. 5C, S6A and B). Since we measure dilp8 transcript levels by qPCR, we detect both transcriptional and post-transcriptional contributions to dilp8 regulation. In addition, we have performed a new experiment to check the post-transcriptional regulation of dilp8, in response to tissue damage. Though the change in the dilp8-3′UTR GFP reporter upon RicinA expression in the ptc domain of the wingdisc is mild (Figs. S6F-G’), this strongly suggests a post-transcriptional outcome of the reduction of miR-184 levels on dilp8. Hence, we propose that tissue damage induces strong transcriptional activation of dilp8, while the reduction of miR-184, despite its smaller magnitude, contributes to dilp8 upregulation via post-transcriptional regulation. In support of this, our experiments demonstrate direct regulation of the dilp8-3′UTR by miR-184 (Figs. 4C-F’), and show strong dilp8 mRNA upregulation in miR-184 deficient conditions (Fig. 4A and B), suggesting the role of miR-184 in maintaining dilp8 levels. We also show that RicinA induced effects on dilp8 and pupariation delay are reversed by co-expression of miR-184 (Fig. 5C). We do not claim that regulation by miR-184 is the sole mechanism for driving dilp8 induction during tissue damage, but suggest that miR-184-mediated post-transcriptional regulation acts in a complementary manner to transcriptional responses. Furthermore, we believe that the mild effect of JNK signaling on miR-184 (as shown by the bskDN experiment) is sufficient for the moderate reduction of miR-184 in response to tissue damage.

Comment 3: ____Regarding the expression levels, it does not help that the authors show bar graphs with standard errors of the mean instead of the actual data points to allow reliable appreciation of the data dispersion.

Response: We have modified our figures and have performed statistical analysis according to the suggestions of the reviewers, please see responses to comments 1-9, and 13-19.

Comment 4: It is difficult to understand how minute changes in miR-184 levels can lead to over an order of magnitude differences (in some cases) in dilp8 mRNA levels considering that it is a stoichiometric relationship. Maybe ?miR-184-Dicer1? complexes are highly stable and re-used for multiple dilp8 transcripts - the authors could discuss how they understand this occurring in their manuscript.

On the same line, discussion is also rather weak on what regards the mechanism of control of dilp8 mRNA levels by miR-184. Please discuss eg, the evidence for mRNA degradation induction by microRNAs with this UTR binding profile (imperfect UTR binding Fig S4) and-if appropriate-how other possible regulatory models (direct and indirect) could explain the findings.

Response: We accept the reviewers comment that 25-30% reduction of miR-184 is low in comparison to the many fold increase in dilp8 levels. We believe that both post-transcriptional and transcriptional changes are responsible for the induction of dilp8 in response to tissue damage. However, our experiments suggest the role of post-transcriptional regulation by miR-184, as pupariation delay is rescued by miR-184 overexpression (also please see the response to the previous comment). We are not ruling out the possibility of transcriptional regulation of dilp8 mRNA, rather we are suggesting the possibility that both transcriptional and post-transcriptional means are responsible for changes in dilp8. Moreover, we have not performed absolute measurement of miR-184 in the imaginal discs (what we show is a comparison between control and RicinA expression), hence we do not have an exact estimate of how many miR-184 molecules are reduced and if they would be greatly equal or more in comparison to the dilp8 mRNA molecules that are upregulated, as again while measuring dilp8 mRNA we are not checking how many molecules of dilp8 exactly are increased. As the reviewer suggests, it is possible that miR-184-RISC could be stable to handle multiple dilp8 molecules one after the other, hence it is not a 1:1 relationship between miR-184:dilp8. We have included this in the manuscript. It is also known that imperfect 3’UTR binding as seen in most animal microRNAs leads to translational repression and mRNA deadenylation, which eventually results in mRNA degradation.

Comment 5: ____We suggest the authors carefully revise their citations to cite appropriate work that supports the claims, and also to avoid missing the seminal studies that report the claims they cite.

Response: We are really apologetic for the errors citing the key references. We are grateful to the reviewers for correcting this for us. We have made changes to the text to include and correct the references.

We have the suggestions below which we hope will help the authors improve their manuscript. If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

Detailed Comments:

Comment 1. Results 1st paragraph: please describe the screen in more detail. As written, one only discovers it was a miRNA loss-of-function screen when reading the legend of Table S1. Please show the original data of the screen - with dispersion if possible.

Response: We thank the reviewers for these suggestions, we have now included the data from the screen with SEM, and p-values.

Comment 2. Results 1st paragraph, Fourth line, "While several miRNAs caused delays in pupariation by 12 hours or more..". Please correct, as actually loss of miRNAs caused delays.

Response: We thank the reviewer for pointing out this error, we have corrected the text accordingly.

Comment 3. ____Results (Figure 1) - It says that data from three independent experiments are shown. However there is no dispersion in the data. Could the authors please explain this? Are the results of the three experiments summed and presented as one? or is this one of the three?

Response: We thank the reviewers for these suggestions and have plotted data with the SEM values.

Comment 4. It is reported in the legend of Figure S2 that LogRank test was performed to determine statistical significance. However, no statistical data is presented. Please show the results.

__Response: __We thank the reviewers for these suggestions to improve the data presentation, we have incorporated the p-value as suggested.

Comment 5. Fig2A and B. Please show the data points in the bar graphs (as in Figure. 2C), or choose another data representation. ____Please consider redoing statistical analysis with a simple t-test. ____It is not clear to me why ANOVA was used to compare two samples. Please state that data are normalized also to control (tub-GAL4>UAS-scramble). Please ____state____ the h post-hatching from which the RNA samples were collected (as in Fig 2C for 20HE quantification).

__Response: __We thank the reviewers for these suggestions to improve the data presentation, we have incorporated all changes as suggested. Similar changes have been incorporated to the rest of the figures of the manuscript as well. Hours post-hatching information for each figure is now added to the figure legends. __ __

Comment 6. Fig2C. Fig legend states the bar graphs are "absolute values". Please specify if the bar represents the average, median or something else.

Response: We thank the reviewer for pointing this out, we have made the suggested changes.

Comment 7. Throughout the manuscript: please use GAL4 in capital letters or at least standardize it throughout the ms. Currently there are GAL4s and Gal4s.. eg compare Fig 2 and 3 legends.

Response: We thank the reviewer for pointing this out, we have incorporated all changes as recommended.

Comment 8. FigS3A and B. Please revise as Fig2A and B above. and apply the same criteria in the respective figure legend.

__Response: __We thank the reviewer for pointing this out, we have made the changes as recommended.

Comment 9. Fig. 4 - please indicate on the figures what is whole larvae and what is wing imaginal discs. This will facilitate understanding of the figure.

__Response: __We thank the reviewers for these suggestions and have included this information in all the figures.

Comment 10. Fig 4 - Data - Authors do not show that rn-GAL4>miR-184-sponge causes up regulation of dilp8 mRNA levels, hence the model is weakened. Doing this experiment would significantly strengthen the study whatever the result is.

Response: We thank the reviewer for pointing this out and we have included this in the manuscript (Fig S5B).

Comment 11. The dilp8-3'UTR experiment is weak especially because its generation is not sufficiently well described in the manuscript. "The dilp8 3'UTR-GFP reporter line was created as described in (Vargheese & Cohen, 2007)" is not sufficient. Please describe the construct generation in sufficient detail so that the experiments can be reproduced by others.

Response: We thank the reviewer for pointing this out and we have elaborated in the methods section on how we generated the dilp8 3'UTR-GFP reporter and dilp8 3'UTR mutant GFP reporter lines. The plasmid was originally created in Steve Cohen’s lab at EMBL, by modifying pCasper4 plasmid, by introducing a tubulin promoter, EGFP and a multiple cloning site, which allows one to clone 3’UTRs of target genes into this plasmid. Not1 and Xho1 sites were used to clone the dilp8-3’UTR and mut-3’UTR. We hope this explains our strategy sufficiently.

Comment 12. Making assumptions, if the construct is as described in Vargheese & Cohen, 2007 and contains all of the dilp8 3'UTR - it should be a Tubulin-driven GFP gene with a dilp8-3'UTR "Tub-GFP-(dilp8 3'UTR)". In this case the authors need to rule out the alternative interpretation of the result in Fig. 4D by showing that the expression of miR-184 does not down regulate Tub-GFP expression itself. The best scenario would be to have a mutated dilp8 3'UTR for the miR-184 recognition site. This experiment would significantly strengthen the study and model.

Response: We thank the reviewer for pointing this out. We agree with the reviewers that this experiment is needed to prove direct regulation of the dilp8-3’UTR by miR-184. We have mutated the sequences complementary to the seed region of miR-184 in the dilp8-3’UTR, and demonstrated that overexpression of miR-184 does not regulate the mutated tub-GFP-(dilp8 3'UTR) expression. This confirms that the dilp8 gene is a direct target of miR-184. This data is added to the manuscript as Figs 4E-F’.

Comment 13. Figure 4C-D please separate dilp8 from 3'UTR with a space or hyphen.

Response: We thank the reviewer for pointing this out and have separated dilp8 from 3’UTR with a hyphen.

Comment 14. Figure 4E. Please name the dilp8 allele as MI00727 as it is not a KO, but rather a hypomorphic mutation (fully WT dilp8 transcripts are still generated, albeit at a much lower level).

Response: We thank the reviewer for pointing this out and we have made the necessary changes.

Comment ____15. Figure 6D: please add UAS to bskDN/+. All figures have rn-GAL4 alone or with UAS-GFP as control. This finding would be strengthened with this other control, especially because the size effect is small.____ This being said a general comment for all experiments is that hemi-controls are generally missing for all figures. eg, in Fig 3. One would typically include controls such as A. Phm>+ and +>miR.184; B. aug21>+ and +>miR.184; C. ptth>+ and +>miR.184; D. rn>+ and +>miR.184

Response: We thank the reviewer for pointing this out. We have added UAS to bskDN, now Fig 5D and have also added the rnGAL4/+ control. We have also performed various hemi-control experiments as suggested by the reviewer to our best capabilities. We have added a separate graph with the hemicontrols in the as a Reviewer Response Figure 1.

Comment 16. Figure 7: Are IPCs necessary for the model? If not, I suggest removing them and placing the Lgr3 neuron cell bodies much more anterior in this scheme. Their cell bodies are as anterior and rostral as it gets, approximately where the IPCs are depicted in this type of view of the CNS.

Response: We thank the reviewer for pointing this out and have removed IPCs from the figure, this figure is now labelled as Fig. 6.

Comment ____17. Table S1- It would be preferable to see the data of these experiments, but if the authors prefer to show this data in a table, please at least add the dispersion analyses (eg standard deviation.. OR median+-quartiles OR Confidence intervals..), N of animals analysed, and statistics against controls.

Response: We thank the reviewer for pointing this out, we have added the number of larvae analysed, SEM values and statistics against the control condition.

Comment ____18. In all figures with pupariation time: please also indicate significant findings in the graphs (with an asterisk, for instance) and adjust figure legends accordingly. This could facilitate understanding the data.

__Response: __Thanks for the suggestion. We have incorporated this information into figure legends.

Comment ____19. Please revise Figure legends for punctuation.

__Response: __We have rectified all the errors in punctuation. We thank the reviewers for suggesting this.

__Comment ____20. __

a) Abstract:

Line 10: What is the evidence to call Dilp8 a "paracrine" factor?

Response: We thank the reviewer for pointing this out, we have changed the text to ‘secreted factor’.

b) Introduction:

4th paragraph, 3rd sentence " Dilp8... buffers developmental noise and delays pupariation..." Buffering of developmental noise was first shown in Garelli et al., Science 2012, so this publication should be cited. ____4th paragraph, 5th sentence: please include Jaszczak et al., Genetics 2016. This paper was published together with the 2015 papers, just a matter of timing that it got a 2016 date. Moreover, I do not think Katsuyama et al., 2015 is well cited to back up the statement in this sentence, hence I recommend removing that citation in this sentence.

Response: We thank the reviewer for pointing this out and have made necessary changes.

c) 6th paragraph: 5th line "targeting dilp8" : please specify if you mean the gene or the mRNA, or both. Same for line 7.

Response: We thank the reviewer for pointing this out and have made necessary changes.

d) Results Page 10, 1st paragraph, 1st sentence: the works cited are not the appropriate studies that demonstrated what is being stated. This was shown in Garelli et al., Science 2012 and Colombani et al., Science 2012. Results Page 10, 1st paragraph, line 11: Please also cite Colombani et al., Science 2012, who first showed that JNK is required for dilp8 regulation.

Response: We thank the reviewer for pointing this out and are extremely apologetic for this oversight. We have made necessary changes to the manuscript.

e) Discussion, 2nd paragraph, line 4: again, please indicate the rationale for using "paracrine" to describe Dilp8's activities. The current widely accepted model is that Dilp8 acts on interneurons in the brain ____(eg, reviewed in Juarez-Carreno et al., Cell Stress, 2018; Gontijo and Garelli, Mech Dev, 2018; Mirth and Shingleton, Front Cell Dev Biol, 2019; Texada et al., Genetics 2020; Boulan and Leopold, 2021).____ In order to reach the brain, Dilp8 has to be secreted from the discs and travel to the brain. This is as an endocrine mechanism as it gets for a small larva, considering that some discs can be on the opposite side of the larva (eg, genital discs). While this does not exclude that Dilp8 could also act paracrinally, the only evidence that I am aware of comes from other contexts such as during transdetermination (where Dilp8 has been proposed to work in an autocrine or paracrine fashion, via Drl in imaginal discs (Nemoto et al., Genes to Cells, 2023), however, this is not cited appropriately in this manuscript and is less related to the Lgr3-dependent pathway being studied here.

Response: We totally agree with the reviewer and appreciate clarifying this for us. We have made necessary changes to the text.

f) Discussion Page 13, 1st paragraph, This claim is supported by data presented in Garelli et al., Science 2012, not the other two papers. Garelli et al., 2015 shows that the Lgr3 receptor also participates in buffering developmental noise. Other studies have corroborated the Garelli et al., 2012 finding: eg, Colombani et al., Curr Biol 2015; Boone et al., Nat Commun 2016; Blanco-Obregon et al., Nat Commun 2022). Many other studies have shown that Dilp8 promotes developmental stability under tissue stress and challenges.

Discussion Page 12, 3rd paragraph, 2nd sentence: "The Lgr3 neurons directly interact with ... PTTH ...and insulin-producing neurons" Please cite Colombani et al., 2015 and Vallejo et al., Science 2015. Vallejo et al., propose that circuit with insulin-producing neurons. In the 3rd sentence, only Jaszczak et al., 2016 is cited, whereas this claim/model comes from many studies, such as Halme et al., Curr Biol, 2010; Hackney et al., PLoS One 2012; Garelli et al. Science 2012; Colombani et al., Science, 2012; and the Lgr3 papers from 2015). Jaszczak et al., actually propose that Lgr3 is also required in the ring gland in addition to neurons.

Discussion page 14 last paragraph,10 line, "In Aedes aegypti ....regulates ilp8 (Ling et al., 2017)". As far as I understand mosquitoes do not have a dilp8 orthologue (see for instance Gontijo and Gontijo, Mech Dev 2018; and Jan Veenstra's work). ilp nomenclature (numbering) does not follow that of Drosophila, so ilp8 is probably a typical Insulin/IGF-like peptide and is NOT an orthologue of Dilp8, a relaxin, so this citation needs to be removed or placed into the broader context of microRNA regulation of ilps.

Response: We are really sorry for the numerous glaring errors in the references. We thank the reviewers for correcting this for us. We have made necessary changes to the text.

Thank you for the opportunity to review your interesting work,

Alisson Gontijo and Rebeca Zanini

Reviewer #3 (Significance (Required)):

If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

__Author’s concluding response: __

We thank all the reviewers for the overall positive comments and suggestions that we believe have helped us to improve our manuscript. We have incorporated all the changes suggested, especially regarding errors in citing key references. We have performed most of the experimental suggestions. Also, we have modified the way in which graphs are presented, including statistical tests as suggested by the reviewers. Several controls have been performed to strengthen the manuscript further. We believe that this review process aided in significantly improving this manuscript.

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Referee #3

Evidence, reproducibility and clarity

This is an interesting study demonstrating an interaction between miR-184 and the Drosophila insulin-like peptide 8 (dilp8) in the tissue damage response. The authors show that Dilp8 activity is negatively regulated by miR-184, apparently through direct interaction between miR-184 and the dilp8-3'UTR, which leads to lower dilp8 mRNA transcript levels, via an undetermined mechanism, supposedly its degradation? Furthermore, the authors show that during aberrant tissue growth, miR-184 levels are very slightly downregulated (see comment below), and based on other experiments, imply causation of this with the increased dilp8 mRNA levels that occur in these tissues, again via an unclear mechanism: upregulation or stabilization of dilp8 mRNA. The authors present evidence that the JNK pathway, which had been known to be critical for dilp8 mRNA upregulation upon tissue damage, does so via miR-184. The data showing the direct regulation of dilp8-3'UTR by miR-184 are not very strong and would require more controls to strengthen the claim, as described below. The miR-184 effects are also very small (less than 2-fold reduction with tissue damage; or less than 2-fold induction with JNK-pathway inhibition via bsk-DN). These two points are the weakest part of the manuscript and model. Regarding the expression levels, it does not help that the authors show bar graphs with standard errors of the mean instead of the actual datapoints to allow reliable appreciation of the data dispersion. It is difficult to understand how minute changes in miR-184 levels can lead to over an order of magnitude differences (in some cases) in dilp8 mRNA levels considering that it is a stoichiometric relationship. Maybe ?miR-184-Dicer1? complexes are highly stable and re-used for multiple dilp8 transcripts - the authors could discuss how they understand this occurring in their manuscript. On the same line, discussion is also rather weak on what regards the mechanism of control of dilp8 mRNA levels by miR-184. Please discuss eg, the evidence for mRNA degradation induction by microRNAs with this UTR binding profile (imperfect UTR binding Fig S4) and-if appropriate-how other possible regulatory models (direct and indirect) could explain the findings. We suggest the authors carefully revise their citations to cite appropriate work that supports the claims, and also to avoid missing the seminal studies that report the claims they cite. We have the suggestions below which we hope will help the authors improve their manuscript. If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

Comments:

Results 1st paragraph: please describe the screen in more detail. As written, one only discovers it was a miRNA loss-of-function screen when reading the legend of Table S1. Please show the original data of the screen - with dispersion if possible.

Results 1st paragraph, Fourth line, "While several miRNAs caused delays in pupariation by 12 hours or more..". Please correct, as actually loss of miRNAs caused delays.

Results (Figure 1) - It says that data from three independent experiments are shown. However there is no dispersion in the data. Could the authors please explain this? Are the results of the three experiments summed and presented as one? or is this one of the three?

It is reported in the legend of Figure S2 that LogRank test was performed to determine statistical significance. However, no statistical data is presented. Please show the results.

Fig2A and B. Please show the data points in the bar graphs (as in Figure. 2C), or choose another data representation. Please consider redoing statistical analysis with a simple t-test. It is not clear to me why ANOVA was used to compare two samples. Please state that data are normalized also to control (tub-GAL4>UAS-scramble). Please state the h post-hatching from which the RNA samples were collected (as in Fig 2C for 20HE quantification).

Fig2C. Fig legend states the bar graphs are "absolute values". Please specify if the bar represents the average, median or something else.

Throughout the manuscript: please use GAL4 in capital letters or at least standardize it throughout the ms. Currently there are GAL4s and Gal4s.. eg compare Fig 2 and 3 legends.

FigS3A and B. Please revise as Fig2A and B above. and apply the same criteria in the respective figure legend.

Fig. 4 - please indicate on the figures what is whole larvae and what is wing imaginal discs. This will facilitate understanding of the figure.

Fig 4 - Data - Authors do not show that rn-GAL4>miR-184-sponge causes up regulation of dilp8 mRNA levels, hence the model is weakened. Doing this experiment would significantly strengthen the study whatever the result is.

The dilp8-3'UTR experiment is weak especially because its generation is not sufficiently well described in the manuscript. "The dilp8 3'UTR-GFP reporter line was created as described in (Vargheese & Cohen, 2007)" is not sufficient. Please describe the construct generation in sufficient detail so that the experiments can be reproduced by others.

Making assumptions, if the construct is as described in Vargheese & Cohen, 2007 and contains all of the dilp8 3'UTR - it should be a Tubulin-driven GFP gene with a dilp8-3'UTR "Tub-GFP-(dilp8 3'UTR)". In this case the authors need to rule out the alternative interpretation of the result in Fig. 4D by showing that the expression of miR-184 does not down regulate Tub-GFP expression itself. The best scenario would be to have a mutated dilp8 3'UTR for the miR-184 recognition site. This experiment would significantly strengthen the study and model.

Figure 4C-D please separate dilp8 from 3'UTR with a space or hyphen.

Figure 4E. Please name the dilp8 allele as MI00727 as it is not a KO, but rather a hypomorphic mutation (fully WT dilp8 transcripts are still generated, albeit at a much lower level).

Figure 6D: please add UAS to bskDN/+. All figures have rn-GAL4 alone or with UAS-GFP as control. This finding would be strengthened with this other control, especially because the size effect is small. This being said a general comment for all experiments is that hemi-controls are generally missing for all figures. eg, in Fig 3. One would typically include controls such as A. Phm>+ and +>miR.184; B. aug21>+ and +>miR.184; C. ptth>+ and +>miR.184; D. rn>+ and +>miR.184

Figure 7: Are IPCs necessary for the model? If not, I suggest removing them and placing the Lgr3 neuron cell bodies much more anterior in this scheme. Their cell bodies are as anterior and rostral as it gets, approximately where the IPCs are depicted in this type of view of the CNS.

Table S1- It would be preferable to see the data of these experiments, but if the authors prefer to show this data in a table, please at least add the dispersion analyses (eg standard deviation.. OR median+-quartiles OR Confidence intervals..), N of animals analysed, and statistics against controls.

In all figures with pupariation time: please also indicate significant findings in the graphs (with an asterisk, for instance) and adjust figure legends accordingly. This could facilitate understanding the data.

Please revise Figure legends for punctuation.

Abstract: Line 10: What is the evidence to call Dilp8 a "paracrine" factor?

Introduction:

4th paragraph, 3rd sentence " Dilp8... buffers developmental noise and delays pupariation..." Buffering of developmental noise was first shown in Garelli et al., Science 2012, so this publication should be cited.

4th paragraph, 5th sentence: please include Jaszczak et al., Genetics 2016. This paper was published together with the 2015 papers, just a mater of timing that it got a 2016 date. Moreover, I do not think Katsuyama et al., 2015 is well cited to back up the statement in this sentence, hence I recommend removing that citation in this sentence.

6th paragraph: 5th line "targeting dilp8" : please specify if you mean the gene or the mRNA, or both. Same for line 7.

Results Page 10, 1st paragraph, 1st sentence: the works cited are not the appropriate studies that demonstrated what is being stated. This was shown in Garelli et al., Science 2012 and Colombani et al., Science 2012.

Results Page 10, 1st pagragraph, line 11: Please also cite Colombani et al., Science 2012, who first showed that JNK is required for dilp8 regulation.

Discussion, 2nd paragraph, line 4: again, please indicate the rationale for using "paracrine" to describe Dilp8's activities. The current widely accepted model is that Dilp8 acts on interneurons in the brain (eg, reviewed in Juarez-Carreno et al., Cell Stress, 2018; Gontijo and Garelli, Mech Dev, 2018; Mirth and Shingleton, Front Cell Dev Biol, 2019; Texada et al., Genetics 2020; Boulan and Leopold, 2021). In order to reach the brain, Dilp8 has to be secreted from the discs and travel to the brain. This is as an endocrine mechanism as it gets for a small larva, considering that some discs can be in the opposite side of the larva (eg, genital discs). While this does not exclude that Dilp8 could also act paracrinally, the only evidence that I am aware of comes from other contexts such as during transdetermination (where Dilp8 has been proposed to work in an autocrine or paracrine fashion, via Drl in imaginal discs (Nemoto et al., Genes to Cells, 2023), however, this is not cited appropriately in this manuscript and is less related to the Lgr3-dependent pathway being studied here.

Discussion Page 13, 1st paragraph, This claim is supported by data presented in Garelli et al., Science 2012, not the other two papers. Garelli et al., 2015 shows that the Lgr3 receptor also participates in buffering developmental noise. Other studies have corroborated the Garelli et al., 2012 finding: eg, Colombani et al., Curr Biol 2015; Boone et al., Nat Commun 2016; Blanco-Obregon et al., Nat Commun 2022). Many other studies have shown that Dilp8 promotes developmental stability under tissue stress and challenges.

Discussion Page 12, 3rd paragraph, 2nd sentence: "The Lgr3 neurons directly interact with ... PTTH ...and insulin-producing neurons" Please cite Colombani et al., 2015 and Vallejo et al., Science 2015. Vallejo et al., propose that circuit with insulin-producing neurons. In the 3rd sentence, only Jaszczak et al., 2016 is cited, whereas this claim/model comes from many studies, such as Halme et al., Curr Biol, 2010; Hackney et al., PLoS One 2012; Garelli et al. Science 2012; Colombani et al., Science, 2012; and the Lgr3 papers from 2015). Jaszczak et al., actually propose that Lgr3 is also required in the ring gland in addition to neurons.

Discussion page 14 last paragraph,10 line, "In Aedes aegypti ....regulates ilp8 (Ling et al., 2017)". As far as I understand mosquitoes do not have a dilp8 orthologue (see for instance Gontijo and Gontijo, Mech Dev 2018; and Jan Veenstra's work). ilp nomenclature (numbering) does not follow that of Drosophila, so ilp8 is probably a typical Insulin/IGF-like peptide and is NOT an orthologue of Dilp8, a relaxin, so this citation needs to be removed or placed into the broader context of microRNA regulation of ilps.

Thank you for the opportunity to review your interesting work, Alisson Gontijo and Rebeca Zanini

Significance

If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Drosophila has helped to characterize the mechanisms that coordinate tissue growth with developmental timing. The insulin/relaxin-like peptide Dilp8 has been identified as a key factor that communicates the abnormal growth status of larval imaginal discs to neuroendocrine neurons responsible for regulating the timing of metamorphosis. Dilp8, derived from imaginal discs, targets four Lgr3-positive neurons in the central nervous system, activating cyclic-AMP signaling in an Lgr3-dependent manner. This signaling pathway reduces the production of the molting hormone, ecdysone, delaying the onset of metamorphosis. Simultaneously, the growth rates of healthy imaginal tissues slow down, enabling the development of proportionate individuals. In this manuscript "miR-184 modulates dilp8 to control developmental timing during normal growth conditions and in response to developmental perturbations" by Dr. Varghese and colleagues, the authors identify a new post transcriptional regulator of Dilp8. The authors show that miR-184 plays a pivotal role in tissue damage responses by inducing dilp8 expression, which in turn delays pupariation to allow sufficient time for damage repair mechanisms to take effect.

Major points:

• In most of the experiments for percentage of pupariation, the 50% pupariation in control is around 110 hours AED in figures 1, 2 and 3. In figures 5 and 6 using the UAS Ricin, the controls are more around 90 hours AED. Why this discrepancy?
• What is the mechanism behind the expression of miR-184 in stress conditions? Does miR-184 also implicated in other conditions giving rise to a developmental delay (X-rays irradiation or animal bearing rasV12, scrib-/- tumors)?
• dilp8 mutant animals have also been shown to be more resistant to starvation or desiccation (https://doi.org/10.3389/fendo.2020.00461 ). Is miR-184 implicated in this answer?
• dilp8 expression has been also shown to be regulated by Xrp1 in response to ribosome stress (https://doi.org/10.1016/j.devcel.2019.03.016). This paper should be included in the manuscript Is it possible that the expression levels of miR184 are regulated by Xrp1?

Minor points:

• Does the overexpression of miR184 induce an increased fluctuating asymmetry?
• There are 2 references Colombani et al. (2012 for Dilp8 and 2015 for Lgr3). Can you double check that they are used accordingly

Significance

Altogether, the paper present compiling lines of evidence supporting the proposed model. The experiments are well designed and are convincing. The papers is interesting and relevant for a broad audience.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this study, Fernandes and colleagues addressed the question of the role of micro-RNAs in regulating the coupling between organ growth and developmental timing. Using Drosophila, they identified the conserved micro-RNA miR-184 as a regulator of the developmental transition between juvenile larval stages and metamorphosis. This transition is under the control of the steroid hormone Ecdysone, and has been shown to be modulated in case of abnormal tissue growth to adjust the duration of larval growth in response to developmental perturbations. The relaxin-like hormone Dilp8 has been identified as a key secreted factor involved in this coupling. Here, the authors show that miR-184 is involved in the regulation of Dilp8 expression both in physiological conditions and upon growth perturbation. They propose that this function is carried out in imaginal tissues, where miR-184 levels are modulated by tissue stress. While several factors have already been involved in triggering sharp dilp8 induction at the transcriptional level, this study adds another level of complexity to the regulation of Dilp8 by proposing that its expression is fine-tunned post-transcriptionally through repression by miR-184.

Major Comments

Overall, the manuscript is well organized, and the logics of the experimental plan well presented. The results are clear, and I appreciate the quality of the pupariation curves. However, I believe that two main conclusions of the paper are not fully supported by the results presented in the figures: the direct regulation of dilp8 3'UTR by miR-184, and the specificity of this regulation in imaginal discs. Here I develop in more details these two aspects. 1. The strategy of the 3'UTR sensor is not fully optimized. Indeed, in most experiments, qRT-PCR is used to assess dilp8 expression levels, although it reflects both transcriptional and post-transcriptional. Importantly, to show that post-transcriptional regulation is involved in the response to tissue damage, the levels of the 3'UTR sensor should be analyzed in discs expressing RAcs (showing at the same time that the response is cell-autonomous in the discs). The expected upregulation of the sensor should be prevented by simultaneous expression of miR-184. This approach would shed light on the relative contribution of transcriptional versus post-transcriptional regulation of dilp8 in response to growth perturbation. 2. In my opinion, the use of a 3'UTR sensor is not sufficient to conclude that the regulation by miR-184 is direct, as miR-184 could also regulate an intermediate factor that acts on dilp8 post-transcriptional regulation. To solve this issue, a common strategy is to generate a 3'UTR sensor with mutated binding sites that should abolish the regulation by miR-184. This mutated 3'UTR might also respond differently to tissue damage, which would strongly support the conclusions of the study. 3. Concerning the tissue-specific regulation of Dilp8 by miR-184, these results need to be strengthened. Indeed, this comes mostly from phenotypes observed with rn-GAL4. Although this is a classical tool for driving expression in imaginal discs, rn-GAL4 also drives strong expression in other tissues that could contribute to triggering a delay, such as the CNS and part of the gut (proventriculus). In our hands, some growth phenotypes in the wing obtained with rn-GAL4 could be fully reverted by blocking GAL4 in the CNS indicating that the phenotype was not wing-specific. Importantly, miR-184 seems to be highly expressed in the CNS according to FlyBase, reinforcing the possibility that it plays a role in this organ. Here I propose approaches to confirm that miR-184 mediated regulation of dilp8 and developmental timing indeed occur in the discs: - Another driver with less secondary expression sites could be used (pdmR11F02-GAL4), or rn-GAL4 could be combined with an elav-GAL80 to prevent expression in most neurons. - The authors could identify the source of Dilp8 upregulation in miR-184 mutants using tissue-specific qRT-PCR instead of whole larvae expression like in Fig 4A-B. - This tissue-specific upregulation could be functionally tested using a rescue experiment, in which the delay observed in miR-184 mutants could be rescued by disc-specific downregulation of Dilp8 (using pdm2-GAL4 for instance).

Optional: Because it is known that dilp8 is strongly regulated at the transcriptional level, the relative input from post-transcriptional upregulation is an important question arising from this study. Although it might be a more long-term approach, I believe that generating a Dilp8 mutant lacking its 3'UTR or, even better, with mutated miR-184 binding sites, would shed light on the role of this regulation for the response to growth perturbation and/or developmental stability (fluctuating asymmetry).

Minor Comments

• I think that a number of results could be moved to SI as they are either controls, or reproduce published data without bringing novelty. For instance, results in Fig 5A-D are similar to data published by Sanchez et al, as stated in the text. Fig6A as well.
• Fig 6D is quite mysterious, as it suggests that basal JNK activation regulates miR-184, which is different from a context of tissue damage. I think that this result could be removed. Alternatively, if the authors want to dig in that direction, more experiments should be provided, such as bskDN expression in an RAcs context and the effects on miR-184 levels and the 3'UTR sensor (since transcript levels are already published).
• The references related to Dilp8 should be checked more in detail in the intro and discussion. About Dilp8 and developmental stability: remove the ref to Colombani et al 2012, instead put Boone et al 2016 and add Blanco-Obregon et al 2022 (in addition to Garelli et al 2012 who initially identified this phenotype. About Lgr3 as the receptor for Dilp8: add Colombani et al, Current Biology 2015, and cite here Vallejo et al 2015, Garelli et al 2015. Among the important transcriptional regulators of Dilp8, Xrp1 could be mentioned (Boulan et al 2019, Destefanis et al 2022) as it plays a complementary function to JNK depending on the type of tissue stress.

Significance

General Assessment

This study provides convincing data showing that the conserved microRNA miR-184 plays a role in regulating developmental timing in Drosophila through modulating the levels of Dilp8, a key factor in the coupling between tissue growth and developmental transitions. The results are convincing, but the general conclusions of the paper need to be strengthened regarding the direct regulation of dilp8 by miR-184 and the tissue-specificity of this interaction.

Advance

Dilp8 is a key factor that modulates growth and timing in response to developmental perturbations and contributes to developmental precision in physiological conditions. As such, its regulation has been studied by different groups in the last decade, leading to the identification of several inputs for its transcriptional regulation. Here, the authors uncover a post-transcriptional regulation by miR-184, adding another level of regulation of Dilp8 that contribute to ensuring proper regulation of developmental timing, and opening the possibility that miR-184 might play similar roles in other species.

Audience

This study is of interest for researchers in the field of basic science, with a focus on developmental timing, tissue damage and biological function of microRNAs.

Reviewer expertise

Drosophila, growth control, developmental timing, Dilp8.

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Reply to the reviewers

1. General Statements

We thank the reviewer for their positive comments regarding the research article titled "The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish" by Uddin GM and colleagues. We appreciate your input, and we will address these comments as indicated below with specific responses to each point raised by reviewers.

The main changes in the updated manuscript are as follows:

We have revised the introduction to now incorporate additional background information on mitochondria, NAD, and mitochondrial dynamics and function. This addition aims to provide readers with a broader understanding of the mitochondrial context in relation to our study.

Furthermore, we recognize that previous studies have explored mitochondrial function in the context of the ketogenic diet. While our specific investigation centered on mitochondrial morphology, we acknowledge the importance of comprehensively investigating mitochondrial function. To this end, we have added new data showing how BHB impacts mitochondrial oxidative phosphorylation in HeLa cells (Sup Fig 2), and how both BHB and NMN impact oxygen consumption/glycolysis in zebrafish (Fig 7).

We have also added new behaviour analysis of the zebrafish (Fig 6), and have re-framed the discussion around neurodevelopment generally, rather than ASD specifically.

Finally, we have now included a section in our manuscript that discusses the limitations of our study. These limitations can be further investigated to explore and characterize the full mechanistic potential behind the effects of the ketogenic diet and/or NMN on mitochondrial dynamics.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

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

Uddin GM and colleagues presented a research article entitled 'The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish'. Roles of ketogenic diet (KD) and NAD+ precursors in health promotion and longevity, as well as on the alleviation of a broad range of diseases are evident. However, their roles in autism are not well done, which is the novelty of the current study. Addressing below questions will improve the quality of the paper.

Major concerns 1. In the introduction section, a broad overview of the roles of ketogenic diet (KD) in neurodegenerative disease (and ageing, if possible) should be provided. E.g., the authors should summarize exciting progress on the use of KD to treat Alzheimer's disease in animal models (PMID: 23276384). *

Response: Thank you for your valuable suggestion. While it is true that the KD appears to be beneficial in neurodegenerative (and other disease) models, our focus in this paper is looking at neurodevelopment, rather than all potential benefits of the KD. Nonetheless, we have addressed this comment by incorporating a brief overview of the roles of the KD in neurodegenerative diseases, including Alzheimer's disease (AD), in the introduction section of the manuscript. Specifically, we have summarized the exciting progress made in utilizing KD to treat AD in animal models, as highlighted in the suggested study. This addition helps to provide a better overview of the potential therapeutic effects of KD in neurodegenerative diseases and strengthens the introduction section of the manuscript.

• Roles of high fat diet to treat diseases could be extended to rare premature ageing diseases. In such scenario, high fat and NAD+ boosting shared some joint mechanisms (PMID: 25440059 ). *

Response: This information and the reference are now added to the discussion.

*In the introduction, a more detailed introduction of NAD+ and its roles in mitochondrial homeostasis (especially mitophagy and the mitochondrial fusion-fission balance) should be included (PMID: 24813611; PMID: 30742114; PMID: 31577933). *

Response: Although our paper focused primarily on mitochondrial fission and fusion, we have incorporated a new paragraph in the introduction to provide a more detailed introduction detailing NAD+ and its roles in mitochondrial homeostasis, specifically highlighting mitophagy. We have included the suggested references.

• In regarding to the statement of KD increases NAD+, was it due to increased generation (to check protein levels and activities of different NAD+ synthetic enzymes, such as iNAMPT, NMNAT1-3, and NRK) and/or reduced consumption (in addition to reduced glycolysis, does KD inhibit the activities of CD38 and PARPs? In this paper, Sirtuins' activities is (are increased)). Detailed exploration of the activities of these proteins will unveil a clear molecular mechanisms on how KD affects/regulates NAD+. *

Response: Thank you for the comment. We agree that exploring the detailed mechanism of how the ketogenic diet (KD) affects NAD+ is an interesting question that will have important implications once answered. However, fully elucidating the mechanism of action would require a more comprehensive investigation, which is beyond the scope of this current project. We have now added this as a future direction in the manuscript.

*Fig. 1: in the NAD+ field, the normal used NR/NMN concentrations are normally high like to use 500 µM to 2-5 mM (as the NAD+ levels in cells are high). In addition to use 50 µM, the authors are strongly to have a dose-dependent study (50 µM, 500µM, 1, 2, 5 mM), and see changes of mitochondrial funciton and parameters. In this condition, NAD+ levels should be also checked. *

Response: We have added new supplemental data showing the initial dose response of the effects of BHB and NMN on mitochondrial morphology, which led us to choosing the relevant doses for the remainder of the paper. Our objective was not to investigate the broad impacts of different NMN concentrations on mitochondrial function and parameters, or NAD+ levels. As such, we have only focused on doses where we see effects on mitochondrial morphology.

*Fig. 2: a comprehensive characterization of mitochondrial fusion-fission should be performed. In addition to the protein evaluated, changes on other key fusion-fission proteins, like Bax, Bak, Mfn-1, Mfn-2, etc should be performed (PMID: 17035996; PMID: 24813611). *

Response: We agree that looking at other key proteins involved in mediating mitochondrial fission and fusion could provide additional insight. Indeed, given the changes in global acetylation that we see, it is expected that some other proteins may also be regulated in this way. However, there are at least a dozen proteins involved in mediating mitochondrial fusion and fission, not to mention many more proteins that regulate these proteins. Unfortunately, it is not feasible to analyze all the proteins involved in mitochondrial fusion-fission. Moreover, looking only at protein levels, doesn't necessarily inform about the activity of any protein. Instead, we concentrated in this paper on investigating known links between protein acetylation and mitochondrial dynamics, particularly focusing on the proteins that have known links to acetylation (i.e., DRP1, OPA1, MFNs). We have added a note in the discussion acknowledging that other means of regulation could also be occurring in parallel.

*Figs. 1-5 were focused on mitochondrial morphology, whether KD and NMN changed mitochondrial funciton should be explored, such as to use seahorse to check ECR and OCR. *

Response: Although our question was focused on morphology, we agree that mitochondrial function is important. We have added new data showing that BHB increases basal oxygen consumption in HeLa cells (Sup Fig 2), as well as new data showing that BHB and NMN influence oxygen consumption and glycolysis in our zebrafish model (Fig 7)

• Fig. 6: NR/NMN used in animal studies (via gavage or in drinking water in mice, and on plate for worms and flies) are normally high (e.g., in drinking water for mice could be 4-12 mM; for worms and flies are normally 1-5 mM); for zebrafish, while they are swimming in water, this reviewer concerned whether it was true that 50 µM of NMN was sufficient to show the benefit presented.*

Response: Our data show that these doses are indeed sufficient. We did look at some higher doses for NMN, but these were toxic, leading to poor survival and were not studied further.

*Minor concerns 1. Line 26: For 'a growing list of neurological disorders, including autism spectrum disorder (ASD)', please add AD in. *

Response: Line 26 is part of the abstract, which we feel should be focused more on the main message of the paper, which does not involve AD. As addressed above, we have added AD as an example in the introduction.

*Line 57: For 'with side effects such as gastrointestinal disturbances, nausea/vomiting, diarrhea, constipation, and hypertriglyceridemia being reported', rate of frequency shall be provided if any. *

Response: We have modified the statement to indicate the relative percent of patients suffering the various side effects.

*Reviewer #1 (Significance (Required)):

The novelty of the current study was to investigate effects of KD and NAD+ on autism. This investigation was not performed before and thus is the novelty.

Weakness, effects of KD and NAD+/NMN on mitochondrial function were not well-investigated and should be done. Introduction was not well done, many key information in the fields were not provided which may mislead the readers an over-evaluation of the novelty of the current study.*

Response: As outlined above, we have edited the introduction to include additional information requested by the reviewer. Moreover, our focus in this manuscript was to look at the mechanisms underlying changes in mitochondrial morphology, not mitochondrial function per se, though this is clearly important and related. Nonetheless, as discussed above, we have also added new data showing how BHB impacts mitochondrial function.

*My expertise lies in NAD+, mitochondria, and brain health.

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

The study examined the effect of beta-hydroxybutyrate and nicotinamide nucleotide on mitochondrial morphology and the molecular pathways which mitigate this effect as well as the effect of these treatments on behavior in zebrafish. The study is well done and well written. The only thing I think that could be improved are the bar in the graph some the significant comparisons. It is sometimes difficult to see which groups are being compared.*

Response: We're happy to adjust how the data is displayed in the relevant bar graphs, but it is not clear exactly what changes the reviewer would like. To some degree this will depend on the specific guideline of the final journal where we hope the manuscript will be published. As such, we have not made changes at this point.

***Referees cross-commenting**

The other reviewers do have some fair comments. Multiple doses would be helpful and showing bioenergetic data would complement the morphological measurements. Additionally, behavioral assays showing changes in social behavior in the Zebrafish would provide a stronger link to ASD. *

Response: As discussed above, we have added new information on doses and mitochondrial bioenergetics. With respect to behaviour, we have added thigmotaxis data and reworked the discussion around behaviour and neurodevelopment so that it is less specific to ASD.

*Reviewer #2 (Significance (Required)):

As beta-hydroxybutyrate is an important substrate for the ketogenic diet, this study helps explain the potential mechanisms in which the ketogenic diet may enhance mitochondrial function.

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

In this paper, Uddin and colleagues have investigated components of the ketogenic diet to understand changes in both mitochondrial morphology and protein expression, and zebrafish locomotor behaviour. They investigate whether beta-hydroxybutyrate (BHB) or nicotinamide nucleotide (NMN) application can later human mitochondria in HeLA cell lines, and also recue a locomotion defect in shank3b+/- zebrafish larvae that have previously been proposed as a model for autism. This study is strengthened by showing data from two species; however the link between the HeLA cell line data and larval zebrafish is not strong. The study would be improved by assessing zebrafish mitochondrial changes after drug application, and testing more than one concentration of BH and NMN in the behavioural assay. This is an interesting study, and it is nicely written and presented. I have made some comments to strengthen the study below.

Major comments My expertise is in modelling some aspects of autism in zebrafish. To this end I have focussed on the zebrafish part of this manuscript more fully. I have several comments related to the zebrafish experiments. 1. The changes in mitochondrial morphology, peroxisome number and mitochondrial protein levels were measured in HeLA cells and not comparable data is shown for zebrafish. The same experiments should be repeated using larval zebrafish or a zebrafish cell line. *

Response: We chose to use HeLa cells for the mechanistic studies due to practical reasons. Cell lines offer a controlled and well-established system for investigating cellular processes and molecular mechanisms. Measuring these parameters in tissues is significantly more challenging and requires different reagents (e.g., antibodies) and methodology (electron microscopy) that are not feasible in the current study.

On the other hand, zebrafish larvae were employed for the behavior studies, which cannot be conducted using cell lines. By utilizing zebrafish, we were able to examine the effects of beta-hydroxybutyrate (BHB) and nicotinamide nucleotide (NMN) on locomotor behavior, providing valuable insights into potential therapeutic implications for autism.

While we acknowledge the limitations of not directly measuring mitochondrial morphology, peroxisome number, and mitochondrial protein levels in zebrafish, we believe that our study provides significant contributions to understanding the effects of BHB and NMN in zebrafish behavior. Future studies could certainly consider incorporating zebrafish-specific experiments to complement the findings in HeLa cells.

• How did you choose the concentration of BHB and NMN to use in behavioural experiments? And the timing of application - I don't really understand why you waited 3 days after drug application to measure locomotion. *

Response: These doses chosen initially as they were similar the doses that induced mitochondrial elongation in HeLa cells and were tolerated by the fish larvae. As we saw promising effects at these initial doses, we decided to explore them in more detail. While we agree that it would be worth comparing the effects of additional doses, as well as looking at their effects at other timepoints, such work would be a major endeavour and is beyond the scope of our initial investigations, which we feel are worth reporting in their current state.

With respect to the treatment paradigm, fish larvae were treated 10-48 hours post fertilization, as this is a critical neurogenic developmental timepoint that is often used for exposure studies. Fish do not fully hatch until 3-4 days post fertilization, and display only minimal movement before 5 days, which is why we waited until 5 days to look at movement.

• Do the shank3b+/- larvae show any morphological deficits? Their decrease in locomotion is striking. Is the morphology also rescued by drug application? Can you tie this to the mitochondrial changes that you observed in HeLA cells?*

Response: We do not observe any gross changes in fish morphology that might explain a decrease in locomotion. Unfortunately, it is not feasible to look at mitochondrial morphology in the fish at this time. However, based on previous published work showing that the ketogenic diet promotes mitochondrial elongation in mouse brains (PMID:32380723), we would expect mitochondrial morphology also to be changed in the fish. Nonetheless, as we have not examined this directly in fish, we are not making this specific claim in this manuscript.

• In figure 6A you use time spent swimming as a readout of distance. This doesn't really make sense, because without also showing speed of swimming it is not possible to know whether time and distance correlate in the same way across genotypes. This figure could be improved by showing more detail - speed of swimming, time spent immobile etc. This can easily be extracted from the films that you have already made using the ViewPoint software. *

Response: As requested, we have reanalyzed the zebrafish movement data for a more refined analysis. In the revised version (Fig 6), we include analysis of both speed and distance travelled within a defined time. Importantly, these findings still support differences between WT and shank3b+/- fish that are restored by BHB and NMN to varying degrees.

• Showing a change in locomotion is not enough to claim that a model is autism-like. At a minimum I think that you need to show changes in social behaviour - likely using older fish (more than three weeks) that interact with each other. Changes in locomotion can be caused by so many factors, many of which are not indicative of autism. It is important that as a field we do not simply claim that locomotion can be used as a proxy for more complex disease phenotypes. This recent review may help you with this point:* https://www.frontiersin.org/articles/10.3389/fnmol.2020.575575/full.

Response: The reviewer makes an important point that the movement behaviour phenotypes that we see do not necessarily represent classic ASD phenotypes (i.e., repetitive behaviour, reduced sociability, and reduced communication). To begin to address this issue, we analyzed thigmotaxis, which can be a measure of anxiety. Notably, we also see differences that are reversed by BHB and NMN. However, we cannot model all ASD behaviours in a fish model, and we are not set up to look at social behaviour, especially in the young fish that we were studying. As such, even though Shank3 is a recognized ASD gene, and the shank3b+/- model we are studying is a validated ASD model (PMID: 29619162), we have re-phrased the manuscript in the context of neurodevelopment generally, rather than with respect to ASD specifically. As such, we ascribe the movement and thigmotaxis phenotypes as neurodevelopmental phenotypes that are improved by BHB and NMN.

*For the statistics, as far as I can tell, all of the data should be analysed by ANOVA or the non-parametric equivalent followed by a post-hoc test. Please check this and add information about normality in. *

Response: As requested, we have clarified our statistical methodology throughout the manuscript.

For the mechanistic data, we used t-tests for direct comparisons between two groups (e.g., vehicle vs. treatment). While multiple conditions such as vehicles, NMN, BHB, or etomoxir were tested, statistical comparisons were only conducted comparisons between the vehicle and each treatment group individually. As we are not also making comparisons between treatments this is not a multiple comparison, and ANOVA is not applicable in this context. We have clarified this rationale in the manuscript to avoid any confusion.

For the zebrafish study, where multiple factors were involved (e.g., treatments across different time points or conditions), we performed a two-way ANOVA followed by Tukey's post-hoc test to identify specific group differences. This approach was appropriate for analyzing these datasets and ensures robust conclusion.

With respect to normality testing, all datasets were assessed for normality using the Shapiro-Wilk test, and no violations of normality were observed. The updated text now includes these details.

*Minor comments

1. Make sure that you refer to the fish line as shank3b+/- throughout - see abstract.*

This has bee corrected.

• Please add a space between all numbers and units (e.g. 5 Mm). *

This has bee corrected.

• There is a spelling error on line 340 page 16: finings instead of findings. *

This has bee corrected.

• In figure 1, if each dot represents a different sample, then there appear to be many fewer samples analysed in 1D compared to 1B. Can you comment upon this please*

__Response: __A total of 80-150 cells were counted per condition, and the analyses were performed on 3 independent replicates with 2 independent technical replicates for each treatment condition. The quantification of mean mitochondrial branch length in Figure 1B was measured using Image-J and the MiNA plugin. The measurements were taken from three independent replicates using a standard region of interest (ROI) and randomly selected areas from each image.

In Figure 1D, NAD+ levels were measured 24 hours after treatment of vehicle, βHB, NMN, or Eto+βHB in HeLa cells (n=3-6/group). Each sample lysate represents an independent experimental dish from which coverslips were collected for image analysis.

The difference in sample numbers between Figure 1B and 1D arises because image analysis involves individual cells fixed and stained on coverslips, whereas the NAD assay requires the whole lysate from the entire cell culture dish. Therefore, the higher cell count in Figure 1B represents the number of cells analyzed on coverslips, while Figure 1D represents NAD levels from the lysate normalized to the protein concentration.

*Reviewer #3 (Significance (Required)):

I think that this will be interesting to autism researchers and it could lead to more investigation of the ketogenic diet. Some more work is needed, likely in other model organisms, before this research can be translated to human patients. *

__Response: __We agree that the findings of our study could be of interest to autism researchers and have implications for further investigation of the ketogenic diet (KD). It is important to note that further work, including studies in other model organisms, would be beneficial before translating this research to human patients.

Our study aimed to provide mechanistic insights into the effects of the KD on mitochondrial morphology and behavior. We recognize that the translation of research findings to human patients requires rigorous investigation, including preclinical and clinical studies. Our study contributes to the understanding of the underlying mechanisms involved in the KD's effects, laying the groundwork for future research and potential therapeutic avenues.

We appreciate your perspective and emphasize that our intention is to provide valuable insights into the mechanisms underlying the KD's effects rather than suggesting immediate translation to human patients. Further investigation and validation in diverse models and clinical settings will be necessary before considering clinical applications.

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Referee #3

Evidence, reproducibility and clarity

In this paper, Uddin and colleagues have investigated components of the ketogenic diet to understand changes in both mitochondrial morphology and protein expression, and zebrafish locomotor behaviour. They investigate whether beta-hydroxybutyrate (BHB) or nicotinamide nucleotide (NMN) application can later human mitochondria in HeLA cell lines, and also recue a locomotion defect in shank3b+/- zebrafish larvae that have previously been proposed as a model for autism. This study is strengthened by showing data from two species; however the link between the HeLA cell line data and larval zebrafish is not strong. The study would be improved by assessing zebrafish mitochondrial changes after drug application, and testing more than one concentration of BH and NMN in the behavioural assay.

This is an interesting study, and it is nicely written and presented. I have made some comments to strengthen the study below.

Major comments

My expertise is in modelling some aspects of autism in zebrafish. To this end I have focussed on the zebrafish part of this manuscript more fully. I have several comments related to the zebrafish experiments.

1. The changes in mitochondrial morphology, peroxisome number and mitochondrial protein levels were measured in HeLA cells and not comparable data is shown for zebrafish. The same experiments should be repeated using larval zebrafish or a zebrafish cell line.
2. How did you choose the concentration of BHB and NMN to use in behavioural experiments? And the timing of application - I don't really understand why you waited 3 days after drug application to measure locomotion.
3. Do the shank3b+/- larvae show any morphological deficits? Their decrease in locomotion is striking. Is the morphology also rescued by drug application? Can you tie this to the mitochondrial changes that you observed in HeLA cells?
4. In figure 6A you use time spent swimming as a readout of distance. This doesn't really make sense, because without also showing speed of swimming it is not possible to know whether time and distance correlate in the same way across genotypes. This figure could be improved by showing more detail - speed of swimming, time spent immobile etc. This can easily be extracted from the films that you have already made using the ViewPoint software.
5. Showing a change in locomotion is not enough to claim that a model is autism-like. At a minimum I think that you need to show changes in social behaviour - likely using older fish (more than three weeks) that interact with each other. Changes in locomotion can be caused by so many factors, many of which are not indicative of autism. It is important that as a field we do not simply claim that locomotion can be used as a proxy for more complex disease phenotypes. This recent review may help you with this point: https://www.frontiersin.org/articles/10.3389/fnmol.2020.575575/full.
6. For the statistics, as far as I can tell, all of the data should be analysed by ANOVA or the non-parametric equivalent followed by a post-hoc test. Please check this and add information about normality in.

Minor comments

1. Make sure that you refer to the fish line as shank3b+/- throughout - see abstract.
2. Please add a space between all numbers and units (e.g. 5 Mm).
3. There is a spelling error on line 340 page 16: finings instead of findings.
4. In figure 1, if each dot represents a different sample, then there appear to be many fewer samples analysed in 1D compared to 1B. Can you comment upon this please?

Significance

I think that this will be interesting to autism researchers and it could lead to more investigation of the ketogenic diet. Some more work is needed, likely in other model organisms, before this research can be translated to human patients.

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Referee #2

Evidence, reproducibility and clarity

The study examined the effect of beta-hydroxybutyrate and nicotinamide nucleotide on mitochondrial morphology and the molecular pathways which mitigate this effect as well as the effect of these treatments on behavior in zebrafish. The study is well done and well written. The only thing I think that could be improved are the bar in the graph some the significant comparisons. It is sometimes difficult to see which groups are being compared.

Referees cross-commenting

The other reviewers do have some fair comments. Multiple doses would be helpful and showing bioenergetic data would complement the morphological measurements. Additionally, behavioral assays showing changes in social behavior in the Zebrafish would provide a stronger link to ASD.

Significance

As beta-hydroxybutyrate is an important substrate for the ketogenic diet, this study helps explain the potential mechanisms in which the ketogenic diet may enhance mitochondrial function.

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Referee #1

Evidence, reproducibility and clarity

Uddin GM and colleagues presented a research article entitled 'The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish'. Roles of ketogenic diet (KD) and NAD+ precursors in health promotion and longevity, as well as on the alleviation of a broad range of diseases are evident. However, their roles in autism are not well done, which is the novelty of the current study. Addressing below questions will improve the quality of the paper.

Major concerns

1. In the introduction section, a broad overview of the roles of ketogenic diet (KD) in neurodegenerative disease (and ageing, if possible) should be provided. E.g., the authors should summarize exciting progress on the use of KD to treat Alzheimer's disease in animal models (PMID: 23276384).
2. Roles of high fat diet to treat diseases could be extended to rare premature ageing diseases. In such scenario, high fat and NAD+ boosting shared some joint mechanisms (PMID: 25440059 ).
3. In the introduction, a more detailed introduction of NAD+ and its roles in mitochondrial homeostasis (especially mitophagy and the mitochondrial fusion-fission balance) should be included (PMID: 24813611; PMID: 30742114; PMID: 31577933).
4. In regarding to the statement of KD increases NAD+, was it due to increased generation (to check protein levels and activities of different NAD+ synthetic enzymes, such as iNAMPT, NMNAT1-3, and NRK) and/or reduced consumption (in addition to reduced glycolysis, does KD inhibit the activities of CD38 and PARPs? In this paper, Sirtuins' activities is (are increased)). Detailed exploration of the activities of these proteins will unveil a clear molecular mechanisms on how KD affects/regulates NAD+.
5. Fig. 1: in the NAD+ field, the normal used NR/NMN concentrations are normally high like to use 500 µM to 2-5 mM (as the NAD+ levels in cells are high). In addition to use 50 µM, the authors are strongly to have a dose-dependent study (50 µM, 500µM, 1, 2, 5 mM), and see changes of mitochondrial funciton and parameters. In this condition, NAD+ levels should be also checked.
6. Fig. 2: a comprehensive characterization of mitochondrial fusion-fission should be performed. In addition to the protein evaluated, changes on other key fusion-fission proteins, like Bax, Bak, Mfn-1, Mfn-2, etc should be performed (PMID: 17035996; PMID: 24813611).
7. Figs. 1-5 were focused on mitochondrial morphology, whether KD and NMN changed mitochondrial funciton should be explored, such as to use seahorse to check ECR and OCR.
8. Fig. 6: NR/NMN used in animal studies (via gavage or in drinking water in mice, and on plate for worms and flies) are normally high (e.g., in drinking water for mice could be 4-12 mM; for worms and flies are normally 1-5 mM); for zebra fish, while they are swimming in water, this reviewer concerned whether it was true that 50 µM of NMN was sufficient to show the benefit presented.

Minor concerns

1. Line 26: For 'a growing list of neurological disorders, including autism spectrum disorder (ASD)', please add AD in.
2. Line 57: For 'with side effects such as gastrointestinal disturbances, nausea/vomiting, diarrhea, constipation, and hypertriglyceridemia being reported', rate of frequency shall be provided if any.

Significance

The novelty of the current study was to investigate effects of KD and NAD+ on autism. This investigation was not performed before and thus is the novelty.

Weakness, effects of KD and NAD+/NMN on mitochondrial function were not well-investigated and should be done. Introduction was not well done, many key information in the fields were not provided which may mislead the readers an over-evaluation of the novelty of the current study.

My expertise lies in NAD+, mitochondria, and brain health.

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Reply to the reviewers

We thank the reviewers for their thoughtful comments and overall very supportive feedback.

Reviewer #1 writes: "The study is very thorough and the experiments contain the appropriate controls. (...) The findings of the study can have relevance for human conditions involving disrupted mitochondrial dynamics, caused for example by mutations in mitofusins." Reviewer #2 writes: "The dataset is rich and the time-resolved approach strong." Reviewer #3 writes: "I admire the philosophy of the research, acknowledging an attempt to control for the many possible confounding influences. (...) This is a powerful and thoughtful study that provides a collection of new mechanistic insights into the link between physical and genetic properties of mitochondria in yeast."

We address all points below. We have not yet updated our text and figures since we expect substantial additions from new experiments. But we have included Figure R1 with some additional analyses of existing data at the bottom of the manuscript.

Reviewer1

1.1 Statistical comparisons are missing throughout the manuscript (with the exception of Fig. 2c). Appropriate statistical tests, along with p-values, should be used and reported where different gorups are compared, for example (but not limited to) Fig. 3d and most panels of Fig. 4.

We initially decided not to add too many extra labels to the already very busy plots, given that the magnitude of change mostly speaks for itself. However, we will try to find meaningful statistical tests together with a sensible graphical representation for all of the figures. For one example see Figure R1A.

1.2. I do not agree with the use of Atp6 protein as a direct read-out of mtDNA content. While Atp6 protein levels will decrease with decreasing mtDNA content, the inverse is not necessarily true: decreased Atp6 protein levels do not necessarily indicate decreased mtDNA levels, because they could alternatively or additionally be caused by decreased transcription and/or translation. Therefore, please do not equate Atp6 protein levels to mtDNA levels, and instead rephrase the text referencing the Atp6 experiments in the Results and Discussion sections to measure "mtDNA expression" or "mt-encoded protein" or similar. For example, on p. 14 line 431 should read "mtDNA expression" rather than "decreased synthesis of mtDNA", and line 440 on the same page "mean mtDNA levels" should be "mtDNA expression" or similar.

All three reviewers agree that using Atp6-NG as a direct proxy for mtDNA requires more validation, or at least rephrasing of the text. We agree that this is the most important point to address. We had previously tried using the mtDNA LacO array (Osman et al. 2015) to directly assess the amount of nucleoids per cell. However, the altered mitochondrial morphology of the Fzo1 depleted cells combined with the LacI-GFP which is still in mitochondria even when mtDNA is gone, increases the noise level to a point that we cannot interpret the signal. However, as this manuscript was in the submission process, the Schmoller lab (co-authors #2 and #7) adapted the HI-NESS system to label mtDNA in live yeast cells(Deng et al. 2025). This system promises much better signal to noise and we expect we can address all concerns regarding the actual count of nucleoids per cell. Should this unexpectedly fail for technical reasons, we will try to calibrate the Atp6-levels with DAPI staining at defined time points and will rephrase the text as the reviewer suggests.

1.3. In Fig. 3, the authors use the fluorescence intensity of a mitochondrially-targeted mCardinal as a read-out of mitochondrial mass. Please provide evidence that this is not affected by MMP, either with relevant references or by control experiments (e.g. comparing it to N-acridine orange or other MMP-independent dyes or methods).

Whether or not the import of any mitochondrial protein is dependent on the MMP depends largely on the signal sequence. The preSu9-signaling sequence was previously characterized as largely independent of the MMP compared to other presequences (Martin, Mahlke, and Pfanner 1991), which is why Vowinckel (Vowinckel et al. 2015) and others (Di Bartolomeo et al. 2020; Perić et al. 2016; Ebert et al. 2025) have previously used this as a neutral reference to the strongly MMP-dependent pre-Cox4 signal to estimate MMP. As one control in our own data, we consider that the population-averaged mitochondrial fluorescent signal Figure S3C stays constant in the first few hours, in agreement with the total averaged mitochondrial proteome (Fig R1E). As additional controls, we plan to compare the signal to an MMP independent dye as the reviewer suggests.

1.4. In Fig. 2e-f, the authors use a promoter reporter with Neongreen to answer whether the reduced levels of the nuclear-encoded mitochondrial proteins Mrps5 and Qcr7 are due to decreased expression or to protein degradation, and find no evidence of degradation of the Neongreen reporter protein. However, subcellular localization might affect the availability of the protein to proteases. Although not absolutely required, it would be relevant to know if the Neongreen fusion protein is found in the same subcellular compartment as Mrps5 and Qcr7 at 0h and 9h after Fzo1 depletion.

Here, it seems we need to explain the set-up and interpretation of the data better. The key point we are trying to make with the promoter-Neongreen construct is that the regulation is not mainly at the level of transcription. We are showing that the reduction in the levels of the actual protein (orange bars) is not (mainly) explained by a reduction in expression, since the promoter is similarly active at 0 and at 9 hours (grey bars). If expression from the promoter were strongly reduced, the Neongreen would be diluted with growth and would also decrease, but this is not the case. The fluorophore itself is just floating around in the cytosol and is not subject to the same post-translational regulation as Mrps5 and Qcr7, so there is no reason to expect degradation.

1.5. Fzo1 depletion leads to a very rapid drop in MMP during the first hour of depletion. In the Discussion, can the authors speculate on the possible mechanism of this rapid MMP drop that occurs well before mtDNA or mt-encoded proteins are decreased in level?

This is indeed an interesting point. We think there are likely three reasons causing this initial drop: Firstly, due to the fragmentation the mixing of mitochondrial content is disturbed and smaller fragments may have suboptimal stoichiometry of components (see also (Khan et al. 2024) who look at this in detail including the Fzo1 deletion); secondly, already fairly early, some mitochondrial fragments may not contain any mtDNA and therefore will be unable to synthesize ETC proteins; thirdly, altered morphological features like changes in the surface-to-volume ratios may play a role. Sadly, mechanistically following up on this is not possible with the tools in our hands and therefore outside of the scope of this manuscript. But we are happy to include these speculations in our discussion.

1.6. In Fig. 2a, the mtDNA copy number of Fzo1-depleted cells is ca 1.3-fold of the control cells at the 0h timepoint. Why might this be? Is it an impact of one of the inducers? If so, we might be looking at the combination of two different processes when measuring copy number: one that is an induction caused by the inducer(s), and the other a consequence of Fzo1 depletion itself.

We believe that this 30% increase is within the noise of the experiment rather than an effect of the induction. Since we normalize to t=0 uninduced, the first black data point does not have error bars, emphasizing this difference. None of the protein data suggests that there is an increase in mtDNA encoded proteins (see e.g. 2B, or Atp6 fluorescence data). In the planned HI-NESS experiment, we will see in our single cell data whether there is an actual increase in mtDNA upon TIR induction. Additionally, we will run a qPCR to carefully determine mtDNA levels of untreated wild-type cells, tetracycline treated wild-type cells and tetracycline induced TIR expressing cells to exclude effects of tetracycline as well as the expression of TIR on mtDNA.

Minor comments:

1.7. p. 3, line 71: "ten thousands of dividing cells.." should be "tens of thousands of dividing cells".

Thank you, will correct.

1.8.-p.4, line 116: please be even more clear with what the "depleted" cells and controls are treated with: are depleted cells treated with both inducers, and controls with neither?

We will make this more clear. Depleted cells are treated with both inducers, the control cells are not. However, in Figure 1A and in S1 we do controls to show that inducing TIR per se or adding aTC per se does not change growth rate or mitochondrial morphology. We will make this more clear.

1.9. -p.5, lines 147-148: the authors write "the rate with which the abundance of Cox2 and Var1 proteins decreases was similar to the rate of mtDNA loss" though the actual rate is not shown. Please calculate and show rates for these processes side by side to make comparison possible, or alternatively rephrase the statement.

Indeed this was not phrased well. We will call it dynamics rather than rates.

1.10. -Fig. 2d: changing the y-axis numbering to match those in panels a and b would facilitate comparisons.

Makes sense, we will change this.

1.11. Fig. 2e: it is recommended to label the western blot panels to indicate what protein is being imaged in each (Neongree,, Mrps5, Qcr7).

We will adapt the labelling to make it more clear.

1.12. -p.9, line 262: I suggest referencing Fig. 4e at the end of the first sentence for clarity.

We will modify the sentence as suggested.

1.13. -In the sections related to Fig. 3a and Fig. 5a as well as the connected supplemental data, the authors discuss both the median and the mean of mitochondrial mass and Atp6 protein, respectively. For purposes of clarity, I suggest decreasing the focus on the mean (that is provided only in the supplemental data) and focusing the text mainly on the median. The two show differing trends and it is very good that both are shown, but the clarity of the text can be improved by focusing more on the median where possible.

We will check the phrasing and simplify.

1.14. -p. 14, line 435: the statement that mt mass is maintained over the first 9h of depletion is only true for the mean mt mass, not for the median. Please make this clear or rephrase.

We will check phrasing, make it more clear and also point out the extended proteomics data (see Fig R1), which corresponds to the mean of the populations

1.15.-p.14, line 452: "mitofusions" should be "mitofusins".

Thanks for catching this.

Reviewer 2:

2.1. While inducible TIR is used to reduce background, the manuscript should rigorously exclude auxin/TIR off-targets (growth, mitochondrial phenotypes, gene expression). Please include full matched controls: (plus minus)auxin, (plus minus)TIR, epitope tag alone, and a degron control on an unrelated mitochondrial membrane protein.

We agree that rigorous controls are crucial for the interpretation of the results. However, we think we have already included most of the controls the reviewer is asking for, but we might have not pointed this out clearly enough. For example, in Fig 1A, we could make it more clear by adding more labels in which samples we added aTC, which is only described in the figure legend.

Here is a list of all the controls:

• Each depletion experiment is always matched with an experiment of the same strain without induction. So the genetic background as well as effects such as light exposure, time spent in the microfluidics systems, etc are controlled for.
• Figure S1D shows that the growth rate is wildtype like in a strain containing either the AID tag or the TIR protein AND upon addition of both chemicals. It also shows that the final genetic background (AID-tag and TIR) also grows like wildtype if the inducers are not added. This conclusively shows that neither the tags/constructs nor the chemicals per se affect growth rate
• In Figure S1C we show the mitochondrial morphology of the same controls. We will make sure to label them more consistently to match panel D, and include an actual wildtype and a FLAG-AID-Fzo1 strain without TIR treated with both aTC and 5-Ph-IAA as direct comparison
• In figure 1A we compare the Fzo1 protein levels of a strain with and without TIR. We show that in absence of TIR, adding either aTC or Auxin does not change Fzo1 levels and that the levels are comparable in the strain that is able to deplete Fzo1 directly before addition of 5-Ph-IAA (after 2 h of induction of TIR through addition of tetracycline)
• Additionally, in Figure S2C we show that two hours after adding aTC, the entire proteome does not change significantly apart from a strong induction of TIR. We can also make this more clear in the figure legend.
• Additionally, we will run a qPCR to carefully determine mtDNA levels of untreated wild-type cells, tetracycline treated wild-type cells and tetracycline induced TIR expressing cells to exclude effects of tetracycline as well as the expression of TIR on mtDNA. (also in response to 1.6.) In summary, we think we have controlled sufficiently for all confounding parameters and most importantly showed that addition of either aTC or Auxin as well as the FLAG-AID tag per se does not disturb mitochondria or cell growth. We do not see what a degron control on an unrelated protein will tell us. Depending on the nature of the protein, it may or may not have a phenotype that may or may not be related to morphology changes etc.

2.2. The Mitoloc preSu9 vs Cox4 import ratio is only a proxy of mitochondrial membrane potential (ΔΨm) and itself depends on mitochondrial mass, protein expression, matrix ATP, and import saturation. The authors need to calibrate ΔΨm with orthogonal dyes (TMRE/TMRM) and pharmacologic titrations (FCCP/antimycin/oligomycin) to generate a response curve; show that Mitoloc tracks dye-based ΔΨm across the relevant range and corrects for mass/photobleaching. Report single-cell ΔΨm vs mass residuals.

We completely agree that the MitoLoc system is only a rough proxy for the actual membrane potential. That is why we make no quantitative claims on the absolute value or absolute difference between groups of cells. We also make very clear in Fig 3B what we are actually measuring and can emphasize again in the text that this is only a proxy. We agree that it is a good idea to compare MitoLoc values to TMRE staining as the reviewer suggests, we will do these experiments in depleted and control cells at different timepoints. Please note though that also dye staining has its caveats, especially in dynamic live cell experiments. TMRM for example is not compatible with the acidic pH 5 medium that is typically used for yeast and subjecting cells to washing steps and higher pH may change both morphology of mitochondria and the MMP, especially in cells that are already “stressed”. We prefer not to complete elaborate pharmacological titration experiments because firstly, this was extensively done in the original MitoLoc paper by the Ralser lab ((Vowinckel et al. 2015), cited 120 times); secondly, the value of the MMP is not the most critical claim of the manuscript. See also 3.12. Please note that in Figure S4D we had already plotted MMP vs mitochondrial concentration.