Author response:

We thank both reviewers for their thorough and insightful feedback, which will contribute to improving our manuscript. In summary, the key concerns raised include the potential induction of GLV volatiles due to plant handling, limitations in the design of the "wind tunnel" bioassay, and the need for a deeper analysis of specific volatile compounds that contribute to the success of push-pull systems. We are happy to revise the entire manuscript according to all comments of the reviewers. This includes clarification of our methodology and providing a more reflective discussion on how physical stress might have influenced volatile emissions. Additionally, we will conduct new experiments with a modified bioassay setup to address concerns about directional cues and airflow control, minimizing cross-contamination. While the identification of individual compounds was beyond the scope of this study, we acknowledge its importance and propose it as a direction for future research.

Reviewer #1 (Public review):

Summary:

The manuscript of Odermatt et al. investigates the volatiles released by two species of Desmodium plants and the response of herbivores to maize plants alone or in combination with these species. The results show that Desmodium releases volatiles in both the laboratory and the field. Maize grown in the laboratory also released volatiles, in a similar range. While female moths preferred to oviposit on maize, the authors found no evidence that Desmodium volatiles played a role in lowering attraction to or oviposition on maize.

Strengths:

The manuscript is a response to recently published papers that presented conflicting results with respect to whether Desmodium releases volatiles constitutively or in response to biotic stress, the level at which such volatiles are released, and the behavioral effect it has on the fall armyworm. These questions are relevant as Desmodium is used in a textbook example of pest-suppressive sustainable intercropping technology called push-pull, which has supported tens of thousands of smallholder farmers in suppressing moth pests in maize. A large number of research papers over more than two decades have implied that Desmodium suppresses herbivores in push-pull intercropping through the release of large amounts of volatiles that repel herbivores. This premise has been questioned in recent papers. Odermatt et al. thus contribute to this discussion by testing the role of odors in oviposition choice. The paper confirms that ovipositing FAW preferred maize, and also confirmed that odors released from Desmodium appeared not important in their bioassays.

The paper is a welcome addition to the literature and adds quality headspace analyses of Desmodium from the laboratory and the field. Furthermore, the authors, some of whom have since long contributed to developing push-pull, also find that Desmodium odors are not significant in their choice between maize plants. This advances our knowledge of the mechanisms through which push-pull suppresses herbivores, which is critically important to evolving the technique to fit different farming systems and translating this mechanism to fit with other crops and in other geographical areas.

Thank you for your careful assessment of our manuscript.

Weaknesses:

Below I outline the major concerns:

(1) Clear induction of the experimental plants, and lack of reflective discussion around this: from literature data and previous studies of maize and Desmodium, it is clear that the plants used in this study, particularly the Desmodium, were induced. Maize appeared to be primarily manually damaged, possibly due to sampling (release of GLV, but little to no terpenoids, which is indicative of mostly physical stress and damage, for example, one of the coauthor's own paper Tamiru et al. 2011), whereas Desmodium releases a blend of many compounds (many terpenoids indicative of herbivore induction). Erdei et al. also clearly show that under controlled conditions maize, silver leaf and green leaf Desmodium release volatiles in very low amounts. While the condition of the plants in Odermatt et al. may be reflective of situations in push-pull fields, the authors should elaborate on the above in the discussion (see comments) such that the readers understand that the plant's condition during the experiments. This is particularly important because it has been assumed that Desmodium releases typical herbivore-induced volatiles constitutively, which is not the case (see Erdei et al. 2024). This reflection is currently lacking in the manuscript.

We acknowledge the need for a more reflective discussion on the possible causes of GLV (green leaf volatiles) emission, particularly regarding physical damage. Although the field plants were carefully handled, it is possible that some physical stress may have contributed to the release of GLVs. We will ensure the revised manuscript reflects this nuanced interpretation. However, we will also explain more clearly that our aim was to capture the volatile emission of plants used by farmers under realistic conditions and moth responses to these plants, not to be able to attribute the volatile emission to a specific cause. We think that this is also clear in the manuscript. However, we plan to revise relevant passages throughout the manuscript to ensure that we do not make any claims about the reason for volatile emissions, and that our claims regarding these plants and their headspace being representative of the system as practiced by farmers are supported. In the revised manuscript we will explain better that the volatile profiles comprise a majority of non-GLV compounds. As shown in figure 1, the majority of the substances that were found in the headspace of the sampled plants of Desmodium intortum or Desmodium incanum are non-GLV monoterpenes, sesquiterpenes, or aromatic compounds. We will also note that the experimental plants used in the study were grown in insect proof screenhouses and were checked for any insect damage before volatile collection and bioassay.

(2) Lack of controls that would have provided context to the data: The experiments lack important controls that would have helped in the interpretation:

(2a) The authors did not control the conditions of the plants. To understand the release of volatiles and their importance in the field, the authors should have included controlled herbivory in both maize and Desmodium. This would have placed the current volatile profiles in a herbivory context. Now the volatile measurements hang in midair, leading to discussions that are not well anchored (and should be rephrased thoroughly, see eg lines 183-188). It is well known that maize releases only very low levels of volatiles without abiotic and biotic stressors. However, this changes upon stress (GLVs by direct, physical damage and eg terpenoids upon herbivory, see above). Erdei et al. confirm this pattern in Desmodium. Not having these controls, means that the authors need to put the data in the context of what has been published (see above).

We appreciate this concern. Our study aimed to capture the real-world conditions of push-pull fields, where Desmodium and maize grow in natural environments without the direct induction of herbivory for experimental purposes. We will update the discussion to provide better context based on existing literature regarding the volatile release under stress conditions. We agree that in further studies it would be important to carry out experiments under different environmental conditions, including herbivore damage. However, this was not within the scope of the present study.

(2b) It would also have been better if the authors had sampled maize from the field while sampling Desmodium. Together with the above point (inclusion of herbivore-induced maize and Desmodium), the levels of volatile release by Desmodium would have been placed into context.

We acknowledge that sampling maize and other intercrop plants, such as edible legumes, alongside Desmodium in the push-pull field would have allowed us to make direct comparisons of the volatile profiles of different plants in the push-pull system under shared field conditions. Again, this should be done in future experiments but was beyond the scope of the present study. Due to the amount of samples, we could handle given cost and workload, we chose to focus on Desmodium because there is much less literature on the volatile profiles of field-grown Desmodium than maize plants in the field: we are aware of one study attempting to measure field volatile profiles from Desmodium intortum (Erdei et al. 2024) and no study attempting this for Desmodium incanum. We will point out this justification for our focus on Desmodium in the manuscript. Additionally, we will suggest in the discussion that future studies should measure volatile profiles from maize and intercrop legumes alongside Desmodium and border grass in push-pull fields.

(2c) To put the volatiles release in the context of push-pull, it would have been important to sample other plants which are frequently used as intercrop by smallholder farmers, but which are not considered effective as push crops, particularly edible legumes. Sampling the headspace of these plants, both 'clean' and herbivore-induced, would have provided a context to the volatiles that Desmodium (induced) releases in the field - one would expect unsuccessful push crops to not release any of these 'bioactive' volatiles (although 'bioactive' should be avoided) if these odors are responsible for the pest suppressive effect of Desmodium. Many edible intercrops have been tested to increase the adoption of push-pull technology but with little success.

Again, we very much agree that such measurements are important for the longer-term research program in this field. But again, for the current study this would have exploded the size of the required experiment. Regarding bioactivity, we have been careful to use the phrase "potentially bioactive", or to cite other studies showing bioactivity, where we have not demonstrated bioactivity ourselves.

Because of the lack of the above, the conclusions the authors can draw from their data are weakened. The data are still valuable in the current discussion around push-pull, provided that a proper context is given in the discussion along the points above.

We agree that our study is limited to its specific aims. Therefore, we think the revisions will make these more explicit and help to avoid misleading claims.

(3) 'Tendency' of the authors to accept the odor hypothesis (i.e. that Desmodium odors are responsible for repelling FAW and thereby reduce infestation in maize under push-pull management) in spite of their own data: The authors tested the effects of odor in oviposition choice, both in a cage assay and in a 'wind tunnel'. From the cage experiments, it is clear that FAW preferred maize over Desmodium, confirming other reports (including Erdei et al. 2024). However, when choosing between two maize plants, one of which was placed next to Desmodium to which FAW has no tactile (taste, structure, etc), FAW chose equally. Similarly in their wind tunnel setup (this term should not be used to describe the assay, see below), no preference was found either between maize odor in the presence or absence of Desmodium. This too confirms results obtained by Erdei et al. (but add an important element to it by using Desmodium plants that had been induced and released volatiles, contrary to Erdei et al. 2024). Even though no support was found for repellency by Desmodium odors, the authors in many instances in the manuscript (lines 30-33, 164-169, 202, 279, 284, 304-307, 311-312, 320) appear to elevate non-significant tendencies as being important. This is misleading readers into thinking that these interactions were significant and in fact confirming this in the discussion. The authors should stay true to their own data obtained when testing the hypothesis of whether odors play a role in the pest-suppressive effect of push-pull.

We appreciate this feedback and agree that we may have overstated claims that could not be supported by strict significance tests. However, we believe that non-significant tendencies can still provide valuable insights. In the revised version of the manuscript, we will ensure a clear distinction between statistically significant findings and non-significant trends and remove any language that may imply stronger support for the odor hypothesis that what the data show.

(4) Oviposition bioassay: with so many assays in close proximity, it is hard to certify that the experiments are independent. Please discuss this in the appropriate place in the discussion.

We have pointed this out in the submitted manuscript in the lines 275 – 279. Furthermore, we include detailed captions to figure 4 - supporting figure 3 & figure 4 - supporting figure 4. We are aware that in all such experiments there is a danger of between-treatment interference, which we will point out for our specific case. We will also mention that this common caveat does not invalidate experimental designs when practicing replication and randomization and assume insect’s ability to select suitable oviposition site in the background of such confounding factors under realistic conditions. We will also mention explicitly that with our experimental setup we tried to minimize interference between treatments by spacing and temporal staggering.

(5) The wind tunnel has a number of issues (besides being poorly detailed):

(5a) The setup which the authors refer to as a 'wind tunnel' does not qualify as a wind tunnel. First, there is no directional flow: there are two flows entering the setup at opposite sides. Second, the flow is way too low for moths to orient in (in a wind tunnel wind should be presented as a directional cue. Only around 1.5 l/min enters the wind tunnel in a volume of 90 l approximately, which does not create any directional flow. Solution: change 'wind tunnel' throughout the text to a dual choice setup /assay.)

We agree with these criticisms and will change the terminology accordingly. We also plan to conduct an additional experiment with a no-choice arena that provides conditions closer to a true wind tunnel. The setup of the added experiment features an odor entry point at only one side of the chamber to create a more directional airflow. Each treatment (maize alone, maize + D. intortum, maize + D. incanum, and a control with no plants) will be tested separately, with only one treatment conducted per evening to avoid cross-contamination.

(5b) There is no control over the flows in the flight section of the setup. It is very well possible that moths at the release point may only sense one of the 'options'. Please discuss this.

We will add this to the discussion. The newly planned assays also address this concern by using a setup with laminar flow.

(5c) Too low a flow (1,5 l per minute) implies a largely stagnant air, which means cross-contamination between experiments. An experiment takes 5 minutes, but it takes minimally 1.5 hours at these flows to replace the flight chamber air (but in reality much longer as the fresh air does not replace the old air, but mixes with it). The setup does not seem to be equipped with e.g. fans to quickly vent the air out of the setup. See comments in the text. Please discuss the limitations of the experimental setup at the appropriate place in the discussion.

We will add these limitations to the discussion and will address these concerns with new experiments (see answer 5a).

(5d) The stimulus air enters through a tube (what type of tube, diameter, length, etc) containing pressurized air (how was the air obtained into bags (type of bag, how is it sealed?), and the efflux directly into the flight chamber (how, nozzle?). However, it seems that there is no control of the efflux. How was leakage prevented, particularly how the bags were airtight sealed around the plants? 

We will add the missing information to the methods and provide details about types of bags, manufacturers, and pre-treatments. In short, Teflon tubes connected bagged plants to the bioassay setup and air was pumped in at an overpressure, so leakage was not eliminated but contamination from ambient air was avoided.

(5e) The plants were bagged in very narrowly fitting bags. The maize plants look bent and damaged, which probably explains the GLVs found in the samples. The Desmodium in the picture (Figure 5 supplement), which we should assume is at least a representative picture?) appears to be rather crammed into the bag with maize and looks in rather poor condition to start with (perhaps also indicating why they release these volatiles?). It would be good to describe the sampling of the plants in detail and explain that the way they were handled may have caused the release of GLVs.

We will include a more detailed description of the plant handling and bagging processes to the methods to clarify how the plants were treated during all assays reported in the submitted manuscript and the newly planned assays. This will address concerns about the possible influence of plant stress, such as GLV emission due to bagging, on the results. We politely disagree that the maize plants were damaged and the Desmodium plants not representative of those encountered in the field. The Desmodium plant pictured was D. incanum, which has sparser foliage and smaller leaves than D. intortum.

(6) Figure 1 seems redundant as a main figure in the text. Much of the information is not pertinent to the paper. It can be used in a review on the topic. Or perhaps if the authors strongly wish to keep it, it could be placed in the supplemental material.

We think that Figure 1 provides essential information about the push-pull system and the FAW. To our knowledge, this partly contradictory evidence so far has not been synthesized in the literature. We realize that such a figure would more commonly be provided in a review article, but we do not think that the small number of studies on this topic so far justify a stand-alone review. Instead, the introduction to our manuscript includes a brief review of these few studies, complemented by the visual summary provided in Figure 1 and a detailed supplementary table. We will revise the figure and associated text in the introduction to highlight its relevance for the current study and to reduce redundant information.

Reviewer #2 (Public review):

Based on the controversy of whether the Desmodium intercrop emits bioactive volatiles that repel the fall armyworm, the authors conducted this study to assess the effects of the volatiles from Desmodium plants in the push-pull system on behavior of FAW oviposition. This topic is interesting and the results are valuable for understanding the push-pull system for the management of FAW, the serious pest. The methodology used in this study is valid, leading to reliable results and conclusions. I just have a few concerns and suggestions for improvement of this paper:

(1) The volatiles emitted from D. incanum were analyzed and their effects on the oviposition behavior of FAW moth were confirmed. However, it would be better and useful to identify the specific compounds that are crucial for the success of the push-pull system.

We fully agree that identifying specific volatile compounds responsible for the push-pull effect would provide valuable insights into the underlying mechanisms of the system. However, the primary focus of this study was to address the still unresolved question whether Desmodium emits volatiles at all under field conditions, and the secondary aim was to test whether we could demonstrate a behavioral effect of Desmodium headspace on FAW moths. Before conducting our experiments, we carefully considered the option of using single volatile compounds and synthetic blends in bioassays. We decided against this because we judged that the contradictory evidence in the literature was not a sufficient basis for composing representative blends. Furthermore, we think it is an important first step to test for behavioral responses to the headspaces of real plants. We consider bioassays with pure compounds to be important for confirmation and more detailed investigation in future studies. There was also contradictory evidence in the literature regarding moth responses to plants. We thus opted to focus on experiments with whole plants to maintain ecological relevance.

(2) That would be good to add "symbols" of significance in Figure 4 (D).

We report the statistical significance of the parameters in Figure 4 (D) in Table 3. While testing significance between groups is a standard approach, we used a more robust model-based analysis to assess the effects of multiple factors simultaneously. We will clarify this in the figure legend and provide a cross-reference to Table 3 for readers to easily find the statistical details.

(3) Figure A is difficult for readers to understand.

Unfortunately, it is not entirely clear which specific figure is being referred to as "Figure A" in this comment. We kindly request further clarification on which figure needs improvement, and we will make adjustments accordingly to ensure that all figures are easily comprehensible for readers.

(4) It will be good to deeply discuss the functions of important volatile compounds identified here with comparison with results in previous studies in the discussion better.

Our study does not provide strong evidence that specific volatiles from Desmodium plants are important determinants of FAW oviposition or choice in the push-pull system. Therefore, we prefer to refrain from detailed discussions of the potential importance of individual compounds. However, in the revised version, we will indicate specifically which of the volatiles we identified overlap with those previously reported from Desmodium, as only the total numbers are summarized in the discussion of the submitted paper.

Reviewer #1 (Public review):

Summary & Assessment:

The catalytic core of the eukaryotic decapping complex consists of the decapping enzyme DCP2 and its key activator DCP1. In humans, there are two paralogs of DCP1, DCP1a and DCP1b, that are known to interact with DCP2 and recruit additional cofactors or coactivators to the decapping complex; however, the mechanisms by which DCP1 activates decapping and the specific roles of DCP1a versus DCP1b, remain poorly defined. In this manuscript, the authors used CRISPR/Cas9-generated DCP1a/b knockout cells to begin to unravel some of the differential roles for human DCP1a and DCP1b in mRNA decapping, gene regulation, and cellular metabolism. While this manuscript presents some new and interesting observations on human DCP1 (e.g. human DCP1a/b KO cells are viable and can be used to investigate DCP1 function; only the EVH1 domain, and not its disordered C-terminal region which recruits many decapping cofactors, is apparently required for efficient decapping in cells; DCP1a and b target different subsets of mRNAs for decay and may regulate different aspects of metabolism), there is one key claim about the role of DCP1 in regulating DCP2-mediated decapping that is still incompletely or inconsistently supported by the presented data in this revised version of the manuscript.

Strengths & well-supported claims:

• Through in vivo tethering assays in CRISPR/Cas9-generated DCP1a/b knockout cells, the authors show that DCP1 depletion leads to significant defects in decapping and the accumulation of capped, deadenylated mRNA decay intermediates.<br /> • DCP1 truncation experiments reveal that only the EVH1 domain of DCP1 is necessary to rescue decapping defects in DCP1a/b KO cells.<br /> • RNA and protein immunoprecipitation experiments suggest that DCP1 acts as a scaffold to help recruit multiple decapping cofactors to the decapping complex (e.g. EDC3, DDX6, PATL1 PNRC1, and PNRC2), but that none of these cofactors are essential for DCP2-mediated decapping in cells.<br /> • The authors investigated the differential roles of DCP1a and DCP1b in gene regulation through transcriptomic and metabolomic analysis and found that these DCP1 paralogs target different mRNA transcripts for decapping and have different roles in cellular metabolism and their apparent links to human cancers. (Although I will note that I can't comment on the experimental details and/or rigor of the transcriptomic and metabolomic analyses, as these are outside my expertise.)

Weaknesses & incompletely supported claims:

(1) One of the key mechanistic claims of the paper is that "DCP1a can regulate DCP2's cellular decapping activity by enhancing DCP2's affinity to RNA, in addition to bridging the interactions of DCP2 with other decapping factors. This represents a pivotal molecular mechanism by which DCP1a exerts its regulatory control over the mRNA decapping process." Similar versions of this claim are repeated in the abstract and discussion sections. However, this claim appears to be at odds with the observations that: (a) in vitro decapping assays with immunoprecipitated DCP2 show that DCP1 knockout does not significantly affect the enzymatic activity of DCP2 (Fig 2C&D; I note that there may be a very small change in DCP2 activity shown in panel D, but this may be due to slightly different amounts of immunoprecipitated DCP2 used in the assay); and (b) the authors show only weak changes in relative RNA levels immunoprecipitated by DCP2 with versus without DCP1 (~2-3 fold change in Fig 3H, where expression of the EVH1 domain, previously shown in this manuscript to fully rescue the DCP1 KO decapping defects in cells, looks to be almost within error of the control in terms of increasing RNA binding). If DCP1 pivotally regulates decapping activity by enhancing RNA binding to DCP2, why is no difference in in vitro decapping activity observed in the absence of DCP1, and very little change observed in the amounts of RNA immunoprecipitated by DCP2 with the addition of the DCP1 EVH1 domain?

In the revised manuscript and in their response to initial reviews, the authors rightly point out that in vivo effects may not always be fully reflected by or recapitulated in in vitro experiments due to the lack of cellular cofactors and simpler environment for the in vitro experiment, as compared to the complex environment in the cell. I fully agree with this of course! And further completely agree with the authors that this highlights the critical importance of in cell experiments to investigate biological functions and mechanisms! However, because the in vitro kinetic and IP/binding data both suggest that the DCP1 EVH1 domain has minimal to no effects on RNA decapping or binding affinity, while the in cell data suggest the EVH1 domain alone is sufficient to rescue large decapping defects in DCP1a/b KO cells (and that all the decapping cofactors tested were dispensable for this), I would argue there is insufficient evidence here to make a claim that (maybe weakly) enhanced RNA binding induced by DCP1 is what is regulating the cellular decapping activity. Maybe there are as-yet-untested cellular cofactors that bind to the EVH1 domain of DCP1 that change either RNA recruitment or the kinetics of RNA decapping in cells; we can't really tell from the presented data so far. Furthermore, even if it is the case that the EVH1 domain modestly enhances RNA binding to DCP2, the authors haven't shown that this effect is what actually regulates the large change in DCP2 activity upon DCP1 KO observed in the cell.

Overall, while I absolutely appreciate that there are many possible reasons for the differences observed in the in vitro versus in cell RNA decapping and binding assays, because this discrepancy between those data exists, it seems difficult to draw any clear conclusions about the actual mechanisms by which DCP1 helps regulate RNA decapping by DCP2. For example, in the cell it could be that DCP1 enhances RNA binding, or recruits unidentified cofactors that themselves enhance RNA binding, or that DCP1 allosterically enhances DCP2-mediated decapping kinetics, or a combination of these, etc; my point is that without in vitro data that clearly support one of those mechanisms and links this mechanism back to cellular DCP2 decapping activity (for example, in cell data that show EVH1 mutants that impair RNA binding fail to rescue DCP1 KO decapping defects), it's difficult to attribute the observed in cell effects of DCP1a/b KO and rescue by the EVH1 domain directly to enhancement of RNA binding (precisely because, as the authors describe, the decapping process and regulation may be very complex in the cell!).

This contradiction between the in vitro and in-cell decapping data undercuts one of the main mechanistic takeaways from the first half of the paper; I still think this conclusion is overstated in the revised manuscript.

Additional minor comment:

• Related to point (1) above, the kinetic analysis presented in Fig 2C shows that the large majority of transcript is mostly decapped at the first 5 minute timepoint; it may be that DCP2-mediated decapping activity is actually different in vitro with or without DCP1, but that this is being missed because the reaction is basically done in less than 5 minutes under the conditions being assayed (i.e. these are basically endpoint assays under these conditions). It may be that if kinetics were done under conditions to slow down the reaction somewhat (e.g. lower Dcp2 concentration, lower temperatures), so that more of the kinetic behavior is captured, the apparent discrepancy between in vitro and in-cell data would be much less. Indeed, previous studies have shown that in yeast, Dcp1 strongly activates the catalytic step (kcat) of decapping by ~10-fold, and reduces the KM by only ~2 fold (Floor et al, NSMB 2010). It might be beneficial to use purified proteins here, if possible, to better control reaction conditions.

In their response to initial reviews, the authors comment that they tried to purify human DCP2 from E coli, but were unable to obtain active enzyme in this way. Fair enough! I will only comment that just varying the relative concentration of immunoprecipitated DCP2 would likely be enough to slow down the reaction and see if activity differences are seen in different kinetic regimes, without the need to obtain fully purified / recombinant Dcp2.

Author response:

The following is the authors’ response to the previous reviews.

Removing claims of causality: To avoid confusion, we have now removed claims of causality from our manuscript and also changed the title of the manuscript accordingly

"Electrophysiological dynamics of salience, default mode, and frontoparietal networks during episodic memory formation and recall: A multi-experiment iEEG replication".

Control analyses directly comparing AI and IFG: As per the reviewer’s suggestion, we have carried out additional control analyses by directly comparing the net inward/outward balance between the AI and the IFG. Our analysis revealed that the net outflow for the AI is significantly higher compared to the IFG during both encoding and recall phases, a pattern that was replicated across all four experiments. 

These findings further highlight the unique role of the AI as a key hub in coordinating network interactions during episodic memory formation and retrieval, distinguishing it from a key anatomically adjacent prefrontal region implicated in cognitive control.

We have incorporated these results into the manuscript (see new Figure S6 and updated Results section). 

Control analyses directly comparing task with resting state: As per the reviewer’s suggestion, we compared the AI's net outflow during task periods to resting state, finding significantly higher outflow during both encoding and recall across all experiments (ps < 0.05). These results provide further evidence for enhanced role of AI net directed information flow to the DMN and FPN during memory processing compared to the resting state. 

We have incorporated these results into the manuscript (see new Figure S9 and updated Results section). 

Control analysis using every region of the brain outside the considered networks: We appreciate the reviewer's suggestion to conduct additional control analyses. However, we have concerns about implementing this approach for several reasons:

(1) Hypothesis-driven research: Our study was designed based on a strong hypothesis derived from prior fMRI studies, which have consistently shown that the salience network (SN), anchored by the anterior insula (AI), plays a critical role in regulating the engagement and disengagement of the default mode network (DMN) and frontoparietal network (FPN) across diverse cognitive tasks.

(2) Risk of p-hacking: Running analyses on a large number of brain regions outside our networks of interest without a priori hypotheses could lead to p-hacking, a practice strongly criticized in the scientific community, including by eLife editors (Makin & Orban de Xivry, 2019). Such an approach could potentially yield spurious results and undermine the validity of our findings.

(3) Principled control region selection: Our choice of the inferior frontal gyrus (IFG) as a control region was hypothesis-driven, based on its: a) Anatomical adjacency to the AI b) Involvement in cognitive control functions, including response inhibition c) Frequent coactivation with the AI in fMRI studies. 

(4) Robustness of current findings: Our PTE analysis involving the IFG, along with the additional control analyses requested by the reviewer (comparing the task-related net balance of the AI with the IFG and with resting state, see response to reviewer comment 2.1), strongly support a key role for the AI in orchestrating large-scale network dynamics during memory processes.

(5) Specificity of findings: The contrast between AI and IFG results demonstrates that our observed patterns are not general to all task-active regions but are specific to the AI's role in network coordination. 

We believe that our current analyses, including the additional controls, provide a comprehensive and rigorous examination of the AI's role in memory-related network dynamics. Adding analyses of numerous additional regions without clear hypotheses could potentially dilute the focus and interpretability of our results. 

However, we acknowledge the importance of considering broader network interactions. In future studies, we could explore the role of other key regions in a hypothesis-driven manner, potentially expanding our understanding of the complex interactions between multiple brain networks during memory processes.

These revisions, combined with our rigorous methodologies and comprehensive analyses, provide compelling support for the central claims of our manuscript. We believe these changes significantly enhance the scientific contribution of our work.

Our point-by-point responses to the reviewers' comments are provided below.

Reviewer 1:

(1.1) Because phase-transfer entropy is referenced as a "causal" analysis in this investigation (PTE), I believe it is important to highlight for readers recent discussions surrounding the description of "causal mechanisms" in neuroscience (see "Confusion about causation" section from Ross and Bassett, 2024, Nature Neuroscience). A large proportion of neuroscientists (myself included) use "causal" only to refer to a mechanism whose modulation or removal (with direct manipulation, such as by lesion or stimulation) is known to change or control a given outcome (such as a successful behavior). As Ross and Bassett highlight, it is debatable whether such mechanistic causality is captured by Granger "causality" (a.k.a. Granger prediction) or the parametric PTE, and imprecise use of "causation" may be confusing. The authors have defined in the revised Introduction what their definition of "causality" is within the context of this investigation. 

We appreciate the reviewer's feedback in terms of the terminology used in our manuscript. To avoid confusion, we have now removed claims of causality from our manuscript and also changed the title of the manuscript accordingly. 

Reviewer 2:

(2.1) Clarifying the new control analyses. The authors have been responsive to our feedback and implemented several new analyses. The use of a pre-task baseline period and a control brain region (IFG) definitively help to contextualize their results, and the findings shown in the revision do suggest that (1) relative to a pre-task baseline, directed interactions from the AI are stronger and (2) relative to a nearby region, the IFG, the AI exhibits greater outward-directed influence. 

However, it is difficult to draw strong quantitative conclusions from the analyses as presented, because they do not directly statistically contrast the effect in question (directed interactions with the FPN and DMN) between two conditions (e.g. during baseline vs. during memory encoding/retrieval). As I understand it, in their main figures the authors ask, "Is there statistically greater influence from the AI to the DMN/FPN in one direction versus another?" And in the AI they show greater "outward" PTE than "inward" PTE from other networks during encoding/retrieval. The balance of directed information favors an outward influence from the AI to DMN/FPN. 

But in their new analyses, they simply show that the degree of "outward" PTE is greater during task relative to baseline in (almost) all tasks. I believe a more appropriately matched analysis would be to quantify the inward/outward balance during task states, quantify the inward/outward balance during rest states, and then directly statistically compare the two. It could be that the relative balance of directed information flow is nonsignificantly changed between task and rest states, which would be important to know. 

We thank the reviewer for this suggestion. We have now run additional analysis by directly comparing the inward/outward balance during the task versus the rest states. To calculate the net inward/outward balance, we calculated the net outflow as the difference between the total outgoing information and total incoming information (PTE(out)–PTE(in)). This analysis revealed that net outflow during task periods is significantly higher compared to rest, during both encoding and recall, and across the four experiments (ps < 0.05). These results provide further evidence for enhanced role of AI net directed information flow to the DMN and FPN during memory processing compared to the resting state. These new results have now been included in the revised manuscript (page 12). 

Likewise, a similar principle applies to their IFG analysis. They show that the IFG tends to have an "inward" balance of influence from the DMN/FPN (the opposite of the AIs effect), but this does not directly answer whether the AI occupies a statistically unique position in terms of the magnitude of its influence on other regions. More appropriate, as I suggest above, would be to quantify the relative balance inward/outward influence, both for the IFG and the AI, and then directly compare those two quantities. (Given the inversion of the direction of effect, this is likely to be a significant result, but I think it deserves a careful approach regardless.) 

We appreciate the reviewer's suggestion. As per the reviewer’s suggestion, we directly compared the net inward/outward balance between the AI and the IFG. Specifically, we compared the net outflow (PTE(out)–PTE(in)) for the AI with the IFG. This analysis revealed that the net outflow for the AI is significantly higher compared to the IFG during both encoding and recall, and across the four experiments. These findings further highlight a key role for the AI in orchestrating large-scale network dynamics during memory processes. The AI's pattern of directed information flow stands in contrast to that of the IFG, despite their anatomical proximity and shared involvement in cognitive control processes. This dissociation underscores the specificity of the AI's function in coordinating network interactions during memory formation and retrieval. These new results have now been included in our revised manuscript (page 11). 

(2.2) Consider additional control regions. The authors justify their choice of IFG as a control region very well. In my original comments, I perhaps should have been more clear that the most compelling control analyses here would be to subject every region of the brain outside these networks (with good coverage) to the same analysis, quantify the degree of inward/outward balance, and then see how the magnitude of the AI effect stacks up against all possible other options. If the assertion is that the AI plays a uniquely important role in these memory processes, showing how its influence stacks up against all possible "competitors" would be a very compelling demonstration of their argument. 

We thank the reviewer for this suggestion. However, please note that running a large number of random analysis by including a large number of brain regions (every region of the brain outside these networks) and comparing their dynamics to the AI without a hypothesis or solid principle amounts to p-hacking, which has been previously strongly criticized by the eLife editors (Makin & Orban de Xivry, 2019). Our study was strongly driven by a solid hypothesis based on prior fMRI studies that have shown that the SN, anchored by the anterior insula (AI), plays a critical role in regulating the engagement and disengagement of the DMN and FPN across diverse cognitive tasks (Bressler & Menon, 2010; Cai et al., 2016; Cai, Ryali, Pasumarthy, Talasila, & Menon, 2021; Chen, Cai, Ryali, Supekar, & Menon, 2016; Kronemer et al., 2022; Raichle et al., 2001; Seeley et al., 2007; Sridharan, Levitin, & Menon, 2008). Moreover, our selection of the IFG as a control region for comparison was also very strongly hypothesis driven, due to its anatomical adjacency to the AI, its involvement in a wide range of cognitive control functions including response inhibition (Cai, Ryali, Chen, Li, & Menon, 2014), and its frequent co-activation with the AI in fMRI studies. Furthermore, the IFG has been associated with controlled retrieval of memory (Badre, Poldrack, Paré-Blagoev, Insler, & Wagner, 2005; Badre & Wagner, 2007; Wagner, Paré-Blagoev, Clark, & Poldrack, 2001), making it a compelling region for comparison. Our findings related to the PTE analysis involving the IFG and also the additional control analyses requested by the reviewer (directly comparing the task-related net balance of the AI with the IFG and also to resting state, please see response to reviewer comment 2.1) strongly highlight a key role of the AI in orchestrating large-scale network dynamics during memory processes. 

We believe that our current analyses, including the additional controls, provide a comprehensive and rigorous examination of the AI's role in memory-related network dynamics. Adding analyses of numerous additional regions without clear hypotheses could potentially dilute the focus and interpretability of our results.

However, we acknowledge the importance of considering broader network interactions. In future studies, we could explore the role of other key regions in a hypothesis-driven manner, potentially expanding our understanding of the complex interactions between multiple brain networks during memory processes.

(2.3) Reporting of successful vs. unsuccessful memory results. I apologize if I was not clear in my original comment (2.7, pg. 13 of the response document) regarding successful vs. unsuccessful memory. The fact that no significant difference was found in PTE between successful/unsuccessful memory is a very important finding that adds valuable context to the rest of the manuscript. I believe it deserves a figure, at least in the Supplement, so that readers can visualize the extent of the effect in successful/unsuccessful trials. This is especially important now that the manuscript has been reframed to focus more directly on claims regarding episodic memory processing; if that is indeed the focus, and their central analysis does not show a significant effect conditionalized on the success of memory encoding/retrieval, it is important that readers can see these data directly.

As per the reviewer’s suggestion, we have now included a Figure related to the results for the successful versus unsuccessful comparison in the Supplementary materials of the revised manuscript (Figures S10, S11).   

(2.4) Claims regarding causal relationships in the brain. I understand that the authors have defined "causal" in a specific way in the context of their manuscript; I do believe that as a matter of clear and transparent scientific communication, the authors nonetheless bear a responsibility to appreciate how this word may be erroneously interpreted/overinterpreted and I would urge further review of the manuscript to tone down claims of causality. Reflective of this, I was very surprised that even as both reviewers remarked on the need to use the word "causal" with extreme caution, the authors added it to the title in their revised manuscript.

We thank the reviewer for this suggestion. To avoid confusion, we have now removed claims of causality from our manuscript and also changed the title of the manuscript accordingly. 

References 

Badre, D., Poldrack, R. A., Paré-Blagoev, E. J., Insler, R. Z., & Wagner, A. D. (2005). Dissociable controlled retrieval and generalized selection mechanisms in ventrolateral prefrontal cortex. Neuron, 47(6), 907-918. doi:10.1016/j.neuron.2005.07.023

Badre, D., & Wagner, A. D. (2007). Left ventrolateral prefrontal cortex and the cognitive control of memory. Neuropsychologia, 45(13), 2883-2901. doi:10.1016/j.neuropsychologia.2007.06.015

Bressler, S. L., & Menon, V. (2010). Large-scale brain networks in cognition: emerging methods and principles. Trends in Cognitive Sciences, 14(6), 277-290. doi:10.1016/j.tics.2010.04.004

Cai, W., Chen, T., Ryali, S., Kochalka, J., Li, C. S., & Menon, V. (2016). Causal Interactions Within a Frontal-Cingulate-Parietal Network During Cognitive Control: Convergent Evidence from a Multisite-Multitask Investigation. Cereb Cortex, 26(5), 2140-2153. doi:10.1093/cercor/bhv046

Cai, W., Ryali, S., Chen, T., Li, C. S., & Menon, V. (2014). Dissociable roles of right inferior frontal cortex and anterior insula in inhibitory control: evidence from intrinsic and taskrelated functional parcellation, connectivity, and response profile analyses across multiple datasets. J Neurosci, 34(44), 14652-14667. doi:10.1523/jneurosci.3048-14.2014

Cai, W., Ryali, S., Pasumarthy, R., Talasila, V., & Menon, V. (2021). Dynamic causal brain circuits during working memory and their functional controllability. Nat Commun, 12(1), 3314. doi:10.1038/s41467-021-23509-x

Chen, T., Cai, W., Ryali, S., Supekar, K., & Menon, V. (2016). Distinct Global Brain Dynamics and Spatiotemporal Organization of the Salience Network. PLOS Biology, 14(6), e1002469. doi:10.1371/journal.pbio.1002469

Kronemer, S. I., Aksen, M., Ding, J. Z., Ryu, J. H., Xin, Q., Ding, Z., . . . Blumenfeld, H. (2022). Human visual consciousness involves large scale cortical and subcortical networks independent of task report and eye movement activity. Nat Commun, 13(1), 7342. doi:10.1038/s41467-022-35117-4

Makin, T. R., & Orban de Xivry, J. J. (2019). Ten common statistical mistakes to watch out for when writing or reviewing a manuscript. Elife, 8. doi:10.7554/eLife.48175

Raichle, M. E., MacLeod, A. M., Snyder, A. Z., Powers, W. J., Gusnard, D. A., & Shulman, G. L. (2001). A default mode of brain function. Proc Natl Acad Sci U S A, 98(2), 676-682. doi:10.1073/pnas.98.2.676

Seeley, W. W., Menon, V., Schatzberg, A. F., Keller, J., Glover, G. H., Kenna, H., . . . Greicius, M. D. (2007). Dissociable Intrinsic Connectivity Networks for Salience Processing and Executive Control. Journal of Neuroscience, 27(9), 2349-2356. doi:10.1523/JNEUROSCI.5587-06.2007

Sridharan, D., Levitin, D. J., & Menon, V. (2008). A critical role for the right fronto-insular cortex in switching between central-executive and default-mode networks. Proceedings of the National Academy of Sciences, 105(34), 12569-12574. doi:10.1073/pnas.0800005105

Wagner, A. D., Paré-Blagoev, E. J., Clark, J., & Poldrack, R. A. (2001). Recovering meaning: left prefrontal cortex guides controlled semantic retrieval. Neuron, 31(2), 329-338. doi:10.1016/s0896-6273(01)00359-2

Welcome to this video which will be a fairly high level introduction to YAML.

Now YAML stands for YAML 8 Markup Language and for any key observers that's a recursive acronym.

Now I want this video to be brief but I think it's important that you understand YAML's structure.

So let's jump in and get started.

YAML is a language which is human readable and designed for data serialization.

Now that's a mouthful but put simply it's a language for defining data or configuration which is designed to be human readable.

At a high level a YAML document is an unordered collection of key value pairs separated by a colon.

It's important that you understand this lack of order.

At this top level there is no requirement to order things in a certain way.

Although there may be conventions and standards none of that is imposed by YAML.

An example key value pair might be the key being cat1 and the value being raffle.

One of my cats in this example both the key and the value are just normal strings.

We could further populate our YAML file with a key of cat2 and a value of truffles and other cat of mine.

Or a key of cat3 and a value of penny and a key of cat4 and a value of winkey.

These are all strings.

Now YAML supports other types numbers such as one and two, floating point values such as 1.337, boolean so true or false and even null which represents nothing.

Now YAML also supports other types and one of those are lists known as arrays or other names depending on what if any programming languages that you're used to.

A list is essentially an ordered set of values and in YAML we can represent a list by having a key let's say Adrian's cats.

And then as a value we might have something that looks like this, a comma separated set of values inside swear brackets.

Now this is known as inline format where the list is placed where you expect the value to be after the key and the colon.

Now the same list can also be represented like this where you have the key and then a colon and then you go to a new line and each item in the list is represented by hyphen and then the value.

Now notice how for some of the values are actually enclosed in speech marks or quotation marks and so on.

This is optional.

All of these are valid.

Often though it's safe for you to enclose things as it allows you to be more precise and it avoids confusion.

Now in YAML indentation really matters.

Indentation is always done using spaces and the same level of indentation means that the things are within the same structure.

So we know that because all of these list items are indented by the same amount they're all part of the same list.

We know they're a list because of the hyphens.

So same indent always using hyphens means that they're all part of the same list, same structure.

Now these two styles are two methods for expressing the same thing.

A key called Adrian's cats whose value is a list.

This is the same structure.

It represents the same data.

Now there's one final thing which I want to cover with YAML and that's a dictionary.

A dictionary is just a data structure.

It's a collection of key value pairs which are unordered.

A YAML template has a top level dictionary.

It's a collection of key value pairs.

So let's look at an example.

Now this looks much more complicated but it's not if you just follow it through from the start.

So we start with a key value pair.

Adrian's cats at the top.

So the key is Adrian's cats and the value is a list.

And we can tell that it's a list because of the hyphens which are the same level of indentation.

But, and this is important, notice how for each list item we don't just have the hyphen and a value.

Instead we have the hyphen and for each one we have a collection of key value pairs.

So for the final list item at the bottom we have a dictionary containing a number of key value pairs.

The first has a key of name with a value of winky.

The second a key color with a value of white.

And then for this final list item a key, num of eyes and a value of one.

And each item in this list, each value is a dictionary.

A collection of one or more key value pairs.

So values can be strings, numbers, floats, booleans, lists or dictionaries or a combination of any of them.

Note how the color key value pair in the top list item, so the raffle dictionary at the top, its value is a list.

So this structure that's on screen now, we have Adrian's cats which are a value, has a list.

Each value in the list is a dictionary.

Each dictionary contains a name, key, with a value, a color key, with a value.

And then the third item in the list also has a num of eyes key and a value.

Now using YAML key value pairs, lists and dictionaries allows you to build complex data structures in a way which once you have practice is very human readable.

In this case, it's a database of somebody's cats.

Now YAML can be read into an application or written out by an application.

And YAML is commonly used for the storage and passing of configuration.

For now thanks for watching, go ahead, complete the video and when you're ready I'll look forward to you joining me in the next.

Welcome back.

In this fundamentals video, I want to briefly talk about Kubernetes, which is an open source container orchestration system.

You use it to automate the deployment, scaling and management of containerized applications.

At a super high level, Kubernetes lets you run containers in a reliable and scalable way, making a vision fuse of resources, and lets you expose your containerized applications to the outside world or your business.

It's like Docker, only with robots automated and super intelligence for all of the thinking.

Now, Kubernetes is a cloud agnostic product, so you can use it on premises and within many public cloud platforms.

Now, I want to keep this video to a super high level architectural overview, but that's still a lot to cover.

So let's jump in and get started.

Let's quickly step through the architecture of the Kubernetes cluster.

A cluster in Kubernetes is a highly available cluster of compute resources, and these are organized to work as one unit.

The cluster starts with a cluster control plane, which is the part which manages the cluster.

It performs scheduling, application management, scaling and deployment, and much more.

Compute within a Kubernetes cluster is provided via nodes, and these are virtual or physical servers, which function as a worker within the cluster.

These are the things which actually run your containerized applications.

Running on each of the nodes is software, and at minimum, this is container D or another container runtime, which is the software used to handle your container operations.

And next, we have KubeLit, which is an agent to interact with the cluster control plane.

And on each of the nodes communicates with the cluster control plane using Kubernetes API.

Now, this is the top level functionality of the Kubernetes cluster.

The control plane orchestrates containerized applications which run on nodes.

But now let's explore the architecture of control planes and nodes in a little bit more detail.

On this diagram, I've zoomed in a little.

We have the control plane at the top and a single cluster node at the bottom, complete with the minimum Docker and KubeLit software running for control plane communications.

Now, on to step through the main components which might run within the control plane and on the cluster nodes.

Keep in mind, this is a fundamental level video.

It's not meant to be exhaustive.

Kubernetes is a complex topic, so I'm just covering the parts that you need to understand to get started.

Now, the cluster will also likely have many more nodes.

It's rare that you only have one node unless this is a testing environment.

Now, first, I want to talk about pods and pods at the smallest unit of computing within Kubernetes.

You can have pods which have multiple containers and provide shared storage and networking for those pods.

But it's very common to see a one-container, one-pod architecture, which as the name suggests, means each pod contains only one container.

Now, when you think about Kubernetes, don't think about containers.

Think about pods.

You're going to be working with pods and you're going to be managing pods.

The pods handle the containers within them.

Architecturally, you would generally only run multiple containers in a pod when those containers are tightly coupled and require close proximity and rely on each other in a very tightly coupled way.

Additionally, although you'll be exposed to pods, you'll rarely manage them directly.

Pods are non-permanent things.

In order to get the maximum value from Kubernetes, you need to view pods as temporary things which are created, do a job, and are then disposed of.

Pods can be deleted when finished, evicted for lack of resources, or the node itself fails.

They aren't permanent and aren't designed to be viewed as highly available entities.

There are other things linked to pods which provide more permanence, but more on that elsewhere.

So now let's talk about what runs on the control plane.

Firstly, I've already mentioned this one, the API, known formally as Q-API server.

This is the front end for the control plane.

It's what everything generally interacts with to communicate with the control plane, and it can be scaled horizontally for performance and to ensure high availability.

Next, we have ETCD, and this provides a highly available key value store.

So a simple database running within the cluster, which acts as the main backing store for data for the cluster.

Another important control plane component is Q-scheduler, and this is responsible for constantly checking for any pods within the cluster which you don't have a node assigned.

And then it assigns a node to that pod based on resource requirements, deadlines, affinity, or anti-affinity, data locality needs, and any other constraints.

Remember, nodes are the things which provide the raw compute and other resources to the cluster, and it's this component which makes sure the nodes get utilized effectively.

Next, we have an optional component, the Cloud Controller Manager, and this is what allows Kubernetes to integrate with any cloud providers.

It's common that Kubernetes runs on top of other cloud platforms such as AWS, Azure, or GCP, and it's this component which allows the control plane to closely interact with those platforms.

Now, it is entirely optional, and if you run a small Kubernetes deployment at home, you probably won't be using this component.

Now, lastly, in the control plane is the Q-Controller Manager, and this is actually a collection of processors.

We've got the node controller, which is responsible for monitoring and responding to any node outages, the job controller, which is responsible for running pods in order to execute jobs, the endpoint controller, which populates endpoints in the cluster, more on this in a second, but this is something that links services to pods.

Again, I'll be covering this very shortly.

And then the service account and token controller, which is responsible for account and API token creation.

Now, again, I haven't spoken about services or endpoints yet, just stick with me.

I will in a second.

Now, lastly, on every node is something called K-Proxy, known as Cube Proxy, and this runs on every node and coordinates networking with the cluster control plane.

It helps implement services and configs rules allowing communications with pods from inside or outside of the cluster.

You might have a Kubernetes cluster, but you're going to want some level of communication with the outside world, and that's what Cube Proxy provides.

Now, that's the architecture of the cluster and nodes in a little bit more detail, but I want to finish this introduction video with a few summary points of the terms that you're going to come across.

So, let's talk about the key components.

So, we start with the cluster, and conceptually, this is a deployment of Kubernetes.

It provides management orchestration, healing, and service access.

Within a cluster, we've got the nodes which provide the actual compute resources, and pods run on these nodes.

A pod is one or more containers, and it's the smallest admin unit within Kubernetes, and often, as I mentioned previously, you're going to see the one container, one pod architecture.

Simply put, it's cleaner.

Now, a pod is not a permanent thing, it's not long-lived.

The cluster can and does replace them as required.

Services provide an abstraction from pods, so the service is typically what you will understand as an application.

An application can be containerized across many pods, but the service is the consistent thing, the abstraction.

Service is what you interact with if you access a containerized application.

Now, we've also got a job, and a job is an ad hoc thing inside the cluster.

Think of it as the name suggests, as a job.

A job creates one or more pods, runs until it completes, retries if required, and then finishes.

Now, jobs might be used as back-end isolated pieces of work within a cluster.

Now, something new that I haven't covered yet, and that's Ingress.

Ingress is how something external to the cluster can access a service.

So, you have external users, they come into an Ingress, that's routed through the cluster to a service, the service points at one or more pods, which provides the actual application.

So, Ingress is something that you will have exposure to when you start working with Kubernetes.

And next is an Ingress controller, and that's a piece of software which actually arranges for the underlying hardware to allow Ingress.

For example, there is an AWS load balancer, Ingress controller, which uses application and network load balancers to allow the Ingress.

But there are also other controllers such as Nginx and others for various cloud platforms.

Now, finally, and this one is really important, generally it's best to architect things within Kubernetes to be stateless from a pod perspective.

Remember, pods are temporary.

If your application has any form of long-running state, then you need a way to store that state somewhere.

Now, state can be session data, but also data in the more traditional sense.

Any storage in Kubernetes by default is ephemeral, provided locally by a node, and thus, if a pod moves between nodes, then that storage is lost.

Conceptually, think of this like instant store volumes running on AWS EC2.

Now, you can configure persistent storage known as persistent volumes or PVs, and these are volumes whose lifecycle lives beyond any one single pod, which is using them.

And this is how you would provision normal long-running storage to your containerized applications.

Now, the details of this are a little bit beyond this introduction level video, but I wanted you to be aware of this functionality.

OK, so that's a high-level introduction to Kubernetes.

It's a pretty broad and complex product, but it's super powerful when you know how to use it.

This video only scratches the surface.

If you're watching this as part of my AWS courses, then I'm going to have follow-up videos which step through how AWS implements Kubernetes with their EKS service.

If you're taking any of the more technically deep AWS courses, then maybe other deep-dive videos into specific areas that you need to be aware of.

So there may be additional videos covering individual topics at a much deeper level.

If there are no additional videos, then don't worry, because that's everything that you need to be aware of.

Thanks for watching this video.

Go ahead and complete the video, and when you're ready, I look forward to you joining me in the next.

I think this is very true specifically regarding age. In class we talked about the common idea that you can't learn a language after the age of 13. This idea can make it very intimidating for people wanting to start learning a new language as an adult. In reality the truth behind the rumor is that you can't completely gain a new accent after 13 but even that is not always the case.

Having scepticism to a certain extent can help the human mind come up with various questions, allowing them to deeply think about the topic and find value in them. However, while it may cause one to thoroughly think about what they do on the daily, it may pose a threat to them as a result of coming up with unnecssary and troublesome scenarios.

There are many different perspectives as to why one should study philosophy and while this perspective may seem simple, it is an extremely useful skill to be able to "think and write logically and clearly." Regardless of major or occupation, everyone has to use these skills every day as it allows us to communicate easier.

This seems like a good way to recall people into seeing more just and humanely as they are not sure how their own policies will affect their unknown life.

It is hard to think ahead when you have to self conserve and take care of those who you love. This is why we fail to make considerable change as a population regardless of the changes individuals may make.

Author response:

The following is the authors’ response to the current reviews.

We thank the reviewers and editor for their positive assessment of our work. For the Version of Record, we have made small revisions addressing the remaining concerns of reviewer #3. We have also reformatted the supplementary material to conform to eLife’s style.

While the manuscript was under review, we discussed our work with Bill Bialek, who suggested clarifying the effect of cell rearrangements on genetic patterns. Using the tracked cell trajectories we found that the highly coordinated intercalations in the germ band preserve the relative AP positions of cells. We have added an Appendix subsection (Appendix 1.5) explaining this finding and highlighting its relevance in a short paragraph added to the discussion.

Reviewer #2

Main comment from 1st review:

Weaknesses:

The modeling is interesting, with the integration of tension through tension triangulation around vertices and thus integrating force inference directly in the vertex model. However, the authors are not using it to test their hypothesis and support their analysis at the tissue level. Thus, although interesting, the analysis at the tissue level stays mainly descriptive.

Comments on the revised version:

My main concern was that the author did not use the analysis of mutant contexts such as Snail and Twist to confirm their predictions. They made a series of modifications, clarifying their conclusions. In particular, they now included an analysis of Snail mutant and show that isogonal deformations in the ventro-lateral regions are absent when the external pulling force of the VF is abolished, supporting the idea that isogonal strain could be used as an indicator of external forces (Fig7 and S6).

They further discuss their results in the context of what was published regarding the mutant backgrounds (fog, torso-like, scab, corkscrew, ksr) where midgut invagination is disrupted, and where germ band buckles, and propose that this supports the importance of internal versus external forces driving GBE.

Overall, these modifications, in addition to clarifications in the text, clearly strengthen the manuscript.

We thank the reviewer for assessing our manuscript again and are happy to hear that they find the added data on the snail mutant convincing and that our revised manuscript is stronger.

Reviewer #3

In their article "The Geometric Basis of Epithelial Convergent Extension", Brauns and colleagues present a physical analysis of drosophila axis extension that couples in toto imaging of cell contours (previously published dataset), force inference, and theory. They seek to disentangle the respective contributions of active vs passive T1 transitions in the convergent extension of the lateral ectoderm (or germband) of the fly embryo.

The revision made by the authors has greatly improved their work, which was already very interesting, in particular the use of force inference throughout intercalation events to identify geometric signatures of active vs passive T1s, and the tension/isogonal decomposition. The new analysis of the Snail mutant adds a lot to the paper and makes their findings on the criteria for T1s very convincing.

About the tissue scale issues raised during the first round of review. Although I do not find the new arguments fully convincing (see below), the authors did put a lot of effort to discuss the role of the adjacent posterior midgut (PMG) on extension, which is already great. That will certainly provide the interested readers with enough material and references to dive into that question.

We appreciate the referee’s positive assessment of our manuscript and their careful reading and constructive feedback. In particular, we are happy to hear that the referee finds our added data on the snail mutant very convincing and finds that the extended discussion on the role of the PMG is helpful. We address the remaining concerns in our detailed response below.

I still have some issues with the authors' interpretation on the role of the PMG, and on what actually drives the extension. Although it is clear that T1 events in the germ band are driven by active local tension anisotropy (which the authors show but was already well-established), it does not show that the tissue extension itself is powered by these active T1s. Their analysis of "fence" movies from Collinet et al 2015 (Tor mutants and Eve RNAi) is not fully convincing. Indeed, as the authors point out themselves, there is no flow in Tor mutant embryos, even though tension anisotropy is preserved. They argue that in Tor embryos the absence of PMG movement leaves no room for the germband to extend properly, thus impeding the flow. That suggests that the PMG acts as a barrier in Tor mutants - What is it attached to, then?

We thank the referee for pointing out this omission: The PMG is attached to the vitelline membrane in the scab domain (Munster et al. Nature 2019) and is also obstructed from moving by more anterior laying tissue (amnioserosa). It therefore acts as an obstacle for GBE extension if it fails to invaginate (e.g. in a Tor embryo). We have clarified this in the discussion of the Tor mutants.

The authors also argue that the posterior flow is reduced in "fenced" Eve RNAi embryos (which have less/no tension anisotropy), to justify their claim that it is the anisotropy that drives extension. However, previous data, including some of the authors' (Irvine and Wieschaus, 1994 - Fig 8), show that the first, rapid phase of germband extension is left completely unaffected in Eve mutants (that lack active tension anisotropy). Although intercalation in Eve mutants is not quantified in that reference, this was later done by others, showing that it is strongly reduced.

The quantification of GBE in Irvine and Wieschaus 1994 was based on the position of the PMG from bright field imaging, making it hard to distinguish the contributions of ventral furrow, PMG, and germ band, particularly during the early phase of GBE where all these processes happen simultaneously. More detailed quantifications based on PIV analysis of in toto light-sheet imaging show significantly reduced tissue flow in eve mutants after the completion of ventral furrow invagination (Lefebvre et al., eLife 2023). That the initial fast flow is driven by ventral furrow invagination, not by the PMG is apparent from twist/snail embryos where the initial phase is significantly slower (Lefebvre et al., eLife 2023, Gustafson et al., Nat Comms 2022). We have added these references to the re-analysis and discussion of the Collinet et al 2015 experiments.

Similarly, the Cyto-D phenotype from Clement et al 2017, in which intercalation is also strongly reduced, also displays normal extension.

We agree that a careful quantification of tissue flow in Cyto-D-treated embryos would be interesting. Whether they show normal extension is not clear from the Clement et al. 2017 paper, as no quantification of total tissue flow is performed and no statements regarding extension are made there.

Reviewer #3 (Recommendations For The Authors):

• A lot of typos / grammar mistakes / repetitions are still found here and there in the paper. Authors should plan a careful re-reading prior to final publication.

We have carefully checked the manuscript and fixed the typos and grammar mistakes.

• I failed to point to a very relevant reference in the previous round of review, which I think the authors should cite and comment: A review by Guirao & Bellaiche on the mechanics of intercalation in the fly germband, which notably discusses the passive/active and stress-relaxing/stress-generating nature of T1s. (Guirao and Bellaiche, Current opinions in cell biology 2017), in particular figures 1 and 2.

We thank the referee for pointing us to this relevant reference which we now cite in the introduction.

• Any new arguments/discussion the authors see fit to include in the paper to comment on the Eve/Tor phenotypes. As far as I am concerned, I am not fully convinced at the moment (see review), but I think the paper has other great qualities and findings, and now (since the first round of review) sufficiently discusses that particular matter. I leave it up to the authors how much (more) they want to delve into this in their final version!

We have added clarifications and references to the discussion of the Eve/Tor phenotypes.

The following is the authors’ response to the original reviews.

Public Review:

Joint Public Review:

Summary:

Brauns et al. work to decipher the respective contribution of active versus passive contributions to cell shape changes during germ band elongation. Using a novel quantification tool of local tension, their results suggest that epithelial convergent extension results from internal forces.

Reading this summary, and the eLife assessment, we realized that we failed to clearly communicate important aspects of our findings in the first version of our manuscript. We therefore decided to largely restructure and rewrite the abstract and introduction to emphasize that:

● Our analysis method identifies active vs passive contributions to cell and tissue shape changes during epithelial convergent extension

● In the context of Drosophila germ band extension, this analysis provides evidence for a major role for internal driving forces rather than external pulling force from neighboring tissue regions (posterior midgut), thus settling a question that has been debated due to apparently conflicting evidence from different experiments.

● Our findings have important implications for local, bottom-up self-organization vs top-down genetic control of tissue behaviors during morphogenesis.

Strengths:

The approach developed here, tension isogonal decomposition, is original and the authors made the demonstration that we can extract comprehensive data on tissue mechanics from this type of analysis.

They present an elegant diagram that quantifies how active and passive forces interact to drive cell intercalations.

The model qualitatively recapitulates the features of passive and active intercalation for a T1 event.

Regions of high isogonal strains are consistent with the proximity of known active regions.

We think this statement is somewhat ambiguous and does not summarize our findings precisely. A more precise statement would be that high isogonal strain identifies regions of passive deformation, which is caused by adjacent active regions.

They define a parameter (the LTC parameter) which encompasses the geometry of the tension triangles and allows the authors to define a criterium for T1s to occur.

The data are clearly presented, going from cellular scale to tissue scale, and integrating modeling approaches to complement the thoughtful description of tension patterns.

Weaknesses:

The modeling is interesting, with the integration of tension through tension triangulation around vertices and thus integrating force inference directly in the vertex model. However, the authors are not using it to test their hypothesis and support their analysis at the tissue level. Thus, although interesting, the analysis at the tissue level stays mainly descriptive.

We fully agree that a full tissue scale model is crucial to support the claims about tissue scale self-organization we make in the discussion. However, the full analysis of such a model is beyond the scope of the present manuscript. We have therefore split off that analysis into a companion manuscript (Claussen et al. 2023). In this paper, we show that the key results of the tissue-scale analysis of the Drosophila embryo, in particular the order-to-disorder transition associated with slowdown of tissue flow, are reproduced and rationalized by our model.

We now refer more closely to this companion paper to point the reader to the results presented there.

Major points:

(1) The authors mention that from their analysis, they can predict what is the tension threshold required for intercalations in different conditions and predict that in Snail and Twist mutants the T1 tension threshold would be around √2. Since movies of these mutants are most probably available, it would be nice to confirm these predictions.

This is an excellent suggestion. We have included an analysis of a recording of a Snail mutant, which is presented in the new Figures 4 and S6. As predicted, we find that isogonal deformations in the ventro-lateral regions are absent when the external pulling force of the VF is abolished. Further, in the absence of isogonal deformation, T1 transitions indeed occur at a critical tension of approx. √2, as predicted by our model. Both of these results provide important experimental evidence for our model and for isogonal strain as a reliable indicator of external forces.

(2) While the formalism is very elegant and convincing, and also convincingly allows making sense of the data presented in the paper, it is not all that clear whether the claims are compatible with previous experimental observations. In particular, it has been reported in different papers (including Collinet et al NCB 2015, Clement et al Curr Biol 2017) that affecting the initial Myosin polarity or the rate of T1s does not affect tissue-scale convergent extension. Analysis/discussion of the Tor phenotype (no extension with myosin anisotropy) and the Eve/Runt phenotype (extension without Myosin anisotropy), which seem in contradiction with an extension mostly driven by myosin anisotropy.

We are happy to read that the referees find our approach elegant and convincing. The referees correctly point out that we have failed to clearly communicate how our findings connect to the existing literature on Drosophila GBE. Indeed, the conflicting results reported in the literature on what drives GBE – internal forces (myosin anisotropy) or external forces (pulling by the posterior midgut) – were a motivation for our study. We have extensively rewritten the introduction, results section (“Isogonal strain identifies regions of passive tissue deformation”), and discussion (“Internal and external contributions to germ band extension”) in response to the referee’s request.

In brief, distinguishing active internal vs passive external driving of tissue flow has been a fundamental open question in the literature on morphogenesis. Our tension-isogonal decomposition now provides a way to answer this question on the cell scale, by identifying regions of passive deformation due to external forces. As we now explain more clearly, our analysis shows that germ band extension is predominantly driven by internal tension dynamics, and not pulling forces from the posterior midgut.

We put this cell-scale evidence into the context of previous experimental observations on the tissue scale: Genetic mutants (fog, torso-like, scab, corkscrew, ksr), where posterior midgut invagination is disrupted (Muenster et al. 2019, Smits et al. 2023). In these mutants, the germ band buckles forming ectopic folds or twists into a corkscrew shape as it extends, pointing towards a buckling instability characteristic of internally driven extensile flows.

To address the apparently conflicting evidence from Collinet et al. 2015, we carried out a

quantitative re-analysis of the data presented in that reference (see new SI section 3 and Fig.

S11). The results support the conclusion that the majority of GBE flow is driven internally, thus resolving the apparent conflict.

Lastly, as far as we understand, Clement et al. 2017 appears to be compatible with our picture of active T1 transitions. Clement et al. report that the actin cortex, when loaded by external forces, behaves visco-elastically with a relaxation time of the order of minutes, in line with our model for emerging interfaces post T1.

We again thank the referees for prompting us to address these important issues and believe that including their discussion has significantly strengthened our manuscript.

Recommendations for the authors:

Minor points:

- Fig 2 : authors should state in the main text at which scale the inverse problem is solved. (Intercalating quartet, if I understood correctly from the methods) ? and they should explain and justify their choice (why not computing the inverse at a larger scale).

We have rephrased the first sentence of the section “Cell scale analysis” to clarify that we use local tension inference. This local inference is informative about the relative tension of one interface to its four neighbors. The focus on this local level is justified because we are interested in local cell behaviors, namely rearrangements. Tension inference is also most robust on the local level, since this is where force balance, the underlying physical determinant of the link between mechanics and geometry, resides. In global tension inference, spurious large scale gradients can appear when small deviations from local force balance accumulate over large distances. We have added a paragraph in SI Sec. 1.4 to explain these points.

-Fig 2 : how should one interpret that tension after passive intercalation (amnioserosa) is higher than before. On fig 2E, tension has not converged yet on the plot, what happens after 20 minutes ?

Recall that the inferred tension is the total tension on an interface. While on contracting interfaces, the majority of this tension will be actively generated by myosin motors, on extending interfaces there is also a contribution carried by passive crosslinkers. The passive tension can be effectively viewed as viscous dissipation on the elongating interface as crosslinkers turn over (Clement et al. 2017). Note that this passive tension is explicitly accounted for in the model presented in Fig. 5. Notably, it is crucial for the T1 process to resolve in a new extending junction. In the amnioserosa, the tension post T1 remains elevated because the amnioserosa is continually stretched by the convergence of the germ band. The tension hence does not necessarily converge back to 1. However, our estimates for the tension after 20 mins post T1 are very noisy because most of the T1s happen relatively late in the movie (past the 25 min mark) and therefore there are only a few T1s where we can track the post-T1 dynamics for more than 20 mins.

We have added a brief explanation of the high post-T1 tension at the end of the section entitled “Relative tension dynamics distinguishes active and passive intercalations”. Further, we have moved up the section describing the minimal model right after the analysis of the relative tension during intercalations. We believe that this helps the reader better understand these findings before moving on to the tension-isogonal decomposition which generalizes them to the tissue scale.

Page 7-8 / Figure 3: It is unclear how the decomposition into 1) physical shape 2) tension shape 2) isogonal shape works exactly. A more detailed explanation and more clear illustration of what a quartet is and its labels could help.

We have added a more detailed explanation in the main text. See our response to the longer question regarding this point below.

-What exactly defines the boundary curve in figure 3E? How is it computed?

We have added a sentence in the caption for Fig. 3E explaining that the boundary curve is found by solving Eq. (1) with l set to zero for the case of a symmetric quartet. We have also added a brief explanation immediately below Eq. (1) pointing out that this equation defines the T1 threshold in the space of local tensions T_i in terms of the isogonal length l_iso.

-The authors should consider incorporating some details described in the SI file to the main text to clarify some points, as long as the accessible style of the manuscript can be kept. The points mentioned below may also be clarified in the SI doc. The specific points that could be elaborated are: Page 7-8 / Figure 3: It is unclear how the decomposition into 1) physical shape 2) tension shape 2) isogonal shape works exactly. A more detailed explanation and more clear illustration of what a quartet is and its labels could help. The mapping to Maxwell-Cremona space is fine, but which subset is the quartet? For a set of 4 cells with two shared vertices and a junction, aren't there 5 different tension vectors? Are we talking two closed force triangles? Separately, how do you exactly decompose the deformation (of 4 full cell shapes or a subset?) into isogonal and non-isogonal parts? What is the least squares fit done over - is this system underdetermined? Is this statistically averaged or computed per quartet and then averaged?

We thank the referees for pointing us to unclear passages in our presentation. We hope that our revisions have resolved the referee’s questions. As described above, we have clarified the tension-isogonal decomposition in the main text. We have also revised the corresponding SI section (1.5) to address the above questions. A sketch of the quartet with labels is found in SI Fig. S7A which we now refer to explicitly in the main text.

We always consider force-balance configurations, i.e. closed force triangles. Therefore in the “kite” formed by two adjacent tension triangles, only three tension vectors are independent.

The decomposition of deformation is performed as follows: For each of the four cells, the center of mass c_i is calculated. Next, tension inference is performed to find the two tension triangles with tension vectors T_ij. Now there are three independent centroidal vectors c_j - c_i and three corresponding independent tension vectors T_ij. We define the isogonal deformation tensor I_quratet as the tensor that maps the centroidal vectors to the tension vectors. In general this is not possible exactly, because I_quartet has only three independent components, but there are six equations.

The plots in Fig. 3C, C’ are obtained by performing this decomposition for each intercalating quartet individually. The data is then aligned in time and ensemble averages are calculated for each timepoint.

For tissue-scale analysis in Fig. 6, the decomposition is performed for individual vertices (i.e. the corresponding centroidal and tension triangles) and then averaged locally to find the isogonal strain fields shown in Fig. 6B, B’.

- Line 468: "Therefore, tissue-scale anisotropy of active tension is central to drive and orient convergent-extension flow [10, 57, 59, 60]." Authors almost never mention the contribution of the PMG to tissue extension. Yet it is known to be crucial (convergent extension in Tor mutants is very much affected). Please discuss this point further.

The referees raise an important point: as discussed in our response to major point (2), we now explicitly discuss the role of internal (active tension) and external (PMG pulling) forces during germ band extension. Please see our response to major point (2) for the changes we made to the manuscript to address this.

In particular, we now explain that in mutants where PMG invagination is impaired (fog, torso-like, torso, scab, corkscrew), the germ band buckles out of plane or extends in a twisted, corkscrew fashion (Smits et al. 2023). This shows that the germ band generates extensile forces largely internally. In torso mutants, the now stationary PMG acts as a barrier which blocks GBE extension; the germ band buckles as a response.

The role of PMG invagination hence lies not in creating pulling forces to extend the germ band, but rather in “making room” to allow for its orderly extension. As shown by the genetics mutants just discussed, the synchronization of PMG invagination and GBE is crucial for successful gastrulation.

-Typos:

Line 74: how are intercalations are

Line 84: vertices vertices

Line 233: very differently

Line 236: are can

Line 390: energy which is the isogonal mode must

Line 1585: reveals show

Line 603: area Line 618: in terms of on the

We have fixed these typos.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

This valuable study revisits the effects of substitution model selection on phylogenetics by comparing reversible and non-reversible DNA substitution models. The authors provide evidence that 1) non time-reversible models sometimes perform better than general time-reversible models when inferring phylogenetic trees out of simulated viral genome sequence data sets, and that 2) non time-reversible models can fit the real data better than the reversible substitution models commonly used in phylogenetics, a finding consistent with previous work. However, the methods are incomplete in supporting the main conclusion of the manuscript, that is that non time-reversible models should be incorporated in the model selection process for these data sets.

The non-reversible models should be incorporated in the selection model process not because the significantly perform better but only because the do not perform worse than the reversible models and that true biochemical processes of nucleotide substitution does support the science of non-reversibility.

Reviewer #1 (Public Review):

The study by Sianga-Mete et al revisits the effects of substitution model selection on phylogenetics by comparing reversible and non-reversible DNA substitution models. This topic is not new, previous works already showed that non-reversible, and also covarion, substitution models can fit the real data better than the reversible substitution models commonly used in phylogenetics. In this regard, the results of the present study are not surprising. Specific comments are shown below.

True.

Major comments

It is well known that non-reversible models can fit the real data better than the commonly used reversible substitution models, see for example,

https://academic.oup.com/sysbio/article/71/5/1110/6525257

https://onlinelibrary.wiley.com/doi/10.1111/jeb.14147?af=R

The manuscript indicates that the results (better fitting of non-reversible models compared to reversible models) are surprising but I do not think so, I think the results would be surprising if the reversible models provide a better fitting.

I think the introduction of the manuscript should be increased with more information about non-reversible models and the diverse previous studies that already evaluated them. Also I think the manuscript should indicate that the results are not surprising, or more clearly justify why they are surprising.

The surprise in the findings is in NREV12 performing better than NREV6 for double stranded DNA viruses as it was expected that NREV6 would perform better given the biochemical processes discussed in the introduction.

In the introduction and/or discussion I missed a discussion about the recent works on the influence of substitution model selection on phylogenetic tree reconstruction. Some works indicated that substitution model selection is not necessary for phylogenetic tree reconstruction, https://academic.oup.com/mbe/article/37/7/2110/5810088 https://www.nature.com/articles/s41467-019-08822-w https://academic.oup.com/mbe/article/35/9/2307/5040133

While others indicated that substitution model selection is recommended for phylogenetic tree reconstruction, https://www.sciencedirect.com/science/article/pii/S0378111923001774 https://academic.oup.com/sysbio/article/53/2/278/1690801 https://academic.oup.com/mbe/article/33/1/255/2579471

The results of the present study seem to support this second view. I think this study could be improved by providing a discussion about this aspect, including the specific contribution of this study to that.

In our conclusion we have stated that: The lack of available data regarding the proportions of viral life cycles during which genomes exist in single and double stranded states makes it difficult to rationally predict the situations where the use of models such as GTR, NREV6 and NREV12 might be most justified: particularly in light of the poor over-all performance of NREV6 and GTR relative to NREV12 with respect to describing mutational processes in viral genome sequence datasets. We therefore recommend case-by-case assessments of NREV12 vs NREV6 vs GTR model fit when deciding whether it is appropriate to consider the application of non-reversible models for phylogenetic inference and/or phylogenetic model-based analyses such as those intended to test for evidence of natural section or the existence of molecular clocks.

The real data was downloaded from Los Alamos HIV database. I am wondering if there were any criterion for selecting the sequences or if just all the sequences of the database for every studied virus category were analysed. Also, was any quality filter applied? How gaps and ambiguous nucleotides were considered? Notice that these aspects could affect the fitting of the models with the data.

We selected varying number of sequences of the database for every studied virus type. Using the software aliview we did quality filter by re-aligning the sequences per virus type.

How the non-reversible model and the data are compared considering the non-reversible substitution process? In particular, given an input MSA, how to know if the nucleotide substitution goes from state x to state y or from state y to state x in the real data if there is not a reference (i.e., wild type) sequence? All the sequences are mutants and one may not have a reference to identify the direction of the mutation, which is required for the non-reversible model. Maybe one could consider that the most abundant state is the wild type state but that may not be the case in reality. I think this is a main problem for the practical application of non-reversible substitution models in phylogenetics.

True.

Reviewer #2 (Public Review):

The authors evaluate whether non time reversible models fit better data presenting strand-specific substitution biases than time reversible models. Specifically, the authors consider what they call NREV6 and NREV12 as candidate non time-reversible models. On the one hand, they show that AIC tends to select NREV12 more often than GTR on real virus data sets. On the other hand, they show using simulated data that NREV12 leads to inferred trees that are closer to the true generating tree when the data incorporates a certain degree of non time-reversibility. Based on these two experimental results, the authors conclude that "We show that non-reversible models such as NREV12 should be evaluated during the model selection phase of phylogenetic analyses involving viral genomic sequences". This is a valuable finding, and I agree that this is potentially good practice. However, I miss an experiment that links the two findings to support the conclusion: in particular, an experiment that solves the following question: does the best-fit model also lead to better tree topologies?

By NREV12 leading to inferred trees that are closer to the true generating tree as compared to GTR, it then shows that the best-fit model in this case being NREV12 leads to better tree topologies.

On simulated data, the significance of the difference between GTR and NREV12 inferences is evaluated using a paired t test. I miss a rationale or a reference to support that a paired t test is suitable to measure the significance of the differences of the wRF distance. Also, the results show that on average NREV12 performs better than GTR, but a pairwise comparison would be more informative: for how many sequence alignments does NREV12 perform better than GTR?

We have used the popular paired t-test as it is the most widely used when comparing means values between two matched samples where the difference of each mean pair is normally distributed. And the wRF distances do match the guidelines above.

The paired t-test contains the pairwise comparison and the boxplots side by side show the pairwise wRF comparisions..

Reviewer #1 (Recommendations For The Authors):

Minor comments

The reversible and non-reversible models used in this study assume that all the sites evolve under the same substitution matrix, which can be unrealistic. This aspect could be mentioned.

Done.

The manuscript indicates that "a phylogenetic tree was inferred from an alignment of real sequences (Avian Leukosis virus) with an average sequence identity (API) of ~90%.". I was wondering under which substitution model that phylogenetic tree reconstruction was performed? could the use of that model bias posterior results in terms of favoring results based on such a model?

We have stated on page ….. that the GTR+G model was used to reconstruct the tree. The use of the GTR+G model could yes bias the posterior results as we have stated on page ….

I was wondering which specific R function was used to calculate the weighted Robinson-Foulds metric. I think this should be included in the manuscript.

We stated that We used the weighted Robinson-Foulds metric (wRF; implemented in the R phangorn package (Schliep, 2011)⁠)

Despite a minority, several datasets fitted better with a reversible model than with a non-reversible model. I think that should be clearly indicated.

In addition, in my opinion the AIC does not enough penalizes the number of parameters of the models and favors the non-reversible models over the reversible models, but this is only my opinion based on the definition of AIC and it is not supported. Thus, I think the comparison between phylogenetic trees reconstructed under different substitution models was a good idea (but see also my second major comment).

Noted.

When comparing phylogenetic trees I was wondering if one should consider the effect of the estimation method and quality of the studied data? For example, should bootstrap values be estimated for all the ancestral nodes and only ancestral nodes with high support be evaluated in the comparison among trees?

Yes the estimation method and quality of the studied data should be considered. When using RF unlike wRF this will not matter but for weighted RF it does. When building the trees, using RaxML only high support nodes are added to the tree.

In Figure 3, I do not see (by eye) significant differences among the models. I see in the legend that the statistical evaluation was based on a t test but I am not much convinced. Maybe it is only my view. Exactly, which pairs of datasets are evaluated with the t test? Next, I would expect that the influence of the substitution model on the phylogenetic tree reconstruction is higher at large levels of nucleotide diversity because with more substitution events there is more information to see the effects of the model. However, the t test seems to show that differences are only at low levels of nucleotide diversity (and large DNR), what could be the cause of this?

The paired T-tests compares the wRF distances of the inferred tree real tree and the trees simulated using the GTR model verses the wRF distances of the inferred true tree from the trees simulated using the NREV12 model.

The reason why the influence of the NREV12 model on the tree reconstructed is not significantly higher at large levels of nucleotide diversity could be because at a certain level the DNR are simply unrealistic.

Can the user perform substitution model selection (i.e., AIC) among reversible and non-reversible substitution models with IQTREE? If yes, then doing that should be the recommendation from this study, correct?

But, can DNR be estimated from a real dataset? DNR seems to be the key factor (Figure 3) for the phylogenetic analysis under a proper model.

Substitution model selection can be performed among reversible and non-reversible using both HyPhy and IQTREE. And we have recommended that model tests should be done as a first step before tree building. Estimating DNR from real datasets requires a substation rate matrix of a non-reversible.

The manuscript has many text errors (including typos and incorrect citations). For example, many citations in page 20 show "Error! Reference source not found.". I think authors should double check the manuscript before submitting. Also, some text is not formally written. For example, "G represents gamma-distributed rates", rates of what? The text should be clear for readers that are not familiar with the topic (i.e., G represents gamma-distributed substitution rates among sites). In general, I recommend a detailed revision of the whole text of the manuscript.

Done.

Reviewer #2 (Recommendations For The Authors):

The authors reference Baele et al., 2010 for describing NREV6 and NREV12. I suggest using the same name used in the referenced paper: GNR-SYM and GNR respectively. Although I do not think there is a standard name for these models, I would use a previously used one.

We have built studies based on the names NREV6 and NREV12. We would like to keep the naming as standard for our studies.

GTR and NREV12 models are already described in many other papers. I do not see the need to include such an extensive description. Also, a reference should be included to the discrete Gamma rate categories [1]

We included the extensive description to enable other readers who are not super familiar with these models better understanding since we have given the models our own naming different from those used in other papers.

We have added referencing for the discrete gamma rate as recommended. (Yang, 1994)

To evaluate the exhaustiveness and correctness of the results, I would recommend publishing as supplementary material the simulated data sets or the scripts for generating the data set, the scripts or command lines for the analysis, and the versions of the software used (e.g., IQTREE). Also, to strongly support the main conclusion of the manuscript, I suggest adding to the simulations section results the RF-distances of the best-fit selected model under AIC, AICc, and BIC as well.

We can go ahead and submit all the needed datasets. The simulated data RF-Distances results are available and will be submitted. We cannot however add them to the main document as this will create very long data tables.

In some instances, it is mentioned that the selection criterion used is AIC, while in others, AIC-c is referenced. Even in the table captions, both terms are mixed. It should be made clearer which criterion is being employed, as AIC is not suitable for addressing the overparameterization of evolutionary models, given that it does not account for the sample size. A previous pre-print of this article [2] does not mention AIC-c, but also explicitly includes the formulas for AIC that do not take the sample size into account, and reports the same results as this manuscript, what indicates that AIC and not AIC-c was used here. This should be clarified. It is recommended to use AIC-c instead of AIC, especially if the sample size to model parameters ratio is low [3]. Two things may be appointed here: some authors consider tree branch lengths as model free parameters and others do not. In this paper it is not specified how the model parameters are counted. AIC tends to select more parameterized models than AIC-c, and overparameterization can lead to different tree inferences, as evidenced in Hoff et al., 2016. Therefore, it is expected that NREV12 is more frequently selected than NREV6 and GTR.

In my opinion, a pairwise comparison between GTR and NREV12 performance is of great interest here, and the whiskers plots are not useful. Scatterplots would display the results better.

Boxplots are meant to offer a simplified view of the results as the paired t-tests does all of the comparisons. We shall provide the scatter plots as supplementary information so that readers can get full detailed plots as recommended.

Some references are missing

Missing references added

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper seeks to understand the upstream regulation and downstream effectors of glycolysis in retinal progenitor cells, using mouse retinal explants as the main model system. The paper presents evidence that high glycolysis in retinal progenitor cells is required for their proliferation and timely differentiation into photoreceptors. Retinal glycolysis increases after the deletion of Pten. The authors suggest that high glycolysis controls cell proliferation and differentiation by promoting intracellular alkalinization, beta-catenin acetylation and stabilization, and consequent activation of the canonical Wnt pathway.

Strengths:

(1) The experiments showing that PFKFB3 overexpression is sufficient to increase the proliferation of retinal progenitors (which are already highly dividing cells) and photoreceptor differentiation are striking and the result is unanticipated. It suggests that glycolytic flux is normally limiting for proliferation in embryos.

In our BrdU birthdating experiment, we showed that PFKB3 expression drives the precocious differentiation of retinal progenitor cells (RPCs) into photoreceptors. However, we did not determine if there is an associated change in the number of dividing RPCs. To examine the proliferative status of PFKB3-overexpressing RPCs, we will perform short-term BrdU labeling to measure the number of RPCs in S-phase of the cell cycle. Additionally, we will count the number of RPCs expressing pHH3, a mitotic marker, and Ki67, a marker of cycling cells in all cell cycle phases.

(2) Likewise the result that an increase in pH from 7.4 to 8.0 is sufficient to increase proliferation implies that pH regulation may have instructive roles in setting the tempo of retinal development and embryonic cell proliferation. Similarly, the results show that acetate supplementation increases proliferation (I think this result should be moved to the main figures).

We thank the reviewer for these positive comments on our work. We will move the acetate data to the main figure as requested.

Weaknesses:

(1) Epistatic experiments to test if changes in pH mediate the effects of glycolysis on photoreceptor differentiation, or if Wnt activation is the main downstream effector of glycolysis in controlling differentiation are not presented.

Traditionally, epistasis is tested using double knock-out (DKO) studies with null mutant alleles. If two genes operate in the same pathway, the downstream phenotype prevails, whereas phenotypic worsening is observed if two genes act in parallel pathways. Our data suggests the following order of events: Pten¯®glycolysis­®intracellular pH­®Wnt signaling­®photoreceptor differentiation. In this model, Wnt signaling is the downstream-most effector. To test our epistatic model, we will assess RPC proliferation and the differentiation of Crx+ photoreceptor precursors with the following assays:

(1) To confirm that Wnt signaling acts downstream of Pten, we will generate DKOs of Pten and Ctnnb1, a downstream effector of Wnt signaling. We know that fewer photoreceptors are generated in single Pten-cKO and Ctnnb1-cKO retinas, with a disruption of the outer nuclear layer only in Ctnnb1-cKOs. If Pten and Wnt act in the same pathway, Pten;Ctnnb1 DKOs will resemble single Ctnnb1-cKOs.

(2) While epistasis is traditionally examined using genetic mutants, we will perform proxy experiments using pharmacological agents. To test whether Wnt activation acts downstream of a pH increase, we will activate Wnt signaling with recombinant Wnt3a at high and low pH. While low pH inhibits photoreceptor differentiation, if Wnt signaling is downstream, it should promote differentiation even at low pH. Conversely, we will alter pH in the presence of a Wnt inhibitor, FH535, which should block the positive effects of high pH on photoreceptor differentiation.

(3) To test whether Wnt activation acts downstream of glycolysis to increase photoreceptor differentiation, we will apply recombinant Wnt3a to retinal explants while simultaneously inhibiting glycolysis with 2DG.  While 2DG inhibits photoreceptor differentiation, if Wnt signaling is downstream, it should still be able to promote differentiation. 

(4) To test whether pharmacological inhibition of Wnt signaling reverses the effects of high glycolytic activity in Pten cKO retinas, we will treat wild-type and Pten-cKO retinas with the Wnt inhibitor FH535 and/or the glycolytic inhibitor 2DG.

(2) It is likely that metabolism changes ex vivo vs in vivo, and therefore stable isotope tracing experiments in the explants may not reflect in vivo metabolism.

We agree with the reviewer that metabolism likely changes ex vivo compared to in vivo. However, we did not perform stable isotope tracing experiments to directly examine glycolytic flux in this study. While outside the scope of the current study, this type of analysis is an important future direction that we will bring up in the discussion.

(3) The retina at P0 is composed of both progenitors and differentiated cells. It is not clear if the results of the RNA-seq and metabolic analysis reflect changes in the metabolism of progenitors, or of mature cells, or changes in cell type composition rather than direct metabolic changes in a specific cell type.

We mined a scRNA-seq dataset to show that Pgk1, a rate-limiting enzyme for glycolysis, is specifically elevated in early-stage RPCs versus later stage. We have since analysed additional glycolytic pathway genes, and observed a similar enrichment of Pfkl, Eno1 and Slc16a3 transcripts in early RPCs, while other genes were equally expressed in both early and late RPCs.

To functionally demonstrate that there are differences in glycolysis between early and late RPCs, we will use CD133 to sort RPCs at E15 (early) and P0 (late). We will perform qPCR on sorted cells to validate the transcriptional differences in glycolytic gene expression. Additionally, we will perform two proxy measures of glycolysis: 1) We will measure lactate levels in sorted RPCs at both stages, and 2) We will use a Seahorse assay and assess ECAR in sorted RPCs at both stages.

(4) The biochemical links between elevated glycolysis and pH and beta-catenin stability are unclear. White et al found that higher pH decreased beta-catenin stability (JCB 217: 3965) in contrast to the results here. Oginuma et al found that inhibition of glycolysis or beta-catenin acetylation does not affect beta-catenin stability (Nature 584:98), again in contrast to these results. Another paper showed that acidification inhibits Wnt signaling by promoting the expression of a transcriptional repressor and not via beta-catenin stability (Cell Discovery 4:37). There are also additional papers showing increased pH can promote cell proliferation via other mechanisms (e.g. Nat Metab 2:1212). It is possible that there is organ-specificity in these signaling pathways however some clarification of these divergent results is warranted.

The pleiotropic actions of Wnt signaling on cell proliferation and differentiation are well known, even shifting from pro-proliferative to anti-proliferative depending on tissue or cell type. It is thus not surprising that different studies found unique effects of pH and glycolysis on b-catenin modifications and the activation of downstream signaling. Thus, as suggested by the reviewer, the difference between our data and other studies could be attributed to tissue and organism. In our revision, we will more fully assess our findings in the context of published studies, as recommended by the reviewer.

To summarize our data, in the developing retina, we found that non-phosphorylated b-catenin protein levels increase in Pten-cKO retinas in vivo, while conversely, non-phosphorylated b-catenin protein levels decrease upon 2DG treatment and at low pH 6.5 in vitro.

The Oginuma et al. 2020 (Nature 584: 98-101) study was performed on the chick tailbud and investigated lineage decisions by neuromesodermal progenitors in the presomitic mesoderm. In this context, WNT activity, glycolysis and pHi all decline in tandem, complementary to our findings. However, Oginuma et al. found that while phosphorylated and non-phosphorylated b-catenin levels do not vary, K49 b -catenin acetylation is reduced at low pHi. In their system, K49 b -catenin acetylation is associated with a switch in cell fate choice from neural to mesodermal in the chick tailbud. We will now assess this modification.

Hauck et al. 2021 (Cell Death & Differentiation 28:1398-1417) found that by mutating Pkm, a rate-limiting glycolytic enzyme, b-catenin can more efficiently shuttle to the nucleus to activate Wnt-signaling and promote cardiomyocyte proliferation. This study highlights the importance of examining b-catenin protein levels in both cytoplasmic and nuclear fractions. They also examined transcriptional targets of Wnt signaling, such as Axin2, Ccnd1, Myc, Sox2 and Tnnt3, which we will also now assess.

In a separate study in cancer cells, high pH leads to increased expression of Ccnd1, a b-catenin target gene, and promotes proliferation (Koch et al. 2020. Nat Metab. 2:1212-1222). These findings are consistent with our demonstration that b-catenin levels are stabilized at pH 8, and RPC proliferation is enhanced. A separate study by Melnik et al 2018 (Cell Discovery 4:37) performed in cancer cells found that acidification induced by metformin indirectly suppresses Wnt signaling by activating the DDIT3 transcriptional repressor, consistent with our data showing low pH suppresses b-catenin stability. Melnik et al also used Mcl inhibitors, as we did in our study, and showed that this treatment blocked Wnt signaling. While we did not look at the impact of CNCn on Wnt signaling, we did see a decline in proliferation, as expected if Wnt levels are low. The relationship between CNCn and Wnt activity will now be assessed.

The one study that fits less well is from Czowski and White (BioRxiv), where they found that higher pH levels decrease b-catenin levels in the cytoplasm, nucleus and junctional complexes in MDCK cells. In this study, the authors altered pH using inhibitors for a sodium-proton exchanger and a sodium bicarbonate transporter. The Oginuma paper instead used the ionophores nigericin and valinomycin to equilibrate intracellular pHi to media pH, which we will now incorporate into our study.

In summary, to more comprehensively examine the link between Pten loss, glycolytic activity, pHi and Wnt signaling, we will examine levels of phosphorylated, non-phosphorylated and K49 acetylated b-catenin after each manipulation (i.e., Pten loss, pH manipulations, CNCn treatment, glycolysis inhibition, acetate treatments). For pH manipulations, we will use nigericin and valinomycin to equilibrate pH. These studies will be performed on cytoplasmic and nuclear fractions from CD133+ MACS-enriched RPCs, to add cell type and stage specificity to our study. We will also use qPCR to examine Wnt signaling genes, such as Axin2, Ccnd1, Myc, Sox2 and Tnnt3.

(5) The gene expression analysis is not completely convincing. E.g. the expression of additional glycolytic genes should be shown in Figure 1. It is not clear why Hk1 and Pgk1 are specifically shown, and conclusions about changes in glycolysis are difficult to draw from the expression of these two genes. The increase in glycolytic gene expression in the Pten-deficient retina is generally small.

See response to point 3.

(6) Is it possible that glycolytic inhibition with 2DG slows down the development and production of most newly differentiated cells rather than specifically affecting photoreceptor differentiation?

We thank the reviewer for this excellent suggestion. We will examine the impact of  2DG on the differentiation of other retinal cell types, including bipolar and amacrine cells and Muller glia. For technical reasons, we will exclude ganglion cells, which die in culture and are not possible to examine in explants, and horizontal cells, which are a rare cell type, and hence, difficult to accurately quantify.

(7) Are the prematurely-born cells caused by PFKFB3 overexpression photoreceptors as assessed by morphology or markers (in addition to position)?

We will immunostain treated retinas with additional cell-type specific markers to examine rod and cone photoreceptor numbers and morphologies.

Reviewer #2 (Public review):

Summary:

The manuscript by Hanna et al., addresses the question of energy metabolism in the retina, a neuronal tissue with an inordinately high energy demand. Paradoxically, the retina appears to employ to a large extent glycolysis to satisfy its energetic needs, even though glycolysis is far less efficient than oxidative phosphorylation (OXPHOS). The focus of the present study is on the early development of the retina and the retinal progenitor cells (RPCs) that proliferate and differentiate to form the seven main classes of retinal neurons. The authors use different genetic and pharmacological manipulations to drive the metabolism of RPCs or the retina towards higher or lower glycolytic activity. The results obtained suggest that increased glycolytic activity in early retinal development produces a more rapid differentiation of RPCs, resulting in a more rapid maturation of photoreceptors and photoreceptor segment growth. The study is significant in that it shows how metabolic activity can determine cell fate decisions in retinal neurons.

Strengths:

This study provides important findings that are highly relevant to the understanding of how early metabolism governs the development of the retina. The outcomes of this study could be relevant also for human diseases that affect early retinal development, including retinopathy of maturity where an increased oxygenation likely causes a disturbance of energy metabolism.

We thank the reviewer for these positive comments on our study.

Weaknesses:

The restriction to only relatively early developmental time points makes it difficult to assess the consequences of the different manipulations on the (more) mature retina. Notably, it is conceivable that early developmental manipulations, while producing relevant effects in the young post-natal retina, may "even out" and may no longer be visible in the mature, adult retina.

While we agree that it would be interesting to observe the long-term consequences of our manipulations, we are limited by our retinal explant model, which can at best be cultured for 2 weeks in vitro. Additional limitations include the lack of photoreceptor outer segment development in our in vitro model. However, we can perform more extensive analyses of our genetic models in vivo (i.e., Pten-cKO, cyto-PFKB3-GOF, Ctnnb1-cKO). For these lines, we will focus on more in-depth analyses of photoreceptor differentiation and outer segment maturation using additional markers and one later stage of development.

Reviewer #3 (Public review):

Summary:

This study examines the metabolic regulation of progenitor proliferation and differentiation in the developing retina. The authors observe dynamic changes in glycolytic gene expression in retinal progenitors and use various strategies to test the role of glycolysis. They find that elevated glycolysis in Pten-cKO retinas results in alteration of RPC fate, while inhibition of glycolysis has converse effects. They specifically test the role of elevated glycolysis using dominant active cytoPFKB3, which demonstrates the selective effects of elevated glycolysis on progenitor proliferation and rod differentiation. They then show that elevated glycolysis modulates both pHi and Wnt signaling, and provide evidence that these pathways impact proliferation and differentiation of progenitors, particularly affecting rod photoreceptor differentiation.

Strengths:

This is a compelling and rigorous study that provides an important advance in our understanding of metabolic regulation of retina development, addressing a major gap in knowledge. A key strength is that the study utilizes multiple genetic and pharmacological approaches to address how both increased or decreased glycolytic flux affect retinal progenitor proliferation and differentiation. They discover elevated Wnt signaling pathway genes in Pten cKO retina, revealing a potential link between glycolysis and Wnt pathway activation. Altogether the study is comprehensive and adds to the growing body of evidence that regulation of glycolysis plays a key role in tissue development.

We thank the reviewer for these positive comments on our study.

Weaknesses:

(1) Following the expression of cytoPFKB3, which results in increased glycolytic flux, BrDU labeling was performed at e12.5 and increased labeled cells were detected in the outer nuclear layer. However whether these are cones or rods is not established. The rest of the analysis is focused on the precocious maturation of rhodopsin-labeled outer segments, and the major conclusions emphasize rod photoreceptor differentiation. Therefore, it is unclear whether there is an effect on cone differentiation for either Pten cKO or cytoPFKB3 transgenic retina. It is also not established whether rods are born precociously. Presumably, this would be best detected by BrDU labeling at later embryonic stages.

We agree with the reviewer that we should expand our study to also examine cone differentiation and outer segment maturation, which we will now do by adding additional markers to our study.

(2) The authors find that there is upregulation of multiple Wnt pathway components in Pten cKO retina. They further show that inhibiting Wnt signaling phenocopies the effects of reducing glycolysis. However, they do not test whether pharmacological inhibition of Wnt signaling reverses the effects of high glycolytic activity in Pten cKO retinas. Thus the argument that Wnt is a key downstream effector pathway regulating rod photoreceptor differentiation is weak.

See Reviewer 1, point 1

(3) The use of sodium acetate to force protein acetylation is quite non-specific and will have effects beyond beta-catenin acetylation (which the authors acknowledge). Thus it is a stretch to state that "forced activation of beta-catenin acetylation" mimics the impact of Pten loss/high glycolytic activity in RPCs since the effects could be due to acetylation of other proteins.

As outlined in our response to Reviewer #1, point 4, we will now assess K49 b-catenin acetylation levels, as conducted by Oginuma et al. This analysis will allow us to determine whether b-catenin acetylation is altered with manipulations of Pten, glycolysis, pH or acetate treatments.

Author response:

The following is the authors’ response to the original reviews.

Reviewer 1：

One major issue arises in Figure 4, the recording of VLPO Ca2+ activity. In Lines 211-215, they stated that they injected AAV2/9-DBH-GCaMP6m into the VLPO, while activating LC NE neurons. As they claimed in line 157, DBH is a specific promoter for NE neurons. This implies an attempt to label NE neurons in the VLPO, which is problematic because NE neurons are not present in the VLPO. This raises concerns about their viral infection strategy since Ca activity was observed in their photometry recording. This means that DBH promoter could randomly label some non-NE neurons. Is DBH promoter widely used? The authors should list references. Additionally, they should quantify the labeling efficiency of both DBH and TH-cre throughout the paper.

In Figure 5, we found that the VLPO received the noradrenergic projection from LC, indicating the recorded Ca2+ activity may come from the axon fibers corresponding to the projection. Similarly, Gunaydin et al. (2014) demonstrated that fiber photometry can be used to selectively record from neuronal projection.

We appreciate the reviewer's insightful suggestion to elaborate on the DBH promoter, we have now expanded our discussion to address the DBH (pg. 18): “DBH (Dopamine-beta-hydroxylase), located in the inner membrane of noradrenergic and adrenergic neurons, is an enzyme that catalyzes the conversion of dopamine to norepinephrine, and therefore plays an important role in noradrenergic neurotransmission. DBH is a marker of noradrenergic neurons. Zhou et al. (2020) clarified the probe specifically labeled noradrenergic neurons by immunolabeling for DBH. Recently, DBH promoter have been used in several studies (e.g., Han et al., 2024; Lian et al., 2023). The DBH-Cre mice are widely used to specifically labeled noradrenergic neurons (e.g., Li et al., 2023; Breton-Provencher et al., 2022; Liu et al., 2024). It is difficult to distinguish the role of NE or DA neurons when using the TH promoter in VLPO. Therefore, we used DBH promoter with more specific labeling. LC is the main noradrenergic nucleus of the central nervous system. In our study, we injected rAAV-DBH-GCaMP6m-WPRE (Figure 2 and 8) and rAAV-DBH-EGFP-S'miR-30a-shRNA GABAA receptor)-3’-miR30a-WPRES (Figure 9) into the LC. The results showed that DBH promoter could specifically label noradrenergic neurons in the LC, while non-specific markers outside the LC were almost absent.”

As suggested, we have quantified the labeling efficiency of both DBH and TH-cre throughout the revised manuscript (Fig.2D; Fig.3D, N-O; Fig.4E-F, J, L; Fig.5E, L; Fig.6L, S, X; Fig.7G).

A similar issue arises with chemogenetic activation in Fig. 5 L-R, the authors used TH-cre and DIO-Gq virus to label VLPO neurons. Were they labelling VLPO NE or DA neurons for recording? The authors have to clarify this.

As previously addressed in response to Comment #1, we agree that it is difficult to distinguish the role of NE or DA neurons when using the TH promoter in the VLPO. Therefore, we injected the mixture of DBH-Cre-AAV and AAV-EF1a-DIO-hChR2(H134R)-eYFP/AAV-Ef1a-DIO-hM3Dq-mCherry viruses into bilateral LC and AAV-EF1a-DIO-hChR2(H134R)-eYFP/AAV-Ef1a-DIO-hM3Dq-mCherry virus into bilateral VLPO. Moreover, we quantified the labeling efficiency of DBH in the LC to demonstrate that this promoter can specifically label NE neurons (Fig. 5). Importantly, these corrections did not alter the outcomes of our results. Both photogenetic and chemogenetic activation of LC-NE terminals in the VLPO can effectively promote midazolam recovery (Fig. 5G, N).

Another related question pertains to the specificity of LC NE downstream neurons in the VLPO. For example, do they preferentially modulate GABAergic or glutamatergic neurons?

Our study primarily aimed to explore the role of the LC-VLPO NEergic neural circuit in modulating midazolam recovery. We acknowledge that our evidence for the role of LC NE downstream neurons in the VLPO, derived from activation of LC-NE terminals and pharmacological intervention in the VLPO (Fig.5, Fig.6, Fig.8, Fig.9) is limited. Accordingly, we now present the VLPO’s role as a promising direction for future research in the limitation section of our revised manuscript: “This study shows that the LC-VLPO NEergic neural circuit plays an important role in modulating midazolam recovery. However, the specificity of LC NE downstream neurons in the VLPO is not explained in this paper, which is our next research direction, VLPO neurons and their downstream regulatory mechanisms may be involved in other nervous systems except the NE nervous system, and the deeper and more complex mechanisms need to be further investigated.”

In Figure 1A-D, in the measurement of the dosage-dependent effect of Mida in LORR, were they only performed one batch of testing? If more than one batch of mice were used, error bar should be presented in 1B. Also, the rationale of testing TH expression levels after Mid is not clear. Is TH expression level change related to NE activation specifically? If so, they should cite references.

As recommended, we have supplemented error bar and modified the graph of LORR’s rate in the revised manuscript. (Fig. 1A-B; Fig. 9G-H).

We agree that the use of TH as a marker of NE activation is controversial, so in the revised manuscript, we directly determined central norepinephrine content to reflect the change of NE activity after midazolam administration (Fig. 1D).

Regarding the photometry recording of LC NE neurons during the entire process of midazolam injection in Fig. 2 and Fig. 4, it is unclear what time=0 stands for. If I understand correctly, the authors were comparing spontaneous activity during the four phases. Additionally, they only show traces lasting for 20s in Fig. 2F and Fig. 4L. How did the authors select data for analysis, and what criteria were used? The authors should also quantify the average Ca2+ activity and Ca2+ transient frequency during each stage instead of only quantifying Ca2+ peaks. In line 919, the legend for Figure 2D, they stated that it is the signal at the BLA; were they also recorded from the BLA?

In this study, we used optical fiber calcium signal recording, which is a fluorescence imaging based on changes in calcium. The fluorescence signal is usually divided into different segments according to the behavior, and the corresponding segments are orderly according to the specific behavior event as the time=0. The mean calcium fluorescence signal in the time window 1.5s or 1s before the event behavior is taken as the baseline fluorescence intensity (F0), and the difference between the fluorescence intensity of the occurrence of the behavior and the baseline fluorescence intensity is divided by the difference between the baseline fluorescence intensity and the offset value. That is, the value ΔF/F0 represents the change of calcium fluorescence intensity when the event occurs. The results of the analysis are commonly represented by two kinds of graphs, namely heat map and event-related peri-event plot (e.g., Cheng et al., 2022; Gan-Or et al., 2023; Wei et al., 2018). In Fig. 2, the time points for awake, midazolam injection, LORR and RORR in mice were respectively selected as time=0, while in Fig. 4, RORR in mice was selected as time=0. The selected traces lasting for 20s was based on the length of a complete Ca2+ signal. We have explained the Ca2+ recording experiment more specifically in the figure legends and methods sections of our revised manuscript.

To the BLA, we sincerely apologize for our carelessness, the signal we recorded were from the LC rather than the BLA. We have carefully checked and corrected similar problems in the revised manuscript.

Reviewer 2：

In figure legends, abbreviations in figure should be supplemented as much as possible. For example, "LORR" in Figure 1.

As suggested, we have supplemented abbreviations in figure as much as possible in the revised manuscript.

Additional recommendations:

The main conceptual issue in the paper is the inflation of the conclusion regarding the mechanism of sedation induced by midazolam. The authors did not reveal the full mechanism of this but rather the relative contribution of NE system. Several conclusions in the text should be edited to take into account this starting from the title. I think the following examples are more appropriate: "NE contribution to rebooting unconsciousness caused by midazolam' or 'NE contribution to reverse the sedation induced by midazolam'.

As suggested, we have moderated the assertions about the mechanism of sedation induced by midazolam in several conclusions starting from the title (Line 1,125,150,169,202,237,482), to present a more measured interpretation in the manuscript.

Line 178-179, the authors state 'these suggest that intranuclear ... suppresses recovery from midazolam administration'. In fact, this intervention prolonged or postponed recovery from midazolam.

In our revised manuscript, we have corrected this inappropriate term (Line 178).

Pharmacology part (page 12) that aimed to pinpoint which NE receptor is implicated would suffer from specificity issues.

In relation to the specificity issue, the focus on VLPO might be rational but again other areas are most likely involved given the pharmacological actions of midazolam.

In the revised manuscript, we have discussed those specificity issues of NE receptor and areas involved throughout the midazolam-induced altered consciousness: “In addition, given the pharmacological actions of midazolam, other areas may also be involved. Current studies suggest that the neural network involved in the recovery of consciousness consists of the prefrontal cortex, basal forebrain, brain stem, hypothalamus and thalamus. The role of these regions in midazolam recovery remains to be further investigated. Therefore, we will apply more specific experimental methods to determine the importance of LC-VLPO NEergic neural circuit and related NE receptors in the midazolam recovery, and conduct further studies on other relevant brain neural regions, hoping to more fully elucidate the mechanism of midazolam recovery in the future”.

Line 274, the authors used 'inhibitory EEG activity'. what does it mean? a description of which rhythm-related power density is affected would be more objective.

Example of conclusion inflation: in line 477, the word 'contributes' is better than 'mediates' if the specificity issue is taken into account.

As suggested, we have improved our expression of words in our revised manuscript (pg. 13-14).

References

Gunaydin LA, Grosenick L, Finkelstein JC, et al. Natural neural projection dynamics underlying social behavior. Cell. 2014;157(7):1535-1551. doi:10.1016/j.cell.2014.05.017

Zhou N, Huo F, Yue Y, Yin C. Specific Fluorescent Probe Based on "Protect-Deprotect" To Visualize the Norepinephrine Signaling Pathway and Drug Intervention Tracers. J Am Chem Soc. 2020;142(41):17751-17755. doi:10.1021/jacs.0c08956

Han S, Jiang B, Ren J, et al. Impaired Lactate Release in Dorsal CA1 Astrocytes Contributed to Nociceptive Sensitization and Comorbid Memory Deficits in Rodents. Anesthesiology. 2024;140(3):538-557. doi:10.1097/ALN.0000000000004756

Lian X, Xu Q, Wang Y, et al. Noradrenergic pathway from the locus coeruleus to heart is implicated in modulating SUDEP. iScience. 2023;26(4):106284. Published 2023 Feb 27. doi:10.1016/j.isci.2023.106284

Li C, Sun T, Zhang Y, et al. A neural circuit for regulating a behavioral switch in response to prolonged uncontrollability in mice. Neuron. 2023;111(17):2727-2741.e7. doi:10.1016/j.neuron.2023.05.023

Breton-Provencher V, Drummond GT, Feng J, Li Y, Sur M. Spatiotemporal dynamics of noradrenaline during learned behaviour. Nature. 2022;606(7915):732-738. doi:10.1038/s41586-022-04782-2

Liu Q, Luo X, Liang Z, et al. Coordination between circadian neural circuit and intracellular molecular clock ensures rhythmic activation of adult neural stem cells. Proc Natl Acad Sci U S A. 2024;121(8):e2318030121. doi:10.1073/pnas.2318030121

Cheng J, Ma X, Li C, et al. Diet-induced inflammation in the anterior paraventricular thalamus induces compulsive sucrose-seeking. Nat Neurosci. 2022;25(8):1009-1013. doi:10.1038/s41593-022-01129-y

Gan-Or B, London M. Cortical circuits modulate mouse social vocalizations. Sci Adv. 2023;9(39):eade6992. doi:10.1126/sciadv.ade6992

Wei YC, Wang SR, Jiao ZL, et al. Medial preoptic area in mice is capable of mediating sexually dimorphic behaviors regardless of gender. Nat Commun. 2018;9(1):279. Published 2018 Jan 18. doi:10.1038/s41467-017-02648-0

Reviewer #3 (Public review):

Summary:

This study used transcranial direct current stimulation administered using small 'high-definition' electrodes to modulate neural activity within the non-human primate prefrontal cortex during both wakefulness and anaesthesia. Functional magnetic resonance imaging (fMRI) was used to assess the neuromodulatory effects of stimulation. The authors report on the modification of brain dynamics during and following anodal and cathodal stimulation during wakefulness and following anodal stimulation at two intensities (1 mA, 2 mA) during anaesthesia. This study provides some possible support that prefrontal direct current stimulation can alter neural activity patterns across wakefulness and sedation in monkeys. However, the reported findings need to be considered carefully against several important methodological limitations.

Strengths:

A key strength of this work is the use of fMRI-based methods to track changes in brain activity with good spatial precision. Another strength is the exploration of stimulation effects across wakefulness and sedation, which has the potential to provide novel information on the impact of electrical stimulation across states of consciousness.

Weaknesses:

The lack of a sham stimulation condition is a significant limitation, for instance, how can the authors be sure that results were not affected by drowsiness or fatigue as a result of the experimental procedure?

In the anaesthesia condition, the authors investigated the effects of two intensities of stimulation (1 mA and 2 mA). However, a potential confound here relates to the possibility that the initial 1 mA stimulation block might have caused plasticity-related changes in neural activity that could have interfered with the following 2 mA block due to the lack of a sufficient wash-out period. Hence, I am not sure any findings from the 2 mA block can really be interpreted as completely separate from the initial 1 mA stimulation period, given that they were administered consecutively. Several previous studies have shown that same-day repeated tDCS stimulation blocks can influence the effects of neuromodulation (e.g., Bastani and Jaberzadeh, 2014, Clin Neurophysiol; Monte-Silva et al., J. Neurophysiology).

The different electrode placement for the two anaesthetised monkeys (i.e., Monkey R: F3/O2 montage, Monkey N: F4/O1 montage) is problematic, as it is likely to have resulted in stimulation over different brain regions. The authors state that "Because of the small size of the monkey's head, we expected that tDCS stimulation with these two symmetrical montages would result in nearly equivalent electric fields across the monkey's head and produce roughly similar effects on brain activity"; however, I am not totally convinced of this, and it really would need E-field models to confirm. It is also more likely that there would in fact be notable differences in the brain regions stimulated as the authors used HD-tDCS electrodes, which are generally more focal.

Given the very small sample size, I think it is also important to consider the possibility that some results might also be impacted by individual differences in response to stimulation. For instance, in the discussion (page 9, paragraph 2) the authors contrast findings observed in awake animals versus anaesthetised animals. However, different monkeys were examined for these two conditions, and there were only two monkeys in each group (monkeys J and Y for awake experiments [both male], and monkeys R and N [male and female] for the anaesthesia condition). From the human literature, it is well known that there is a considerable amount of inter-individual variability in response to stimulation (e.g., Lopez-Alonso et al., 2014, Brain Stimulation; Chew et al., 2015, Brain Stimulation), therefore I wonder if some of these differences could also possibly result from differences in responsiveness to stimulation between the different monkeys? At the end of the paragraph, the authors also state "Our findings also support the use of tDCS to promote rapid recovery from general anesthesia in humans...and suggest that a single anodal prefrontal stimulation at the end of the anesthesia protocol may be effective." However, I'm not sure if this statement is really backed-up by the results, which failed to report "any behavioural signs of awakening in the animals" (page 7)?

Author response:

We are pleased that the reviewers found our study thought-provoking and appreciate the care they have taken in providing constructive feedback. Focusing on the main issues raised by the reviewers, we provide here a provisional response to the Public Comments and outline our revision plan.

A) Reviewers 1 and 2 were concerned that our task and analyses were limited by the fact that we only tested the model based on biases in movement direction (angular biases) and did not examine biases in movement extent (radial biases).

While we think the angular biases provide a sufficient test to compare the set of models presented in the paper, we appreciate that there was a missed opportunity to also look at movement extent.  Looking at predictions concerning both movement direction and extent would provide a stronger basis for model comparison. To this end, we will take a two-step approach:

(1) Re-analysis of existing datasets from experiments that involve a pointing task (movements terminate at the target position) rather than a shooting task (movements terminate further than the target distance).  We will conduct a model comparison using these data. 

(2) If we are unable to obtain a suitable dataset or datasets because we cannot access individual data or there are too few participants, we will conduct a new experiment using a pointing task.  We will use these new data to evaluate whether the transformation model can accurately predict biases in both movement direction and extent.

We will incorporate those new results in our revision.

B) Reviewer 3 noted that model fitting was based on group average data. They questioned if this was representative across individuals and how well the model would account for individual patterns of reach biases.

To address this issue, we propose to do the following:

(1) We will first fit the model to individual data in Exp 1 and assess whether a two-peak function, the signature of the transformation model, is characteristic of most the fits. We recognize that the results at the individual level may not support the model.  This could occur because the model is not correct.  Alternatively, the model could be correct but difficult to evaluate at the individual level for several reasons. First, the data set may be underpowered at the individual level. Second, motor biases can be idiosyncratic (e.g., within subject correlation is greater than between subject correlation), a point we noted in the original submission. Third, as observed in previous studies, transformation biases also show considerable individual variability (Wang et al, 2020); as such, even if the model is correct, a two-peaked function may not hold for all individuals.

(2) If the individual variability is too large to draw meaningful conclusions, we will conduct a new experiment in which we measure motor and proprioceptive biases. Our plan would be to collect a large data set from a limited number of participants.  These data should allow us to evaluate the models on an individual basis, including using each participant’s own transformation/proprioceptive bias function to predict their motor biases.

C) The reviewers have comments regarding the assumptions and form of the different models. Reviewer 3 questioned the visual bias model presented in the paper, and Reviewers 2 and 3 suggested additional visual bias/ biomechanical models to consider.

We agree that what we call a visual bias effect is not confined to the visual modality: It is observed when the target is presented visually or proprioceptively, and in manifest in both reaching movements, saccades, and pressing keys to adjust a dot to match with the remembered target (Kosovicheva & Whitney, 2017; Yousif et al. 2023). As such, the bias may reflect a domain-general distortion in the representation of goals within polar space. We refer to this component as a "visual bias" because it is associated with the representation of the visual target in the reaching task.

We do think the version of the visual bias model in the original submission is reasonable given that the bias pattern has been observed in perceptual tasks with stimuli that were very similar to ours (e.g., Kosovicheva & Whitney, 2017). We have explored other perceptual models in evaluating the motor biases observed in Experiment 1. For example, several models discuss how visual biases may depend on the direction of a moving object or the orientation of an object (Wei & Stocker, 2015; Patten, Mannion & Clifford, 2017). However, these models failed to account for the motor biases observed in our experiments, a not surprising outcome since the models were not designed to capture biases in perceived location.  There are also models of visual basis associated with viewing angle (e.g., based on retina/head position).  Since we allow free viewing, these biases are unlikely to make substantive contributions to the biases observed in our reaching tasks.

Given that some readers are likely to share the reviewers’ concerns on this issue, we will extend our discussion to describe alternative visual models and provide our arguments about why these do not seem relevant/appropriate for our study.

In terms of biomechanical models, we plan to explore at least one alternative model, the MotorNet Model (https://elifesciences.org/articles/88591). This recently published model combines a six-muscle planar arm model with artificial neural networks (ANNs) to generate a control policy. The model has been used to predict movement curvature in various contexts.  We will focus on its utility to predict biases in reaching to visual targets.

D) Reviewer 1 had concerns with how we measured the transformation bias. In particular, they asked why the data from Wang et al (2020) are used as an estimate of transformation biases, and not as the joint effects of visual and proprioceptive biases in the sensed target and hand location, respectively.

We define transformation error as the misalignment between the visual target and the hand position. We quantify this transformation bias by referencing studies that used a matching task in which participants match their unseen hand to a visual target, or vice versa. Errors observed in these tasks are commonly attributed to proprioceptive bias, although they could also reflect a contribution from visual bias. We utilized the same data set to simulate both the transformation bias model and the proprioceptive bias model.

Although it may seem that we are simply renaming concepts, the concept of transformation error addresses biases that arise during motor planning. For the proprioceptive bias model, the bias only influences the perceived start position but not the goal since proprioception will influence the perceived position of the target before the movement begins. In contrast, the transformation bias model proposes that movements are planned toward a target whose location is biased due to discrepancies between visual and proprioceptive representations.

The question then arises whether measurements of proprioceptive bias also reflect a transformation bias. We believe that the transformation bias is influenced by proprioceptive feedback, or at the very least, proprioceptive and transformation bias share a common source of error and thus, are highly correlated. We will revise the Introduction and Results sections to more clearly articulate these relationships and assumptions.

E) Reviewer 3 asked whether the oblique effect in visual perception could account for our motor bias.

The potential link between the oblique effect and the observed motor bias is an intriguing idea, one that we had not considered. However, after giving this some thought, we see several arguments against the idea that the oblique effect accounts for the pattern of motor biases.

First, by the oblique effect, variance is greater for diagonal orientations compared to Cartesian orientations. These differences in perceptual variability can explain the bias pattern in visual perception through a Bayesian efficient coding model (Wei & Stocker, 2015). We note that even though participants showed large variability for stimuli at diagonal orientations, the bias for these stimuli was close to zero. As such, we do not think it can explain the motor bias function given the large bias for targets at locations along the diagonal axes.

Second, the reviewer suggested an "oblique effect" within the motor system, proposing that motor variability is greater for diagonal directions due to increased visual bias. If this hypothesis is correct, a visual bias model should account for the motor bias observed, particularly for diagonal targets. In other words, when estimating the visual bias from a reaching task, a similar bias pattern should emerge in tasks that do not involve movement. However, this prediction is not supported in previous studies. For example, in a position judgment task that is similar to our task but without the reaching response, participants exhibited minimal bias along the diagonals (Kosovicheva & Whitney, 2017).

Despite our skepticism, we will keep this idea in mind during the revision, investigating variability in movement across the workspace.

Reviewer #1 (Public review):

Summary:

In the abstract and throughout the paper, the authors boldly claim that their evidence, from the largest set of data ever collected on inattentional blindness, supports the views that "inattentionally blind participants can successfully report the location, color, and shape of stimuli they deny noticing", "subjects retain awareness of stimuli they fail to report", and "these data...cast doubt on claims that awareness requires attention." If their results were to support these claims, this study would overturn 25+ years of research on inattentional blindness, resolve the rich vs. sparse debate in consciousness research, and critically challenge the current majority view in cognitive science that attention is necessary for awareness.

Unfortunately, these extraordinary claims are not supported by extraordinary (or even moderately convincing) evidence. At best, the results support the more modest conclusion: If sub-optimal methods are used to collect retrospective reports, inattentional blindness rates will be overestimated by up to ~8% (details provided below in comment #1). This evidence-based conclusion means that the phenomenon of inattentional blindness is alive and well as it is even robust to experiments that were specifically aimed at falsifying it. Thankfully, improved methods already exist for correcting the ~8% overestimation of IB rates that this study successfully identified.

Comments:

(1) In experiment 1, data from 374 subjects were included in the analysis. As shown in figure 2b, 267 subjects reported noticing the critical stimulus and 107 subjects reported not noticing it. This translates to a 29% IB rate, if we were to only consider the "did you notice anything unusual Y/N" question. As reported in the results text (and figure 2c), when asked to report the location of the critical stimulus (left/right), 63.6% of the "non-noticer" group answered correctly. In other words, 68 subjects were correct about the location while 39 subjects were incorrect. Importantly, because the location judgment was a 2-alternative-forced-choice, the assumption was that if 50% (or at least not statistically different than 50%) of the subjects answered the location question correctly, everyone was purely guessing. Therefore, we can estimate that ~39 of the subjects who answered correctly were simply guessing (because 39 guessed incorrectly), leaving 29 subjects from the non-noticer group who may have indeed actually seen the location of the stimulus. If these 29 subjects are moved to the noticer group, the corrected rate of IB for experiment 1 is 21% instead of 29%. In other words, relying only on the "Y/N did you notice anything" question leads to an overestimate of IB rates by 8%. This modest level of inaccuracy in estimating IB rates is insufficient for concluding that "subjects retain awareness of stimuli they fail to report", i.e. that inattentional blindness does not exist.

In addition, this 8% inaccuracy in IB rates only considers one side of the story. Given the data reported for experiment 1, one can also calculate the number of subjects who answered "yes, I did notice something unusual" but then reported the incorrect location of the critical stimulus. This turned out to be 8 subjects (or 3% of the "noticer" group). Some would argue that it's reasonable to consider these subjects as inattentionally blind, since they couldn't even report where the critical stimulus they apparently noticed was located. If we move these 8 subjects to the non-noticer group, the 8% overestimation of IB rates is reduced to 6%.

The same exercise can and should be carried out on the other 4 experiments, however, the authors do not report the subject numbers for any of the other experiments, i.e., how many subjects answered Y/N to the noticing question and how many in each group correctly answered the stimulus feature question. From the limited data reported (only total subject numbers and d' values), the effect sizes in experiments 2-5 were all smaller than in experiment 1 (d' for the non-noticer group was lower in all of these follow-up experiments), so it can be safely assumed that the ~6-8% overestimation of IB rates was smaller in these other four experiments. In a revision, the authors should consider reporting these subject numbers for all 5 experiments.

(2) Because classic IB paradigms involve only one critical trial per subject, the authors used a "super subject" approach to estimate sensitivity (d') and response criterion (c) according to signal detection theory (SDT). Some readers may have issues with this super subject approach, but my main concern is with the lack of precision used by the authors when interpreting the results from this super subject analysis.

Only the super subject had above-chance sensitivity (and it was quite modest, with d' values between 0.07 and 0.51), but the authors over-interpret these results as applying to every subject. The methods and analyses cannot determine if any individual subject could report the features above-chance. Therefore, the following list of quotes should be revised for accuracy or removed from the paper as they are misleading and are not supported by the super subject analysis:

"Altogether this approach reveals that subjects can report above-chance the features of stimuli (color, shape, and location) that they had claimed not to notice under traditional yes/no questioning" (p.6)

"In other words, nearly two-thirds of subjects who had just claimed not to have noticed any additional stimulus were then able to correctly report its location." (p.6)

"Even subjects who answer "no" under traditional questioning can still correctly report various features of the stimulus they just reported not having noticed, suggesting that they were at least partially aware of it after all." (p.8)

"Why, if subjects could succeed at our forced-response questions, did they claim not to have noticed anything?" (p.8)

"we found that observers could successfully report a variety of features of unattended stimuli, even when they claimed not to have noticed these stimuli." (p.14)

"our results point to an alternative (and perhaps more straightforward) explanation: that inattentionally blind subjects consciously perceive these stimuli after all... they show sensitivity to IB stimuli because they can see them." (p.16)

"In other words, the inattentionally blind can see after all." (p.17)

(3) In addition to the d' values for the super subject being slightly above zero, the authors attempted an analysis of response bias to further question the existence of IB. By including in some of their experiments critical trials in which no critical stimulus was presented, but asking subjects the standard Y/N IB question anyway, the authors obtained false alarm and correct rejection rates. When these FA/CR rates are taken into account along with hit/miss rates when critical stimuli were presented, the authors could calculate c (response criterion) for the super subject. Here, the authors report that response criteria are biased towards saying "no, I didn't notice anything". However, the validity of applying SDT to classic Y/N IB questioning is questionable.

For example, with the subject numbers provided in Box 1 (the 2x2 table of hits/misses/FA/CR), one can ask, 'how many subjects would have needed to answer "yes, I noticed something unusual" when nothing was presented on the screen in order to obtain a non-biased criterion estimate, i.e., c = 0?' The answer turns out to be 800 subjects (out of the 2761 total subjects in the stimulus-absent condition), or 29% of subjects in this condition.

In the context of these IB paradigms, it is difficult to imagine 29% of subjects claiming to have seen something unusual when nothing was presented. Here, it seems that we may have reached the limits of extending SDT to IB paradigms, which are very different than what SDT was designed for. For example, in classic psychophysical paradigms, the subject is asked to report Y/N as to whether they think a threshold-level stimulus was presented on the screen, i.e., to detect a faint signal in the noise. Subjects complete many trials and know in advance that there will often be stimuli presented and the stimuli will be very difficult to see. In those cases, it seems more reasonable to incorrectly answer "yes" 29% of the time, as you are trying to detect something very subtle that is out there in the world of noise. In IB paradigms, the stimuli are intentionally designed to be highly salient (and unusual), such that with a tiny bit of attention they can be easily seen. When no stimulus is presented and subjects are asked about their own noticing (especially of something unusual), it seems highly unlikely that 29% of them would answer "yes", which is the rate of FAs that would be needed to support the null hypothesis here, i.e., of a non-biased criterion. For these reasons, the analysis of response bias in the current context is questionable and the results claiming to demonstrate a biased criterion do not provide convincing evidence against IB.

(4) One of the strongest pieces of evidence presented in the entire paper is the single data point in Figure 3e showing that in Experiment 3, even the super subject group that rated their non-noticing as "highly confident" had a d' score significantly above zero. Asking for confidence ratings is certainly an improvement over simple Y/N questions about noticing, and if this result were to hold, it could provide a key challenge to IB. However, this result hinges on a single data point, it was not replicated in any of the other 4 experiments, and it can be explained by methodological limitations. I strongly encourage the authors (and other readers) to follow up on this result, in an in-person experiment, with improved questioning procedures.

In the current Experiment 3, the authors asked the standard Y/N IB question, and then asked how confident subjects were in their answer. Asking back-to-back questions, the second one with a scale that pertains to the first one (including a tricky inversion, e.g., "yes, I am confident in my answer of no"), may be asking too much of some subjects, especially subjects paying half-attention in online experiments. This procedure is likely to introduce a sizeable degree of measurement error.

An easy fix in a follow-up study would be to ask subjects to rate their confidence in having noticed something with a single question using an unambiguous scale:

On the last trial, did you notice anything besides the cross?

(1) I am highly confident I didn't notice anything else<br /> (2) I am confident I didn't notice anything else<br /> (3) I am somewhat confident I didn't notice anything else<br /> (4) I am unsure whether I noticed anything else<br /> (5) I am somewhat confident I noticed something else<br /> (6) I am confident I noticed something else<br /> (7) I am highly confident I noticed something else

If we were to re-run this same experiment, in the lab where we can better control the stimuli and the questioning procedure, we would most likely find a d' of zero for subjects who were confident or highly confident (1-2 on the improved scale above) that they didn't notice anything. From there on, the d' values would gradually increase, tracking along with the confidence scale (from 3-7 on the scale). In other words, we would likely find a data pattern similar to that plotted in Figure 3e, but with the first data point on the left moving down to zero d'. In the current online study with the successive (and potentially confusing) retrospective questioning, a handful of subjects could have easily misinterpreted the confidence scale (e.g., inverting the scale) which would lead to a mixture of genuine high-confidence ratings and mistaken ratings, which would result in a super subject d' that falls between zero and the other extreme of the scale (which is exactly what the data in Fig 3e shows).

One way to check on this potential measurement error using the existing dataset would be to conduct additional analyses that incorporate the confidence ratings from the 2AFC location judgment task. For example, were there any subjects who reported being confident or highly confident that they didn't see anything, but then reported being confident or highly confident in judging the location of the thing they didn't see? If so, how many? In other words, how internally (in)consistent were subjects' confidence ratings across the IB and location questions? Such an analysis could help screen-out subjects who made a mistake on the first question and corrected themselves on the second, as well as subjects who weren't reading the questions carefully enough. As far as I could tell, the confidence rating data from the 2AFC location task were not reported anywhere in the main paper or supplement.

(5) In most (if not all) IB experiments in the literature, a partial attention and/or full attention trial (or set of trials) is administered after the critical trial. These control trials are very important for validating IB on the critical trial, as they must show that, when attended, the critical stimuli are very easy to see. If a subject cannot detect the critical stimulus on the control trial, one cannot conclude that they were inattentionally blind on the critical trial, e.g., perhaps the stimulus was just too difficult to see (e.g., too weak, too brief, too far in the periphery, too crowded by distractor stimuli, etc.), or perhaps they weren't paying enough attention overall or failed to follow instructions. In the aggregate data, rates of noticing the stimuli should increase substantially from the critical trial to the control trials. If noticing rates are equivalent on the critical and control trials one cannot conclude that attention was manipulated.

It is puzzling why the authors decided not to include any control trials with partial or full attention in their five experiments, especially given their online data collection procedures where stimulus size, intensity, eccentricity, etc. were uncontrolled and variable across subjects. Including such trials could have actually helped them achieve their goal of challenging the IB hypothesis, e.g., excluding subjects who failed to see the stimulus on the control trials might have reduced the inattentional blindness rates further. This design decision should at least be acknowledged and justified (or noted as a limitation) in a revision of this paper.

(6) In the discussion section, the authors devote a short paragraph to considering an alternative explanation of their non-zero d' results in their super subject analyses: perhaps the critical stimuli were processed unconsciously and left a trace such that when later forced to guess a feature of the stimuli, subjects were able to draw upon this unconscious trace to guide their 2AFC decision. In the subsequent paragraph, the authors relate these results to above-chance forced-choice guessing in blindsight subjects, but reject the analogy based on claims of parsimony.

First, the authors dismiss the comparison of IB and blindsight too quickly. In particular, the results from experiment 3, in which some subjects adamantly (confidently) deny seeing the critical stimulus but guess a feature at above-chance levels (at least at the super subject level and assuming the online subjects interpreted and used the confidence scale correctly), seem highly analogous to blindsight. Importantly, the analogy is strengthened if the subjects who were confident in not seeing anything also reported not being confident in their forced-choice judgments, but as mentioned above this data was not reported.

Second, the authors fail to mention an even more straightforward explanation of these results, which is that ~8% of subjects misinterpreted the "unusual" part of the standard IB question used in experiments 1-3. After all, colored lines and shapes are pretty "usual" for psychology experiments and were present in the distractor stimuli everyone attended to. It seems quite reasonable that some subjects answered this first question, "no, I didn't see anything unusual", but then when told that there was a critical stimulus and asked to judge one of its features, adjusted their response by reconsidering, "oh, ok, if that's the unusual thing you were asking about, of course I saw that extra line flash on the left of the screen". This seems like a more parsimonious alternative compared to either of the two interpretations considered by the authors: (1) IB does not exist, (2) super-subject d' is driven by unconscious processing. Why not also consider: (3) a small percentage of subjects misinterpreted the Y/N question about noticing something unusual. In experiments 4-5, they dropped the term "unusual" but do not analyze whether this made a difference nor do they report enough of the data (subject numbers for the Y/N question and 2AFC) for readers to determine if this helped reduce the ~8% overestimate of IB rates.

(7) The authors use sub-optimal questioning procedures to challenge the existence of the phenomenon this questioning is intended to demonstrate. A more neutral interpretation of this study is that it is a critique on methods in IB research, not a critique on IB as a manipulation or phenomenon. The authors neglect to mention the dozens of modern IB experiments that have improved upon the simple Y/N IB questioning methods. For example, in Michael Cohen's IB experiments (e.g., Cohen et al., 2011; Cohen et al., 2020; Cohen et al., 2021), he uses a carefully crafted set of probing questions to conservatively ensure that subjects who happened to notice the critical stimuli have every possible opportunity to report seeing them. In other experiments (e.g., Hirschhorn et al., 2024; Pitts et al., 2012), researchers not only ask the Y/N question but then follow this up by presenting examples of the critical stimuli so subjects can see exactly what they are being asked about (recognition-style instead of free recall, which is more sensitive). These follow-up questions include foil stimuli that were never presented (similar to the stimulus-absent trials here), and ask for confidence ratings of all stimuli. Conservative, pre-defined exclusion criteria are employed to improve the accuracy of their IB-rate estimates. In these and other studies, researchers are very cautious about trusting what subjects report seeing, and in all cases, still find substantial IB rates, even to highly salient stimuli. The authors should consider at least mentioning these improved methods, and perhaps consider using some of them in their future experiments.

Determine the number of pages for batch allocating based on a heuristic. Using a (2^n - 1) to minimize cache aliasing issues.

but I think it may also be categorized as a configuration policy because the code execution depends on CONFIG_MMU.

-carson s This is annoying, I had written out a page note before but it deleted when I came back to this page. As such, this note will be shorter. Anyway, I liked this podcast overall, especially the discussion on group dynamics towards the end. that was really fascinating. I think that I agree with the idea that people should learn to disagree with each other and that the way to do that is by practicing. I mean, we learn everything else by practice, so why not this too? I also appreciated the point that reasonable people can disagree on things and that we need to be open tp the possibility that we may be wrong. that is something that I try to keep in mind day to day.

I really connect with this sentence because, as a teacher, I’ve noticed that challenging students' established ways of thinking can be uncomfortable for them, and I always try to acknowledge that discomfort. When we ask students to rethink long-held beliefs, especially around sensitive topics like race and racism, it can be unsettling. I feel it's my responsibility to guide them through this discomfort, helping them see that growth often comes from questioning old ideas and embracing new perspectives, even when it’s difficult.

Educational inequality has a ripple effect that goes far beyond the classroom, shaping the entire course of a student's life. The fact that success in today’s world is so closely tied to a college degree highlights just how deep this problem runs. It’s frustrating to think that a student's potential is often dictated by the resources their family can provide, rather than their talents or drive. Wealthier students have the advantage of tutors, better schools, extracurricular activities, and financial stability, while students from lower-income families may be just as capable but are held back by factors beyond their control.

It’s frustrating to see how intertwined class and race continue to be in the U.S. education system. While we’ve made strides in abolishing legal discrimination, the lingering effects of historical inequities still impact students today. It’s like we’ve removed some of the barriers, but others remain firmly in place, making it really tough for many kids to achieve the American dream. The point about anxiety around diversity and citizenship is particularly interesting. It seems like there’s this constant struggle between wanting to uphold the values of opportunity and competition while also addressing the realities of inequality. This creates a complicated dynamic where policies and practices often reflect more about societal fears than about truly supporting all students. It’s also alarming to think that these intertwined issues can create such a significant barrier to educational achievement. It raises questions about how we can create a more equitable system that not only acknowledges these disparities but actively works to dismantle them. We need to focus on comprehensive solutions that tackle both class and racial inequities, rather than treating them as separate issues.

This is interesting as you may want to think that the more we put into education the more 'employment' we get. However, this is not the case.

Author response:

The following is the authors’ response to the original reviews.

Reviewer 1 (Public Review):

Comment 1. Clinical Data on Patient Brain Samples: The inclusion of specific details such as postmortem intervals and the age at disease onset for patient brain samples would be valuable. These factors could significantly affect the quality of the tissues and their relevance to the study. Moreover, given the large variation in disease duration between PD and PDD, it’s important to consider disease duration as a potential confounding factor, especially when concluding that PDD patients have a more severe form of synucleinopathy compared to PD.

We thank the reviewer for this valuable comment. We have included the post-mortem interval (PMI) and age of death in Table S1, showing the clinicopathological information. Changes on page 16. As suggested by the reviewer, we included the discussion on the large variation in disease duration between PD and PDD cases. We noted that DLB cases also have shorter disease durations but still demonstrate seeding kinetics similar to PDD. Therefore, we hypothesise that the molecular differences we observed between different diseases were due to the strain properties or higher pathological load (seen in both PDD and DLB) and are unlikely due to the disease duration. Changes on pages 9-11, lines 204-212.

Comment 2. Inclusion of Healthy Controls in Multiple Tests: Given the importance of healthy controls in scientific studies, especially those involving human brain samples, the authors could consider using healthy controls in more tests to strengthen the robustness of the findings. Expanding the use of healthy controls in biochemical profiling and phosphorylation profiles would provide a better basis for comparison and clarify the significance of results in a disease context. This will help the authors to elaborate on the interpretation of results, for example, in Figure 3, where the authors claim that PD brains show mostly monomeric _α_Syn forms (line 119 and 120, and also in 222 and 223). Whether it implies the absence of alpha-syn pathology in PD brains? If there are differences from healthy controls? What are these low molecular weight bands (¡15kD) (line 125-126) and whether they are also present in healthy controls? Also, we do not have a perfect pS129-specific (anti-p_α_Syn) antibody. They are known for non-specific labeling. Investigating the phosphorylation levels in healthy controls and comparing them to PD brains, especially considering the predominance of monomeric (healthy _α_Syn?) in PD brains, would help clarify the observed changes.

We agree with the reviewer’s assessment and consider this an important suggestion. We performed biochemical profiling and immunogold imaging with the three HC cases and presented the results in Figure 4. aSyn in healthy controls was completely digested by PK. The low MW bands were absent in PD and HC, and there was no difference in the PK profiles. However, this may be due to the low pathology load and amount of pathological aSyn in the selected PD brains. Additional comments were added to the results. Changes are on pages 4 (lines 136-137) and page 7 (Figure 4).

Comment 3. Age of Healthy Controls: Providing information about the age at death for healthy controls is crucial, as age can impact the accumulation of aSyn. Also include if the brain samples were age-matched, or analyses were age-adjusted.

We have described the age of each patient, and the analyses were age-adjusted. Changes on page 16 (Table S1).

Comment 4. Braak Staging Discrepancy: The study reports the same Braak staging for both PD and PDD, despite the significant difference in disease duration. Maybe other reviewers with clinical experience might have a better take on this. This observation merits discussion in the paper, allowing readers to better understand the implications of this finding.

ddressed: Our PD and PDD cases are Braak stage 6, indicating that the LB pathology had progressed to the neocortex. It‘s important to note that Braak stage represents only where the LB pathogy has spread and does not indicate anything about the load of LBs. However, our immunohistochemistry results (page 20) show that PDD demonstrates a higher LB load than PD cases in the entorhinal cortex. As the reviewer has suggested, this comment has been amended in the manuscript. Changes on pages 9-11, lines 204-212.

Comment 5. Citation of Relevant Studies: The paper should consider citing and discussing a recent celebrated study on PD biomarkers that used thousands of cerebrospinal fluid (CSF) samples from different PD patient cohorts to demonstrate the effectiveness of SAA as a biochemical assay for diagnosing PD and its subtypes.

As suggested by the reviewer, we included this study in the discussion. Changes on page 12, lines 275-278.

Reviewer 3 (Public Review):

The experiments are missing two important controls. 1) what to fibrils generated by different in vitro fibril preparations made from recombinant synclein protein look like; and 2) the use of CSF from the same patients whose brain tissue was used to assess whether CSF and brain seeds look and behave identically. The latter is perhaps the most important question of all - namely how representative are CSF seeds of what is going on in patients’ brains?

We thank the reviewers for this valuable comment. Although in vitro preformed fibrils (PFFs) made out of recombinant aSyn are still important sources for cellular and animal studies to generate disease models and investigate mechanisms, many studies have now turned to use human brain amplified fibrils considering them to more closely present the human structure. Therefore, our study was designed to specifically address this hypothesis by comparing e human derived and SAA-amplified fibrils. It would be interesting to compare these structures also to PFFs but this was beyond the scope of our study. Comparing the CSF and brain seed from the same patients would be very interesting indeed but also difficult as this would require biosample collection during life followed by brain donation. The SAA cannot be done from the PM CSF due to contamination with blood. However, we are in a privileged position to examine such a comparison soon with our longitudinal Discovery cohort, where some participants have donated their brains. These future studies will address the critical question of whether the CSF seeds reflect those in the brain.

In their discussion the authors do not comment on the obvious differences in the conditions leading to the formation of seeds in the brain and in the artificial conditions of the seeding assay. Why should the two sets of conditions be expected to yield similar morphologies, especially since the extracted fibrils are subjected to harsh conditions for solubilization and re-suspension.

We agree with the reviewer that the formation of seeds in the brain and the SAA reaction conditions are very different, and one would not expect similar fibrillar morphologies. However, the theory is that pathological seeds are known to amplify through templated seeding, where seeds copy their intrinsic properties to the growing SAA fibrils. Thus, numerous studies use the SAA fibrils as model fibrils to investigate the different aSyn strains. Our study aimed to test whether the SAA fibrils are representative models of the brain fibrils. We included a more explicit comment on this discussion. Changes on page 3, lines 78-83.

Finally, the key experiment was not performed - would the resultant seeds from SAA preparations from the different nosological entities produce different pathologies when injected into animal brains? But perhaps this is the subject of a future manuscript.

We agree this is an essential experiment to build on our conclusion. Animal studies would be imperative to assess whether the SAA fibrils reflect the brain fibrils’ toxicity. However, these were beyond the scope of the present study but are being performed in collaboration with some expert groups.

Furthermore, the authors comment on phosphorylation patterns, stating that the resultant seeds are less heavy phosphorylated than the original material. Again, this should not be surprising, since the SAA assay conditions are not known to contain the enzymes necessary to phosphorylate synuclein. The discussion of PTMs is limited to pS-129 phosphorylation. What about other PTMs? How does the pattern of PTMs affect the seeding pattern.

We agree with the reviewer that other PTMs should be explored, but this was beyond the scope of this study. Here, we could focus on pS129, which has multiple reliable antibodies that also work with immunogold-TEM.

Lastly, the manuscript contains no data on how the diagnostic categories were assigned at autopsy. This information should be included in the supplementary material.

Clinical and neuropathological diagnostic criteria are now included in Table S1. Changes on page 16, lines 448-461.

Reviewer 1 (Recommendations for the authors):

(1) Remove a duplicate sentence in line 94-96.

Addressed: Thank you for pointing this out. The duplicated sentence has been corrected. Changes are on page 4, lines 105-106.

(2) Figure 1 Placement of Healthy Controls: Moving the graph representing healthy controls from the supplementary materials to the main figures could help readers better appreciate the results of diseased states.

The healthy control SAA curves were moved to the main figure. Changes are on page 5, Figure 2.

(3) Commenting on Case 2 Healthy Control: In the discussion section, you may comment on the case of the healthy control that showed amplification towards the end. While definitive conclusions may be challenging, acknowledging the possibility of incidental Lewy bodies or the prodromal phase of the disease would add depth to the analysis? But make sure to include the age information for healthy controls.

We believe this is an important point to discuss in the manuscript. We have referenced other studies with similar observations and stated that it is currently unknown what this phenomenon reflects (page 11, lines 221-226). The age information of the healthy control subjects was added to Table S1.

(4) Figure S3 Clarity: To enhance the clarity of Figure S3, consider adding a reference marker or arrow in the low-magnification image that points to the region being magnified in the insets. This visual cue will make it easier for readers to connect the detailed insets with the corresponding area in the broader image.

In Figure S3, we included a reference arrow in the low-magnification images to clarify where the higher-magnification images are taken. Changes are on page 19, Figure S3.

Reviewer 2 (Recommendations for the authors):

(1) A major issue confronting the field is the conflation of the PMCA and RT-QuIC assays (the latter of which was used here). The decision to rename and combine the two under the umbrella of SAAs does a major disservice to the field for many reasons. Recognizing that the push for this did not come from the authors, clarifying the differences in their Introduction would be very useful. I suggest this, in large part, because in the prion field, PMCA is known to amplify prion strains with high fidelity whereas the product from RT-QuIC does not. In fact, the RT-QuIC product for PrP is not even infectious, while the synuclein field uses it as a means to generate material for subsequent studies. Highlighting these differences would certainly strengthen the arguments the authors are making about the inadequacy of the synuclein RT-QuIC approach in research.

We thank the reviewers for these very valuable comments. We have included a further introduction on PMCA and RT-QuIC, explaining the differences and clearly stating our selection of the RT-QuIC method in this paper (page 3, lines 55-68). In addition, we have highlighted that, unlike PMCA, the RT-QuIC end-products are non-infectious and biologically dissimilar to the seed protein. Combined with our results, the findings demonstrate the methodological limitation of RT-QuIC in reproducing the seed fibrils and replicating their intrinsic biophysical information.

(2) On page 4, sentences starting on lines 94 and 95 are a duplication.

The duplicated sentence has been corrected. Changes are on page 4, lines 105-106.

(3) In the Results, noting that the pSyn staining on the RT-QuIC fibrils is coming from the human patient sample used to seed the reaction would be useful. This is mentioned in the Discussion, but the lack of mention in the Results made me pause reading to double check the methods. I think this could also be addressed a bit more clearly in the Abstract.

We have clarified this in the Results and Abstract. Changes on page 1 (lines 21-22) and page 9 (lines 192-194)

(4) On page 8 line 188, change was to were in the sentence, ”First, faster seeding kinetics was...”

This grammar error has been corrected. Changes are on page 9, line 200.

(5) The authors may want to comment on the unexpected finding that despite the RT-QuIC fibrils having a difference in twisted vs straight filaments, all 4 seeded reactions gave identical results in the conformational stability assay.

Addressed: We want to thank the reviewer for this comment and have highlighted the unexpected finding with a comment on what could be causing the identical results in the conformational stability assay. Changes are on page 12, lines 297-303.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The study "Endogenous oligomer formation underlies DVL2 condensates and promotes Wnt/βcatenin signaling" by Senem Ntourmas et al. contributes to the understanding of phase separation in Dishevelled (DVL) proteins, specifically focusing on DVL2. It builds upon existing research by investigating the endogenous complexes of DVL2 using ultracentrifugation and contrasting them with DVL1 and DVL3 behavior. The study identifies a DVL2-specific region involved in condensate formation and introduces the "two-step" concept of DVL2 condensate formation, enriching the field's knowledge. 

Strengths: 

A notable strength of this study is the validation of endogenous DVL2 complexes, providing insights into its behavior compared to DVL1 and DVL3. The functional validation of the DVL C-terminus (here termed conserved domain 2 (CD2) and the identification of DVL2-specific regions (here termed LCR4) involved in condensate formation are significant contributions that complement the current knowledge on the importance of DVL DIX domain, DEP domain and intrinsically disordered regions between DIX and PDZ domains. Additionally, the introduction of the concept where oligomerization (step 1) precedes condensate formation (step 2) is an interesting hypothesis, which can be further experimentally challenged in the future.

We thank the reviewer for her/his interest in our work and for acknowledging our significant contributions to the understanding of DVL2 phase separation.   

Weaknesses: 

However, the applicability of the findings to full-length DVL2 protein, hence the physiological relevance, is limited. This is mostly due to the fact that the authors almost completely depend on the set of DVL2 mutants, which lack the (i) DEP domain and (ii) nuclear export signal (NES). These variants fail to establish DEP domain-mediated interactions, including those with FZD receptors. Of note, the DEP domain itself represents a dimerization/tetramerization interface, which could affect the protein condensate formation of these mutants. Possibly even more importantly, the used mutants localize into the nucleus, which has different biochemical & biophysical properties than a cytoplasm, where DVL typically reside, which in turn affects the condensate formation. On top, in the nucleus, most of the DVL binding partners, including relevant kinases, which were reported to affect protein condensate formation, are missing.

The most convincing way to address this valid concern and to support a physiological relevant role of our findings is to extend our experiments with full-length DVL2, which we did alongside the suggestion in point two (please see below). In addition, we address the specific issues as follows:

We completely agree that interaction through the DEP domain contributes to condensate formation, which was thoroughly demonstrated in great studies by Melissa Gammons and Mariann Bienz, and complex formation (Fig. 2B, C). We deleted this domain on purpose for our mapping experiments, since we obtained more consistent results without any additional contribution of the DEP domain. Once we mapped CFR and identified crucial amino acids within CFR (VV, FF), we demonstrated that CFR-mediated interaction contributes to complex formation, condensate formation and pathway activation in the context of full-length DVL2 (Fig. 7A-G). 

We also agree that the nuclear localization may affect condensate formation because of the reasons mentioned by the reviewer or others, such as differences in DVL2 protein concentration. However, later proof-of-concept experiments in full-length DVL2 confirmed that CFR and its identified crucial amino acids (VV, FF), which were mapped in this rather artificial nuclear context, contribute to the typical cytosolic condensate formation of DVL2 (Fig. 7C, D). Moreover, we also observed cells with cytosolic condensates for the NES-lacking DVL2 constructs, although to a lower extent as compared to cells with nuclear condensates. A new analysis of NES-lacking key constructs focusing exclusively on cells with cytosolic condensates revealed similar differences between the DVL2 mutants as were observed before when investigating cells with nuclear (and cytosolic) condensates (new Fig. S3E, F), suggesting that the detected differences are not due to nuclear localization but reflect the overall condensation capacity. 

In addition, our condensate-challenging experiments (osmotic shock, 1,6-hexandiol) suggested that cytosolic condensates of full-length DVL2 and nuclear CFR-mediated condensates of deletion proteins lacking the DEP domain behave quite similar (Fig. 6A-C).

Second, the use of an overexpression system, while suitable for comparing DVL2 protein condensate features, falls short in functional assays. The study could benefit from employing established "rescue systems" using DVL1/2/3 knockout cells and re-expression of DVL variants for more robust functional assessments. 

We used the suggested established rescue system of DVL1/2/3 knockout cells (T-REx DVL1/2/3 triple knockout cells and T-REx DVL1/2/3 RNF43 ZNRF3 penta knockout cells, which are even more sensitive towards DVL re-expression as they lack RNF43/ZNRF3-mediated degradation of DVL activating receptors; both cell lines from the Bryja lab). Upon overexpression, our key mutants DVL2 VV-AA FF-AA and ∆CFR showed markedly reduced pathway activation compared to WT DVL2 (new Figs. 7F and S5J), as we observed before. Especially in the DVL1/2/3 triple knockout cells, DVL2 VV-AA FF-AA hardly activated the pathway and was as inactive as the established M2 mutant (new Fig. 7F). Most importantly, while re-expression of WT DVL2 at close to endogenous expression levels fully rescued Wnt3a-induced pathway activation in DVL1/2/3 knockout cells, DVL2 VV-AA FF-AA revealed significantly reduced rescue capacity and was almost as inactive as DVL2 M2 (new Figs. 7G and S5K). 

Furthermore, the discussion and introduction overlook some essential aspects of DVL biology. One such example is the importance of the open/close conformation of DVL and its effects on DVL phase separation and activity. In the context of this study, it is important to say that this conformational plasticity is mediated by DVL C-terminus (CD2 in this study). The second example is the reported roles of DVL1 and DVL3, which can both mediate the Wnt3a signal. How this can be interpreted when DVL1 and DVL3 lack LCR4 and still form condensates? 

We included the open/close conformation of DVL in our manuscript (introduction p. 3 and new discussion paragraph p. 10) and discussed it in the context of our findings. It is intriguing to speculate that Wnt-induced opening of DVL2 increases the accessibility of LCR4 and CD2, thereby triggering pre-oligomerization and subsequent phase separation of DVL2 (see discussion).

We extended the last paragraph of the discussion to interpret the roles of DVL1 and DVL3 lacking LCR4 (see p. 10). In short, the general ability of DVL1 and DVL3 to form condensates and to activate the Wnt pathway can be potentially explained through the other interaction sites (DIX, DEP, intrinsically disordered region). However, previous studies suggest that the DVL paralogs exhibit (quantitative) differences in Wnt pathway activation and that all three paralogs have to interact at a certain ratio for optimal pathway activation. In this context, a physiologic role for DVL2 LCR4 may be to promote the formation of these DVL1/2/3 assemblies and/or to enhance the stability of these assemblies.

In order to increase the physiological relevance of the study, I would recommend analyzing several key mutants in the context of the full-length DVL2 protein using the rescue/complementation system. Further, a more thorough discussion and connections with the existing literature on DVL protein condensates/puncta/LLPS can improve the impact of the study. 

We thank the reviewer for her/his suggestions to improve our study, which we addressed as detailed above.

Reviewer #2 (Public Review): 

Summary: 

The authors aimed to identify which regions of DVL2 contribute to its endogenous/basal clustering, as well as the relevance of such domains to condensate/phase separation and WNT activation. 

Strengths: 

A strength of the study is the focus on endogenous DVL2 to set up the research questions, as well as the incorporation of various techniques to tackle it. I found also quite interesting that DVL2-CFR addition to DVL1 increased its MW in density gradients. 

We thank the reviewer for her/his interest in our work and the constructive suggestions to improve our study.

Weaknesses: 

I think that several of the approaches of the manuscript are subpar to achieve the goals and/or support several of the conclusions. For example: 

(1) Although endogenous DVL2 indeed seems to form complexes (Figure 1A), neither the number of proteins involved nor whether those are homo-complexes can be determined with a density gradient. Super-resolution imaging or structural analyses are needed to support these claims. 

We agree that it will be very interesting to study the nature of the detected endogenous complexes in detail and we will consider this for any follow-up study, as structural analyses were out of scope for the revision of the presented manuscript. To address the issue, we mentioned that the calculation of about eight DVL2 molecules per complex is based on the assumption of homotypic complexes (results p. 4) and we discussed, why we think that homotypic complexes are the most likely assumption based on the currently available (limited) data (discussion p. 8).

(2) Follow-up analyses of the relevance of the DVL2 domains solely rely on overexpressed proteins. However, there were previous questions arising from o/e studies that prompted the focus on endogenous, physiologically relevant DVL interactions, clustering, and condensate formation.

Although the title, conclusions, and relevance all point to the importance of this study for understanding endogenous complexes, only Figures 1A and B deal with endogenous DVL2. 

We think that the biochemical detection of endogenous DVL2 complexes itself represents a valuable contribution to the understanding of endogenous DVL clustering, especially (i) since it is still lively discussed in the field whether and to which extent endogenous DVL assemblies exist (see introduction) and (ii) since recent studies addressing this issue rely on fluorescent tagging of the endogenous protein, which, among all benefits, harbors the risk to artificially affect DVL assembly. The follow-up analysis predominantly strengthens this key finding through (i) associating the detected complexes with established (DEP domain) and newly mapped (LCR4) DVL2 interaction sites, which we think is crucial to validate our biochemical approach, and (ii) linking the complexes with condensate formation and pathway activation for functional insights.

In addition, we performed new experiments with re-expression of DVL2 and our key mutants at close to endogenous expression levels in DVL1/2/3 knockout cells, supporting a physiological relevant role of our findings (new Figs. 7G and S5K, please also see point (5) below).

(3) Mutants lacking activity/complex formation, e.g. DVL2_1-418, may need further validation. For instance, DVL2_1-506 (same mutant but with DEP) seems to form condensates and it is functional in WNT signalling (King et al., 20223). These differences could be caused by the lack of DEP domain in this particular construct and/or folding differences. 

We would definitely expect that DVL2 1-506 exhibits increased condensate formation and pathway activation as compared to DVL2 1-418, since the DEP domain was thoroughly characterized as interaction domain in the Bienz lab and the Gammons lab (see references), which we confirmed in our assays (Fig. 2B-D). However, as the DEP domain is an established DVL2 interaction site, we were not interested to further characterize the DEP domain but to explain the marked difference in complex formation between DVL2 ∆DEP and 1-418 (Fig. 2A-C), which could not be associated with any known DVL2 interaction site and which we finally mapped to CFR (Fig. 4A-D). 

Since fusion of the newly-characterized interaction site CFR to DVL2 1-418 (1-418+CFR) rescued complex formation, condensate formation and signaling activity (Fig. 3B-E and Fig. 4C, D), we think that the lacking activity/complex formation of DVL2 1-418 is more likely due to missing interaction sites than due to folding problems. However, as it is hard to exclude folding differences of deletion mutants, we confirmed the CFR activity through loss-of-function experiments in the context of fulllength DVL2 with minimal point mutations (Fig. 7A-G, VV,FF). 

(4) The key mutants, DeltaCFR and VV/FF only show mild phenotypes. The authors' results suggest that these regions contribute but are not necessary for 1) complex formation (Density gradient Figures 7A and B), condensate formation (Figures 7C and D), and WNT activity (Figure 7E). Of note Figure 7C shows examples for the mutants with no condensates while the qualification indicates that 50% of the cells do have condensates. 

Condensate formation and Wnt pathway activation by DVL VV-AA FF-AA were reduced by more than 50% as compared to WT (Fig. 7D, E). We consider these marked differences, since loss of function always ranges between 0% and 100%. In newly performed experiments in DVL1/2/3 knockout cells, the differences were even more pronounced, see point (5) below.

Yes, Fig. 7C shows an example to qualitatively visualize the change in condensate formation, while Fig. 7D provides the corresponding quantification allowing quantitative assessment of the differences.

(5) Most of the o/e analyses (including all reporter assays) should be performed in DVL1-3 KO cells in order to explore specifically the behaviour of the investigated mutants. 

As suggested, we employed DVL1/2/3 knockout cells for performing reporter assays (T-REx DVL1/2/3 triple knockout cells and T-REx DVL1/2/3 RNF43 ZNRF3 penta knockout cells, which are even more sensitive towards DVL re-expression as they lack RNF43/ZNRF3-mediated degradation of DVL activating receptors; both cell lines from the Bryja lab). Here, we focused on key mutants in the context of full-length DVL2, as they are closest to the physiologic situation. Upon overexpression, DVL2 VV-AA FF-AA and DVL2 ∆CFR showed markedly reduced pathway activation as compared to WT DVL2 (new Figs. 7F and S5J). Especially in the DVL1/2/3 triple knockout cells, DVL2 VV-AA FF-AA hardly activated the pathway and was as inactive as the established M2 mutant (new Fig. 7F). Moreover, re-expression at close to endogenous expression levels revealed that DVL2 VV-AA FF-AA less efficiently rescued Wnt3a-induced pathway activation as compared to WT (Figs. 7G and S5K).

(6) How comparable are condensates found in the cytoplasm (usually for wt DVL) with those located in the nucleus (DEP mutants)? 

In principal, cytosolic condensates could differ from nuclear condensates due to various reasons, such as e.g. different protein concentration, different availability of interaction partners or different biochemical/biophysical properties (please also see point 1 of reviewer 1). In our condensatechallenging experiments (osmotic shock, 1,6-hexandiol), cytosolic condensates of full-length DVL2 and nuclear condensates of DVL2 mutants behaved quite similar (Fig. 6A-C).

We are confident that the differences between different DEP mutants in our mapping experiments are not due to nuclear localization but reflect the overall condensation capacity because later proofof-concept experiments demonstrated that CFR, which was identified in these mapping experiments, contributes to cytosolic condensate formation in the context of full-length DVL2 (Fig. 7C, D). Moreover, a new analysis focusing only on cells with cytosolic condensates, which can also be observed for DEP mutants to a low extent, revealed similar differences between key DEP mutants as observed before (Fig. S3E, F; for details please also see point 1 of reviewer 1).

Several studies in the last two decades have analysed the relevance of DVL homo - and heteroclustering by relying on overexpressed proteins. Recent studies also explored the possibility of DVL undergoing liquid-liquid phase separation following similar principles. As highlighted by the authors in the introduction, there is a need to understand DVL dynamics under endogenous/physiological conditions. Recent super-resolution studies aimed at that question by characterising endogenously edited DVL2. The authors seemed to aim in the same direction with their initial findings (Figure 1A) but quickly moved to o/e proteins without going back to the initial question. This reviewer thinks that to support their conclusions and advance in this important question, the authors should introduce the relevant mutations in the endogenous locus (e.g. by Cas9+ donor template encoding the required 3' exons, as done by others before for WNT components, including DVL2) and determine their impact in the above-indicated processes.

We agree that genomic editing of the DVL2 locus would be the cleanest system to study the relevance of CFR at endogenous expression levels. As we did not have the resources to generate the suggested cells, we, as an alternative, transiently re-expressed DVL2 and the respective mutants at low levels that were really close to the endogenous expression levels in DVL1/2/3 triple knockout cells (Fig. S5K). These experiments revealed that DVL2 VV-AA FF-AA less efficiently rescued Wnt3ainduced pathway activation as compared to DVL2 WT (Fig. 7G).

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary: 

This is a detailed description of the role of PKCδ in Drosophila learning and memory. The work is based on a previous study (Placais et al. 2017) that has already shown that for the establishment of long-term memory, the repetitive activity of MP1 dopaminergic neurons via the dopamine receptor DAMB is essential to increase mitochondrial energy flux in the mushroom body. 

In this paper, the role of PKCδ is now introduced. PKCδ is a molecular link between the dopaminergic system and the mitochondrial pyruvate metabolism of mushroom body Kenyon cells. For this purpose, the authors establish a genetically encoded FRET-based fluorescent reporter of PKCδspecific activity, δCKAR. 

Strengths: 

This is a thorough study of the long-term memory of Drosophila. The work is based on the extensive, high-quality experience of the senior authors. This is particularly evident in the convincing use of behavioral assays and imaging techniques to differentiate and explore various memory phases in Drosophila. The study also establishes a new reporter to measure the activity of PKCδ - the focus of this study - in behaving animals. The authors also elucidate how recurrent spaced training sessions initiate a molecular gating mechanism, linking a dopaminergic punishment signal with the regulation of mitochondrial pyruvate metabolism. This advancement will enable a more precise molecular distinction of various memory phases and a deeper comprehension of their formation in the future. 

Weaknesses: 

Apart from a few minor technical issues, such as the not entirely convincing visualisation of the localisation of a PKCδ reporter in the mitochondria, there are no major weaknesses. Likewise, the scientific classification of the results seems appropriate, although a somewhat more extensive discussion in relation to Drosophila would have been desirable.

We are very grateful for this very positive appreciation of our work. Following this comment, we have revised our manuscript to bring more compelling evidence of the mitochondrial localization of the PKCδ reporter. We also developed the discussion of our results with respect to the Drosophila learning and memory literature.

Reviewer #2 (Public Review):

Summary 

This study deepens the former authors' investigations of the mechanisms involved in gating the longterm consolidation of an associative memory (LTM) in Drosophila melanogaster. After having previously found that LTM consolidation 1. costs energy (Plaçais and Préat, Science 2013) provided through pyruvate metabolism (Plaçais et al., Nature Comm 2017) and 2. is gated by the increased tonic activity in a type of dopaminergic neurons ('MP1 neurons') following only training protocol relevant for LTM, i.e. interspaced in time (Plaçais et al., Nature Neuro 2012), they here dig into the intra-cell signalling triggered by dopamine input and eventually responsible for the increased mitochondria activity in Kenyon Cells. They identify a particular PKC, PKCδ, as a major molecular interface in this process and describe its translocation to mitochondria to promote pyruvate metabolism, specifically after spaced training. 

Methodological approach 

To that end, they use RNA interference against the isozyme PKCδ, in a time-controlled way and in the whole Kenyon cell populations or in the subpopulation forming the α/β lobe. This knock-down decreased the total PKCδ mRNA level in the brain by ca. 30%, and is enough to observe decreased in flies performances for LTM consolidation. Using Pyronic, a sensor for pyruvate for in vivo imaging, and pharmacological disruption of mitochondrial function, the authors then show that PKCδ knockdown prevents a high level of pyruvate from accumulating in the Kenyon cells at the time of LTM consolidation, pointing towards a role of PKCδ in promoting pyruvate metabolism. They further identify the PDH kinase PDK as a likely target for PKCδ since knocking down both PKCδ and PDK led to normal LTM performances, likely counterbalancing PKCδ knock-down alone. 

To understand the timeline of PKCδ activation and to visualise its mitochondrial translocation in a subpart of Mushroom body lobes they imported in fruitfly the genetically-encoded FRET reporters of PKCδ, δCKAR, and mitochondria-δCKAR (Kajimoto et al 2010). They show that PKCδ is activated to the sensor's saturation only after spaced training, and not other types of training that are 'irrelevant' for LTM. Further, adding thermogenetic activation of dopaminergic neurons and RNA interference against Gq-coupled dopamine receptor to FRET imaging, they identify that a dopamine-triggered cascade is sufficient for the elevated PKCδ-activation. 

Strengths and weaknesses 

The authors use a combination of new fluorescent sensors and behavioral, imaging, and pharmacological protocols they already established to successfully identify the molecular players that bridge the requirement for spaced training/dopaminergic neurons MP1 oscillatory activity and the increased metabolic activity observed during long-term memory consolidation. 

The study is dense in new exciting findings and each methodological step is carefully designed. Almost all possible experiments one could think of to make this link have been done in this study, with a few exceptions that do not prevent the essential conclusions from being drawn. 

The discussion is well conducted, with interesting parallels with mammals, where the possibility that this process takes place as well is yet unknown. 

Impact 

Their findings should interest a large audience: 

They discover and investigate a new function for PKCδ in regulating memory processes in neurons in conjunction with other physiological functions, making this molecule a potentially valid target for neuropathological conditions. They also provide new tools in drosophila to measure PKCδ activation in cells. They identify the major players for lifting the energetic limitations preventing the formation of a long-term memory. 

We warmly thank Reviewer #2 for the enthusiastic assessment of our work. There were no specific point to address in the Public Review.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have a few comments that could help improve the paper and help the reader navigate the detailed analysis.

(1) Perhaps the authors could add a sentence or two in the intro about the different PKC genes in Drosophila and whether they are expressed in the MB.

We thank Reviewer #1 for this suggestion. We now describe in the introduction the various subfamilies of PKCs downstream of Gq signaling , the Drosophila members of those different PKC subfamilies, and their expression in the brain. 

(2) Italicise Drosophila throughout the text.

We have done this correction.

(3) In Figure 1, you could change the scheme in Figure F-H and have the timeline always start after training. Then you could see that the training varies in time (perhaps provide the exact duration for each training protocol) and the test interval is constant. Why is it actually measured in a time window and not at an exact time?

This is indeed a good suggestion to clarify the presentation of our results. We changed the timelines schemes in all the figures with the t=0 starting at the end of the conditioning. Indeed, each conditioning protocol has a different duration as represented on these timelines: as one-cycle training lasts 5 min, 5x massed training has a duration of 20 min, and 5x spaced training takes 1 hours and 30 min to be completed, with its 15 min intertrial intervals. In vivo imaging experiments are performed during a certain time window after conditioning during which, according to our previous experience, the activity of MP1 dopamine neurons after spaced training remains constant (Plaçais et al., 2012). This offers the practical advantage that we can image several flies after a given training session, instead of having to perform many consecutive conditioning protocols.  

(4) In Figure 2 you could show the massed training data from the supplement. This is very similar to what is shown in Figure 1. Are there also imaging experiments on massed training?

The reason why massed training data was initially displayed in the supplementary data is that α/β neurons are known to be crucial for LTM formation but are not required for memory formed after massed training, so that the absence of effect was somehow expected. Nonetheless, we performed δCKAR imaging in α/β neurons after 5x massed training and found that PKCδ activity was not increased post-conditioning as expected (Figure 2C). This experiment was performed in parallel of additional data after 5x spaced conditioning δCKAR imaging in α/β neurons as a positive control (these new data were added to the Figure 2B). Following Reviewer #1’s suggestion, all data investigating the effect of PKCδ in α/β neurons are now displayed on Figure 2.

(5) Figure 3: I am not sure if the blue curve in Figure A really represents an upregulated pyruvate flux compared to the control (mentioned in line 210). It may be the case initially, but it is clearly below the control after 40s. Why is that?

This visual effect is due to the fact that PDBu injection in itself increases the pyruvate level in MB neurons (independently of its effect on PKCδ), before sodium azide injection. As a result, the baseline of the PDBu treated flies is above the DMSO control flies when sodium azide is injected, which results in the fact that the pyronic sensor saturates quicker and therefore reaches its plateau before the control when traces where normalized right before sodium azide injection. 

That being said, the measure of the slope in itself following sodium azide injection is not affected by these differences, and is always measured between 10 and 70% of the plateau. 

Given this remark, and another comment from Reviewer#2 about this experiment, we removed the panel 3A and present only the complete recording of this experiment, that is now displayed on Figure 3 – figure supplement 1C.

(6) For me, the localisation of the mitochondrial reporter in the mitochondria is not clear. The image in the supplement is not sufficient to show this clearly. What is missing here is a co-staining in the same brain of UAS-mito-δCKAR and a mitochondrial marker to label the mitochondria and the reporter at the same time in the same animal.

We agree with Reviewer #1’s remark and added new data to make this point more convincing. As suggested, we co-expressed mito-δCKAR with the mitochondrial reporter mito-DsRed in MB neurons (Lutas et al., 2012). We observed a clear colocalization of both signals by performing confocal imaging in the MB neurons somas, indicating that mito-δCKAR is indeed addressed to mitochondria (Figure 4 – figure supplement 1B and 2). 

(7) Are there controls that the MB expression of the reporters in the flies does not influence the learning ability? In order to make statements about the physiology of the cells, it must also be shown that the cells still have normal activity and allow learning behaviour comparable to wild-type flies.

This is indeed an important control that we added in the revised version. We tested the memory after 5x spaced, 5x massed and 1x training of flies expressing in the MB the various imaging probes used in our study (cyto-δCKAR, mito-δCKAR and Pyronic). Memory performance was similar to controls in all cases (Figure 1 – figure supplement 1E).  

(8) Perhaps the authors could go into more detail on two points in the discussion and shorten the comprehensive comparison to the vertebrate system somewhat. It would be nice to know how the local transfer from the peduncle to the vertical lobus is supposed to take place. What is the mechanism here? Any suggestions from the literature? It would also be useful to mention the compartmentalisation of the MB and how the information can overcome these boundaries from the peduncle to the vertical lobe.

We now elaborate on this question in the discussion (lines 368-386). To sum up, given that the compartmentalization of the MBs is anatomically defined by the presence of specific subset of MBON and DAN cell types (forming different information-processing units), rather than by physical boundaries per se, we can consider two main hypotheses to explain PKCδ activation transfer from the peduncle to the lobes: passive diffusion of activated PKCδ, or mitochondrial motility that would displace PKCδ from its place of first activation. We indeed found that mitochondrial motility was occurring upon 5x spaced conditioning for LTM formation (Pavlowsky et al. 2024).

In principle, one could also consider that PKCδ could be activated in the lobes by a relaying neuron. The MVP2 neuron (aka MBON-γ1>pedc) presents dendrites facing MP1 and makes synapses with the α/β neurons at the level of the α and β lobes, which makes it a good candidate. Furthermore, as we show that PKCδ activation in the lobes requires DAMB (Figure 4C, Figure 5A-B, Figure 5 – figure supplement 1), one could imagine the following activation loop: MP1 activates the MB neurons via DAMB, that activate MVP2 at the level of the peduncle, which activates in turn the MB neurons at the level of the lobes. However, we did not retain this hypothesis, because MVP2 is GABAergic, which makes it highly unlikely to be able to activate a kinase like PKCδ.

Regarding the comparative discussion with mammalian systems, we appreciate Reviewer #1’s remark that it may appear too detailed, but given that Reviewer #2 (public comment) highlighted the ‘interesting parallel with mammals’ in our discussion, we finally chose not to reduce this part in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

Fig 1G: is there a decrease in PKCδ activation after mass training as compared to the control, indicating an inhibitory mechanism onto PKCδ following mass training? Or is this an artifact of the PDBu application procedure in the control group? 

We thank Reviewer #2 for this careful comment. The dent in the timetrace following PDBu application after massed training (Figure 1G) is indeed an artifact due to the manual injection of the drug. But we would like to emphasize that what matters in the determination of PKCδ activity is the level of the baseline before PDBu application after normalization to the final plateau, so that variation around the injection time do not impact the result of the analysis. Moreover, in the revised version, we performed a similar series of experiments, using an α/β neuron-specific driver (Figure 2C). In this series of experiments, there were limited injection artefacts, and we obtained the same conclusion as Figure 1G that PKCδ activity is left unchanged by 5x massed conditioning. 

Fig 3A: I suggest moving this panel in the supplement: I found it difficult to process the effect of PDBu that is unspecific to PKCδ and that leads to a different plateau because of a different baseline. It would be better explained in more detail in the supplement, especially given that the 3B panel can lead to a similar conclusion and does not have this specificity problem. Up to the authors.

We thank Reviewer #2 for this feedback. We followed the suggestion and now only display the full recording of this experiment on Figure 3 – figure supplement 1C.

Fig 3C: To go further, one wonders if knocking-down PDK would act as a switch for gating LTM formation, i.e. if done during a 1x training or a 5x massed training would it gate long-term consolidation?

This is indeed an excellent suggestion. We performed this experiment and showed that in flies expressing the PDK RNAi in adult MB neurons, only one cycle of training was sufficient to induce longterm memory formation (Figure 3A), instead of the 5 spaced cycles normally required. This confirms the model we previously established in Plaçais et al. 2017, where long-term memory formation was observed upon PDK MB knock-down after 2 cycles of spaced training. This new result goes further in characterizing this facilitation effect, now showing that even a single cycle is sufficient. Altogether these data show that mitochondrial metabolic activation is the critical gating step in long-term memory formation. Spaced training achieves this activation through PDK inhibition, mediated by PKCδ.

What is the level of mRNA in this construct? I don't see a quantification, can you justify it?

We thank Reviewer #2 for this remark. This PDK RNAi had been used in a previous work in pyruvate imaging experiment, where it successfully boosted mitochondrial pyruvate uptake. But indeed we had not validated it at the mRNA level. In the revised version of the present manuscript, we now confirm by RT-qPCR that the PDK RNAi efficiently downregulates PDK expression in neurons (Figure 3 – figure supplement 1A).

Fig. 4C: Is PKCδ activation increase in Vertical lobe DAMB-dependent? One wonders, because MP1 may somehow activate other neurons that could reach this part of the Kenyon Cells. I do not see in the results what could disprove this possibility. The mechanism linking DAMB activation in the peduncle and PKCδ activation in the VL is mysterious, see also Fig. 5.

This is a very sound remark. In the revised version we have checked whether PKCδ activation in the vertical lobes is also dependent on DAMB.  We performed thermogenetic activation of MP1 neurons and imaged mito-δCKAR signal in the vertical lobes upon DAMB MB knock-down. We found that as for the peduncle, DAMB was required for PKCδ mitochondrial activation (Figure 4C, right panel). This experiment was performed in parallel with similar measurements in flies that did not express DAMB RNAi, as a positive control (these new control data were added to the Figure 4C, left panel).

This result supports a model where dopamine from MP1 neurons directly acts on Kenyon cells, even for PKCδ activation in the vertical lobes. Thus, this advocates for a diffusion of DAMB-activated PKCδ from the peduncle to the vertical lobes, either by passive diffusion or by mitochondrial motility - two hypotheses that we added in the discussion. 

Fig. 5: If MP1 neurons release dopamine only to the peduncle, how do you expect PKCδ to be translocated to mitochondria all the way to the vertical lobe? Also is it specific to the vertical lobe and not found in the medial lobe?

Investigating the spatial distribution of PKCδ is, once again, a very sound suggestion. We re-analyzed our dataset of the mito-δCKAR signal after spaced training for peduncle measurement, as the imaging plane also included the β lobe. We found that PKCδ is also activated at that level, and that its activation also depends on DAMB (Figure 5 – figure supplement 1). We also performed additional pyruvate measurements in the medial lobes, and observed that mitochondria pyruvate uptake presents the same extension in time in the medial lobes as in the vertical lobes when comparing spaced training (Figure 6 E-F and Figure 6 – figure supplement 1E-F) to 1x training (Figure 6A-B and Figure 6 – figure supplement 1C-D). Therefore, the metabolic action of PKCδ seems not to be restricted to the vertical lobes, but spreads across the whole axonal compartment.

Altogether, these data point toward the fact that activated PKCδ diffuse from its point of activation, the peduncle, where dopamine is released by MP1 and DAMB is activated, to both the vertical and medial lobes, either by passive diffusion, or taking advantage of mitochondrial movement that was shown to be triggered by spaced training (Pavlowsky et al. 2024), from the MB neurons somas to the axons. To further characterize the kinetics of PKCδ activation, we measured its activity using the mitoδCKAR sensor at 3 and 8 hours following spaced training. We found that while PKCδ was still active at 3 hours, it was back to its baseline activity level at 8 hours, both at the level of the peduncle and the vertical lobes (Figure 5 C-F). However, at 8 hours, pyruvate metabolism is still upregulated in the lobes, which indicates that an additional mechanism is relaying PKCδ action to maintain the high energy state of the MBs at later time points. As we propose in the revised discussion, the mitochondrial motility hypothesis makes sense here (Pavlowsky et al. 2024), as the progressive increase in the number of mitochondria in the lobes would be able to sustain high mitochondrial metabolism beyond PKCδ activation at 8 hours post-conditioning. This new result and its implications open exciting perspectives for future research about the different mitochondrial regulations occurring after spaced training, their organization over time and their interactions.

Fig.7:  PDK written in yellow is almost invisible

This has been changed.

It is unfortunate that the act of an individual person can permanently taint the work of hundreds, directly affecting those around him who weren't even involved in the perpetrated crime. It is also unfortunate that in the process of trying to protect women, or any victims for a matter of fact, we unintentionally are harming them as well. In this case, it seems that the choice to pull the reruns of The Cosby Show was more of a publicity stunt instead of a legitimate attempt to protect the demographic most harmed by Bill Cosby's actions. They could have easily simply done something to his residual payments to prevent him from profiting off the work he worked in—not his work, he was simply just one of the many people that helped The Cosby Show become reality. This is why it's important to think thoroughly of the consequences an action may have on not just the perpetuator, but also the victims and other parties, directly or indirectly, involved.

The impact of language, especially in news articles, is blatantly clear. We get a lot of our information of the outside world from the news, and the first source of information we see and consume from these news articles are the headlines. These titles often introduce bias, either exaggerating or downplaying the content to attract readers and generate revenue, which is why it's important to also read the content of the article, and other articles, to fully grasp the situation the article is reporting on.

This is particularly problematic in cases of sexual violence, where articles frequently minimize the severity of the crime and may even favor the abuser. The distinction between "sex" and "sexual violence" hinges on one important element: consent. This difference is significant. It's not uncommon for me to see articles that cover rape, not label what is rape as rape (a 'recent' case I could think of is the mass rape trial in France). The connotations of the words used shape our perceptions (e.g. words like dislike, hate, detest, loathe---we feel different things regarding each of these words even though they are often referred to as synonym of each other), influencing how we judge the seriousness of these incidents.

Very symbolic of life. There is a famous quote "life is ten percent of what happens to you and ninety percent of how you react to it." We may think in Gone Home that the ten percent is happening. That something is happening to us. But, in reality we as the character are only reacting to what is already happening.

I find this first section introducing walking’s purpose in games and specifically as the base of “walking simulators” interesting because I had always viewed walking as a waste of time. I think it was an important thing to note that some people do feel this way, which has caused many games to include a “fast pass” that can be purchased or is a complete replacement for any walking. It’s especially interesting to look at how walking or the lack thereof can affect our “fun”, agency, and a sort of challenge. If we don’t have this break time to think and reflect, then it feels like it would be a lot harder to be able to overcome any obstacles we may face. I never understood the immersive power of walking through an environment for the player, but now that I think about it, having a “fast pass” model for the game feels like it would disconnect the player from the character they’re playing as. If we don’t get to experience the character’s entire journey, are we really in full control of the character? If we aren’t, how are we going to feel like we are the character themselves?

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The overall analysis and discovery of the common motif are important and exciting. Very few human/primate ribozymes have been published and this manuscript presents a relatively detailed analysis of two of them. The minimized domains appear to be some of the smallest known self-cleaving ribozymes.

Strengths:

The manuscript is rooted in deep mutational analysis of the OR4K15 and LINE1 and subsequently in modeling of a huge active site based on the closely-related core of the TS ribozyme. The experiments support the HTS findings and provide convincing evidence that the ribozymes are structurally related to the core of the TS ribozyme, which has not been found in primates prior to this work.

Weaknesses:

(1) Given that these two ribozymes have not been described outside of a single figure in a Science Supplement, it is important to show their locations in the human genome, present their sequence and structure conservation among various species, particularly primates, and test and discuss the activity of variants found in non-human organisms. Furthermore, OR4K15 exists in three copies on three separate chromosomes in the human genome, with slight variations in the ribozyme sequence. All three of these variants should be tested experimentally and their activity should be presented. A similar analysis should be presented for the naturally-occurring variants of the LINE1 ribozyme. These data are a rich source for comparison with the deep mutagenesis presented here. Inserting a figure (1) that would show the genomic locations, directions, and conservation of these ribozymes and discussing them in light of this new presentation would greatly improve the manuscript. As for the biological roles of known self-cleaving ribozymes in humans, there is a bioRxiv manuscript on the role of the CPEB3 ribozyme in mammalian memory formation (doi.org/10.1101/2023.06.07.543953), and an analysis of the CPEB3 functional conservation throughout mammals (Bendixsen et al. MBE 2021). Furthermore, the authors missed two papers that presented the discovery of human hammerhead ribozymes that reside in introns (by de la PeÃ{plus minus}a and Breaker), which should also be cited. On the other hand, the Clec ribozyme was only found in rodents and not primates and is thus not a human ribozyme and should be noted as such.

We thank this Reviewer for his/her input and acknowledgment of this work. To improve the manuscript, we have included the genomic locations in Figure 1A, Figure 6A and Figure 6C. And we have tested the activity of representative variants found in the human genome and discussed the activity of the variants in other primates. All suggested publications are now properly cited.

Line 62-66: It has been shown that single nucleotide polymorphism (SNP) in CPEB3 ribozyme was associated with an enhanced self-cleavage activity along with a poorer episodic memory (14). Inhibition of the highly conserved CPEB3 ribozyme could strengthen hippocampal-dependent long-term memory (15, 16). However, little is known about the other human self-cleaving ribozymes.

Line 474-501: Homology search of two TS-like ribozymes. To locate close homologs of the two TS-like ribozymes, we performed cmsearch based on a covariance model (38) built on the sequence and secondary structural profiles. In the human genome, we got 1154 and 4 homolog sequences for LINE-1-rbz and OR4K15-rbz, respectively. For OR4K15-rbz, there was an exact match located at the reverse strand of the exon of OR4K15 gene (Figure 6A). The other 3 homologs of OR4K15-rbz belongs to the same olfactory receptor family 4 subfamily K (Figure 6C). However, there was no exact match for LINE-1-rbz (Figure 6A). Interestingly, a total of 1154 LINE-1-rbz homologs were mapped to the LINE-1 retrotransposon according to the RepeatMasker (http://www.repeatmasker.org) annotation. Figure 6B showed the distribution of LINE-1-rbz homologs in different LINE-1 subfamilies in the human genome. Only three subfamilies L1PA7, L1PA8 and L1P3 (L1PA7-9) can be considered as abundant with LINE-1-rbz homologs (>100 homologs per family). The consensus sequences of all homologs obtained are shown in Figure 6D. In order to investigate the self-cleavage activity of these homologs, we mainly focused on the mismatches in the more conserved internal loops. The major differences between the 5 consensus sequences are the mismatches in the first internal loop. The widespread A12C substitution can be found in majority of LINE-1-rbz homologs, this substitution leads to a one-base pair extension of the second stem (P2) but almost no activity (RA’: 0.03) based on our deep mutational scanning result. Then we selected 3 homologs without A12C substitution for LINE-1-rbz for in vitro cleavage assay (Figure 6E). But we didn’t observe significant cleavage activity, this might be caused by GU substitutions in the stem region. For 3 homologs of OR4K15-rbz, we only found one homolog of OR4K15 with pronounced self-cleavage activity (Figure 6F). In addition, we performed similar bioinformatic search of the TS-like ribozymes in other primate genomes. Similarly, the majority (15 out of 18) of primate genomes have a large number of LINE-1 homologs (>500) and the remaining three have essentially none. However, there was no exact match. Only one homolog has a single mutation (U38C) in the genome assembly of Gibbon (Figure S15). The majority of these homologs have 3 or more mismatches (Figure S15). For OR4K15-rbz, all representative primate genomes contain at least one exact match of the OR4K15-rbz sequence.

Line 598-602: According to the bioinformatic analysis result, there are some TS-like ribozymes (one LINE-1-rbz homolog in the Gibbon genome, and some OR4K15-rbz homologs) with in vitro cleavage activity in primate genomes. Unlike the more conserved CPEB3 ribozyme which has a clear function, the function of the TS-like ribozymes is not clear, as they are not conserved, belong to the pseudogene or located at the reverse strand.

(2) The authors present the story as a discovery of a new RNA catalytic motif. This is unfounded. As the authors point out, the catalytic domain is very similar to the Twister Sister (or "TS") ribozyme. In fact, there is no appreciable difference between these and TS ribozymes, except for the missing peripheral domains. For example, the env33 sequence in the Weinberg et al. 2015 NCB paper shows the same sequences in the catalytic core as the LINE1 ribozyme, making the LINE1 ribozyme a TS-like ribozyme in every way, except for the missing peripheral domains. Thus these are not new ribozymes and should not have a new name. A more appropriate name should be TS-like or TS-min ribozymes. Renaming the ribozymes to lanterns is misleading.

Although we observed some differences in mutational effects, we agree with the reviewer that it is more appropriate to call them TS-like ribozymes. We have replaced all “lantern ribozyme” with “TS-like ribozyme” as suggested.

(3) In light of 2) the story should be refocused on the fact the authors discovered that the OR4K15 and LINE1 are both TS-like ribozymes. That is very exciting and is the real contribution of this work to the field.

We thank this Reviewer for their acknowledgement of this work. To improve the manuscript, we have re-named the ribozymes as suggested.

(4) Given the slow self-scission of the OR4K15 and LINE1 ribozymes, the discussion of the minimal domains should be focused on the role of peripheral domains in full-length TS ribozymes. Peripheral domains have been shown to greatly speed up hammerhead, HDV, and hairpin ribozymes. This is an opportunity to show that the TS ribozymes can do the same and the authors should discuss the contribution of peripheral domains to the ribozyme structure and activity. There is extensive literature on the contribution of a tertiary contact on the speed of self-scission in hammerhead ribozymes, in hairpin ribozyme it's centered on the 4-way junction vs 2-way junction structure, and in HDVs the contribution is through the stability of the J1/2 region, where the stability of the peripheral domain can be directly translated to the catalytic enhancement of the ribozymes.

We appreciate your question and the valuable suggestions provided. We have included the citations and discussion about the peripheral domains in other ribozymes.

Line 570-576: Thus, a more sophisticated structure along with long-range interactions involving the SL4 region in the twister sister ribozyme must have helped to stabilize the catalytic region for the improved catalytic activity. Similarly, previous studies have demonstrated that peripheral regions of hammerhead (49), hairpin (50) and HDV (51, 52) ribozymes could greatly increase their self-cleavage activity. Given the importance of the peripheral regions, absence of this tertiary interaction in the TS-like ribozyme may not be able to fully stabilize the structural form generated from homology modelling.

(5) The argument that these are the smallest self-cleaving ribozymes is debatable. LÃ1/4nse et al (NAR 2017) found some very small hammerhead ribozymes that are smaller than those presented here, but the authors suggest only working as dimers. The human ribozymes described here should be analyzed for dimerization as well (e.g., by native gel analysis) particularly because the authors suggest that there are no peripheral domains that stabilize the fold. Furthermore, Riccitelli et al. (Biochemistry) minimized the HDV-like ribozymes and found some in metagenomic sequences that are about the same size as the ones presented here. Both of these papers should be cited and discussed.

We apologize for any confusion caused by our previous statement. To clarify, we highlighted “35 and 31 nucleotides only” because 46 and 47 nt contain the variable hairpin loops which are not important for the catalytic activity. By comparing the conserved segments, the TS-like ribozyme discussed in this paper is the shortest with the simplest secondary structure. And we have replaced the terms “smallest” and “shortest” with “simplest” in our manuscript. The title has been changed to “Minimal twister sister (TS)-like self-cleaving ribozymes in the human genome revealed by deep mutational scanning”. All the publications mentioned have been cited and discussed. Regarding possible dimerization, we did not find any evidence but would defer it to future detailed structural analysis to be sure.  

Line 605-608: Previous studies also have revealed some minimized forms of self-cleaving ribozymes, including hammerhead (19, 53) and HDV-like (54) ribozymes. However, when comparing the conserved segments, they (>= 36 nt) are not as short as the TS-like ribozymes (31 nt) found here.

(6) The authors present homology modeling of the OR4K15 and LINE1 ribozymes based on the crystal structures of the TS ribozymes. This is another point that supports the fact that these are not new ribozyme motifs. Furthermore, the homology model should be carefully discussed as a model and not a structure. In many places in the text and the supplement, the models are presented as real structures. The wording should be changed to carefully state that these are models based on sequence similarity to TS ribozymes. Fig 3 would benefit from showing the corresponding structures of the TS ribozymes.

We thank the reviewer for pointing these out and we have already fixed them. We have replaced all “lantern ribozyme” with “TS-like ribozyme” as suggested. The term “Modelled structures” were used for representing the homology model. And we have included the TS ribozyme structure in Fig 3.

Reviewer #2 (Public Review):

Summary:

This manuscript applies a mutational scanning analysis to identify the secondary structure of two previously suggested self-cleaving ribozyme candidates in the human genome. Through this analysis, minimal structured and conserved regions with imminent importance for the ribozyme's activity are suggested and further biochemical evidence for cleavage activity are presented. Additionally, the study reveals a close resemblance of these human ribozyme candidates to the known self-cleaving ribozyme class of twister sister RNAs. Despite the high conservation of the catalytic core between these RNAs, it is suggested that the human ribozyme examples constitute a new ribozyme class. Evidence for this however is not conclusive.

Strengths:

The deep mutational scanning performed in this study allowed the elucidation of important regions within the proposed LINE-1 and OR4K15 ribozyme sequences. Part of the ribozyme sequences could be assigned a secondary structure supported by covariation and highly conserved nucleotides were uncovered. This enabled the identification of LINE-1 and OR4K15 core regions that are in essence identical to previously described twister sister self-cleaving RNAs.

Weaknesses:

I am skeptical of the claim that the described catalytic RNAs are indeed a new ribozyme class. The studied LINE-1 and OR4K15 ribozymes share striking features with the known twister sister ribozyme class (e.g. Figure 3A) and where there are differences they could be explained by having tested only a partial sequence of the full RNA motif. It appears plausible, that not the entire "functional region" was captured and experimentally assessed by the authors.

We thank this Reviewer for his/her input and acknowledgment of this work. Because a similar question was raised by reviewer 1, we decided to name the ribozymes as TS-like ribozymes. Regarding the entire regions, we conducted mutational scanning experiments at the beginning of this study. The relative activity distributions (Figure 1B, 1C) have shown that only parts of the sequence contributes to the self-cleavage activity. That is the reason why we decided to focus on the parts of the sequence afterwards.

They identify three twister sister ribozymes by pattern-based similarity searches using RNA-Bob. Also comparing the consensus sequence of the relevant region in twister sister and the two ribozymes in this paper underlines the striking similarity between these RNAs. Given that the authors only assessed partial sequences of LINE-1 and OR4K15, I find it highly plausible that further accessory sequences have been missed that would clearly reveal that "lantern ribozymes" actually belong to the twister sister ribozyme class. This is also the reason I do not find the modeled structural data and biochemical data results convincing, as the differences observed could always be due to some accessory sequences and parts of the ribozyme structure that are missing.

We appreciate the reviewer for raising this question. As we explained in the last question, we now called the ribozymes as TS-like ribozymes. We also emphasize that the relative activity data of the original sequences have indicated that the other part did not make any contribution to the activity of the ribozyme. The original sequences provided in the Science paper (Salehi-Ashtiani et al. Science 2006) were generated from biochemical selection of the genomic library. It did not investigate the contribution of each position to the self-cleavage activity.

Highly conserved nucleotides in the catalytic core, the need for direct contacts to divalent metal ions for catalysis, the preference of Mn2+ oder Mg2+ for cleavage, the plateau in observed rate constants at ~100mM Mg2+, are all characteristics that are identical between the proposed lantern ribozymes and the known twister sister class.

The difference in cleavage speed between twister sister (~5 min-1) and proposed lantern ribozymes could be due to experimental set-up (true single-turnover kinetics?) or could be explained by testing LINE-1 or OR4K15 ribozymes without needed accessory sequences. In the case of the minimal hammerhead ribozyme, it has been previously observed that missing important tertiary contacts can lead to drastically reduced cleavage speeds.

We thank the reviewer for this question. We now called the ribozymes as TS-like ribozymes. As we explained in the last question, the relative activity data of the original sequences have proven that the other part did not make any contribution to the activity of the ribozyme. Moreover, we have tested different enzyme to substrate ratios to achieve single turn-over kinetics (Figure S13). The difference in cleavage speed should be related to the absence of peripheral regions which do not exist in the original sequences of the LINE-1 and OR4K15 ribozyme. We have included the publications and discussion about the peripheral domains in other ribozymes.

Line 458-463: The kobs of LINE-1-core was ~0.05 min-1 when measured in 10mM MgCl2 and 100mM KCl at pH 7.5 (Figure S13). Furthermore, the single-stranded ribozymes exhibited lower kobs (~0.03 min-1 for LINE-1-rbz) (Figure S14) when comparing with the bimolecular constructs. This confirms that the stem loop region SL2 does not contribute much to the cleavage activity of the TS-like ribozymes.

Line 570-576: Thus, a more sophisticated structure along with long-range interactions involving the SL4 region in the twister sister ribozyme must have helped to stabilize the catalytic region for the improved catalytic activity. Similarly, previous studies have demonstrated that peripheral regions of hammerhead (49), hairpin (50) and HDV (51, 52) ribozymes could greatly increase their self-cleavage activity. Given the importance of the peripheral regions, absence of this tertiary interaction in the TS-like ribozyme may not be able to fully stabilize the structural form generated from homology modelling.

Reviewer 2: ( Recommendations For The Authors):

Major points

It would have made it easier to connect the comments to text passages if the submitted manuscript had page numbers or even line numbers.

We thank the reviewer for pointing this out and we have already fixed it.

In the introduction: "...using the same technique, we located the functional and base-pairing regions of..." The use of the adjective functional is imprecise. Base-paired regions are also important for the function, so what type of region is meant here? Conserved nucleotides?

We thank the reviewer for pointing this out. We were describing the regions which were essential for the ribozyme activity. And we have defined the use of “functional region” in introduction.

Line 95: we located the regions essential for the catalytic activities (the functional regions) of LINE-1 and OR4K15 ribozymes in their original sequences.

In their discussion, the authors mention the possible flaws in their 3D-modelling in the absence of Mg2+. Is it possible to include this divalent metal ion in the calculations?

We thank the reviewer for this question. Currently, BriQ (Xiong et al. Nature Communications 2021) we used for modeling doesn’t include divalent metal ion in modeling.

Xiong, Peng, Ruibo Wu, Jian Zhan, and Yaoqi Zhou. 2021. “Pairing a High-Resolution Statistical Potential with a Nucleobase-Centric Sampling Algorithm for Improving RNA Model Refinement.” Nature Communications 12: 2777. doi:10.1038/s41467-021-23100-4.

Abstract:

It is claimed that ribozyme regions of 46 and 47 nt described in the manuscript resemble the shortest known self-cleaving ribozymes. This is not correct. In 1988, hammerhead ribozymes in newts were first discovered that are only 40 nt long.

We apologize for any confusion caused by our previous statement. To clarify, we highlighted “35 and 31 nucleotides only” as 46 and 47 nt contain the variable hairpin loops which are not important for the catalytic activity. By comparing the conserved segments, the TS-like ribozyme discussed in this paper is the shortest with the simplest secondary structure. And we have replaced the terms “smallest” and “shortest” with “simplest” in our manuscript. The title has been changed to “Minimal TS-like self-cleaving ribozyme revealed by deep mutational scanning”.

The term "functional region" is, to my knowledge, not a set term when discussing ribozymes. Does it refer to the catalytic core, the cleavage site, the acid and base involved in cleavage, or all, or something else? Therefore, the term should be 1) defined upon its first use in the manuscript and 2) probably not be used in the abstract to avoid confusion to the reader.

We apologize for any confusion caused by our previous statement. To clarify, we have changed the term “functional region” in abstract. And we have defined the use of “functional region” in introduction.

Line 34-37: We found that the regions essential for ribozyme activities are made of two short segments, with a total of 35 and 31 nucleotides only. The discovery makes them the simplest known self-cleaving ribozymes. Moreover, the essential regions are circular permutated with two nearly identical catalytic internal loops, supported by two stems of different lengths.

Line 95: we located the regions essential for the catalytic activities (the functional regions) of LINE-1 and OR4K15 ribozymes in their original sequences.

The choice of the term "non-functional loop" in the abstract is a bit unfortunate. The loop might not be important for promoting ribozyme catalysis by directly providing, e.g. the acid or base, but it has important structural functions in the natural RNA as part of a hairpin structure.

We thank the reviewer for pointing this out and we have re-phrased the sentences.

Line 33-34: We found that the regions essential for ribozyme activities are made of two short segments, with a total of 35 and 31 nucleotides only.

Line 283: Removing the peripheral loop regions (Figures 1B and 1C) allows us to recognize that the secondary structure of OR4K15-rbz is a circular permutated version of LINE-1-rbz.

Results:

Please briefly explain CODA and MC analysis when first mentioned in the results (Figure (1) The more detailed explanation of these terms for Figure 2 could be moved to this part of the results section (including explanations in the figure legend).

We thank the reviewer for pointing this out and we included a brief explanation.

Line 150-154: CODA employed Support Vector Regression (SVR) to establish an independent-mutation model and a naive Bayes classifier to separate bases paired from unpaired (26). Moreover, incorporating Monte-Carlo simulated annealing with an energy model and a CODA scoring term (CODA+MC) could further improve the coverage of the regions under-sampled by deep mutations.

Please indicate the source of the human genomic DNA. Is it a patient sample, what type of tissue, or is it an immortalized cell line? It is not stated in the methods I believe.

We thank the reviewer for pointing this out. According to the original Science paper (Salehi-Ashtiani et al. Science 2006), the human genomic DNA (isolated from whole blood) was purchased from Clontech (Cat. 6550-1). In our study, we directly employed the sequences provided in Figure S2 of the Science paper for gene synthesis. Thus, we think it is unnecessary to mention the source of genomic DNA in the methods section of our paper.  

Please also refer to the methods section when the calculation of RA and RA' values is explained in the main text to avoid confusion.

We thank the reviewer for pointing this out and we have fixed it.

Line 207-208: Figure 2A shows the distribution of relative activity (RA’, measured in the second round of mutational scanning) (See Methods) of all single mutations

For OR4K15 it is stated that the deep mutational scanning only revealed two short regions as important. However, there is another region between approx. 124-131 nt and possibly even at positions 47 and 52 (to ~55), that could contribute to effective RNA cleavage, especially given the library design flaws (see below) and the lower mutational coverage for OR4K15. A possible correlation of the mutations in these regions is even visible in the CODA+MC analysis shown in Figure 1D on the left. Why are these regions ignored in ongoing experiments?

We thank the reviewer for this question. As shown in Table S1, although the double mutation coverage of OR4K15-ori was low (16.2 %), we got 97.6 % coverage of single mutations. The relative activity of these single mutations was enough to identify the conserved regions in this ribozyme. Mutations at the positions mentioned by the reviewer did not lead to large reductions in relative activity. Since the relative activity of the original sequence is 1, we presumed that only positions with average relative activity much lower than 1 might contribute to effective cleavage.

Regarding the corresponding correlation of mutations in CODA+MC, they are considered as false positives generated from Monte Carlo simulated annealing (MC), because lack of support from the relative activity results.

Have the authors performed experiments with their "functional regions" in comparison to the full-length RNA or partial truncations of the full-length RNA that included, in the case of OR4K15, nt 47-131? Also for LINE-1 another stem region was mentioned (positions 14-18 with 30-34) and two additional base pairs. Were they included in experiments not shown as part of this manuscript?

We appreciate the reviewer for raising this question. We only compared the full-length or partial truncations of the LINE-1 ribozyme. Since the secondary structure predicted from OR4K15-ori data was almost the same as LINE-1, we didn’t perform deep mutagenesis on the partial truncation of the OR4K15. However, the secondary structure of OR4K15 was confirmed by further biochemical experiments.   

Regarding the second question, the additional base pairs were generated by Monte Carlo simulated annealing (MC). They are considered as false positives because of low probabilities and lack of support from the deep mutational scanning results. The appearance of false positives is likely due to the imperfection of the experiment-based energy function employed in current MC simulated annealing. 

Are there other examples in the literature, where error-prone PCR generates biases towards A/T nucleotides as observed here? Please cite!

We thank the reviewer for pointing this out and we have included the corresponding citation.

Line 161-162: The low mutation coverage for OR4K15-ori was due to the mutational bias (27, 28) of error-prone PCR (Supplementary Figures S1, S2, S3 and S4).

Line 170-171: whose covariations are difficult to capture by error-prone PCR because of mutational biases (27, 28).

The authors mention that their CODA analysis was based on the relative activities of 45,925 and 72,875 mutation variants. I cannot find these numbers in the supplementary tables. They are far fewer than the read numbers mentioned in Supplementary Table 2. How do these numbers (45,925 and 72,875) arise? Could the authors please briefly explain their selection process?

We apologize for any confusion caused by our previous statement. Our CODA analysis only utilized variants with no more than 3 mutations. The number listed in the supplementary tables is the total number of the variants. To clarify, we have included a brief explanation for these numbers.

Line 203-204: We performed the CODA analysis (26) based on the relative activities of 45,925 and 72,875 mutation variants (no more than 3 mutations) obtained for the original sequence and functional region of the LINE-1 ribozyme, respectively.

What are the reasons the authors assume their findings from LINE-1 can be used to directly infer the structure for OR4K15? (Third section in results, last paragraph)

We apologize for any confusion caused by our previous statement. We meant to say that the consistency between LINE-1-rbz and LINE-1-ori results suggested that our method for inferring ribozyme structure was reliable. Thus, we employed the same method to infer the structure of the functional region of OR4K15. To clarify, we have re-phrased the sentence.   

Line 259-261: The consistent result between LINE-1-rbz and LINE-1-ori suggested that reliable ribozyme structures could be inferred by deep mutational scanning. This allowed us to use OR4K15-ori to directly infer the final inferred secondary structure for the functional region of OR4K15.

There are several occasions where the authors use the differences between the proposed lantern ribozymes and twister sister data as reasons to declare LINE-1 and OR4K15 a new ribozyme class. As mentioned previously, I am not convinced these differences in structure and biochemical results could not simply result from testing incomplete LINE-1 and OR4K15 sequences.

We apologize for any confusion caused by our previous statement. Despite we observed some differences in mutational effects, we agree with the reviewer that it is not convincing to claim them as a new ribozyme class. We have replaced all “lantern ribozyme” with “TS-like ribozyme” as the reviewer 1 suggested.

The authors state, that "the result confirmed that the stem loop SL2 region in LINE-1 and OR4K15 did not participate in the catalytic activity". To draw such a conclusion a kinetic comparison between a construct that contains SL2 and does not contain SL2 would be necessary. The given data does not suffice to come to this conclusion.

We appreciate the reviewer for raising this question. To address this, we performed gel-based kinetic analysis of these two ribozymes (Figure S14).

Line 458-462: The kobs of LINE-1-core under single-turnover condition was ~0.05 min-1 when measured in 10mM MgCl2 and 100mM KCl at pH 7.5 (Figure S13). Only a slightly lower value of  kobs (~0.03 min-1) was observed for LINE-1-rbz (Figure S14). This confirms that the stem loop region SL2 does not contribute to the cleavage activity of the TS-like ribozymes.

Construct/Library design:

The last 31 bp in the OR4K15 ribozyme template sequence are duplicated (Supplementary Table 4). Therefore, there are 2 M13 fwd binding sites and several possible primer annealing sites present in this template. This could explain the lower yield for the mutational analysis experiments. Did the authors observe double bands in their PCR and subsequent analysis? The experiments should probably be repeated with a template that does not contain this duplication. Alternatively, the authors should explain, why this template design was chosen for OR4K15.

We apologize for this mistake during writing. Our construct design for OR4K15 contains only one M13F binding site. We thank the reviewer for pointing this out and we have fixed the error.

Figure 5B: Where are the bands for the OR4K15 dC-substrate? They are not visible on the gel, so one has to assume there was no substrate added, although the legend indicates otherwise.

Also this figure, please indicate here or in the methods section what kind of marker was used. In panels A and B, please label the marker lanes.

We apologize for this mistake and we have repeated the experiment. The marker lane was removed to avoid confusion caused by the inappropriate DNA marker. 

The authors investigated ribozyme cleavage speeds by measuring the observed rate constants under single-turnover conditions. To achieve single-turnover conditions enzyme has to be used in excess over substrate. Usually, the ratios reported in the literature range between 20:1 (from the authors citation list e.g.: for twister sister (Roth et al 2014) and hatchet (Li et al. 2015)) or even ~100:1 (for pistol: Harris et al 2015, or others https://www.sciencedirect.com/science/article/pii/S0014579305002061). Can the authors please share their experimental evidence that only 5:1 excess of enzyme over the substrate as used in their experiments truly creates single-turnover conditions?

We greatly appreciate the Reviewer for raising this question. To address this, we performed kinetic analysis using different enzyme to substrate ratios (Figure S13). There is not too much difference in kobs, except that kobs reach the highest value of 0.048 min-1 when using 100:1 excess of enzyme over the substrate. 

Line 458-460: The kobs of LINE-1-core under single-turnover condition was ~0.05 min-1 when measured in 10mM MgCl2 and 100mM KCl at pH 7.5 (Figure S13).

Citations:

In the introduction citation number 12 (Roth et al 2014) is mentioned with the CPEB3 ribozyme introduction. This is the wrong citation. Please also insert citations for OR4K15 and IGF1R and LINE-1 ribozyme in this sentence.

We thank the reviewer for pointing this out and we now have fixed it.

Also in the introduction, a hammerhead ribozyme in the 3' UTR of Clec2 genes is mentioned and reference 16 (Cervera et al 2014) is given, I think it should be reference 9 (Martick et al 2008)

We thank the reviewer for pointing this out and we now have fixed it.

In the results section it is stated that, "original sequences were generated from a randomly fragmented human genomic DNA selection based biochemical experiment" citing reference 12. This is the wrong reference, as I could not find that Roth et al 2014 describe the use of such a technique. The same sentence occurs in the introduction almost verbatim (see also minor points).

We thank the reviewer for pointing this out and we now have fixed it.

Minor points

Headline:

Either use caps for all nouns in the headline or write "self-cleaving ribozyme" uncapitalized

We thank the reviewer for pointing this out and we now have fixed it.

Abstract:

1st sentence: in "the" human genome

"Moreover, the above functional regions are..." - the word "above" could be deleted here

"named as lantern for their shape"- it should be "its shape"

"in term of sequence and secondary structure"- "in terms"

"the nucleotides at the cleavage sites" - use singular, each ribozyme of this class has only one cleavage site

We thank the reviewer for pointing these out and we now have fixed them.

Introduction:

Change to "to have dominated early life forms"

Change to "found in the human genome"

Please write species names in italics (D. melanogaster, B. mori)

Please delete "hosting" from "...are in noncoding regions of the hosting genome"

Please delete the sentence fragment/or turn it into a meaningful sentence: "Selection-based biochemical experiments (12).

Change to "in terms of sequence and secondary structure, suggesting a more"

Please reword the last sentence in the introduction to make clear what is referred to by "its", e.g. probably the homology model of lantern ribozyme generated from twister sister ribozymes?

Please refer to the appropriate methods section when explaining the calculation of RA and RA'.

We thank the reviewer for pointing these out and we now have fixed them.

The last sentence of the second paragraph in the second section of the results states that the authors confirmed functional regions for LINE-1 and OR4K15, however, until that point the section only presents data on LINE-1. Therefore, OR4K15 should not be mentioned at the end of this paragraph.

In response to the reviewer's suggestions, we have removed OR4K15 from this paragraph.

Line 225-228: The consistency between base pairs inferred from deep mutational scanning of the original sequences and that of the identified functional regions confirmed the correct identification of functional regions for LINE-1 ribozyme.

Change to "Both ribozymes have two stems (P1, P2), to internal loops ..."

We thank the reviewer for pointing this out and we now have fixed it.

The section naming the "functional regions" of LINE-1 and OR4K15 lantern ribozymes should be moved after the section in which the circular permutation is shown and explained. Therefore, the headline of section three should read "Consensus sequence of LINE-1 and OR4K15 ribozymes" or something along these lines.

We thank the reviewer for pointing this out and we now have fixed it.

Line 308-309: Given the identical lantern-shaped regions of the LINE-1-rbz and OR4K15-rbz ribozyme, we named them twister sister-like (TS-like) ribozymes.

The statement on the difference between C8 in OR4K15 and U38 in LINE-1 should be further classified. As U38 is only 95% conserved. Is it a C in those other instances or do all other nucleotide possibilities occur? Is the high conservation in OR4K15 an "artifact" of the low mutation rate for this RNA in the deep mutational scanning?

We thank the reviewer for this question. Yes, the high conservation in OR4K15 an "artifact" of the low mutation rate for this RNA in the deep mutational scanning. That is why RA’ value is more appropriate to describe the conservation level of each position. We also mentioned this in the manuscript:

Line 287-288: The only mismatch U38C in L1 has the RA’ of 0.6, suggesting that the mismatch is not disruptive to the functional structure of the ribozyme.

Section five, first paragraph: instead of "two-stranded LINE-1 core" use the term "bimolecular", as it is more commonly used.

We thank the reviewer for pointing this out and we now have changed it.

Figure caption 3 headline states "Homology modelled 3D structure..."but it also shows the secondary structures of LINE1, OR4K15 and twister sister examples.

We thank the reviewer for pointing this out and we now have removed “3D”.

In Figure 3C, we see a nucleobase labeled G37, however in the secondary structure and sequence and 3D structural model there is a C37 at this position. Please correct the labeling.

We thank the reviewer for pointing this out and we now have fixed it.

Section 7 "To address the above question..." please just repeat the question you want to address to avoid any confusion to the reader.

We thank the reviewer for pointing these out and we have re-phrased this sentence.

Line 364: Considering the high similarity of the internal loops, we further investigated the mutational effects on the internal loop L1s.

Please rephrase the sentence "By comparison, mutations of C62 (...) at the cleavage site did not make a major change on the cleavage activity...", e.g. "did not lead to a major change" etc.

Section 8, first paragraph: This result further confirms that the RNA cleavage in lantern...", please delete "further"

Change to "analogous RNAs that lacked the 2' oxygen atom in the -1 nucleotide"

Methods

Change to "We counted the number of reads of the cleaved and uncleaved..."

Change to "...to produce enough DNA template for in vitro transcription."

Change to "The DNA template used for transcription was used..." (delete while)

We thank the reviewer for pointing these out and we now have fixed them.

Supplement

All supplementary figures could use more detailed Figure legends. They should be self-explanatory.

Fig S1/S2: how is "mutation rate" defined/calculated?

We thank the reviewer for pointing this out and we now have added a short explanation. The mutation rate was calculated as the proportion of mutations observed at each position for the DNA-seq library.

Fig S3/S4: axis label "fraction", fraction of what? How calculated?

We thank the reviewer for pointing this out and we now have added a short explanation. The Y axis “fraction” represents the ratio of each mutation type observed in all variants.

Fig S5: RA and RA' are mentioned in the main text and methods, but should be briefly explained again here, or it should be clearly referred to the methods. Also, the axis label could be read as average RA' divided by average RA. I assume that is not the case. I assume I am looking at RA' values for LINE-1 rbz and RA values for LINE-1-ori? Also, mention that only part of the full LINE-1-ori sequence is shown...

We thank the reviewer for pointing this out and we have now added a short explanation. The Y axis represents RA’ for LINE-1-rbz, or RA for LINE-1-ori. The part shown is the overlap region between LINE-1-rbz and LINE-1-ori. We apologize for any confusion caused by our previous statement.

Fig S9 the magenta for coloring of the scissile phosphate is hard to see and immediately make out.

We thank the reviewer for pointing this out and we now have added a label to the scissile phosphate.

Fig S10: Why do the authors only show one product band here? Instead of both cleavage fragments as in Figure 5?

We thank the reviewer for this question. We purposely used two fluorophores (5’ 6-FAM, 3’ TAMRA) to show the two product bands in Figure 5. In Fig S10, long-time incubation was used to distinguish catalysis based self-cleavage from RNA degradation. This figure was prepared before the purchasing of the substrate used in Figure 5. The substrate strand used in Fig S10 only have one fluorophore (5’ 6-FAM) modification. And the other product was too short to be visualized by SYBR Gold staining.

Fig S13: please indicate meaning of colors in the legend (what is pink, blue, grey etc.)

Please change to "RtcB ligase was used to capture the 3' fragment after cleavage...."

We thank the reviewer for pointing this out and we now have fixed it.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Recommendations For The Authors):

Materials and Methods section:

Cell gating and FACS sorting strategies need to be explained. There is no figure legend of supplementary figure 4 which is supposed to explain the gating strategy. Please detail the strategy for each cell types.

Thank you for your suggestion. We have given a detailed description about the gating and FACS sorting strategies for different liver cell types in supplementary figure 1. In addition, flow cytometry plots of CD45+Ly6C-CD64+F4/80+ KCs from Bmp9fl/flBmp10fl/flLrat Cre mouse were also presented in supplementary figure 1.

The genetic background of the different mouse strains and the age of the mice should be noted on each figure.

All the mice used in our study are C57BL/6 background (method section). The age of the mice has been described on each figure.

The Mann Whitney test instead of the two-tailed student's t-test should be used for the different statistical analyses. Why are the expression counts statically analyzed by 2-tailed Student's t test as they were already identified as DE in RNAseq statistical analysis?

Thank you for your suggestion. Statical methods have been corrected in the revised manuscript.

What is the age of the mice and how many are used for each bulk RNAseq?

This information has been added on the corresponding figure legends.

Figure 1:

Figure 1a and c: The qPCR data would be much more interesting if presented as DDct and not as relative value as we do not see the mRNA levels of BMP9 and BMP10 in each Bmp9fl/flBmp10fl/flCre mouse. This would allow to compare the mRNA level of BMP9 versus BMP10. This should be changed in all figures.

The presentation of qPCR data in Figure 1a have been changed, which is allowed to compare the abundance of BMP9 versus BMP10 mRNA. Figure 1c only shows the expression of BMP10, so it is unnecessary to present qPCR data as DDct. In our bulk RNA sequencing data of liver tissues, we found that BMP9 expression counts is higher than that of BMP10, in line with the data from BioGPS.

Figure 1e (IF) and f (FACS), the quantification of these data should be added as shown in Fig2d. What is the difference between Fig1e and Fig2d as they both seem to show the quantification of F4/80 in CTL versus Bmp9fl/flBmp10fl/flLratCre mice. Are the cells sorted in Fig1f and 1e and suppl Fig1b? if yes please precise the strategy. If they are not gated how can the authors obtain 93% of KC? The reference Tillet et al., JBC 2018 should be added in the discussion of figure 1 as it is the first description of BMP10 in HSC.

The quantitative data of Figure 1e and 1f have been added in our revised manuscript. Compared with other tissue-resident macrophages, CLEC4F as a KC-specific marker exclusively expressed on KCs. In our previous report (PMID: 34874921), we demonstrated that BMP9/10-ALK1 signal induced the expression of CLEC4F. The data shown in Figure 1e repeated this phenotype that upon loss of BMP9/10-ALK1 signal, liver macrophages did not express CLEC4F. F4/80 in Figure 1e was used as an internal positive control. Fig2d showed the quantification of F4/80 and CD64, two pan-macrophage markers, which was more accurate to measure the number of liver macrophages, especially given that F4/80 mean fluorescence intensity was reduced in liver macrophages of Bmp9fl/flBmp10fl/flLrat Cre mice. Cells in Fig1f, 1e and suppl Fig1b were not sorted and the flow cytometry plots of these cells were pre-gated on live CD45+Ly6C-CD64+F4/80+ liver macrophages. The reference Tillet et al., JBC 2018 has been added in our revised manuscript.

Supplementary 4 should have a detailed figure legend and should appear before gating experiments. What cell subtype is used for each cell type gating. Please add the exact references of all the antibodies used and if they are fluorescently labeled antibodies. Why is the number of lymphocytes noted and how is it calculated? The gating strategy for the Bmp9fl/flBmp10fl/flLratCre mice should also be showed as the number of FA4/80+ and Tim4+ cells are decreased.

A detailed figure legend has been added in original supplementary figure 4 that has been moved to supplementary figure 1 in our revised manuscript. The antibodies used in our study were also used in our previous report (PMID: 34874921) and others (PMID: 31561945; PMID: 26813785). Lymphocytes number on flow cytometry plots will automatically appear when we analyze flow cytometry data, so it does not mean that these selected cells are lymphocytes. To avoid the misunderstanding, these words have been deleted. The gating strategy of CD45+Ly6C-CD64+F4/80+ liver macrophages for the Bmp9fl/flBmp10fl/flLrat Cre mice was showed in our revised manuscript (Supplementary Figure 1).

Figure 2:

Figure 2a: How many mice were used for bulk RNAseq at what age? Please describe the gating strategy for sorting liver macrophages. The PCA should be shown. The genes represented in Fig2c and cited in the text should be shown on the volcano plot and the heatmap (Timd4, Cdh5, Cd5l). A reference for these KC and monocytic markers should be added in the text.

Control and Bmp9fl/flBmp10fl/flLrat Cre mice at the age of 8-10 weeks (n=3/group) were used for bulk RNAseq. This information has been added in Figure 2a legend. The PCA, Timd4 gene and references for these KC and monocytic markers have been shown in our revised manuscript according to your suggestion.

Figure 2b: How are selected the genes represented in the heatmap? The top ones? If it is a KC signature the authors should give a reference for this signature.

These genes were KC signature genes. The reference (PMID: 30076102) has been given in our revised manuscript.

Fig2e: Please explain what is the Vav1 promoter and in which cells it will delete Alk1and Smad4? The authors also need to show that Alk1 and Smad4 are indeed deleted in these mice and in which cell subtype (EC and KC?). This is an important point as the authors conclude that other molecular mechanisms than Smad4 signaling may affect the phenotypes of liver macrophages in Bmp9fl/flBmp10fl/flLratCre.

Cre recombinase of Vav1Cre mice is expressed at high levels in hematopoietic stem cells (PMID: 27185381). This strain is widely used to target all hematopoietic cells with a high efficiency (PMID: 24857755). In our previous report (PMID: 34874921), we demonstrated that Alk1 (Supplemental Figure 6A) and Smad4 (Supplemental Figure 6G) were efficiently deleted in KCs from Alk1fl/flVav1Cre and Smad4fl/flVav1Cre mice, respectively. This sentence and reference have been added in our revised manuscript. Homozygous loss of ALK-1 causes embryonically lethality due to aberrant angiogenesis (PMID: 28213819). EC-specific ALK1 knockout in the mouse through deletion of the ALK1 gene from an Acvrl12loxP allele with the EC-specific L1-Cre line results in postnatal lethality at P5, and mice exhibiting hemorrhaging in the brain, lung, and gastrointestinal tract (PMID: 19805914). In contrast, Alk1fl/flVav1Cre mice generated in our lab did not observe this phenomenon or body weight loss, and still survived at the age of 16 weeks. Thus, we don’t think that ECs can be targeted by Vav1Cre strain, at least in our experimental system.

Supl Figure 3 (revised Supl Figure 4): The authors need to explain what cell types are affected by Csf1r-Cre and Clec4fDTR. Have the authors tried to perform a similar experiment in Bmp9fl/flBmp10fl/flLratCre? The legend of the Y axis is not clear, why is CD45+ used in the first bar graph while the other two graphs use F4/80+?

We (PMID: 34874921) and others (PMID: 31587991; PMID: 31561945; PMID: 26813785) have demonstrated that Clec4f specifically expressed on KCs and thus only KCs can be deleted in Clec4fDTR mice after DT injection. CSF1R, also known as macrophage colony-stimulating factor receptor (M-CSFR), is the receptor for the major monocyte/macrophage lineage differentiation factor CSF1. Thus, Csf1r-Cre strain can target monocyte, monocyte-derived macrophage and tissue-resident macrophage including liver, spleen, intestine, heart, kidney, and muscle with a high efficiency (PMID: 29761406). We did not perform a similar experiment in Bmp9fl/flBmp10fl/flLrat Cre mice as we have demonstrated that the differentiation of liver macrophages from Bmp9fl/flBmp10fl/flLrat Cre mice is inhibited. The other two graphs in Supl Figure 4C were obtained from Supl Figure 4B. Flow cytometry plots in Supl Figure 4B are pre-gated on CD45+Ly6C-CD64+F4/80+ liver macrophages, so it is appropriate to use F4/80+ as an internal control.

Figure 3: Same remarks as in Figure 2. How many mice were used for bulk RNAseq, at what age? The PCA should be shown. How were selected the genes represented in the heatmap? The top ones? A reference should be given for the sinusoidal EC and the continuous EC signatures and large artery signature. Maf and Gata4 should be shown on the volcano plot. A quantification for CD34 IF (Fig3e) as well as for the quantification of the FACS data (Fig 3f) should be added.

Control and Bmp9fl/flBmp10fl/flLrat Cre mice at the age of 8-10 weeks (n=3/group) were used for bulk RNAseq. According to your suggestion, other revisions have been made.

Figure 4: A quantification and statistical analysis of Prussian staining area and GS IF should be added not just number of mice which were affected.

A quantification and statistical analysis of Prussian staining area and GS IF has been added.

Minor points:

Few spelling mistakes that should be checked.

Figure 5a, some bar graphs are missing.

Spelling mistakes and missing bar graphs in Figure 5a have been corrected.

Reviewer #2 (Recommendations For The Authors):

The authors should provide some additional information:

- Did the single HSC-KO mice for either BMP9 or BMP10 already show partial phenotypes?

We think that under steady state, the phenotype of KCs and ECs, described in our manuscript, in the livers of single HSC-KO mice for either BMP9 or BMP10 was not altered. However, we don’t know whether the role of BMP9 and BMP10 is still redundant in liver diseases or inflammation, which is worth further studying.

- The authors should also stain Endomucin, Lyve1, CD32b on liver tissue to assess endothelial zonation/differentiation in addition to FACS analysis.

In our revised manuscript, we performed immunostaining for Endomucin and Lyve1 and found increased expression of Endomucin and decreased expression of Lyve1 (Figure 3g), suggesting that endothelial zonation/differentiation was disrupt in the liver of Bmp9fl/flBmp10fl/flLrat Cre mice compared to their littermates. We did not stain CD32b expression in the liver section as there is no good antibody against mouse CD32b for frozen sections.

- Did the authors assess BMP9/BMP10 effects individually and combined in vitro on KC and EC? Are these likely only direct effects or may they also involve each other (i.e. also cross talk between KC and EC in response to BMP9/10?). This could be assessed in co-culture models.

Using ALK1 reporter mice, we demonstrated that KCs and liver ECs express ALK1.We and others have shown that in vitro stimulation with BMP9/BMP10 can induce the expression of ID1/ID3 and GATA4/Maf in KCs and ECs (PMID: 34874921; PMID: 35364013; PMID: 30964206), respectively. These results suggested that BMP9/BMP10 can directly function on KCs and ECs. Indeed, we are also interested in the crosstalk between KCs and ECs. However, in vitro coculture system can not mimic the interaction between KCs and ECs in the liver as these cells will lose their identity upon their isolation from liver environment. Nevertheless, Bonnardel et al. applied Nichenet bioinformatic analysis to predict that liver ECs provide anchoring site, Notch and CSF1 signal for KCs (PMID: 31561945). Of course, this prediction still needs experimental validation.

- The abstract should be rephrased and more specific focus on BMP related intercellular crosstalk in the liver and its implications for liver health and disease. At the end of the abstract they should also emphasize for which specific fields/topics/diseases these findings are important.

Thank you for your suggestion. The abstract has been rephrased and we hope this abstract could satisfy you.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

In this important study, Huffer et al posit that non-cold sensing members of the TRPM subfamily of ion channels (e.g., TRPM2, TRPM4, TRPM5) contain a binding pocket for icilin which overlaps with the one found in the cold-activated TRPM8 channel.

The authors identify the residues involved in icilin binding by analyzing the existing TRPM8-icilin complex structures and then use their previously published approach of structure-based sequence comparison to compare the icilin binding residues in TRPM8 to other TRPM channels. This approach uncovered that the residues are conserved in a number of TRPM members: TRPM2, TRPM4, and TRPM5. The authors focus on TRPM4, with the rationale that it has the simplest activation properties (a single Ca2+-binding site). Electrophysiological studies show that icilin by itself does not activate TRPM4, but it strongly potentiates the Ca2+ activation of TRPM4, and introducing the A867G mutation (the mutation that renders avian TRPM8 sensitive to icilin) further increases the potentiating effects of the compound. Conversely, the mutation of a residue that likely directly interacts with icilin in the binding pocket, R901H, results in channels whose Ca2+ sensitivity is not potentiated by icilin.

The data indicate that, just like in TRPV channels, the binding pockets and allosteric networks might be conserved in the TRPM subfamily.

The data are convincing, and the authors employ good experimental controls.

We appreciate the supportive feedback of this reviewer.

Reviewer #2 (Public Review):

Summary:

The authors set out to study whether the cooling agent binding site in TRPM8, which is located between the S1-S4 and the TRP domain, is conserved within the TRPM family of ion channels. They specifically chose the TRPM4 channel as the model system, which is directly activated by intracellular Ca2+. Using electrophysiology, the authors characterized and compared the Ca2+ sensitivity and the voltage dependence of TRPM4 channels in the absence and presence of synthetic cooling agonist icilin. They also analyzed the mutational effects of residues (A867G and R901H; equivalent mutations in TRPM8 were shown involved in icilin sensitivity) on Ca2+ sensitivity and voltage-dependence of TRPM4 in the absence and presence of Ca2+. Based on the results as well as structure/sequence alignment, the authors concluded that icilin likely binds to the same pocket in TRPM4 and suggested that this cooling agonist binding pocket is conserved in TRPM channels.

Strengths:

The authors gave a very thorough introduction to the TRPM channels. They have nicely characterized the Ca2+ sensitivity and the voltage-dependence of TRPM4 channels and demonstrated icilin potentiates the Ca2+ sensitivity and diminishes the outward rectification of TRPM4. These results indicate icilin modulates TRPM4 activation by Ca2+.

We appreciate the supportive feedback of this reviewer.

Weaknesses:

The reviewer has a few concerns. First, icilin alone (at 25µM) and in the absence of Ca2+ does not activate the TRPM4 channel. Have the authors titrated a wide range of icilin concentrations (without Ca2+ present) for TRPM4 activation? It raises the question that whether icilin is indeed an agonist for TRPM4 channel. This has not been tested so it is unclear. One may argue that icilin needs Ca2+ as a co-factor for channel activation just like in TRPM8 channel. This leads to the second concern, which is a complication in the experimental design and data interpretation. TRPM4 itself requires Ca2+ for activation to begin with, thus it is hard to dissect whether the current observed here for TRPM4 is activated by Ca2+ or by icilin plus its cofactor Ca2+. This is the difference between TRPM8 and TRPM4, as TRPM8 itself is not activated by Ca2+, thus TRPM8 activation is through icilin and Ca2+ acts as a prerequisite for icilin activation.

We agree that the comparison between TRPM8 and TRPM4 is not perfect because TRPM4 requires Ca2+ for activation, but it is clear that the current activated by Ca2+ in the presence of icilin also involves icilin because it activates at lower Ca2+ concentrations and lower voltages. We have tested icilin at concentrations between 12.5 and 25 µM and at these concentrations icilin does not activate TRPM4 when applied alone, so we have no evidence that it is an agonist. Both of these concentrations are higher than those reported by Chuang et al. to be saturating for TRPM8 in the presence of Ca2+. We haven’t tested icilin at higher concentrations because we wanted to keep the final concentration of DMSO low enough to avoid any effects of the vehicle. We now emphasize this even more clearly in the revised manuscript.

The results presented in this study are only sufficient to show that icilin modulates the Ca2+-dependent activation of TRPM4 and icilin at best may act as an allosteric modulator for TRPM4 function. One cannot conclude from the current work that icilin is an agonist or even specifically a cooling agonist for TRPM4. Icilin is a cooling agonist for TRPM8, but it does not mean that if icilin modulates TRPM4 activity then it serves as a cooling agonist for TRPM4.

We agree with these comments, and we believe that the intent of our statements in the manuscript are completely in line with this perspective. We never refer to icilin as a cooling agent for TRPM4 but rather refer to the cooling agent binding pocket in TRPM8 and how that appears to be conserved and functions in TRPM4 to modulate opening of the channel. We have carefully gone through the manuscript to refer directly to icilin by name (rather than as a cooling agent) when referring to its actions on TRPM4 to make sure there is no confusion.

For the mutation data on A867G, Figure 4A-B, left panels, it looks like A867G has stronger Ca2+ sensitivity compared to the WT in the absence of icilin and the onset of current activation is faster than the WT, or this is simply due to the scale of the data figure are different between A867G and the WT. Overall the mutagenesis data are weak to support the conclusion that icilin binds to the S1-S4 pocket. The authors need to mutate more residues that are involved in direct interaction with icilin based on the available structural information, including but limited to residues equivalent to Y745 and H845 in human TRPM8.

The A867G mutant does seem to promote opening by Ca2+ in the absence of icilin, and we now comment on this in the manuscript. Having said that, we have not carefully studied the concentration-dependence for activation by Ca2+ because at higher concentrations we see evidence of desensitization. We think Ca2+, icilin and depolarized voltages promote an open state of TRPM4 and the A867G does so as well.

We respectfully disagree about the strength of mutagenesis results present in our manuscript. We present clear gain and loss of function for two mutants corresponding to influential residues within the cooling agent binding pocket of TRPM8. We agree that Y786 mutations would have been a valuable addition, and our plan was to include mutations of this residue. Unfortunately, both the Y786A and Y786H mutants exhibited rundown to repeated stimulation by Ca2+, making them challenging to obtain reliable results on their effects on modulation by icilin.

The authors set out to study the conservation of the cooling agonist binding site in TRPM family, but only tested a synthetic cooling agonist icilin on TRPM4. In order to draw a broad conclusion as the title and the discussion have claimed, the authors need to more cooling compounds, including the most well-known natural cooling agonist menthol, and other cooling agonists such as WS-12 and/or C3, and test their effects on several TRPM channels, not just TRPM4. With the current data, the authors need to significantly tone down the claim of a conserved cooling agonist binding pocket in the TRPM family.

We would have liked to broaden the scope to other ligands that modulate TRPM8 and we agree that including those data would certainly reinforce our conclusions. However, the first author recently moved on to a new faculty position and extending our findings would require enlisting another member of the lab and take away from their independent projects. We also do not agree that this is essential to support any of our conclusions. It is also important to keep in mind that icilin is a high-affinity ligand for TRPM8, such that weaker interactions with TRPM4 can still be readily observed. We think it is likely that lower affinity agonists like menthol might not have sufficient affinity to see activity in TRPM4. This scenario is not unlike our earlier experience with TRPV channels where we succeeded in engineering vanilloid sensitivity into TRPV2 and TRPV3 using the high affinity agonist resiniferatoxin (Zhang et al., 2016, eLife). In the case of TRPV2, another group had made the same quadruple mutant and failed to see activation by capsaicin even though resiniferatoxin also worked in their hands (see Fig. 2 in Yang et al., 2016, PNAS).

On page 11, the authors suggest based on the current data, that TRPM2 and TRPM5 may also be sensitive to cooling agonists because the key residues are conserved. TRPM2 is the closest homolog to TRPM8 but is menthol-insensitive. There are studies that attempted to convert menthol sensitivity to TRPM2, for example, Bandell 2006 attempted to introduce S2 and TRP domains from TRPM8 into TRPM2 but failed to make TRPM2 a menthol-sensitive channel. The sequence conservation or structural similarity is not sufficient for the authors to suggest a shared cooling agonist sensitivity or even a common binding site in the TRPM2 and TRPM5 channels. Again, as pointed out above, the authors need to establish the actual activation of other TRPM channels by these agonists first, before proceeding to functionally probe whether other TRPM channels adopt a conserved agonist binding site.

We are somewhat confused by these comments because we do not comment about whether cooling agents can activate TRPM2 or TRPM5. We simply analyzed the structures to make the point that the key residues in the cooling agent binding pocket of TRPM8 are conserved in these other TRPM channels. The Bandell paper is relevant, but it is also possible that they failed to uncover a relationship because they only used an agonist that has relatively low affinity for TRPM8. It would have been interesting to see what they might have found if they had used a high-affinity ligand like icilin instead of a low affinity ligand like menthol.

Taken together, this current work presents data to show the modulatory effects of icilin on the Ca2+ dependent activation and voltage dependence of the TRPM4 channel.

We agree.

Reviewer #3 (Public Review):

Summary:

The family of transient receptor potential (TRP) channels are tetrameric cation selective channels that are modulated by a variety of stimuli, most notably temperature. In particular, the Transient receptor potential Melastatin subfamily member 8 (TRPM8) is activated by noxious cold and other cooling agents such as menthol and icilin and participates in cold somatosensation in humans. The abundance of TRP channel structural data that has been published in the past decade demonstrates clear architectural conservation within the ion channel family. This suggests the potential for unifying mechanisms of gating despite their varied modes of regulation, which are not yet understood. To address this question, the authors examine the 264 structures of TRP channels determined to date and observe a potential binding pocket for icilin in multiple members of the Melastatin subfamily, TRPM2, TRPM4, and TRPM5. Interestingly, none of the other Melastatin subfamily members had been shown to be sensitive to icilin apart from TRPM8. Each of these channels is activated by intracellular calcium (Ca2+) and a Ca2+ binding site neighbors the predicted pocket for icilin binding in all cryo-EM structures. The authors examined whether icilin could modulate the activation of TRPM4 in the presence of intracellular Ca2+. The addition of icilin enhances Ca2+-dependent activation of TRPM4, promotes channel opening at negative membrane potentials, and improves the kinetics of opening. Furthermore, mutagenesis of TRPM4 residues within the putative icilin binding pocket predicted to enhance or diminish TRPM4 activity elicit these behaviors. Overall, this study furthers our understanding of the Melastatin subfamily of TRP channel gating and demonstrates that a conserved binding pocket observed between TRPM4 and TRPM8 channel structures can function similarly to regulate channel gating.

Strengths:

This is a simple and elegant study capitalizing on a vast amount of high-resolution structural information from the TRP channel of ion channels to identify a conserved binding pocket that was previously unknown in the Melastatin subfamily, which is interrogated by the authors through careful electrophysiology and mutagenesis studies.

Weaknesses:

No weaknesses were identified by this reviewer.

We appreciate the supportive comments of the review.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I don't have any major asks, but a few questions did arise while reading your work.

(1) You refer multiple times to the VSLD pocket as being "open to the cytoplasm". It is not clear if you are implying that compounds such as icilin access the pocket via the cytoplasm (e.g., permeate the membrane to the cytosol, and then enter the binding site?) Is there data to support this? Some clarification here would be helpful, and perhaps explain if there is any distinction between how calcium might enter the VSLD binding site vs hydrophobic compounds like icilin.

This is an excellent point. Our reference to “open to the cytoplasm” was for Ca2+ ions and we have no evidence for how icilin enters the cooling agent binding pocket. We had tried to look for evidence that Ca2+ might trap icilin in TRPM4 but at the end of the day the results were not convincing enough to include in the manuscript. We have added data showing that icilin slows deactivation of TRPM4 after removing Ca2+, which is particularly evident in the A867G mutant, but this doesn’t inform on whether Ca2+ can trap icilin. We have added a statement about not knowing how icilin enters or leaves the cooling agent binding pocket in TRPM channels.

(2) Icilin is referred to as a "cooling compound", but its cooling effects are dependent on its interactions with TRPM8. This might be something to clarify, as it might otherwise be understood that other TRPM channels that interact with icilin also mediate the sensing of cool temperatures.

This is another excellent point and we have no reason to believe that icilin interacting with any TRPM channel other than TRPM8 mediates cooling sensations. We have added a statement to this effect in the discussion when considering actions of icilin that might be mediated by TRPM4 channels.

Reviewer #2 (Recommendations For The Authors):

(1) The title and statements in the results/discussion refer to icilin as a cooling agonist of TRPM4 and binds to a conserved "cooling agonist binding pocket", and the authors suggested a similar role and binding site for icilin in TRPM2 and TRPM5 channel. It is a too broad conclusion that is not fully supported by the current experimental data, which only shows icilin works as a modulator, not an agonist for TRPM4 channel. The authors should change the usage of cooling agonist or conserved cooling agonist binding pocket plus significantly tone down the conclusion of a conserved cooling agonist binding pocket, which is potentially misleading. Alternatively, if the authors insist on using cooling agonist in this context, they should establish the activation of TRPM4, TRPM2, and TRPM5 by icilin as the first step, because the current data only support icilin as a TRPM4 modulator but not an agonist.

We respectfully don’t agree with this opinion. We show broad conservation of the cooling agent binding pocket in structures of many TRPM channels, and we chose one of them to test for a functional relationship. We think that the title accurately reflects the topic of the paper and does not specify the extent to which functional conservation has been demonstrated and we would like to keep it. The distinction between agonist and modulator is not even germane because icilin is not an agonist of TRPM8 either.

(2) The manuscript will be strengthened if the authors test additional cooling compounds of TRPM8, including menthol, the menthol analog WS-12, and C3. More importantly, distinct from icilin, these three compounds do not depend on Ca2+ to activate the TRPM8 channel. Thus when testing these compounds on TRPM4, it may reduce the complication of the role of Ca2+, as TRPM4 channel itself requires Ca2+ for activation.

We restate our response to this point in the public review…

We would have liked to broaden the scope to other ligands that modulate TRPM8 and we agree that including those data would certainly reinforce our conclusions. However, the first author recently moved on to a new faculty position and extending our findings would require enlisting another member of the lab and taking away from their independent projects. We also do not agree that this is essential to support any of our conclusions. It is also important to keep in mind that icilin is a high-affinity ligand for TRPM8, such that weaker interactions with TRPM4 can still be readily observed. We think it is likely that lower affinity agonists like menthol might not have sufficient affinity to see activity in TRPM4 This scenario is not unlike our earlier experience with TRPV channels where we succeeded in engineering vanilloid sensitivity into TRPV2 and TRPV3 using the high affinity agonist resiniferatoxin (Zhang et al., 2016, eLife). In the case of TRPV2, another group had made the same quadruple mutant and failed to see activation by capsaicin even though resiniferatoxin also worked in their hands (see Fig. 2 in Yang et al., 2016, PNAS).

(3) The manuscript will be strengthened if the authors test additional residues in the S1-S4 pocket that form direct interactions or are within interacting distances with icilin based on the cryo-EM structures.

We restate our response to this point in the public review…

We present clear gain and loss of function for two mutants corresponding to influential residues within the cooling agent binding pocket of TRPM8. We agree that Y786 mutations would have been a valuable addition and our plan was to include mutations of this residue. Unfortunately, both the Y786A and Y786H mutants exhibited rundown, making them challenging to obtain reliable results on their effects on modulation by icilin.

Furthermore, the ambiguity in the icilin binding pose based on available TRPM8 structures complicates structure-based identification of the most important interacting residues in TRPM8, and we would have needed to functionally validate the effects of any novel mutations we identified in TRPM8 prior to testing them in TRPM4. Instead, we have based our mutagenesis on constructs that have been previously characterized to affect the sensitivity of TRPM8 to cooling agents. A systematic mutagenesis scan of TRPM8 residues predicted to interact differentially with icilin in the two different available binding poses would likely help clarify the true binding pose of icilin and would be an interesting future study.

Reviewer #3 (Recommendations For The Authors):

I enjoyed reading this manuscript. It was well-executed and written. It will be interesting to corroborate these findings with a cryo-EM structure of TRPM2, TRPM4, or TRPM5 in the presence of icilin.

We agree and may pursue these in future studies. This would be particularly interesting given ambiguities in how icilin docks into TRPM8 in previously published structures.

Minor comments/questions:

Have the authors considered icilin accessibility to its binding pocket? In other words, could the presence of intracellular Ca2+ inhibit the accessibility of icilin to its binding pocket in TRPM4? It should be a straightforward experiment, I think it would be informative, and could further support the authors' conclusion of the location of the TRPM4 icilin binding pocket.

We completely agree and we had tried to look for evidence that Ca2+ might trap icilin in TRPM4 but at the end of the day the results were not convincing enough to include in the manuscript. We have added data showing that icilin slows deactivation of TRPM4 after removing Ca2+, which is particularly evident in the A867G mutant, but this doesn’t inform on whether Ca2+ can trap icilin. We have added a statement about not knowing how icilin enters or leaves the cooling agent binding pocket in TRPM channels.

Figures 7 and 8 are missing the 0 µM Ca2+ control trace in the presence of 25 µM icilin.

All sample traces from Figures 7 and 8 are shown from a single cell for the sake of comparison (Likewise, the sample traces from Figures 3 and 4 come from a single cell, and the sample traces from Figures 5 and 6 come from a single cell). Unfortunately, we were unable to obtain data from an R901H mutant cell that contained all six conditions we wished to show, and there is no representative trace for 0 µM Ca2+ in the presence of 25 µM icilin for that cell.

This is up to the discretion of the authors, but perhaps a better way to arrange the paper Figures would be to combine Figures 5-6 and Figures 7-8 and rearrange the data to place some in a supplementary figure (e.g. Figure 5-6 = Figure 5 and Figure 5 - Figure Supplement 1, Figure 7-8 = Figure 6 and Figure 6 - Figure Supplement 1).

We carefully considered these suggestions and we appreciate the reviewers’ flexibility but would prefer to retain the original arrangement of data in the figures.

Are there any mutations in the icilin binding pocket in TRPM4, and presumably TRPM2 and TRPM5, that are associated with human disease? This is a question that came to my mind and not one that needs to be addressed in the manuscript.

This is an interesting point. There are quite a few disease-associated mutants within TRPM4 at positions corresponding to the cooling agent binding pocket in TRPM8. We could not see an appropriate place in the discussion where we could concisely bring this information in so we decided against commenting.

I think this is something worth repeating. Any of us who have not been to residential schools may try to understand as best we can, educate ourselves, and read survivor's stories, but we will never truly relate to or completely understand the trauma that came with being there.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study provides an incremental advance to the scavenger receptor field by reporting the crystal structures of the domains of SCARF1 that bind modified LDL such as oxidized LDL and acylated LDL. The crystal packing reveals a new interface for the homodimerization of SCARF1. The authors characterize SCARF1 binding to modified LDL using flow cytometry, ELISA, and fluorescent microscopy. They identify a positively charged surface on the structure that they predict will bind the LDLs, and they support this hypothesis with a number of mutant constructs in binding experiments.

Strengths:

The authors have crystallized domains of an understudied scavenger receptor and used the structure to identify a putative binding site for modified LDL particles. An especially interesting set of experiments is the SCARF1 and SCARF2 chimeras, where they confer binding of modified LDLs to SCARF2, a related protein that does not bind modified LDLs, and use show that the key residues in SCARF1 are not conserved in SCARF2.

Weaknesses:

While the data largely support the conclusions, the figures describing the structure are cursory and do not provide enough detail to interpret the model or quality of the experimental X-ray structure data. Additionally, many of the flow cytometry experiments lack negative controls for non-specific LDL staining and controls for cell surface expression of the SCARF constructs. In several cases, the authors interpret single data points as increased or decreased affinity, but these statements need dose-response analysis to support them. These deficiencies should be readily addressable by the authors in the revision.

The paper is a straightforward set of experiments that identify the likely binding site of modified LDL on SCARF1 but adds little in the way of explaining or predicting other binding interactions. That a positively charged surface on the protein could mediate binding to LDL particles is not particularly surprising. This paper would be of greater importance if the authors could explain the specificity of the binding of SCARF1 to the various lipoparticles that it does or does not bind. Incorporating these mutants into an assay for the biological role of SCARF1 would be powerful.

Reviewer #2 (Public Review):

Summary:

The manuscript by Wang and colleagues provided mechanistic insights into SCARF1 and its interactions with the lipoprotein ligands. The authors reported two crystal structures of the N-terminal fragments of SCARF1 ectodomain (ECD). On the basis of the structural analysis, the authors further investigated the interactions between SCARF1 and modified LDLs using cell-based assays and biochemical experiments. Together with the two structures and supporting data, this work provided new insights into the diverse mechanisms of scavenger receptors and especially the crucial role of SCARF1 in lipid metabolism.

Strengths:

The authors started by determining the crystal structures of two fragments of SCARF1 ECD. The superposition of the two high-resolution structures, together with the predicted model by AlphaFold, revealed that the ECD of SCARF1 adopts a long-curved conformation with multiple EGF-like domains arranged in tandem. Non-crystallographic and crystallographic two-fold symmetries were observed in crystals of f1 and f2 respectively, indicating the formation of SCARF1 homodimers. Structural analysis identified critical residues involved in dimerization, which were validated through mutational experiments. In addition, the authors conducted flow cytometry and confocal experiments to characterize cellular interactions of SCARF1 with lipoproteins. The results revealed the vital role of the 133-221aa region in the binding between SCARF1 and modified LDLs. Moreover, four arginine residues were identified as crucial for modified LDL recognition, highlighting the contribution of charge interactions in SCARF1-lipoprotein binding. The lipoprotein binding region is further validated by designing SCARF1/SCARF2 chimeric molecules. Interestingly, the interaction between SCARF1 and modified LDLs could be inhibited by teichoic acid, indicating potential overlap in or sharing of binding sites on SCARF1 ECD.

The author employed a nice collection of techniques, namely crystallographic, SEC, DLS, flow cytometry, ELISA, and confocal imaging. The experiments are technically sound and the results are clearly written, with a few concerns as outlined below. Overall, this research represents an advancement in the mechanistic investigation of SCARF1 and its interaction with ligands. The role of scavenger receptors is critical in lipid homeostasis, making this work of interest to the eLife readership.

Reviewer #3 (Public Review):

Summary:

The manuscript by Wang et. al. described the crystal structures of the N-terminal fragments of Scavenger receptor class F member 1 (SCARF1) ectodomains. SCARF1 recognizes modified LDLs, including acetylated LDL and oxidized LDL, and it plays an important role in both innate and adaptive immune responses. They characterized the dimerization of SCARF1 and the interaction of SCARF1 with modified lipoproteins by mutational and biochemical studies. The authors identified the critical residues for dimerization and demonstrated that SCARF1 may function as homodimers. They further characterized the interaction between SCARF1 and LDLs and identified the lipoprotein ligand recognition sites, the highly positively charged areas. Their data suggested that the teichoic acid inhibitors may interact with SCARF1 in the same areas as LDLs.

Strengths:

The crystal structures of SCARF1 were high quality. The authors performed extensive site-specific mutagenesis studies using soluble proteins for ELISA assays and surface-expressed proteins for flow cytometry.

Weaknesses:

(1) The schematic drawing of human SCARF1 and SCARF2 in Fig 1A did not show the differences between them. It would be useful to have a sequence alignment showing the polymorphic regions.

The schematic drawing in Fig.1A is to give a brief idea about the two molecules, the sequence alignment may take too much space in the figure. A careful alignment between SCARF1 and SCARF2 can be found in Ref. 24 (Ishii, et al., J Biol Chem, 2002. 277, 39696-702) an also mentioned in p.4.

(2) The description of structure determination was confusing. The f1 crystal structure was determined by SAD with Pt derivatives. Why did they need molecular replacement with a native data set? The f2 crystal structure was solved by molecular replacement using the structure of the f1 fragment. Why did they need to use EGF-like fragments predicted by AlphaFold as search models?

The crystal structure of f1 was first determined by SAD using Pt derivatives, but soaking of Pt reduced the resolution of the crystals, therefore we use this structure as a search model for a native data set that had higher resolution for further refinement. For the structural determination of f2, the molecular replacement using f1 structure was not able to show the initial density of the extra region in f2 (residues 133-209), which was missing in f1. Therefore, the EGF-like domains of SCARF1 modeled by AlphaFold were applied as search models for this region (p.18).

(3) It's interesting to observe that SCARA1 binds modified LDLs in a Ca2+-independent manner. The authors performed the binding assays between SCARF1 and modified LDLs in the presence of Ca2+ or EDTA on Page 9. However, EDTA is not an efficient Ca2+ chelator. The authors should have performed the binding assays in the presence of EGTA instead.

The binding assays in the presence of EGTA are included in the revised manuscript (Fig. S7) (p.9), which also suggest that SCARA1 binds OxLDL in a Ca2+-independent manner.

(4) The authors claimed that SCARF1Δ353-415, the deletion of a C-terminal region of the ectodomain, might change the conformation of the molecule and generate hinderance for the C-terminal regions. Why didn't SCARF1Δ222-353 have a similar effect? Could the deletion change the interaction between SCARF1 and the membrane? Is SCARF1Δ353-415 region hydrophobic?

The truncation mutants were constructed to roughly locate the binding region of lipoproteins on SCARF1, and the overall results showed that the sites might locate at the region of 133-221. Mutant Δ222-353 may also affect the conformation, but it still had binding with OxLDL like wild type, suggesting the binding sites were retained in this mutant. Mutant Δ353-415 showed a reduction of binding, implying that the binding sites might be retained but binding was affected, we think it might be due to the conformational change that could reduce the binding or accessibility of lipoproteins. Since this region locates closer to the membrane, it’s possible that it may change the interaction with the membrane. In the AF model, Δ353-415 region does not seem to be more hydrophobic than other regions (Fig. S2C).

(5) What was the point of having Figure 8? Showing the SCARF1 homodimers could form two types of dimers on the membrane surface proposed? The authors didn't have any data to support that.

Fig. 8 shows a potential model of the SCARF1 dimers on the cell surface by combining the structural information from crystals and AF predictions. The two dimers in the figure are identical but with different viewing angles. The lipoprotein binding sites are also indicated (Fig. 8).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The authors need to show examples of the electron density for both structures.

Electron density examples of the two structures are shown in Fig. S2A.

Figure 1)

The figure does not show enough details of the structure. The text mentions hydrogen-bond and disulfide bonds that stabilize the loops, these should be shown.

Disulfide bonds of the two structures are shown in Fig. 1.

Figure 2)

D) The full gel should be shown.

E) Rather than just relying on changes in gel filtration elution volumes, the authors do the appropriate experiment and measure the hydrodynamic radius of the WT and mutant ectodomains by DLS. However, they need to show plots of the size distribution, not just mean radial values, in order to show if the sample is monodisperse.

The full gel and plots of DLS are shown in Fig. S3A-B.

Figure 3)

I have concerns about the rigor of the experiments in panels A-D. The authors include a non-transfected control but do not appear to have treated non-transfected cells with the lipoproteins to evaluate the specificity of binding. Every cell binding assay (flow  or confocal) must show the data from non-transfected cells treated with each lipoprotein, as each lipoprotein species could have a unique non-specific binding pattern. The authors show these controls in Figure 6, but these controls are necessary in every experiment.

In Fig. 3A, since several lipoproteins were included in the figure, we use non-transfected cells without lipoprotein treatment as a negative control. The OxLDL or AcLDL treated non-transfected cells were also used as negative controls and shown in Fig. 3B-C. LDL, HDL or OxHDL may have their own non-specific binding patterns, the treatment of LDL, HDL or OxHDL with the transfected cells all gave negative results (Fig. 3A and D).

Cell-surface of the SCARF1 variants is a major concern. The constructs the authors use are tagged with a GFP on the cytosolic side. However, the Methods to do indicate if they gate on GFP+ transfected cells for analytical flow. Such gating may have been used because the staining experiments in Figures 3 and 4 show uniform cell populations, whereas the staining done with an anti-SCARF1 Ab in S4 shows most of the cells not expressing the protein on the surface. Please clarify.

Data for the anti-SCARF1 Ab assay is gated for GFP in the revised Fig. S4, and  the non-transfected cells are included as a control.

The authors must demonstrate cell-surface staining with an epitope tag on the extracellular side and clarify if the analyzed cells are gated for surface expression. The anti-SCARF antibody used in S4 may not recognize the truncated or mutant SCARFs equally. Cell-surface expression in the flow experiments cannot be inferred from confocal experiments because the flow experiments have a larger quantitative range.

Anti-SCARF1 antibody assay provides an estimation of the surface expression of the proteins. If the epitope of the antibody was mutated or removed in the mutants, most likely it would lose binding activity. Including an epitope tag on the ectodomain could be an option, but if truncation or mutation changes the conformation of the ectodomain, the accessibility of the epitope may also be affected, and addition of an extra sequence or domain, such as an epitope tag, may affect the surface expression of proteins sometimes.

In several places, the authors infer increased or decreased affinity from mean fluorescent intensity values of a single concentration point without doing appropriate dose-curves. These experiments need to be done or else the mentions of changes in apparent affinities should be removed.

We add a concentration for the WT interaction with OxLDL (Fig. S6, p.9) and the manuscript is also modified accordingly.

Figure 7

The concentration of teichoic acid used to inhibit modified LDL binding should be indicated and a dose-curve analysis should be done comparing teichoic acid to some non-inhibitory bacterial polymer.

The concentration of teichoic acids used in the inhibition assays is 100 mg/ml (p.21). Unfortunately, we don’t have other bacterial polymers in the lab and not sure about the potential inhibitory effects.

Reviewer #2 (Recommendations For The Authors):

Major points:

(1) The SCARF1 ECD contains three N-linked glycosylation sites (N289, N382, N393). It remains unclear whether these modifications are involved in SCARF1 binding to modified LDLs. Is it possible to design some experiments to investigate the effect of N-glycans on the recognition of modified LDLs? In particular, N382 and N393 are included in 353-415aa and the truncation mutant of SCARF1Δ353-415aa resulted in reduced binding with OxLDL in Fig.3G. Or whether the reduced binding is only due to the potential conformational changes caused by the deletion of the C-terminal region of the ECD?

A previous study regarding the N-glycans (N289, N382, N393) of SCARF1 (ref.17) has shown that they may affect the proteolytic resistance, ligand-binding affinity and subcellular localization of SCARF1, which is not quite surprising as lipoproteins are large particles, the N-glycans on the surface of SCARF1 could affect accessibility or affinity for lipoproteins. But the exact roles of each glycan could be difficult to clarify as they might also be involved in protein folding and trafficking.

The reduction of the binding of OxLDL for the mutant SCARF1 Δ353-415aa may be due to the conformational change or the loss of the glycans or both.

(2) The authors speculated that the dimeric form of SCARF1 may be more efficient in recognizing lipoproteins on the cell surface. Please highlight the critical region/sites for ligand binding in Figure 8 and discuss the structural basis of dimerization improving the binding.

The binding sites for lipoproteins on SCARF1 are indicated in Fig. 8. According to our data, it might be possible the conformation of the dimeric form of SCARF1 makes it more accessible to the ligands on the cell surface as implied by flow cytometry (p.14-15), but still needs further evidence on this.

(3) Could the two salt bridges (D61-K71, R76-D98) observed in f1 crystals be found in f2 crystals? They seemed to be a little far from the defined dimeric interface (F82, S88, Y94) and how important are these to SCARF1 dimerization?

The two salt bridges observed in f1 crystal are not found in f2 crystal (distances are larger than 5.0 Å), suggesting they are not required for dimerization (p. 7-8), but may be helpful in some cases.

(4) The monomeric mutants (S88A/Y94A, F82A/S88A/Y94A) exhibited opposite affinity trends to OxLDL in ELISA and flow cytometry. The authors proposed steric hinderance of the dimers coated onto the plates as the potential explanation for this observation. However, the method of ELISA stated that OxLDLs, instead of SCARF1 ECD, were coated onto the plates. So what's the underlying reason for the inconsistency in different assays?

Thanks. ELISA was done by coating OxLDLs on the plates as described in the Methods. But still, a dimeric form of SCARF1 may only bind one OxLDL coated on the plates due to steric hinderance. We correct this on p.12.

Minor points:

(1) Figure 2D and Figure S3 - please label the molecular weight marker on the SEC traces to indicate the native size of various purified proteins.

The elution volume of SEC not only reflects the molecular weight, but it’s also affected by the conformation or shape of protein. The ectodomain of SCARF1 has a long curved conformation, the elution volumes of the monomeric or dimeric forms of SCARF1 do not align well with the standard molecular weight marker and elute much earlier in SEC. We include the standard molecular weight marker in Fig. S3C-D.

(2) Could the authors provide SEC profiles of f1 and f2 that were used in crystallographic study?

The SEC profiles of f1 and f2 for crystallization are shown in Fig. S5 (p.6).

(3) The legend of Figure 3A states that the NC in flow cytometry assay represents the non-transfected cells, but please confirm whether the NC in Fig. 3A-C corresponds to non-transfected cells or no lipoprotein.

NC in Fig. 3A represents the non-transfected cells, and no lipoproteins were added in this case as several lipoproteins are included in Fig. 3A. The lipoprotein (OxLDL or AcLDL) treated non-transfected cells (NC) were shown in Fig. 3B-C as negative controls.

Author response:

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript authored by Stockner and colleagues delves into the molecular simulations of Na+ binding pathway and the ionic interactions at the two known sodium binding sites site 1 and site 2. They further identify a patch of two acidic residues in TM6 that seemingly populate the Na+ ions prior to entry into the vestibule. These results highlight the importance of studying the ion-entry pathways through computational approaches and the authors also validate some of their findings through experimental work. They observe that sodium site 1 binding is stabilized by the presence of the substrate in the s1 site and this is particularly vital as the GABA carboxylate is involved in coordinating the Na+ ion unlike other monoamine transporters and binding of sodium to the Na2 site stabilizes the conformation of the GAT1 by reducing flexibility among the helical bundles involved in alternating access.

Strengths:

The study displays results that are generally consistent with available information from experiments on SLC6 transporters particularly GAT1 and puts forth the importance of this added patch of residues in the extracellular vestibule that could be of importance to the ion permeation in SLC6 transporters. This is a nicely performed study and could be improved if the authors could comment on and fix the following queries.

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

Comments on revised version:

The authors have satisfactorily addressed my comments and this has significantly improved the clarity of the manuscript.

The only point that I would like to inquire about is the role of EL4 in modulating Na+ entry.

In the simulations do the authors see no role of EL4 in controlling Na+ entry. It is particularly intriguing as some studies in the recent past displayed charged mutations in EL4 of dDAT, SERT and GAT1 as being detrimental for substrate entry/uptake. It would therefore be nice to add a small discussion if there is any role for EL4 in Na+ entry.

In this study we focused on sodium binding to the sodium binding site NA1 and NA2 and discovered the role of negatively charged residues at the beginning of TM6 contribution to sodium binding. Our data shows less than average interactions of sodium ions with EL4. In particular, we do also not observe any prominent role for D355, which is the only negatively charged residues in EL4a. We associate this effect to the presence of four positively charged residues (R69,Y76, K350, R351) surrounded D355 and an electrostatic repulsion by a local positive field, which is also visible in Figure 1k. Following the suggestion of the reviewer, we added a short statement to the last paragraph of the discussion.

Reviewer #2 (Public Review):

Summary

Starting from an AlphaFold2 model of the outward-facing conformation of the GAT1 transporter, the authors primarily use state-of-the-art MD simulations to dissect the role of the two Na+ ions that are known to be co-transported with the substrate, GABA (and a cotransported Cl- ion). The simulations indicated that Na+ binding to OF GAT depends on the electrostatic environment. The authors identify an extracellular recruiting site including residues D281 and E283 which they hypothesized to increase transport by locally increasing the available Na+ concentration and thus increasing binding of Na+ to the canonical binding sites NA1 and NA2. The charge-neutralizing double mutant D281AE283A showed decreased binding in simulations. The authors performed GABA uptake experiments and whole-cell patch clamp experiments that taken together validated the hypothesis that the Na+ staging site is important for transport due to its role in pulling in Na+.

Detailed analysis of the MD simulations indicated that Na+ binding to NA2 has multiple structural effects: The binding site becomes more compact (reminiscent of induced fit binding) and there is some evidence that it stabilizes the outward-facing conformation.

Binding to NA1 appears to require the presence of the substrate, GABA, whose carboxylate moiety participates in Na+ binding; thus the simulations predict cooperativity between binding of GABA and Na+ binding to NA1.

Strengths

- MD simulations were used to propose a hypothesis (the existence of the staging Na+ site) and then tested with a mutant in simulations AND in experiments. This is an excellent use of simulations in combination with experiments.

- A large number of repeat MD simulations are generally able to provide a consistent picture of Na+ binding. Simulations are performed according to current best practices and different analyses illuminate the details of the molecular process from different angles.

- The role of GABA in cooperatively stabilizing Na+ binding to the NA1 site looks convincing and intriguing.

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

Weaknesses

- Assessing the effects of Na+ binding on the large scale motions of the transporter is more speculative because the PCA does not clearly cover all of the conformational space and the use of an AlphaFold2 model may have introduced structural inconsistencies. For example, it is not clear if movements of the inner gate are due to a AF2 model that's not well packed or really a feature of the open outward conformation.

We do not think that the results of the manuscript and in particular the large scale motions are speculative or dependent too much on the limitations of PCA. We only use PCA for Figure 6a-d,6g,h. Motions of SLC6 transporters (and of any other transporter) are much more complex than a single 2D PCA plot could every capture. We therefore used PCA here only to identify the two motions with the largest amplitude, show in Figure 6a-d, 6g,h.

Given that all the ~13000 degrees of freedom of GAT1 contribute to conformational differences, a dimensionally reduction method like PCA can be very helpful for extracting dominant motions. Structure comparison showed that motions observed in PC1 captured a large portion of the motions of occlusion (Figure 6c,d) when compared to the full transition observed in the unfiltered trajectories (See Figure 6e,f). PCA therefore helps to extract this main motions.

For completeness, we show a series of structures from the unfiltered trajectories in figure 6e,f. In the overlay, the motion of occlusion is more difficult to observe, because convoluted with all other degrees of freedom. In figure 6e,f, the structures are aligned with the maximum likelihood method theseus, while the coloring is based on the amplitudes measured by PCA to visualize the regions moving relative to each other with largest amplitude. All other structural measures, including the opening of the inner gate (Figure 6i-k), are direct measures of the raw trajectories.

With respect to the question of the instability of the inner gate, we made similar observations for hSERT (please see DOI: 10.1038/s41467-023-44637-6) using the experimentally determined structure as starting point. We find a weakening of the inner gate for sodium free SERT and at intermediate or full occlusion of sodium- and serotonin-bound SERT. These previous data on SERT corroborate our finding and indicates that the effect could be a general feature of the SLC6 transporter family.

Unfortunately no outward-open structure of GAT1 was available for this study. AlphaFold2 models have limitations and we are well aware of these limitations, but AlphaFold2 can also make high quality models including small adjustment of backbone positions, if the sequence identity is high, as in the current project (43% sequence identity for the transmembrane region). For GAT1 (as described in the manuscript) we initially tested hSERT based model created with MODELLER. MODELLER uses as premises the assumption that the protein backbone does not change or only very little between the template protein and the target protein. These MODELLER created models did not perform well, because of a slight shift in the position of the backbone, which is a consequence of consistently smaller side chains in the bundle domain-scaffold domain interface of GAT1 as compared to SERT.

In the simulations described in the manuscript (using the AlphaFold created model) we observed that the overall structural and dynamic parameters and in particular also observation at the inner gate are very similar to the results described in our papers on sodium binding to SERT using experimental SERT structures. The differences of Na1 binding are explained in the manuscript and are contingent to the residue difference of D98 in SERT and the corresponding residue G65 in GAT1. This makes us confident about the quality of the obtained data. Please see DOI: 10.3390/cells11020255; DOI: 10.3389/fncel.2021.673782.

- Quantitative analyses are difficult with the existing data; for example, the tICA "free energy" landscape is probably not converged because unbinding events haven't been observed.

The tICA analysis is a Marco State Model approach, which relies on the convergence of transitions between a large number of microstates. A limited number of trajectories showing full sodium unbinding are not obligatory for converged dataset, but the transitions between the microstates must to be converged. For the transitions within the S1 we have many transitions and very good convergence for transition probabilities within the S1. We limit interpretation of free energy data and discussion on this part of the free energy surface. The supporting information (Figure S5) reports on the quality of the tICA analysis. Flat lines with a time lag larger than 40 ns is consistent with a converged model based on the data of the trajectories used for the analysis, and consistently, also the Chapman-Kolmogorov tests show minimal difference between estimates and predictions.

We see about 40 binding event from the extracellular side to the S1, which seems insufficient for a converged quantification for sodium transiting from the extracellular side to the S1. We state this limitation of the dataset in the results section of the manuscript.

This refers to mothers needing personal time for themselves and needing to do things that may not benefit the child but allow the mother some time of peace and cause no harm to the child. This quote shows the complexity of maternal expectations and that mothers need to be able to have their own time when possible. An example of this is an overactive child when mothers put them to sleep to allow them a brief time to themselves. That being said little harm done.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

In this manuscript, Day et al. present a high-throughput version of expansion microscopy to increase the throughput of this well-established super-resolution imaging technique. Through technical innovations in liquid handling with custom-fabricated tools and modifications to how the expandable hydrogels are polymerized, the authors show robust ~4-fold expansion of cultured cells in 96-well plates. They go on to show that HiExM can be used for applications such as drug screens by testing the effect of doxorubicin on human cardiomyocytes. Interestingly, the effects of this drug on changing DNA organization were only detectable by ExM, demonstrating the utility of HiExM for such studies. 

Overall, this is a very well-written manuscript presenting an important technical advance that overcomes a major limitation of ExM - throughput. As a method, HiExM appears extremely useful, and the data generally support the conclusions. 

Strengths: 

Hi-ExM overcomes a major limitation of ExM by increasing the throughput and reducing the need for manual handling of gels. The authors do an excellent job of explaining each variation introduced to HiExM to make this work and thoroughly characterize the impressive expansion isotropy. The dox experiments are generally well-controlled and the comparison to an alternative stressor (H2O2) significantly strengthens the conclusions. 

Weaknesses: 

(1) Based on the exceedingly small volume of solution used to form the hydrogel in the well, there may be many unexpanded cells in the well and possibly underneath the expanded hydrogel at the end of this. How would this affect the image acquisition, analysis, and interpretation of HiExM data? 

The hydrogel footprint covers approximately 5% of the surface within an individual well and only cells within this area are embedded in the polymerized hydrogel for subsequent processing steps. Cells that are outside of this footprint are not incorporated into the gel because these cells are digested by Proteinase K and washed away by the excess water exchange in the gel swelling step. Note that different cell types may require higher or lower concentrations of Proteinase K to adequately digest cells for expansion while maintaining fluorescence signal. Given the compatibility of HiExM with 96-well plates, this titration can be performed rapidly in a single experiment. Although cells outside of the hydrogel footprint are removed prior to imaging, we do occasionally observe Hoechst signal that appears to be underneath the gels. We believe this signal is likely from excess DNA from digested cells that was not fully washed out in the gel swelling step. This signal is both spatially and morphologically distinct from the nuclear signal of intact cells and it does not affect image acquisition, analysis, or data interpretation. 

(2) It is unclear why the expansion factor is so variable between plates (e.g., Figure 2H). This should be discussed in more detail. 

The variability in expansion factor across plates can likely be attributed to the small volume of gel solution (~250 nL) required for expansion within 96 well plates. Small variations in gel volume could impact gel polymerization compared to standard ExM gels. For example, gels in HiExM are more sensitive to evaporation because of the ~1000x reduced volume compared to standard expansion gel preparations, resulting in an increased air-liquid-interface. Evaporation in HiExM gels would increase monomer and cross linker concentrations, leading to variation in expansion factor across plates. We note that expansion factor is robust within well plates and that variance is slightly increased between plates. These considerations are discussed in the revised manuscript.

(3) The authors claim that CF dyes are more resistant to bleaching than other dyes. However, in Figure. S3, it appears that half of the CF dyes tested still show bleaching, and no data is shown supporting the claim that Alexa dyes bleach. It would be helpful to include data supporting the claim that Alexa dyes bleach more than CF dyes and the claim that CF dyes in general are resistant to bleaching should be modified to more accurately reflect the data shown. 

We did not show data using Alexa dyes because these fluorophores are highly sensitive to photobleaching using Irgacure and thus we could not obtain images. In contrast, some CF dyes are more robust to bleaching in HiExM including CF488A, CF568, and CF633 dyes.  We have recently adapted our protocol to PhotoExM chemistry which is compatible with a wider range of fluorophores as described by Günay et al. (2023) and as shown in Fig. S16.

(4) Related to the above point, it appears that Figure S11 may be missing the figure legend. This makes it hard to understand how HiExM can use other photo-inducible polymerization methods and dyes other than CF dyes.

We revised the legend for revised Fig. S11 (now Fig. S16) as follows: Example of a cell expanded in HiExM using Photo-ExM gel chemistry. Photo-ExM does not require an anoxic environment for gel deposition and polymerization, improving ease of use of HiExM. Mitochondria were stained with an Alexa 647 conjugated secondary antibody, demonstrating that HiExM is compatible with additional fluorophores when combined with Photo-ExM.

(5) The use of automated high-content imaging is impressive. However, it is unclear to me how the increased search space across the extended planar area and focal depths in expanded samples is overcome. It would be helpful to explain this automated imaging strategy in more detail. 

We imaged plates on the Opera Phenix using the PreciScan Acquisition Software in Harmony. In brief, each well is imaged at 5x magnification in the Hoechst channel to capture the full well at low resolution. Hoechst is used for this step given its signal brightness, ubiquity across established staining protocols, and spectral independence from most fluorophores commonly conjugated to secondary antibodies. Using this information, the microscope detects regions of interest (nuclei) based on criteria including size, brightness, circularity, etc. Finally, the positional information for each region is stored, and the microscope automatically images those regions at 63x magnification. The working distance for the objective used in this study is 600 µm which is sufficient to capture the entirety of expanded cells in the Z direction. This strategy minimizes offtarget imaging and allows robust image acquisition even in cultures with lower seeding density. A detailed description of the automated imaging strategy is included in the methods section of the revised manuscript.

(6) The general method of imaging pre- and post-expansion is not entirely clear to me. For example, on page 5 the authors state that pre-expansion imaging was done at the center of each gel. Is pre-expansion imaging done after the initial gel polymerization? If so, this would assume that the gelation itself has no effect on cell size and shape if these gelled but not yet expanded cells are used as the reference for calculating expansion factor and isotropy. 

Pre-expansion imaging is performed after staining is complete, but prior to the application of AcX, which is the first step of the HiExM protocol. Following staining and imaging, plates can be sealed with parafilm and stored at 4˚C for up to a week prior to starting the expansion protocol. We typically image 61 fields of view at the center of the well plate (where the gel will be deposited) to obtain sufficient pre-expansion images as shown in Figure 2b (left). After preexpansion imaging, we perform the HiExM protocol followed by image acquisition. We then tile all the images, as shown in Figure 2b, and compare tiled images from the same well pre- and post-expansion to manually identify the same cells. Comparisons of the pre- and postexpansion images of the same cell are used to calculate expansion factor and isotropy measurements as described. A detailed description of this process is included in the revised manuscript.

(7) In the dox experiments, are only 4 expanded nuclei analyzed? It is unclear in the Figure 3 legend what the replicates are because for the unexpanded cells, it says the number of nuclei but for expanded it only says n=4. If only 4 nuclei are analyzed, this does not play to the strengths of HiExM by having high throughput.

We performed the doxorubicin titration assay across four different well plates (n=4). For each condition, the total number of expanded nuclei measured was 118, 111, 110, 113, and 77 for DMSO, 1nM, 10nM, 100nM, and 1µM, respectively. For SEM calculations, we included the number of independent experiments to avoid underestimating error. We revised the Fig. 3 legend to include these experimental details.

(8) I am not sure if the analysis of dox-treated cells is accurate for the overall phenotype because only a single slice at the midplane is analyzed. It would be helpful to show, at least in one or two example cases, that this trend of changing edge intensity occurs across the whole 3D nucleus.  

For this analysis, the result is heavily dependent on the angle at which the edge of the nucleus intersects the image plane in the orthogonal view. For this reason, we opted to only use the optimal image plane for each nucleus. We repeated our analysis on an image using multiple optical sections to demonstrate this point. These new data are included as Fig. S11 of the revised manuscript.

(9) It would be helpful to provide an actual benchmark of imaging speed or throughput to support the claims on page 8 that HiExM can be combined with autonomous imaging to capture thousands of cells a day. What is the highest throughput you have achieved so far?  

The parameters that dictate imaging speed in HiExM include exposure time, z-stack height, and number of fluorophore channels. Depending on the signal intensity for a given channel, exposure times vary from 200ms to 1000ms. For z-stack height, we found that imaging 65 sections with 1µm spacing allowed for robust identification of each region of interest in the 5x pre-scan. As an example, collecting images for a full well plate (e.g., 20 images per well with 4 channels) requires approximately 24 hours of autonomous image acquisition using the Opera Phenix. Depending on cell size, this process yields imaging data for 1200 cells (1 cell per field of view) to 6000 cells (5 cells per field of view). Different autonomous imagers as well as improving staining techniques that increase signal:noise can be expected to significantly decrease the exposure time as it will reduce the number of z-stacks needed for each region.

Reviewer #2 (Public Review): 

Summary: 

In the present work, the authors present an engineering solution to sample preparation in 96well plates for high-throughput super-resolution microscopy via Expansion Microscopy. This is not a trivial problem, as the well cannot be filled with the gel, which would prohibit the expansion of the gel. A device was engineered that can spot a small droplet of hydrogel solution and keep it in place as it polymerizes. It occupies only a small portion of space at the center of each well, the gel can expand into all directions, and imaging and staining can proceed by liquid handling robots and an automated microscope. 

Strengths: 

In contrast to Reference 8, the authors' system is compatible with standard 96 well imaging plates for high-throughput automated microscopy and automated liquid handling for most parts of the protocol. They thus provide a clear path towards high-throughput ExM and highthroughput super-resolution microscopy, which is a timely and important goal. 

Weaknesses: 

The assay they chose to demonstrate what high-throughput ExM could be useful for, is not very convincing. But for this reviewer that is not important. 

We believe the data provide an example of the utility of HiExM that would benefit experiments that require many samples (e.g., conditions, replicates, timepoints, etc.) by enabling easier sample processing and autonomous acquisition of thousands of nanoscale images in parallel. The ability to generate large data sets also enables quantitative analysis of images with appropriate statistical power. The intention of this work is to provide a proof-of-concept example of the robustness, accessibility, and experimental design flexibility of HiExM.

Reviewer #3 (Public Review):

Summary: 

Day et al. introduced high-throughput expansion microscopy (HiExM), a method facilitating the simultaneous adaptation of expansion microscopy for cells cultured in a 96-well plate format. The distinctive features of this method include 1) the use of a specialized device for delivering a minimal amount (~230 nL) of gel solution to each well of a conventional 96-well plate, and 2) the application of the photochemical initiator, Irgacure 2959, to successfully form and expand the toroidal gel within each well.  

Strengths: 

This configuration eliminates the need for transferring gels to other dishes or wells, thereby enhancing the throughput and reproducibility of parallel expansion microscopy. This methodological uniqueness indicates the applicability of HiExM in detecting subtle cellular changes on a large scale. 

Weaknesses: 

To demonstrate the potential utility of HiExM in cell phenotyping, drug studies, and toxicology investigations, the authors treated hiPS-derived cardiomyocytes with a low dose of doxycycline (dox) and quantitatively assessed changes in nuclear morphology. However, this reviewer is not fully convinced of the validity of this specific application. Furthermore, some data about the effect of expansion require reconsideration. 

The application we chose was intended as a methods proof-of-concept that could enable future deep biological investigations using HiExM. We believe the data provide an example of the utility of HiExM for collecting thousands of nanoscale images that would benefit experiments that require many samples (e.g., conditions, replicates, timepoints, etc.). The ability to generate large data sets also enables quantitative analysis of images with appropriate statistical power. The intention of this experiment was to provide a proof-of-concept example of the robustness, accessibility, and experimental design flexibility of HiExM. 

The variability in expansion factor across plates can likely be attributed to the small volume (~250 nL) deposited by the device posts. Small variations in gel volume could impact gel polymerization compared to standard ExM gels. For example, HiExM gels are more sensitive to evaporation due to an increased air-liquid-interface because they are ~1000x smaller than standard expansion gel preparations. Evaporation in HiExM gels likely increases monomer and cross linker concentrations, leading to variation in expansion factor across plates. We note that expansion factor is robust within well plates and that the expansion factor can be more variable between plates, likely due to differences in gel volumes and evaporation. Future iterations of the platform are expected to control for these environmental conditions. These differences are discussed in the revised manuscript.

Recommendations for the authors:.

Reviewer #1 (Recommendations For The Authors):

(1) Please include a scale bar in Figure 3a.

A scale bar has been added to Figure 3a.

(2) Please show the data related to nuclear volume after dox treatment.

We have added a supplementary figure (Fig. S10) showing nuclear volume and sphericity for post-expansion nuclei as well as nuclear area and circularity for pre-expansion nuclei.

(3) I think it would be extremely helpful for the method as a whole if analysis code and files for device fabrication were made publicly available rather than upon request.

The analysis code has been included in the supplementary files as CM_Hoechst_Analysis_for publication.ipynb. Device design files are also available at the supplementary files link as hiExM_device.SLDPRT (96-well plate device) and MultiExM_24_July28_2022.SLDPRT (24-well plate device).

(4) Some details are missing from the methods, such as the concentration of AcX used for HiExM, the concentration of antibodies, etc. Related, how long does the photopolymerization take? Just the 60 seconds that the UVA light is on?

Additional protocol details are included in the methods section of the revised manuscript. The photopolymerization does only take 60 seconds.

Reviewer #2 (Recommendations For The Authors):

(1) The first three references are chosen a little strangely here. I suggest citing STED, SIM, and PALM/STORM from the original manuscripts here. Also, EM is technically not a super-resolution technique as it is within the resolution of electron beams. This reviewer would stay with light microscopy methods when discussing "super-resolution".

We removed the reference to EM and added citations to the original publications for SIM, STED, and STORM.

(2) The sentence after citation 4 is a little off in its meaning.

We have edited the sentence to improve clarity.

(3) It is highly useful and great that the authors include the observations on the effect of photopolymerization with Irgacure 2959 on dyes.

(4) In the discussion, the authors could mention new high NA silicone oil objectives that may further optimise the resolution in their scheme.

We added a sentence in the discussion to reflect this important point.

(5) The files for the manufacture of the HiExM devices must be in the supplementary data rather than available on request.

The Solidworks designs for the 96 and 24 well plate devices are included in the supplementary files as hiExM_device.SLDPRT and MultiExM_24_July28_2022.SLDPRT, respectively.

(6) It would be useful if the authors could discuss their thoughts on the high throughput processing of expansion factors in the data analysis routine.

We added details to the methods section describing how images are processed and analyzed.

Reviewer #3 (Recommendations For The Authors):

Major:

(1) In the experiments depicted in Figure 3, the authors attempted cellular phenotyping using hiPCS-derived cardiomyocytes treated with doxorubicin (dox). They addressed that the relative intensity of Hoechst at the nuclear periphery increased solely in post-expansion images, although this trend is not clearly evidenced in the provided data (e.g., DMSO control vs. 1 nM dox, Figure 3b). Moreover, this observed phenomenon lacks clear biological significance and may not be suitable as a demonstration for proof-of-concept (POC) acquisition. It is crucial to delineate the biological processes linked with the specific enhancement of DNA binding dye signals in the nuclear periphery and how to rule out the possibility of heterogeneous redistribution of nuclear components rather than enhancing resolution. For instance, if this change can be associated with a biological process such as DNA damage, quantitative detection of the accumulated proteins related to DNA repair, or the specific histone marks, may be more suitable and less susceptible to heterogeneous expansion factors. Additionally, the authors noted the absence of significant changes in nuclear volume, yet the corresponding data was not presented. Moreover, the application insufficiently demonstrated the HiExM's scalable feature employing various well plates. If only acquiring images of dozens of nuclei (Figure 3 legend, p15), a single well per condition would suffice. Therefore, it is necessary to elucidate why this application necessitates a 96-well format for demonstration purposes. The potential experimental design should also incorporate the requirement for well-to-well replication and the acquisition of features at the individual well level, rather than at the single-cell level. Also, related to Figure S10, whether outer gradient slope, but not inner gradient slope, is linked to apoptosis (Page 8, Line 2-4) remains unclear in the H2O2-treated cells.

We believe the data provide an example of the utility of HiExM that would benefit experiments that require many samples (e.g., conditions, replicates, timepoints, etc.) by enabling easier sample processing and autonomous acquisition of thousands of nanoscale images in parallel. The ability to generate large data sets also enables quantitative analysis of images with appropriate statistical power. The intention of this work is to provide a proof-of-concept example of the robustness, accessibility, and experimental design flexibility of the HiExM method. As discussed in the manuscript, dox treatment is associated with DNA damage, cellular stress, and apoptosis, and commonly observed at high dox concentrations (>200 nM) in in vitro studies using conventional microscopy. Our data suggest that cardiomyocytes exhibit sensitivity to lower concentrations of dox than previously anticipated. Although direct evidence specifically linking dox to increased DNA condensation at the nuclear periphery is limited, the known proapoptotic effects of dox strongly suggest that our observations correlate with these changes. We have now included the data analysis on nuclear morphology in revised Fig. S10. We agree that deeper biological interpretation of the observed changes in Hoechst signal upon dox treatment (or other cellular stressors such as H2O2) using HiExM and whether these changes are correlated with DNA damage or other cellular alterations remains an exciting future direction to develop a more sensitive platform for assessing drug responses.

For expanded samples, we performed the doxorubicin titration assay across four different well plates (n=4). For each condition, the total number of nuclei measured was 118, 111, 110, 113, and 77 for DMSO, 1nM, 10nM, 100nM, and 1µM, respectively. We apologize for the confusion with respect to the number of replicates and cells analyzed. For SEM calculations, we used the number of independent experiments to avoid underestimating error. 

(2) In Figure 2b, do the orange arrows indicate the same cell with a unique shape in both the pre- and post-expansion images? Additionally, in Figure 3b, why do the pre- and post-expansion nuclei exhibit such different global shapes? Considering that the gel may freely rotate within the well during expansion, it raises doubts about whether one can identify cells with consistent shapes in both the pre- and post-expansion images. Furthermore, this reviewer observed a similar issue regarding reproducibility among different well plates, as shown in Figure 2h. The panel illustrates that different plates yielded distinct populations of gel sizes. The expansion factors provided in the figure legend (page 13) ranged from 3.5x to 5.1x across gels, indicating a relatively large variation in expansion size. What is the reason behind these variations, and how can they be minimized? These variations could become critical when considering large-scale screening across multiple plates.

The orange arrow is intended to indicate the same cell with a unique shape in both the pre- and post-expansion images, albeit at a different orientation given that the gel is not fixed within the well. We agree that improved methods to identify the same cells pre- and post-expansion could facilitate error measurements. We have referenced recent methods that could be combined with HiExM to automate and improve error and distortion detection to the discussion of the revised manuscript. 

Fig. 2 illustrates the ability of HiExM to achieve reproducible gel formation with minimal error within gels, wells, and across plates, measurements consistent with proExM. While uniform within gels, the expansion factor is somewhat variable between gels and plates. We attribute these differences primarily to the small size of the gels, making them vulnerable to the effects of evaporation between experiments. We note this variability should be taken into consideration for studies where absolute length measurements between plates are important for biological interpretation. Future iterations of the platform that allow precise delivery of gel volumes and that minimizes environmental exposure are expected to improve the expansion factor reproducibility across plates to further enable the use of HiExM as a tool for high-throughput nanoscale imaging.

Minor:

(1) Considering the signal loss due to photobleaching and fluorophore dilution during expansion, protein imaging may occasionally lack the sensitivity required to detect subtle morphological changes in cellular machinery. This potential limitation should be addressed or discussed in the text.

A sentence reflecting this point has been added to the manuscript.

(2) On page 15, the figure legend for panel d states, "Heatmaps of nuclei in b showing..." However, it appears that the panel referred to in this sentence corresponds to panel c.

The typo has been fixed.

(3) The type of glass 96-well plate utilized in this study should be specified, as the quality of the product could impact the expansion results.

The supplier and product number of the well plate used in our study has been added to the methods section.

(4) In Figure S3, the raw pixel values of CF305 dye are exceptionally low. Is there a specific reason for the very low signals observed when using this dye?

CF® 350 (305 was a typo) does not excite well at 405 nm, which is the excitation wavelength for the channel we used.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

Understanding large-scale neural activity remains a formidable challenge in neuroscience. While several methods have been proposed to discover the assemblies from such large-scale recordings, most previous studies do not explicitly model the temporal dynamics. This study is an attempt to uncover the temporal dynamics of assemblies using a tool that has been established in other domains.

The authors previously introduced the compositional Restricted Boltzmann Machine (cRBM) to identify neuron assemblies in zebrafish brain activity. Building upon this, they now employ the Recurrent Temporal Restricted Boltzmann Machine (RTRBM) to elucidate the temporal dynamics within these assemblies. By introducing recurrent connections between hidden units, RTRBM could retrieve neural assemblies and their temporal dynamics from simulated and zebrafish brain data.

Strengths:

The RTRBM has been previously used in other domains. Training in the model has been already established. This study is an application of such a model to neuroscience. Overall, the paper is well-structured and the methodology is robust, the analysis is solid to support the authors' claim.

Weaknesses:

The overall degree of advance is very limited. The performance improvement by RTRBM compared to their cRBM is marginal, and insights into assembly dynamics are limited.

(1) The biological insights from this method are constrained. Though the aim is to unravel neural ensemble dynamics, the paper lacks in-depth discussion on how this method enhances our understanding of zebrafish neural dynamics. For example, the dynamics of assemblies can be analyzed using various tools such as dimensionality reduction methods once we have identified them using cRBM. What information can we gain by knowing the effective recurrent connection between them? It would be more convincing to show this in real data.

See below in the recommendations section.

(2) Despite the increased complexity of RTRBM over cRBM, performance improvement is minimal. Accuracy enhancements, less than 1% in synthetic and zebrafish data, are underwhelming (Figure 2G and Figure 4B). Predictive performance evaluation on real neural activity would enhance model assessment. Including predicted and measured neural activity traces could aid readers in evaluating model efficacy.

See below in the recommendations section.

Recommendations:

(1) The biological insights from this method are constrained. Though the aim is to unravel neural ensemble dynamics, the paper lacks in-depth discussion on how this method enhances our understanding of zebrafish neural dynamics. For example, the dynamics of assemblies can be analyzed using various tools such as dimensionality reduction methods once we have identified them using cRBM. What information can we gain by knowing the effective recurrent connection between them? It would be more convincing to show this in real data.

We agree with the reviewer that our analysis does not explore the data far enough to reach the level of new biological insights. For practical reasons unrelated to the science, we cannot further explore the data in this direction at this point, however, funding permitting, we will pick up this question at a later stage. The only change we have made to the corresponding figure at the current stage was to adapt the thresholds, which better emphasizes the locality of the resulting clusters.

(2) Despite the increased complexity of RTRBM over cRBM, performance improvement is minimal. Accuracy enhancements, less than 1% in synthetic and zebrafish data, are underwhelming (Figure 2G and Figure 4B). Predictive performance evaluation on real neural activity would enhance model assessment. Including predicted and measured neural activity traces could aid readers in evaluating model efficacy.

We thank the reviewer kindly for the comments on the performance comparison between the two models. We would like to highlight that the small range of accuracy values for the predictive performance is due to both the sparsity and stochasticity of the simulated data, and is not reflective of the actual percentage in performance improvement. To this end, we have opted to use a rescaled metric that we call the normalised Mean Squared Error (nMSE), where the MSE is equal to 1 minus the accuracy, as the visible units take on binary values. This metric is also more in line with the normalised Log-Likelihood (nLLH) metric used in the cRBM paper in terms of interpretability. The figure shows that the RTRBM can significantly predict the state of the visible units in subsequent time-steps, whereas the cRBM captures the correct time-independent statistics but has no predictive power over time.

We also thank the reviewer for pointing out that there is no predictive performance evaluation on the neural data. This has been chosen to be omitted for two reasons. First, it is clear from Fig. 2 that the (c)RBM has no temporal dependencies, meaning that the predictive performance is determined mostly by the average activity of the visible units. If this corresponds well with the actual mean activity per neuron, the nMSE will be around 0. This correspondence is already evaluated in the first panel of 3F. Second, as this is real data, we can not make an estimate of a lower bound on the MSE that is due to neural noise. Because of this, the scale of the predictive performance score will be arbitrary, making it difficult to quantitatively assess the difference in performance between both models.

(3) The interpretation of the hidden real variable $r_t$ lacks clarity. Initially interpreted as the expectation of $\mathbf{h}_t$, its interpretation in Eq (8) appears different. Clarification on this link is warranted.

We thank the reviewer kindly for the suggested clarification. However, we think the link between both values should already be sufficiently clear from the text in lines 469-470:

“Importantly, instead of using binary hidden unit states 𝐡[𝑡−1], sampled from the expected real valued hidden states 𝐫[𝑡−1], the RTRBM propagates these real-valued hidden unit states directly.”

In other words, both indeed are the same, one could sample a binary-valued 𝐡[𝑡-1] from the real-valued 𝐫[𝑡-1] through e.g. a Bernoulli distribution, where 𝐫[𝑡-1] would thus indeed act as an expectation over 𝐡[𝑡−1]. However, the RTRBM formulation keeps the real-valued 𝐫[𝑡-1] to propagate the hidden-unit states to the next time-step. The motivation for this choice is further discussed in the original RTRBM paper (Sutskever et al. 2008).

(4) In Figure 3 panel F, the discrepancy in x-axis scales between upper and lower panels requires clarification. Explanation regarding the difference and interpretation guidelines would enhance understanding.

Thank you for pointing out the discrepancy in x-axis scales between the upper and lower panels of Figure 3F. The reason why these scales are different is that the activation functions in the two models differ in their range, and showing them on the same scale would not do justice to this difference. But we agree that this could be unclear for readers. Therefore we added an additional clarification for this discrepancy in line 215:

“While a direct comparison of the hidden unit activations between the cRBM and the RTRBM is hindered by the inherent discrepancy in their activation functions (unbounded and bounded, respectively), the analysis of time-shifted moments reveals a stronger correlation for the RTRBM hidden units ($r_s = 0.92$, $p<\epsilon$) compared to the cRBM ($r_s = 0.88$, $p<\epsilon$)”

(5) Assessing model performance at various down-sampling rates in zebrafish data analysis would provide insights into model robustness.

We agree that we would have liked to assess this point in real data, to verify that this holds as well in the case of the zebrafish whole-brain data. The main reason why we did not choose to do this in this case is that we would only be able to further downsample the data. Current whole brain data sets are collected at a few Hz (here 4 Hz, only 2 Hz in other datasets), which we consider to be likely slower than the actual interaction speed in neural systems, which is on the order of milliseconds between neurons, and on the order of ~100 ms (~10 Hz) between assemblies. Therefore reducing the rate further, we expect to only see a reduction in quality, which we considered less interesting than finding an optimum. Higher rates of imaging in light-sheet imaging are only achievable currently by imaging only single planes (which defies the goal of whole brain recordings), but may be possible in the future when the limiting factors (focal plane stepping and imaging) are addressed. For completeness, we have now performed the downstepping for the experimental data, which showed the expected decrease in performance. The results have been integrated into Figure 4.

Reviewer #2 (Public Review):

Summary:

In this work, the authors propose an extension to some of the last author's previous work, where a compositional restricted Boltzmann machine was considered as a generative model of neuron-assembly interaction. They augment this model by recurrent connections between the Boltzmann machine's hidden units, which allow them to explicitly account for temporal dynamics of the assembly activity. Since their model formulation does not allow the training towards a compositional phase (as in the previous model), they employ a transfer learning approach according to which they initialise their model with a weight matrix that was pre-trained using the earlier model so as to essentially start the actually training in a compositional phase. Finally, they test this model on synthetic and actual data of whole-brain light-sheet-microscopy recordings of spontaneous activity from the brain of larval zebrafish.

Strengths:

This work introduces a new model for neural assembly activity. Importantly, being able to capture temporal assembly dynamics is an interesting feature that goes beyond many existing models. While this work clearly focuses on the method (or the model) itself, it opens up an avenue for experimental research where it will be interesting to see if one can obtain any biologically meaningful insights considering these temporal dynamics when one is able to, for instance, relate them to development or behaviour.

Weaknesses:

For most of the work, the authors present their RTRBM model as an improvement over the earlier cRBM model. Yet, when considering synthetic data, they actually seem to compare with a "standard" RBM model. This seems odd considering the overall narrative, and it is not clear why they chose to do that. Also, in that case, was the RTRBM model initialised with the cRBM weight matrix?

Thank you for raising the important point regarding the RTRBM comparison in the synthetic data section. Initially, we aimed to compare the performance of the cRBM with the cRTRBM. However, we encountered significant challenges in getting the RTRBM to reach the compositional phase. To ensure a fair and robust comparison, we opted to compare the RBM with the RTRBM.

A few claims made throughout the work are slightly too enthusiastic and not really supported by the data shown. For instance, when the authors refer to the clusters shown in Figure 3D as "spatially localized", this seems like a stretch, specifically in view of clusters 1, 3, and 4.

Thanks for pointing out this inaccuracy. When going back to the data/analyses to address the question about locality, we stumbled upon a minor bug in the implementation of the proportional thresholding, causing the threshold to be too low and therefore too many neurons to be considered.

Fixing this bug reduces the number of neurons, thereby better showing the local structure of the clusters. Furthermore, if one would lower the threshold within the hierarchical clustering, smaller, and more localized, clusters would appear. We deliberately chose to keep this threshold high to not overwhelm the reader with the number of identified clusters. We hope the reviewer agrees with these changes and that the spatial structure in the clusters presented are indeed rather localized.

Moreover, when they describe the predictive performance of their model as "close to optimal" when the down-sampling factor coincided with the interaction time scale, it seems a bit exaggerated given that it was more or less as close to the upper bound as it was to the lower bound.

We thank the reviewer for catching this error. Indeed, the best performing model does not lay very close to the estimated performance of an optimal model. The text has been updated to reflect this.

When discussing the data statistics, the authors quote correlation values in the main text. However, these do not match the correlation values in the figure to which they seem to belong. Now, it seems that in the main text, they consider the Pearson correlation, whereas in the corresponding figure, it is the Spearman correlation. This is very confusing, and it is not really clear as to why the authors chose to do so.

Thank you for identifying the discrepancy between the correlation values mentioned in the text and those presented in the figure. We updated the manuscript to match the correlation coefficient values in the figure with the correct values denoted in the text.

Finally, when discussing the fact that the RTRBM model outperforms the cRBM model, the authors state it does so for different moments and in different numbers of cases (fish). It would be very interesting to know whether these are the same fish or always different fish.

Thank you for pointing this out. Keeping track of the same fish across the different metrics makes sense. We updated the figure to include a color code for each individual fish. As it turns out each time the same fish are significantly better performing.

Recommendations:

Figure 1: While the schematic in A and D only shows 11 visible units ("neurons"), the weight matrices and the activity rasters in B and C and E and F suggest that there should be, in fact, 12 visible units. While not essential, I think it would be nice if these numbers would match up.

Thank you for pointing out the inconsistency in the number of visible units depicted in Figure 1. We agree that this could have been confusing for readers. The figure has been updated accordingly. As you suggested, the schematic representation now accurately reflects the presence of 12 visible units in both the RBM and RTRBM models.

Figure 3: Panel G is not referenced in the main text. Yet, I believe it should be somewhere in lines 225ff.

Thank you for mentioning this. We added in line 233 a reference to figure 3 panel G to refer to the performance of the cRBM and RTRBM on the different fish.

Line 637ff: The authors consider moments <v\_i h\_μ> and <v\_i h\_j>, and from the context, it seems they are not the same. However, it is not clear as to why because, judging from the notation, they should be the same.

The second-order statistic <v\_i h\_j> on line 639 was indeed already mentioned and denoted as <v\_i h\_μ> on line 638. It has now been removed accordingly in the updated manuscript.

I found the usage of U^ and U throughout the manuscript a bit confusing. As far as I understand, U^ is a learned representation of U. However, maybe the authors could make the distinction clearer.

We understand the usage of Û and U throughout the text may be confusing for the reader. However, we would like to notify the reviewer that the distinction between these two variables is explained in line 142: “in addition to providing a close estimate (̂Û) to the true assembly connectivity matrix U”. However, for added clarification to the reader, we added additional mentions of the estimated nature of Û throughout the text in the updated manuscript.

Equation 3: It would be great if the authors could provide some more explanation of how they arrived at the identities.

These identities have previously been widely described in literature. For this reason, we decided not to include their derivation in our manuscript. However, for completeness, we kindly refer to:

Goodfellow, I., Bengio, Y., & Courville, A. (2016). Chapter 20: Deep generative models [In Deep Learning]. MIT Press. https://www.deeplearningbook.org/contents/generative_models.html

Typos:

-  L. 196: "connectiivty" -> "connectivity"

-  L. 197: Does it mean to say "very strong stronger"?

-  L. 339: The reference to Dunn et al. (2016) should appear in parentheses.

-  L. 504f: The colon should probably be followed by a full sentence.

-  Eq. 2: In the first line, the potential V still appears, which should probably be changed to show the concrete form (-b * h) as in the second line.

-  L. 351: Is there maybe a comma missing after "cRBM"?

-  L. 271: Instead of "correlation", shouldn't it rather be "similarity"? - L. 218: "Figure 3D" -> "Figure 3F"

We thank the reviewer for pointing out these typos, which have all (except one) been fixed in the text. We do emphasize the potential V to show that there are alternative hidden unit potentials that can be chosen. For instance, the cRBM utilizes dReLu hidden unit potentials.

Reviewer #3 (Public Review):

With ever-growing datasets, it becomes more challenging to extract useful information from such a large amount of data. For that, developing better dimensionality reduction/clustering methods can be very important to make sense of analyzed data. This is especially true for neuroscience where new experimental advances allow the recording of an unprecedented number of neurons. Here the authors make a step to help with neuronal analyses by proposing a new method to identify groups of neurons with similar activity dynamics. I did not notice any obvious problems with data analyses here, however, the presented manuscript has a few weaknesses:

(1) Because this manuscript is written as an extension of previous work by the same authors (van der Plas et al., eLife, 2023), thus to fully understand this paper it is required to read first the previous paper, as authors often refer to their previous work for details. Similarly, to understand the functional significance of identified here neuronal assemblies, it is needed to go to look at the previous paper.

We agree that the present Research Advance has been written in a way that builds on our previous publication. It was our impression that this was the intention of the Research Advance format, as spelled out in its announcement "eLife has introduced an innovative new type of article – the Research Advance – that invites the authors of any eLife paper to present significant additions to their original research". In the previous formatting guidelines from eLife this was more evident with a strong limitation on the number of figures and words, however, also for the present, more liberal guidelines, place an emphasis on the relation to the previous article. We have nonetheless tried in several places to fill in details that might simplify the reading experience.

(2) The problem of discovering clusters in data with temporal dynamics is not unique to neuroscience. Therefore, the authors should also discuss other previously proposed methods and how they compare to the presented here RTRBM method. Similarly, there are other methods using neural networks for discovering clusters (assemblies) (e.g. t-SNE: van der Maaten & Hinton 2008, Hippocluster: Chalmers et al. 2023, etc), which should be discussed to give better background information for the readers.

The clustering methods suggested by the reviewer do not include modeling any time dependence, which is the crucial advance presented here by the introduction of the RTRBM, in extending the (c)RBM. In our previous publication on the cRBM (an der Plas et al., eLife, 2023), this comparison was part of the discussion, although it focussed on a different set of methods. While clustering methods like t-SNE, UMAP and others certainly have their value in scientific analysis, we think it might be misleading the reader to think that they achieve the same task as an RTRBM, which adds the crucial dimension of temporal dependence.

(3) The above point to better describe other methods is especially important because the performance of the presented here method is not that much better than previous work. For example, RTRBM outperforms the cRBM only on ~4 out of 8 fish datasets. Moreover, as the authors nicely described in the Limitations section this method currently can only work on a single time scale and clusters have to be estimated first with the previous cRBM method. Thus, having an overview of other methods which could be used for similar analyses would be helpful.

We think that the perception that the RTRBM performs only slightly better is based on a misinterpretation of the performance measure, which we have tried to address (see comments above) in this rebuttal and the manuscript. In addition we would like to emphasize that the structural estimation (which is still modified by the RTRBM, only seeded by the cRBMs output), as shown in the simulated data, makes improved structural estimates, which is important, even in cases where the performance is comparable (which can be the case if the RBM absorbs temporal dependencies of assemblies into modified structure of assemblies). We have clarified this now in the discussion.

Recommendations:

(1) Line 181: it is not explained how a reconstruction error is defined.

Dear reviewer, thanks for pointing this out. A definition of the (mean square) reconstruction error is added in this line.

(2) How was the number of hidden neurons chosen and how does it affect performance?

Thank you for pointing this out. Due to the fact that we use transfer learning, the number of hidden units used for the RTRBM is given by the number of hidden units used for training the cRBM. In further research, when the RTRBM operates in the compositional phase, we can exploit a grid search over a set of hyper parameters to determine the optimal set of hidden units and other parameters.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment 

This study is a detailed investigation of how chromatin structure influences replication origin function in yeast ribosomal DNA, with focus on the role of the histone deacetylase Sir2 and the chromatin remodeler Fun30. Convincing evidence shows that Sir2 does not affect origin licensing but rather affects local transcription and nucleosome positioning which correlates with increased origin firing. However, the evidence remains incomplete as the methods employed do not rigorously establish a key aspect of the mechanism, fully address some alternative models, or sufficiently relate to prior results. Overall, this is a valuable advance for the field that could be improved to establish a more robust paradigm. 

We have added extensive new results to the manuscript that, we believe, address all three criticisms above, namely that the methods employed do not (1) rigorously establish a key aspect of the mechanism; (2) fully address some alternative models; or (3) sufficiently relate to prior results.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

This paper presents a mechanistic study of rDNA origin regulation in yeast by SIR2. Each of the ~180 tandemly repeated rDNA gene copies contains a potential replication origin. Earlyefficient initiation of these origins is suppressed by Sir2, reducing competition with origins distributed throughout the genome for rate-limiting initiation factors. Previous studies by these authors showed that SIR2 deletion advances replication timing of rDNA origins by a complex mechanism of transcriptional de-repression of a local PolII promoter causing licensed origin proteins (MCMcomplexes) to re-localize (slide along the DNA) to a different (and altered) chromatin environment. In this study, they identify a chromatin remodeler, FUN30, that suppresses the sir2∆ effect, and remarkably, results in a contraction of the rDNA to about onequarter it's normal length/number of repeats, implicating replication defects of the rDNA. Through examination of replication timing, MCM occupancy and nucleosome occupancy on the chromatin in sir2, fun30, and double mutants, they propose a model where nucleosome position relative to the licensed origin (MCM complexes) intrinsically determines origin timing/efficiency. While their interpretations of the data are largely reasonable and can be interpreted to support their model, a key weakness is the connection between Mcm ChEC signal disappearance and origin firing.  

Criticism: The reviewer expressed concern about the connection between Mcm ChEC signal disappearance and origin firing.

To further support our claim that the disappearance of the MCM signal in our ChEC datasets reflects origin firing, we now present additional data using the well-established method of MCM Chromatin IP (ChIP).

(1) New Supporting Evidence:  ChIP at genome-wide origins. In Figure 5 figure supplement 2, we demonstrate that the Mcm2 ChIP signal in cells released into hydroxyurea (HU) is significantly reduced at early origins compared to late origins, which mirrors the pattern observed with the MCM2 ChEC signal. This reduction in the ChIP signal at early origins supports the interpretation that the MCM signal disappearance is associated with origin firing.

(2) New supporting based evidence:  ChIP at rDNA Origins. Our ChIP analysis also shows that the disappearance of the MCM signal at rDNA origins in sir2Δ cells released into HU is accompanied by signal accumulation at the replication fork barrier (RFB), indicative of stalled replication forks at this location (Figure 5 figure supplement 3). This pattern is consistent with the initiation of replication at these origins and fork stalling at the RFB.

(3) New supporting evidence:  2D gels with quantification. Furthermore, additional 2D gel electrophoresis results provide ample independent evidence of rDNA origin firing in HU in sir2Δ mutants and suppression of origin firing in sir2 fun30 cells. These new data include 1) quantification of 2D gels in Figure 4D and 2) new 2D gels presented in Figure 4C as described below in greater detail. Collectively, these results demonstrate that rDNA origins fire prematurely in HU in sir2 cells and that firing is suppressed by FUN30 deletion. These additional data reinforce our model and support the association between MCM signal disappearance and replication initiation.

While the cyclical chromatin association-dissociation of MCM proteins with potential origin sequences may be generally interpreted as licensing followed by firing, dissociation may also result from passive replication and as shown here, displacement by transcription and/or chromatin remodeling.

The reviewer raised a concern that the cyclical chromatin association-dissociation of MCM proteins could be interpreted as licensing followed by firing, but might also result from passive replication or displacement by transcription and chromatin remodeling.

Addressing Alternative Explanations:

(1) Selective Disappearance of MCM Complexes: While transcription and passive replication can indeed cause the MCM-ChEC signal to disappear, these processes cannot selectively cause the disappearance of the displaced MCM complex without also affecting the non-displaced MCM complex. Specifically, RNA polymerase transcribing C-pro would first need to dislodge the normally positioned MCM complex before reaching the displaced complex, which is not observed in our data.

(2) Role of FUN30 Deletion:  FUN30 deletion results in increased C-pro transcription and reduced disappearance of the displaced MCM complex. This observation supports our model, as transcription alone would not selectively affect the displaced MCM complex while leaving the normally positioned MCM complex unaffected.

(3) Licensing Restrictions: It is crucial to note that continuous replenishment of displaced MCMs with newly loaded MCMs is not possible in our experimental conditions, as the cells are in S phase and licensing is restricted to G1. This temporal restriction further supports our interpretation that the disappearance of the MCM signal reflects origin firing rather than alternative processes.

In summary, while alternative explanations such as transcription and passive replication could potentially account for MCM signal disappearance, our data indicate that these processes cannot selectively affect the displaced MCM complex without impacting the non-displaced complex. The selective disappearance observed in our experiments, along with the effects of FUN30 deletion and the temporal constraints on MCM loading, strongly support our interpretation that the disappearance of the MCM signal reflects origin firing.

Moreover, linking its disappearance from chromatin in the ChEC method with such precise resolution needs to be validated against an independent method to determine the initiation site(s). Differences in rDNA copy number and relative transcription levels also are not directly accounted for, obscuring a clearer interpretation of the results. 

The reviewer raised concerns about the need to validate the disappearance of MCM from chromatin observed using the ChEC method against an independent method to determine initiation sites. Additionally, they pointed out that differences in rDNA copy number and relative transcription levels are not directly accounted for, which may obscure the interpretation of the results.

(1) Reduced rDNA Copy Number promotes Early Replication: Copy number reduction of the magnitude caused by deletion of both SIR2 and FUN30 is not expected to suppress early rDNA replication in sir2, but rather to exacerbate it. Specifically, deletion of SIR2 and FUN30 causes the rDNA to shrink to approximately 35 copies. Kwan et al., 2023 (PMID: 36842087) have shown that a reduction in rDNA copy number to 35 copies results in a dramatic acceleration of rDNA replication in a SIR2+ strain. Therefore, the effect of rDNA size on replication timing reinforces our conclusion that deletion of FUN30 suppresses rDNA replication.

(2) New 2D Gels in sir2 and sir2 fun30 strains with equal number of rDNA repeats: To directly address the concern regarding differences in the number of rDNA repeats, we have included new 2D gel analyses in the revised manuscript. By using a fob1

background, we were able to equalize the repeat number between the sir2 and sir2 fun30 strains (Figure 4E). The 2D gels conclusively show that the suppression of rDNA origin firing upon FUN30 deletion is independent of both rDNA size and FOB1.

Nevertheless, this paper makes a valuable advance with the finding of Fun30 involvement, which substantially reduces rDNA repeat number in sir2∆ background. The model they develop is compelling and I am inclined to agree, but I think the evidence on this specific point is purely correlative and a better method is needed to address the initiation site question. The authors deserve credit for their efforts to elucidate our obscure understanding of the intricacies of chromatin regulation. At a minimum, I suggest their conclusions on these points of concern should be softened and caveats discussed. Statistical analysis is lacking for some claims. 

Strengths are the identification of FUN30 as suppressor, examination of specific mutants of FUN30 to distinguish likely functional involvement. Use of multiple methods to analyze replication and protein occupancies on chromatin. Development of a coherent model. 

Weaknesses are failure to address copy number as a variable; insufficient validation of ChEC method relationship to exact initiation locus; lack of statistical analysis in some cases. 

With regard to "insufficient validation of ChEC method relationship to exact initiation locus":  The two potential initiation sites that one would monitor (non-displaced and displaced) are separated by less than 150 base pairs, and other techniques simply do not have the resolution necessary to distinguish such differences. Indeed, our new ChIP results presented in Figure 5 figure supplement 3 clearly demonstrate that while the resolution of ChIP is adequate to detect the reduction of MCM signal at the replication initiation site and its relocation to the RFB ( ~2 kb away), it lacks the resolution required to differentiate closely spaced MCM complexes.

Furthermore, as we suggest in the manuscript, our results are consistent with a model in which it is only the displaced MCM complex that is activated, whether in sir2 or WT.  If no genotypedependent difference in initiation sites is even expected, it would be hard to interpret even the most precise replication-based assays.  

We appreciate the reviewer pointing out that some statistical analyses were lacking: we have added statistical analysis for 2D gels (Figures 4D and 4E),  EdU incorporation experiments in Figure 4F and disappearance of MCM ChEC and ChIP signal upon release of cells into HU (Figure 5 supplement 1 and Supplement 2).  

Additional background and discussion for public review: 

This paper broadly addresses the mechanism(s) that regulate replication origin firing in different chromatin contexts. The rDNA origin is present in each of ~180 tandem repeats of the rDNA sequence, representing a high potential origin density per length of DNA (9.1kb repeat unit). However, the average origin efficiency of rDNA origins is relatively low (~20% in wild-type cells), which reduces the replication load on the overall genome by reducing competition with origins throughout the genome for limiting replication initiation factors. Deletion of histone deacetylase SIR2, which silences PolII transcription within the rDNA, results in increased early activation or the rDNA origins (and reduced rate of overall genome replication). Previous work by the authors showed that MCM complexes loaded onto the rDNA origins (origin licensing) were laterally displaced (sliding) along the rDNA, away from a well-positioned nucleosome on one side. The authors' major hypothesis throughout this work is that the new MCM location(s) are intrinsically more efficient configurations for origin firing. The authors identify a chromatin remodeling enzyme, FUN30, whose deletion appears to suppress the earlier activation of rDNA origins in sir2∆ cells. Indeed, it appears that the reduction of rDNA origin activity in sir2∆ fun30∆ cells is severe enough to results in a substantial reduction in the rDNA array repeat length (number of repeats); the reduced rDNA length presumably facilitates it's more stable replication and maintenance. 

Analysis of replication by 2D gels is marginally convincing, using 2D gels for this purpose is very challenging and tricky to quantify. 

We address this criticism by carefuly quantifying 2 D gel results using single rARS signal for normalizing bubble arc as discussed below.

The more quantitative analysis by EdU incorporation is more convincing of the suppression of the earlier replication caused by SIR2 deletion. 

We have also added quantification of EdU results to strengthen our arguments.  

To address the mechanism of suppression, they analyze MCM positioning using ChEC, which in G1 cells shows partial displacement of MCM from normal position A to positions B and C in sir2∆ cells and similar but more complete displacement away from A to positions B and C in sir2fun30 cells. During S-phase in the presence of hydroxyurea, which slows replication progression considerably (and blocks later origin firing) MCM signals redistribute, which is interpreted to represent origin firing and bidirectional movement of MCMs (only one direction is shown), some of which accumulate near the replication fork barrier, consistent with their interpretation. They observe that MCMs displaced (in G1) to sites B or C in sir2∆ cells, disappear more rapidly during S-phase, whereas the similar dynamic is not observed in sir2∆fun30∆. This is the main basis for their conclusion that the B and C sites are more permissive than A. While this may be the simplest interpretation, there are limitations with this assay that undermine a rigorous conclusion (additional points below). The main problem is that we know the MCM complexes are mobile so disappearance may reflect displacement by other means including transcription which is high is the sir2∆ background. Indeed, the double mutant has greater level of transcription per repeat unit which might explain more displaced from A in G1. Thus, displacement might not always represent origin firing. Because the sir2 background profoundly changes transcription, and the double mutant has a much smaller array length associated with higher transcription, how can we rule out greater accessibility at site A, for example in sir2∆, leading to more firing, which is suppressed in sir2 fun30 due to greater MCM displacement away from A? 

I think the critical missing data to solidly support their conclusions is a definitive determination of the site(s) of initiation using a more direct method, such as strand specific sequencing of EdU or nascent strand analysis. More direct comparisons of the strains with lower copy number to rule out this facet. As discussed in detail below, copy number reduction is known to suppress at least part of the sir2∆ effect so this looms over the interpretations. I think they are probably correct in their overall model based on the simplest interpretation of the data but I think it remains to be rigorously established. I think they should soften their conclusions in this respect. 

Please see discussion below about these issues.

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, the authors follow up on their previous work showing that in the absence of the Sir2 deacetylase the MCM replicative helicase at the rDNA spacer region is repositioned to a region of low nucleosome occupancy. Here they show that the repositioned displaced MCMs have increased firing propensity relative to non-displaced MCMs. In addition, they show that activation of the repositioned MCMs and low nucleosome occupancy in the adjacent region depend on the chromatin remodeling activity of Fun30. 

Strengths: 

The paper provides new information on the role of a conserved chromatin remodeling protein in the regulation of origin firing and in addition provides evidence that not all loaded MCMs fire and that origin firing is regulated at a step downstream of MCM loading. 

Weaknesses: 

The relationship between the author's results and prior work on the role of Sir2 (and Fob1) in regulation of rDNA recombination and copy number maintenance is not explored, making it difficult to place the results in a broader context. Sir2 has previously been shown to be recruited by Fob1, which is also required for DSB formation and recombination-mediated changes in rDNA copy number. Are the changes that the authors observe specifically in fun30 sir2 cells related to this pathway? Is Fob1 required for the reduced rDNA copy number in fun30 sir2 double mutant cells? 

We have conducted additional studies in the fob1 background to address how FOB1 and the replication fork barrier (RFB) influence the kinetics of rDNA size reduction upon FUN30 deletion (Figure 2 - figure supplement 2), rDNA replication timing (Figure 2 - figure supplement 3), and rDNA origin firing using 2D gels (Figure 4C).

Strains lacking SIR2 exhibit unstable rDNA size, and FOB1 deletion stabilizes rDNA size in a sir2 background (and otherwise). Similarly, we found that FOB1 deletion influences the kinetics of rDNA size reduction in sir2 fun30 cells. Specifically, we were able to generate a fob1 sir2 fun30 strain with more than 150 copies. Nonetheless, and consistent with our model, this strain still exhibited delayed rDNA replication timing (Figure 2 - figure supplement 3), and its rDNA still shrank upon continuous culture (Figure 2 figure supplement 2). These results demonstrate that, although FOB1 affects the kinetics of rDNA size reduction in sir2 fun30 strains, the reduced rDNA array size or delayed replication timing upon FUN30 deletion size does not depend on FOB1.

The use of the fob1 background allowed us to compare the activation of rDNA origins in sir2 and sir2 fun30 strains with equally short rDNA sizes. 2D gels demonstrate robust and reproducible suppression of rDNA origin activity upon deletion of FUN30 in sir2 fob1 strains with 35 rDNA copies (Figure 4C). These results indicate that the main effect we are interested in—FUN30-induced reduction in origin firing—is independent of both FOB1 and rDNA size.

Our additional studies conclusively show that the FUN30-induced reduction in rDNA origin firing is independent of both FOB1 and rDNA size. These findings provide important insights into the mechanisms regulating rDNA copy number maintenance, placing our results within the broader context of existing knowledge on Sir2 and Fob1 functions.

Reviewer #3 (Public Review): 

Summary: 

Heterochromatin is characterized by low transcription activity and late replication timing, both dependent on the NAD-dependent protein deacetylase Sir2, the founding member of the sirtuins. This manuscript addresses the mechanism by which Sir2 delays replication timing at the rDNA in budding yeast. Previous work from the same laboratory (Foss et al. PLoS Genetics 15, e1008138) showed that Sir2 represses transcription-dependent displacement of the Mcm helicase in the rDNA. In this manuscript, the authors show convincingly that the repositioned Mcms fire earlier and that this early firing partly depends on the ATPase activity of the nucleosome remodeler Fun30. Using read-depth analysis of sorted G1/S cells, fun30 was the only chromatin remodeler mutant that somewhat delayed replication timing in sir2 mutants, while nhp10, chd1, isw1, htl1, swr1, isw2, and irc3 had not effect. The conclusion was corroborated with orthogonal assays including two-dimensional gel electrophoresis and analysis of EdU incorporation at early origins. Using an insightful analysis with an Mcm-MNase fusion (Mcm-ChEC), the authors show that the repositioned Mcms in sir2 mutants fire earlier than the Mcm at the normal position in wild type. This early firing at the repositioned Mcms is partially suppressed by Fun30. In addition, the authors show Fun30 affects nucleosome occupancy at the sites of the repositioned Mcm, providing a plausible mechanism for the effect of Fun30 on Mcm firing at that position. However, the results from the MNAse-seq and ChEC-seq assays are not fully congruent for the fun30 single mutant. Overall, the results support the conclusions providing a much better mechanistic understanding how Sir2 affects replication timing at rDNA, 

The observation that the MNase-seq plot in fun30 mutant shows a large signal at the +3 nucleosome and somewhat smaller at position +2, while the ChEC-seq plot exhibits negligible signals, is indeed an important point of consideration. This discrepancy arises because most of the MCM in fun30 mutant remains at its original site where it abuts +1 nucleosome. As a result, the MCM-MNase fusion protein fails to reach and “light up” the +3 nucleosome, which is, nonetheless, well-visualized with exogenous MNase.  The paucity of displaced MCMs, which is responsible for cutting +2 nucleosome, explains the discrepancy in the +2 nucleosome signal between exogenous MNase and CheC datasets in the fun30 mutant.  

Despite this apparent discrepancy, the overall results support our conclusions and provide a much better mechanistic understanding of how Sir2 affects replication timing at rDNA. The MNaseseq data reflect nucleosome positioning and chromatin structure, while the ChEC-seq data specifically highlights the locations where MCM is bound and active.  

Strengths 

(1) The data clearly show that the repositioned Mcm helicase fires earlier than the Mcm in the wild type position. 

(2) The study identifies a specific role for Fun30 in replication timing and an effect on nucleosome occupancy around the newly positioned Mcm helicase in sir2 cells. 

Weaknesses 

(1) It is unclear which strains were used in each experiment. 

(2) The relevance of the fun30 phospho-site mutant (S20AS28A) is unclear. 

We appreciate the reviewer pointing out places in which our manuscript omitted key pieces of information (items 1 and 3), we have included the strain numbers in our revision.  With regard to point 2, we had written:  

Fun30 is also known to play a role in the DNA damage response; specifically, phosphorylation of Fun30 on S20 and S28 by CDK1 targets Fun30 to sites of DNA damage, where it promotes DNA resection (Chen et al. 2016; Bantele et al. 2017). To determine whether the replication phenotype that we observed might be a consequence of Fun30's role in the DNA damage response, we tested non-phosphorylatable mutants for the ability to suppress early replication of the rDNA in sir2; these mutations had no effect on the replication phenotype (Figure 2B), arguing against a primary role for Fun30 in DNA damage repair that somehow manifests itself in replication. 

(3) For some experiments (Figs. 3, 4, 6) it is unclear whether the data are reproducible and the differences significant. Information about the number of independent experiments and quantitation is lacking. This affects the interpretation, as fun30 seems to affect the +3 nucleosome much more than let on in the description. 

We have provided replicas and quantitation for the results in these figures.

(Replica ChEC Southern blot with quantification (Figure 3 figure supplement 1), quantification and replicas for 2D gels in Figure 4 and replicas for nucleosome occupancy (Figure 6 supplement 1).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Fig. 3-Examination of MCM occupancy at the rDNA ARS region using a variation of ChEC.

Presumably these are these G1-arrested cells but does not seem to be stated. Please confirm. 

The 2D gels results are not very convincing of their conclusions. We are asked to compare bubble to fork arcs at 30 minutes, but this is not feasible. It is the author's job to quantify the data from multiple replicates, but none is given. After much careful examination, comparing the relative intensities of ascending bubble and Y-arcs, I think I can accept that 4A shows highest early efficiency for sir2 over WT and fun30, which are similar to each other, and lowest for sir2 fun30, at 60 and 90 min. 

In the revision we provide a careful quantification of the 2D gels in Figure 4. For assessing rDNA origin activity, we normalized the bubble arc during the HU time course to a single rARS signal, that appears as large 24.4kb Nhe1I fragment originating from the  rightmost rDNA repeat (see Figures 4A and 4B). The description of the quantification in the text is provided below. 

“Prior to separation on 2D gels, DNA was digested with NheI, which releases a 4.7 kb rARScontaining linear DNA fragment at the internal rDNA repeats (1N) and a much larger, 24.5 kb single-rARS-containing fragment originating from the rightmost repeat. In 2D gels, active origins generate replication bubble arc signals, whereas passive replication of an origin appears as a y-arc. Having a signal emanating from a single ARS-containing fragment simplifies the comparison of rDNA origin activity in strains with different numbers of rDNA repeats, such as in sir2 vs sir2 fun30 mutants. Origin activity is expressed as a ratio of the bubble to the single-ARS signal, effectively measuring the number of active rDNA origins per cell at a given time point. 

As seen previously (Foss et al. 2019), deletion of SIR2 increased the number of activated rDNA origins, while deletion of FUN30 suppressed this effect. When analyzed in aggregate at 20, 30, 60 and 90 minutes following release into HU, the average number of activated rDNA origin activity in sir2 mutant was increased 6.3-fold compared to those in WT (5.0±2.3 in sir2 vs 0.8±0.4 in wt, p<0.05 by 2 tailed t-test), and the increased number was reduced upon FUN30 deletion (1.3±0.7 in sir2 fun30, p<0.05 by 2 tailed t-test vs sir2, NS for comparison to WT).”

However, for part 4B, they state (p. 11) that deletion of FUN30 in a SIR2 background had no perceptible effect (on ARS305) but I think the data appear otherwise: the FUN30 cells show more Y-arc than WT.

We now provide the assessment of ARS305 activity in HU cells as a ratio of bubble-arc to 1N signal. The reviewer is right that FUN30 has a more robust bubble arc signal compared to WT.

However, after normalization to 1N this difference did not appear significant (3.7 vs 5.1). Overall the analysis of activity or ARS305 origins demonstrates a reciprocity with the activity of rDNA origins in each of the four genotypes.  Furthermore, this observation is confirmed in our EdU-based analysis of 111 genomic origins, with statistical analysis showing a very high level of significance (see below).  

Ultimately, analysis of unsynchronized cells would give unambiguous results about origin efficiency. In this regard I note that analysis of rDNA origin firing by 2D gels with HU versus asynchronous gives different results in WT versus sir2∆, with no difference in unsynchronized cells (He et al. 2022). It would be interesting to test the strains here unsynchronized, though copy number size would still be a variable to address.

Origin activity in log cultures is typically assessed by comparing replication initiation within an origin, presenting as a bubble arc, to passively replicated DNA (Y-arc). However, such an analysis at tandemly arrayed origins, such as rDNA, is not feasible, as both active and passive replication are the result of activation of the same origins. This explains the lack of difference between WT and sir2 cells previously reported (He et al. 2022), which we have also observed. Differences in activation of rDNA origins in WT vs sir2 cells is clearly reflected in HU experiments, as was the case in the earlier report (He et al. 2022). 

To address the issue of differences in copy number between sir2 and sir2 fun30 cells we have now done experiments in a fob1 background where we can equalize the copy number among the two genotypes. These 2D gels are presented in Figure 4C. We address this issue in the revised manuscript as follows:

“The overall impact of FUN30 deletion on rDNA origin activity in a sir2 background is expected to be a composite of two opposing effects: a suppression of rDNA origin activation and increased rDNA origin activation due to reduced rDNA size (Kwan et al. 2023). To evaluate the effect FUN30 on rDNA origin activation independently of rDNA size, we generated an isogenic set of strains in a fob1 background, all of which contain 35 copies of the rDNA repeat.  (Deletion of FOB1 is necessary to stabilize rDNA copy number.)  Comparing rDNA origin activity in sir2 versus sir2 fun30 genotypes, we observed a robust and reproducible reduction in rDNA origin activity upon FUN30 deletion. This finding confirms that the FUN30 suppresses rDNA origin firing in sir2 background independently of both rDNA size and FOB1 status.”

-EdU analysis is more convincing regarding relative effects on genome versus rDNA, however, again, the effect of reduced rDNA array size in the sir2 fun30 cells may also be the proximal cause of the reduced effect on genome (early origins) replication rather than a direct effect on origin efficiency. No statistic provided to support that fun30 suppresses sir2 for rDNA activity. 

This comment raises three distinct, but related, issues: 

First, the reviewer is asking whether the reduced rDNA size, of the magnitude we observed in sir2 fun30 cells, could by itself be responsible for increased origin activity elsewhere in the genome, just because there is less rDNA that needs to be replicated. As noted earlier (Kwan et al. 2023), Kwan et al. examined the effect of rDNA size reduction and observed: 1) marked increased in rDNA origin activity and 2) reciprocal reduction in origin activity elsewhere in the genome. This counterintuitive finding suggests that a smaller rDNA size exerts more competition for limited replication resources compared to a larger rDNA size. In light of this, our findings with FUN30 deletion become even more compelling. The suppression of rDNA firing upon FUN30 deletion is so significant that it overrides the expected effects of rDNA size reduction.

Second, the reviewer points out our lack of statistical analysis to support our contention that fun30 suppresses sir2 with regard to rDNA origin activity. We have now addressed this issue as well, by quantifying 2D gel signals, as described above in the text that begins with "Prior to separation on 2D gels, DNA was digested with NheI ...". 

Third, we have now provided a statistical analysis to support our conclusion that EdU-based analysis of activity of 111 early origins shows suppression upon deletion of SIR2 that is largely reversed by additional deletion of FUN30. 

"Deletion of FUN30 in a sir2 background partially restored EdU incorporation at early origins, concomitant with reduced EdU incorporation at rDNA origins. In particular, the median value of log10 of read depths at 111 early origins, as the data are shown in Figure 4F, dropped from 6.5 for wild type to 6.2 for sir2 but then returned almost to wild type levels (6.4) in sir2 fun30.  The p value obtained by Student's t test, comparing the drop in 111 origins from wild type to sir2 with that from wild type to sir2 fun30 was highly significant (<< 10-16)  In contrast, FUN30 deletion in the WT background did not reduce EdU incorporation at genomic origins (median 6.6). These findings highlight that FUN30 deletion-induced suppression of rDNA origins in sir2 is accompanied by the activation of genomic origins."

Use loss of Mcm-ChEC signal as proxy for origin firing. Reasonably convincing that decrease correlates with origin firing on a one-to-one basis (Fig. 5B), though no statistic given. 

We provide the statistical analysis in Figure 5-figure supplement 1.

However, there is no demonstration of ability to observe this correlation with fine resolution as needed for the claims here. It seems equally possible that sir2 deletion causes more firing by repositioning MCMs to a better location or that the prior location, which still contains substantial MCM, becomes more permissive. The MCM signal appears to be mobile, so perhaps the role of FUN30 is to prevent to mobility of MCM away from the original site in WT cells; note that significantly less Mcm signal is at the original position in sir2 fun30. No accumulation of MCM occurs near the RFB in WT (and fun30) cells. I understand that origin firing is lower in WT but raises concerns about sensitivity and dynamic range of this assay and that MCM positions may reflect transcription versus replication. 

Please see the section above labeled "Addressing Alternative Explanations".  

Is Fig 6A Y-axis correctly labeled? I understand this figure to represent MNase-seq reads; is there any Mcm2-ChEC-seq in part A? 

We have corrected the labeling. 6A represent MNase-seq reads. Thank you for pointing this out.

I understand part B to represent nucleosome-sized fragments released by Mcm2-ChEC interpreted to be nucleosomes. But could they be large fragments potentially containing adjacent MCM-double hexamers?  

Our representation of ChEC-seq data in Figure 1 supplement 1, where we can see the entire spectrum of fragment sizes, demonstrates two distinct populations of fragments: nucleosome size and MCM-size fragments.

Reviewer #2 (Recommendations For The Authors): 

Suggestions for the authors to consider: 

(1) The authors make a good case for the importance of replication balance between rDNA and euchromatin in ensuring that the genome is replicated in a timely fashion. This seems to be clearly regulated by Sir2. However, Sir2 also affects rDNA copy number and suppresses unequal cross over events, which are stimulates by Fob1. Does Fun30 suppress Fob1-dependent recombination events in sir2D cells? 

It is unclear why FUN30 only affects rDNA repeat copy number in sir2 cells. Why doesn't Fun30 reduce copy number in wild-type cells? 

Deletion of SIR2 causes rightward repositioning of MCMs to a position where they are more prone to fire, as shown by our HU ChEC datasets in which we show that the repositioned MCMs are more prone to activation than the non-repositioned ones. FUN30 deletion suppresses activation of these, activation-prone repositioned MCMs, as shown by HU ChEC. This suppression of rDNA origin activation in sir2 cells causes rDNA to shrink. In fun30 single mutants, due to the paucity of non-repositioned MCMs, we do not observe significant suppression of rDNA origin firing, and consequently, there is no reduction in rDNA size in fun30 cells.

(2) The authors use Mcm-MNase to map the location of the MCM helicase. Can these results be confirmed using the more standard and direct ChIP assay to examine changes in MCM localization

We carried out suggested MCM ChIP experiments and present these results in Figure 5 supplement 2 and supplement 3. These ChIP data demonstrate that: 

(1) MCM signal disappears preferentially at early origins compared to late origins, as seen in our ChEC results.

(2) The disappearance of ChEC signal at rDNA origins in sir2 mutant is accompanied by the signal accumulation at the RFB, consistent with fork stalling at the RFB mirroring the results we obtained by ChEC. While these results indicate that that ChIP has adequate resolution to detect MCM repositioning at 2 kb, scale, its resolution was insufficient for fine scale discrimination of repositioned and non-repositioned MCMs.

In this regard, the specific role of Fun30 in regulation of MCM firing at rDNA is interesting. 

Does Fun30 localize to the ARS region of rDNA? How is Fun30 specifically recruited to rDNA?  

We carried out ChIP for Fun30 and observed, similarly to previous reports (Durand-Dubief et al. 2012), a wide distribution of Fun30 throughout the genome and at rDNA. We have elected not to include these results in the current manuscript.

(3) The 2D gels in Figure 4 are difficult to interpret. The bubble to arc ratios in fun30D seem different from both wild-type and sir2D. It may be helpful to the reader to quantify the bubble to arc ratios. fun30D also seems to be affecting ARS305 by itself.

We provide quantification of 2 D gels in Figure 4.

(4) Figure 5. 

(4.1) For examining origin firing based on the disappearance of the Mcm-MNase reads, is HU arrest necessary? HU may be causing indirect effects due to replication fork stalling. In principle, the authors should be able to perform this analysis without HU, since their cells are released from synchronized arrest in G1 (and at least for the first cell cycle should proceed synchronously on to S phase). In addition, validation of Mcm-ChEC results using ChIP for one of the subunits of the MCM complex would increase confidence in the results. 

The HU arrest allows us to examine early events in DNA replication at much finer spatial and temporal resolution than it would be possible without it.

We have now used Mcm2 ChIP to confirm that the signal disappears at the MCM loading site in HU in sir2 cells as discussed above (Figure 5 figure supplement 3). However, the resolution is inadequate to discriminate non-repositioned vs repositioned MCMs.

(4.2) The non-displaced Mcm-ChEC signal in sir2D seems like it's decreasing more than in wildtype cells. Explain. It would be helpful to quantify these results by integrating the area under each peek (or based on read numbers). It looks like one of the displaced Mcm signals (the one more distal from the non-displaced) is changing at a similar rate to the non-displaced.  

Integrating the area under each Mcm-ChEC peak or using read numbers is superfluous for the following reasons:  (1) The rectangular appearance of the peaks in Figure 5 clearly reflects signal intensity, making additional numerical integration redundant. (2) The visual differences between wild-type and sir2D cells are distinct and sufficient for drawing conclusions without further quantification.  (3) Keeping the analysis straightforward avoids unnecessary complexity and maintains clarity.

(4.3) Can the authors explain why fun30D seems to be suppressing only one of the 2 displaced Mcms from firing? 

We speculate that the local environment is more conductive for firing one of two displaced MCMs, but we do not understand why.

(5) Figure 6. Why would the deletion of SIR2, a silencing factor, results in increased nucleosome occupancy at rDNA? 

If we understand correctly, the reviewer is referring to a small increase in +2 and +3 signal in sir2 compared to the WT. In WT G1 cells, there is a single MCM between +1 and +3 nucleosome. This space cannot accommodate a +2 nucleosome in G1 cells because MCM is loaded at that position in most cells (in G2 cells however, this space is occupied by a nucleosome (Foss et al., 2019). MCM repositioning in sir2 mutant would displace MCM from this location making it possible for this space to be now occupied by a nucleosome.

The changes in nuc density seem modest. Also, nucleosome density is similarly increased in sir2D and fun30D cells, but sir2 has a dramatic effect on origin firing but fun30D does not. Explain. 

We believe that the FUN30 status makes most of the difference for firing of displaced MCMs.

Since there are few displaced MCMs in SIR2 cells, there is not large impact on origin firing. Furthermore, the rDNA already fires late in WT cells, so our ability to detect further delay upon  FUN30 deletion could be more difficult.

(6) Discussion. At rDNA Sir2 may simply act by deacetylating nucleosomes and decreasing their mobility. This is unrelated to compaction which is usually only invoked regarding the activities of the full SIR complex (Sir2/3/4) at telomeres and the mating type locus. The arguments regarding polymerase size, compaction etc may not be relevant to the main point since although the budding yeast Sir2 participates in heterochromatin formation at the mating type loci and telomeres, at rDNA it may act locally near its recruitment site at the RFB. 

This is a valid point. We have added this sentence in the discussion to highlight the differences between silencing at rDNA and those at the silent mating loci and telomeres that SIR-complex dependent.

“Steric arguments such as these are even less compelling when made for rDNA than for the silent mating type loci and telomeres, because chromatin compaction has been studied mostly in the context of the complete Sir complex (Sir1-4). In contrast, Sir1, 3, and 4 are not present at the rDNA.”

Minor 

It would be interesting to see if deletion of any histone acetyltranferases acts in a similar way to Fun30 to reduce rDNA copy number in sir2D cells. 

Thank you for this suggestion.

Reviewer #3 (Recommendations For The Authors): 

(1) The design of Figure 3 could be improved. A scheme could help understand the assay without flipping back to Figure 1. The numbers below the gel bands need definition. 

We have included the scheme describing the restriction and MCM-MNase cut sites and the location of the probe for the Southern blot.

(2) The design of Figure 4 could be improved by adding a scheme to help interpret the 2d gel picture. The figure also lacks quantitation. Are the results reproducible and the differences significant? 

We have added the scheme, quantification and statistics in Figure 4.

(3) Please list in each figure legend the exact strains from Table S1 which were used. 

We have included the strain numbers in the Figure legend.

Durand-Dubief M, Will WR, Petrini E, Theodorou D, Harris RR, Crawford MR, Paszkiewicz K, Krueger F, Correra RM, Vetter AT et al. 2012. SWI/SNF-like chromatin remodeling factor Fun30 supports point centromere function in S. cerevisiae. PLoS Genet 8: e1002974.

Foss EJ, Gatbonton-Schwager T, Thiesen AH, Taylor E, Soriano R, Lao U, MacAlpine DM, Bedalov A. 2019. Sir2 suppresses transcription-mediated displacement of Mcm2-7 replicative helicases at the ribosomal DNA repeats. PLoS Genet 15: e1008138.

He Y, Petrie MV, Zhang H, Peace JM, Aparicio OM. 2022. Rpd3 regulates single-copy origins independently of the rDNA array by opposing Fkh1-mediated origin stimulation. Proc Natl Acad Sci U S A 119: e2212134119.

Kwan EX, Alvino GM, Lynch KL, Levan PF, Amemiya HM, Wang XS, Johnson SA, Sanchez JC, Miller MA, Croy M et al. 2023. Ribosomal DNA replication time coordinates completion of genome replication and anaphase in yeast. Cell Rep 42: 112161.

I'm surprised that Poe, as the pioneer of detective literature, can come up with such a deliberate and coherent process of thinking.

I know that the author wants to create an image of Dupin as a detective who is good at reasoning; however, I wondered, how could he link all these details together and never miss one action or facial expression from our narrator? If the author had cut some of the details, would it be more convincing to most people? Since most of us could barely do that, we might not be able to think of it and resonate with it.

Science Fiction isn't always about terrifying the audience with frightening scenarios, but a tool that can be used to predict the mere future and hopefully change the future scenario with these story that may open the reader mind to understand what is actually happening in their surroundings and start acting now before they encounter somewhat a similar scenario like the ones they read in fiction science stories.

When watching the video "How ChatGPT Works Technically | ChatGPT Architecture" I found it fascinating to learn that words are represented by numbers, as they are easier for the model to process. This gives cause to question just how reliable these models are, as one slight misspelling can skew the results completely. For instance, if I were chatting with a friend via text about my plans for the holidays and they told me they were "going home to visit their parents" and I responded "Yes. I think I will go home to visit my pants too." They would easily be able to deduce my intended statement by referencing the context of our conversation. AI models fail to offer fluid thinking in these situations.

I would like to learn more about what the "constraints" of an AI model mean. When looking at the word constraint from my own personal experience with constraints in manufacturing that represent where we are falling short or what may be holding us back. Does this mean the same thing in AI or does the word simply mean the rules or conditions within which the AI model exists?

Author response:

The following is the authors’ response to the previous reviews.

We are grateful to all three reviewers and editors for their critical comments and suggestions.

Reviewer #2 (Recommendations For The Authors):

The authors responded satisfactorily to all my comments and suggestions.

We thank the reviewer for his time and feedback.

Reviewer #3 (Recommendations For The Authors):

Comments for authors:

The authors have addressed most of the reviewer's concerns. Although no additional data were included to strengthen the manuscript, they have clarified some relevant points, and the manuscript has been updated accordingly. In my view, the current manuscript is well-written and mostly straightforward.

We thank the reviewer for his time and suggestions. Addressing them have improved the quality of our manuscript.

After a second revision, I just have a few minor comments (mostly editorial) that should be easy to address.

(1) Page 16: "The dominant presence of the GRIK1-1 gene was also reported in retinal Off bipolar cells..." Please include reference(s).

We have now cited the following reference:

Lindstrom, S.H., Ryan, D.G., Shi, J., DeVries, S.H., 2014. Kainate receptor subunit diversity underlying response diversity in retinal Off bipolar cells. J. Physiol. 592, 1457–1477. https://doi.org/10.1113/jphysiol.2013.265033

(2) Page 18: "Based on our functional assays, the splice seems to affect the interaction between the receptor and auxiliary proteins". Please remove or tone down this statement; the current data do not support this claim.

We have revised the sentence as following: “Based on our functional assays, the splice may possibly affect the interaction between the receptor and auxiliary proteins.”

(3) Page 24: "cultures ... at 0.5 µg/mL were transfected". In the current context, it is not clear what you mean with 0.5 µg/mL. Please check and correct.

Thanks for pointing out this error. We have corrected it.

(4) Page 30. He et al. reference is repeated.

Thanks. We have fixed it now.

(5) Figure 3, Panel C: Please incorporate the EC50 value for the red trace into the figure; it appears to be a different data set and, consequently, a different fitting compared with Figure 2C.

The GluK1-1a data set (red trace) is identical to that in Figure 2c, though it may appear different due to the scale of the X and Y axis. As suggested, we have now included the EC50 value for this data set in Figure 3, panel C.

(6) Figure legend 4: Please check two minor issues here:

(a) "Bar graphs... with or without Neto1 protein..." This statement is apparently wrong; Figure 4 does not show the effect of Neto1.

(b) "The wild type GluK1 splice variant data is the same as from Figure 1.." I think the authors mean Figure 2A instead of Fig. 1. Please check.

Thanks for pointing out the error. We have fixed the same in the revised manuscript.

(7) Please check and correct spelling/wording issues in the text. Here are some examples:

(a) Page 9 " Figure 3G - I, Table2.." (There is no Panel I). 

Fixed.

(b) Page 16 "... and is involved in various pathophysiology..." 

We have revised the sentence as “… and is involved in various pathophysiological conditions”

(c) Page 19 "The constructs used for this study were HEK293 WT mammalian cells were seeded on..." 

Fixed. Thanks.

(d) Page 23 "The immunoblots were probed..." Please check the whole paragraph and correct the issues.

Fixed. Thanks.

(e) Page 27 "initially, 1,97,908 particles were picked". Check the value; the same issue occurs in Fig.6 table supplement 1. 

Thanks. We have now modified the sentence to clarify that for  GluK1-1aEM ND-SYM, initially, 1,97,908 particles were picked and subjected to multiple rounds of clean-up using 2D and 3D classification. Finally,  24,531 particles were used for the final 3D reconstruction and refinement.

(f) Legend Figure 2: Remove "(F)" from the legend. 

Thanks. Fixed.

(g) Legend Figure 2-Sup.1: Check/correct spelling issues. 

Thanks. Fixed.

(h) Figure 5-figure supplement 1: There is a mistake in panel B: "GFP" label is shown for Gluk1 and Neto2, but the authors mention that the pull-down was done with Anti-His antibodies. Please correct.

Thanks. The pull-down experiments were done with anti-His for both the blots presented in panels A and B as mentioned in both the figures (right side panels of both A and B). However, for the GluK1 and Neto2 pull downs (panel B), the blots were probed with anti-GFP antibody which would detect both the receptor (as the receptor has both GFP-His8) and Neto2-GFP at their respective sizes. This has been indicated in the figure panel B.

(8) Related to the point-by-point document:

Major concern 2: Interpreting the effect of mutants on the regulation by Neto proteins requires knowing how the mutant is affecting the channel properties without Neto. In my view, if the data showing the K368/375/379/382H376-E mutant without Neto is missing (in this case due to low current amplitude), then, the pink bars in Fig. 5 should be removed from the figure. 

We thank the reviewer for raising this interesting point and agree that it would be valuable to characterize the channel properties of all the mutants individually. However, as mentioned earlier, the functions of some mutant receptors are only rescued, or reliable, measurable currents are detected, when they are co-expressed with Neto proteins. We still believe that comparing wild-type and mutant receptors co-expressed with Neto proteins provides important insights, and therefore, we would like to retain the K368/375/379/382H376-E mutant data in the figure.

Major concern 4: Figure 6-figure Supplement 8 is not mentioned in the manuscript. It would help to include a proper description in the Results section similar to the answer included in the point-by-point document.

Figure6-figure Supplement 8 has already been cited on page 15. We have also cited Figure6-figure Supplement 9 on the same page and have added following sentences in the text:

“A superimposition of GluK1-1aEM (detergent-solubilized or reconstituted in nanodiscs) and GluK1-2a (PDB:7LVT) showed an overall conservation of the structures in the desensitized state. No significant movements were observed at both the ATD and LBD layers of GluK1-1a with respect to GluK1-2a (Figure 6; Figure 6-figure supplement 9).”

Major concern 5: The ramp/recovery protocol was not included properly in the manuscript; please include the time of the ramp pulse and the time used for the recovery period.

Elaborated ramp and recovery protocols are included in the methods section. The time used for the recovery period was variable and was tuned as per the recovery kinetics. All the figures were representative traces are shown include the scale bar showing the time period of agonist application.

Minor concern 1: The proposed change was not included in the manuscript; check page 7.

Thanks for highlighting this error. We have now changed it in the revised manuscript.

Minor concern 10: The manuscript was not corrected as indicated. Please check.

Thanks. We have now modified the sentence as following: “…..a reduction was observed for K375/379/382H376-E receptors (1.17 ± 0.28 P=0.3733) compared to wild-type although differences do not reach statistical significance”

Minor concern 14: The figure was not corrected as indicated. Please check.

Thanks for highlighting this error. We have now changed it in the revised manuscript.

Minor concern 19: I suggest including this briefly in the Discussion section.

Thanks for the suggestion. We have included the following sentence in the discussion:

“The differences in observations could be due to variations in experimental conditions, such as the constructs and recording conditions used.”

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Weaknesses:

Given that all mutants tested showed the same degree of activation by PEG400, it seemed possible that PEG400 might be an allosteric activator of WNK1/3 through direct binding interactions. Perhaps PEG400 eliminates CWN1/2 waters by inducing conformational changes so that water loss is an effect not a cause of activation. To address this it would be helpful to comment on whether new electron densities appeared in the X-ray structure of WNK1/SA/PEG400 that might reflect PEG400 interactions with chains A or B.

We re-evaluated the WNK1/SA/PEG400 electron density looking for non-protein densities larger than water. No new densities were found. However, we do observe a PEG400-destabilizing effect using differential scanning fluorimetry, and have included this data into Figure 2. We conclude that the effects on the water structure and destabilization are due to demands on solvent.

We have included in the second paragraph of the introduction references to primary literature that advance similar arguments to explain osmolyte induced effects on activity.

Specifically, Colombo MF, Rau DC, Parsegian VA (1992) Protein solvation in allosteric regulation: a water effect on hemoglobin. Science 256: 655-659 and LiCata VJ, Allewell NM (1997) Functionally linked hydration changes in Escherichia coli aspartate transcarbamylase and its catalytic subunit. Biochemistry 36: 10161—10167. 

It would also be helpful to discuss any experiments that might have been done in previous work to examine the direct binding of glycerol and other osmolytes to WNKs.

We did not observe PEG400 in WNK1/SA/PEG400 despite effects on the space group and subunit packing. On the other hand, glycerol was observed in WNK1/SA, which was cryoprotected in glycerol (PDB file 6CN9). We have highlighted these differences in the second section of the results. A thorough analysis on the effects of various osmolytes on WNK structure, stability, and activity is a potential future direction.

The study would benefit from a deeper discussion about how to reconcile the different effects of mutations. For example, wouldn't most or all of the mutations be expected to disrupt the water network, and relieve the proposed autoinhibition? This seemed especially true for some of the residues, like Y420(Y346), D353(D279), and K310(K236), which based on Fig 3 appeared to interact with waters that were removed by PEG400.

The manuscript has been updated with new data and better discussion of this point. Given the inconsistencies on the effects of mutation in static light scattering (SLS), we addressed the possibility that the reducing agent was not constant across experiments. In a repeated study, including reducing agent (1 mM TCEP), we obtained results on mutant mass more similar to wild-type than in the original experiment. An exception was that two of the mutants were much more monomeric than wild-type. It follows that the network CWN1 stabilizes the inactive dimer. The reduced activity of some of the mutants probably reflects the position of CWN1 and the AL-CL Cluster in the active site, such that mutants can affect substrate binding or catalysis. This is now better discussed both in the data and discussion sections.

Mutants have a tendency to have complex effects on activity and structure. It was satisfying to find any activating mutants. We point out that we have been careful to present all of our data including mutants that are not easily explained by our models.

Alternatively, perhaps the waters in CWN2 are more important for maintaining the autoinhibited structure. This possibility would be useful to discuss, and perhaps comment on what may be known about the energetic contributions of bound water towards stabilizing dimers.

This research focused on the most salient unique feature of WNK1- CWN1. We also identified CWN2. Mutational analysis of CWN2 can’t be done without disrupting the dimer interface, greatly complicating data interpretation.

It would also be useful to comment on why aggregation of E319Q/A (E314) shouldn't inhibit kinase activity instead of activating it.

On recollection of the SLS data in the presence of reducing agent, we saw reduced aggregation. WNK3/D279N and WNK3/E314Q were more monomeric, especially at the higher protein concentration used. WNK3/E314Q is one of the more active mutants.

The X-ray work was done entirely with WNK1 while the mutational work was done entirely with WNK3. Therefore, a simple explanation for the disconnect between structure and mutations might be that WNK1 and WNK3 differ enough that predictions from the structure of one are not applicable to mutations of the other. It would be helpful to describe past work comparing the structure and regulation of WNK1 and WNK3 that support the assumption of their interchangeability.

We have responded directly to this concern. We introduced our most interesting amino acid replacement WNK3/E314A into WNK1, making WNK1/E388A. Similar trends in chloride inhibition and mutational activation were observed in WNK1 as in WNK3. This supports the assumption of interchangeability of WNK1 and WNK3 we invoked for practical reasons.  As expected, the overall activity of WNK1 is lower than WNK3. Overall, the lower activity limited data collection. However, the lower activity did allow us to fit the chloride inhibition data to a kinetic model for WNK1.  Panels on WNK1 activity, mutation, and chloride inhibition were added to Figure 5 and to Supplemental data (Table S6).

Reviewer #2 (Public Review):

Strengths:

The most interesting result presented here is that P1 crystals of WNK1 convert to P21 in the presence of PEG400 and still diffract (rather than being destroyed as the crystal contacts change, as one would expect). All of the assays for activity and osmolyte sensing are carried out well.

Thank you. We have emphasized this point in the Results section with the word “remarkably”

Weaknesses:

The rationale for using WNK3 for the mutagenesis study is that it is more sensitive to osmotic pressure than WNK1. I think that WNK1 would have been a better platform because of the direct correlation to the structural work leading to the hypothesis being tested. All of the crystallographic work is WNK1; it is not logical to jump to WNK3 without other practical considerations.

This point is addressed in the last comment to Reviewer 1. We added autophosphorylation assay data on our most interesting mutant (WNK3/E314A) in WNK1 (WNK1/E388A). Conversely, we have crystallographic data on uWNK3 (on uWNK3/E314A collected to 3.3Å). These new data justify the assumption of interchangeability of results obtained for uWNK1 and uWNK3.

Osmolyte sensing was tested by measuring ATP consumption as a function of PEG400 (Figure 6). Data for the subset of mutants analyzed by this assay showed increasing activity. It is not clear why the same collection of mutant proteins analyzed in the experiments of Figure 5 was not also measured for osmolyte sensing in Figure 6.

These data are now more complete, having been now collected for all of the WNK3 mutants (now Figure 7).

The last set of data presented uses light scattering to test whether the WNK3 mutant proteins exhibit quaternary structural changes consistent with the monomer/dimer hypothesis. If they did, one would expect a higher degree of monomer for those that are activated by mutation, and a lower amount of monomer (like wt) for those that are not. Instead, one of the mutant proteins that showed the most chloride inhibition (Y346F) had a quaternary structure similar to the wt protein, and others have similar monomer/dimer mixtures but distinct chloride inhibition profiles (K307A and M301A). I don't see how the light scattering data contribute to this story other than to refute the hypothesis by showing a lack of correlation between quaternary structure, water binding, and activity. This is another reason why the disconnect between WNK1 and WNK3 could be a problem. All of the detailed structural work with WNK1 must be assumed with WNK3; perhaps the light scattering data are contradicting this assumption?

As noted above, on recollection of the SLS data in the presence of reducing agent, we saw reduced aggregation and more consistency with our model. Thus, we now feel it is a useful contribution to the manuscript. The table in Supplemental data has been updated.

Reviewer #1 (Recommendations For The Authors):

Fig 3D in the PDF manuscript seemed distorted - waters were cut off. Also Fig 2D would benefit from showing the whole molecule, instead of cutting off the top and bottom of the kinase domain.<br /> We suspect this is a data transfer problem, since we don’t see these truncations.

Both Figure 2 and 3 have been changed, addressing these concerns and adding new differential scanning fluorimetry data as discussed in reply to Reviewer 1. Figure 2 was simplified by eliminating Figures 2A-2C, and replacing them with a new Figure 2B, the superposition of WNK1/SA/PEG400 (PDB 9D3F), WNK1/SA (PDB 6CN9).  

In Figure 3, we added a panel highlighting the volume change around CWN1 in presence of PEG400 (Figure 3C). Hopefully, inappropriate cropping has been eliminated.

Line 162: Y314F should be Y346F.

This has been corrected. Thank you.

Lines 211-213 - these two sentences do not seem to logically go together: "Two hyper-active mutants were discovered, WNK3/E314A, and WNK3/E314Q. These mutants are straightforward to interpret based on our model: the mutated residues support and stabilize inactive dimeric WNK."

An extensive rewrite has been conducted to address the difference in activity between the higher activity mutants versus less active mutants, now discussed in two paragraphs, and two Figures, Figure 5 and 6. The SLS data, recollected with more reducing agent, has given more consistent results (Supplemental), making the discussion more straightforward (discussed above).

Reviewer #2 (Recommendations For The Authors)

I think WNK1 would be a better platform for mutagenesis than WNK3. Or minimally the authors should better justify the switch to WNK3 from WNK1. Analyze the same set of mutants in Figure 5 into Figure 6.

Again, we have added assay data on uWNK1/E388A, and structural data on uWNK3/E314A.

I would analyze the same set of mutants in Figures 5 and 6.

We have analyzed all of the WNK3 mutants in the ADP-Glo assays (Figure 7).

Will the P21 crystal form grow independently in PEG400?

Attempts to crystallize WNK1/SA or WNK3/SA or other constructs in PEG400 have been unsuccessful.

I would also add some context about the role of water in allosteric mechanisms. I know there is a long history in hemoglobin in which specific waters have been associated with the T and R states such as that by Marcio Colombo. There is a relatively recent article in J. Phys Chem. that would provide good context. Leitner et al., J. Chem. Phys. 152, 240901 (2020)

Thank you. Good call.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

This fundamental study uses a creative experimental system to directly test Ohno's hypothesis, which describes how and why new genes might evolve by duplication of existing ones. In agreement with existing criticism of Ohno's original idea, the authors present compelling evidence that having two gene copies does not speed up the evolution of a new function as posited by Ohno, but instead leads to the rapid inactivation of one of the copies through the accumulation of mostly deleterious mutations. These findings will be of broad interest to evolutionary biologists and geneticists.

We thank the editors and the reviewers for their positive feedback concerning our experimental system and for the constructive feedback on how to further improve the manuscript. We have now addressed the reviewer’s comments in a revised version.

Reviewer #1 (Public Review):

Overview:

The authors construct a pair of E. coli populations that differ by a single gene duplication in a selectable fluorescent protein. They then evolve the two populations under differing selective regimes to assess whether the end result of the selective process is a "better" phenotype when starting with duplicated copies. Importantly, their starting duplicated population is structured to avoid the duplication- amplification process often seen in bacterial artificial evolution experiments. They find that while duplication increases robustness and speed of adaptation, it does not result in more highly adapted final states, in contrast to Ohno's hypothesis.

Major comments:

This is an excellent study with a very elegant experimental setup that allows a precise examination of the role of duplication in functional evolution, exclusive of other potential mechanisms. My main concern  is  to  clarify  some  of  the  arguments  relating  to  Ohno's  hypothesis.

I think my main confusion on first reading the manuscript was in the precise definition of Ohno's hypothesis. I think this confusion was mine and not the authors, but it is likely common and could be addressed.

Most evolutionary biologists think of gene duplication as making neofunctionalization "easier" by providing functional redundancy and a larger mutational target, such that the evolutionary process of neofunctionalization is faster (as the authors observed). In this framework, the final evolved state might not differ when selection is applied to duplicated copies or a single-copy gene. Ohno's hypothesis, by contrast, argues that there generally exist adaptive conflicts between the ancestral function and the "desired" novel function, such that strong selection on a single-copy gene cannot produce the evolutionary optima that selection on two copies would. This idea is hinted at in the quotation from Ohno in paragraph 2 of the introduction. However, the sentences that follow I don't think reinforce this concept well enough and lead to some confusion.

With that definition in mind, I agree with the authors' conclusion that these data do not support Ohno's hypothesis. My quibble would be that what is actually shown here is that adaptive conflict in function is not universal: there are cases where a single gene can be optimized for multiple functions just as well as duplicated copies. I do not think the authors have, however, refuted the possibility that such adaptive conflicts are nonetheless a significant barrier to evolutionary innovation in the absence of gene duplication generally. Perhaps just a sentence or two to this effect might be appropriate.

We fully agree with the reviewer that trade-offs might play an important role in the evolution of single copy and of duplicated genes, depending on the gene and on the selection regime. And while trade-offs are not likely to play a big role in the selection regime we discuss in detail in the main text (evolution towards more green), they probably are important for at least one our selection regimes. In fact, we so state in the following passage of the discussion. In addition, we have now added a sentence that acknowledges the importance of trade-offs for evolution in the absence of gene duplication:

“A single gene encoding such a protein suffers from an adaptive conflict between the two activities. Gene duplication may provide an escape from this adaptive conflict, because each duplicate may specialize on one activity14, 15. For coGFP, a trade-off likely exists for fluorescence in these two colors, because improvement of green fluorescence entails a loss of blue fluorescence during evolution (Figure S8 and Figure S16). We therefore expected that during selection for both green and blue fluorescence, one cogfp copy in double-copy populations would “specialize” on green fluorescence whereas the other copy would specialize on blue fluorescence. However, when we analyzed individual population members with two active gene copies we could not find any such specialization (Figure S21). Moreover, the identified key mutations at positions 147 and 162 have a very low frequency (<1%) in these populations (Figure S15). Future experiments with different selection strategies might reveal the reasons for this observation and the conditions under which such a specialization can occur.“

I also think the authors need to clarify their approach to normalizing fluorescence between the two populations to control for the higher relative protein expression of the population with a duplicated gene. Since each population was independently selected with the highest fluorescing 60% (or less) of the cells selected, I think this normalization is appropriate. Of course, if the two populations were to compete against each other, this dosage advantage of the duplicates would itself be a selective benefit. Even as it is, the dosage advantage should be a source of purifying selection on the duplication, and perhaps this should be noted.

The reviewer is correct. To be able to follow the evolutionary trajectories of the different constructs, the populations were treated separately. The gates were adjusted for each library separately to select for the top 60, 1 or 0.01% of cells and the gates for the double-copy populations were set to slightly higher fluorescence, reflected in the higher fluorescence of these populations in Figure 3A. Indeed, if individuals in these populations were to compete against each other, the double-copy populations would have a benefit due to the dosage advantage. However, as we already pointed out in the manuscript, we did not see any additional advantage beyond the increased gene dosage provided by the second copy (Figure 3B). To discuss this issue in more detail, we have now added the following text to the discussion:

“It is worth noting that we evolved each of our single- and double-copy populations separately and in parallel to follow their individual evolutionary trajectories. In a natural population, individuals with one or two copies might occur in the same population and compete against each other. In this situation any dosage advantage of a duplicate gene would itself entail selective benefit. Our approach allowed us to find out if gene duplication facilitates phenotypic evolution beyond any such gene dosage effect. At least for the specific genes, selection pressures, and mutation rates we used, the data suggest that it does not.”

Finally, I am slightly curious about the nature of the adaptations that are evolving. The authors primarily discuss a few amino-acid changing mutations that seem to fix early in the experiment. Looking at Figure 3, it however, appears that the populations are still evolving late in the experiment, and so presumably other changes are occurring later on. Do the authors believe that perhaps expression changes to increase protein levels are driving these later changes?

Figure S15 shows that some mutations are indeed still increasing in frequency during late evolutionary rounds, in particular S2L, V141L and V205L. We have measured the emission spectra of these mutants (Figure S16), and these mutations increase fluorescence both in green and blue. It is therefore likely that these mutations, similar to L98M, increase protein expression, solubility, or thermal stability, as suggested by the reviewer. We now clarify this matter in a new passage of the results:

“Like L98M, the additional mutations S2I, V141I and V25L also occurred in all selection regimes, but they reached lower frequencies than L98M during the 5 generations of the experiment. We hypothesized that mutations observed in all selection regimes do not derive their benefit from increasing the intensity of any one fluorescent color. Instead, they may increase protein expression, solubility, or thermal stability.”

Reviewer #2 (Public Review):

Summary:

Drawing from tools of synthetic biology, Mihajlovic et al. use a cleverly designed experimental system to dissect Ohno's hypothesis, which describes the evolution of functional novelty on the gene-level through the process of duplication & divergence.

Ohno's original idea posits that the redundancy gained from having two copies of the same gene allows one of them to freely evolve a new function. To directly test this, the authors make use of a fluorescent protein with two emission maxima, which allows them to apply different selection regimes (e.g. selection for green AND blue, or, for green NOT blue). To achieve this feat without being distracted by more complex evolutionary dynamics caused by the frequent recombination between duplicates, the authors employ a well-controlled synthetic system to prevent recombination: Duplicates are placed on a plasmid as indirect repeats in a recombination-deficient strain of E.coli. The authors implement their directed evolution approach through in vitro mutagenesis and selection using fluorescent-activated cell sorting. Their in-depth analysis of evolved mutants in single-copy versus double-copy genotypes provides clear evidence for Ohno's postulate that redundant copies experience relaxed purifying selection. In contrast to Ohno's original postulate, however, the authors go on to show that this does not in fact lead to more rapid phenotypic evolution, but rather, the rapid inactivation of one of the copies.

Strengths:

This paper contributes with great experimental detail to an area where the literature predominantly leans on genomics data. Through the use of a carefully designed, well-controlled synthetic system the authors are able to directly determine the phenotype & genotype of all individuals in their evolving populations and compare differences between genotypes with a single or double copy of coGFP. With it they find clear evidence for what critics of Ohno's original model have termed "Ohno's dilemma", the rapid non- functionalization by predominantly deleterious mutations.

Including an expressed but non-functional coGFP in (phenotypically) single copy genotypes provides an especially thoughtful control that allows determining a baseline dN/dS ratio in the absence of selection. All in all the study is an exciting example of how the clever use of synthetic biology can lead to new insights.

Weaknesses:

The major weakness of the study is tied to its biggest strength (as often in experimental biology there is a trade-off between 'resolution' and 'realism').

The paper ignores an important component of the evolutionary process in favour of an in-depth characterization of how two vs one copy evolve. Specifically, by employing a recombination-deficient strain and constructing their duplicates as inverted repeats their experimental design completely abolishes recombination between the two copies.

This is problematic for two reasons:

i)  In nature, new duplicates do not arise as inverted, but rather as direct (tandem) repeats and - as the authors correctly point out - these are very unstable, due to the fact that repeated DNA is prone to recA- dependent homologous recombination (which arise orders of magnitude more frequently than point mutations).

ii)  This instability often leads to further amplification of the duplicates under dosage selection both in the lab and in the wild (e.g. Andersson & Hughes, Annu. Rev. Genet. 2009), and would presumably also be an outcome under the current experimental set-up if it was not prevented from happening?

So in sum, recombination between duplicate genes is not merely a nuisance in experiments, but occurring at extremely high frequencies in nature (such that the authors needed to devise a clever engineering solution to abolish it), and is often observed in evolving populations, be it in the laboratory or the wild.

The manuscript sells controlling of copy number as a strength. And clearly, without it, the same insights could not be gained. However, if the basis for the very process of what Ohno's model describes is prevented from happening for the process to be studied, then, for reasons of clarity and context this needs pointing out, especially, to readers less familiar with the principles of molecular evolution.

Connected to this, there are several places in the introduction and the discussion where I feel that the existing literature, in particular models put forward since Ohno that invoke dosage selection (such as IAD) end up being slightly misrepresented.

My point is best exemplified in line 1 of Discussion: "To test Ohno's hypothesis and to distinguish its predictions from those of competing hypotheses, it is necessary to maintain a constant and stable copy number of duplicated genes during experimental evolution."

We understand the reviewer’s position and fully agree that we needed to clarify better what our experiments aimed to achieve. To this end, we rewrote the beginning of the discussion to read:

“Our aim was to study whether gene duplication can affect mutational robustness and phenotypic evolution beyond any effect of increased gene dosage provided by multiple gene copies. To this end, we needed to maintain a constant and stable copy number of duplicated genes during experimental evolution.”

I think this statement is simply not true and might be misleading. To take the exaggerated position of a devil's advocate, the goal of evolutionary biology should be to find out how evolution actually proceeds in nature most of the time, rather than creating laboratory systems that manage to recapitulate influential ideas.

On this point, we respectfully disagree. To ask questions like ours, laboratory experiments that are highly controlled albeit possibly “unnatural” can be essential. And we would argue that our experiments do not merely aim to “recapitulate” an influential idea but to validate it and potentially refute it, as we did for our study system. Validating theory is an essential aspect of experimental science. Textbooks in biology and beyond are rife with examples.

While fixing copy number may be a necessary step to understand how one copy evolves if a second one is present, it seems that if Ohno's hypothesis only works out in recA-deficient bacterial strains and on engineered inverted repeats, that Ohno might have missed one crucial aspect of how paralogs evolve. The mentioned competing hypotheses have been put forward to (a) address Ohno's dilemma (which the present study beautifully demonstrates exists under their experimental conditions) and (b) to reflect a commonly observed evolutionary process in bacteria (dosage gain in response to selection, e.g. a classic way of gaining antibiotic resistance). Fixing the copy number allowed the authors to show which predictions of Ohno's model hold up and which don't (under these specific conditions). But they do so without even preventing the processes described by alternative models from happening, so the experimental system is hardly appropriate to distinguish between Ohno & alternatives. Therefore, I think it could be made clearer that the experimental system is great to look at certain aspects Ohno's hypothesis in  detail, but  it  can  only inform  us about  a  universe  without  recombination.

(1)  Citing the works by ref 8, 26, 27 to merely state that "in some copies were gained and some were lost (ref 6, ref 25)" makes it seem as if fixing at 2 copies is some sort of sensible average. Yet ref 6 (Dhar et al.) specifically states that dosage is the most important response. Moreover, in this study gene copies are lost, but plasmid copies are gained instead. In Holloway et al. 2007 (ref 25), the 2 copies resided on different plasmids, so entirely different underlying molecular genetics might be at work (high cost of plasmid maintenance, and competitive binding on both proteins onto the respective (off)-target, where either way selection favored a single copy, so a different situation altogether). In both cited studies, fixing the copy would have prohibited learning something about the process of duplication & divergence.

Hence this statement seems to distract the readers from the main message, which seems that preventing recombination experimentally allows to follow the divergence of each copy and studying a response that does not involve dosage-increase.

(2)   "These studies highlighted the importance of gene duplication in providing fast adaptation under changing environmental conditions but they focused on the importance of gene dosage." I think this constructs a false dichotomy. Instead, these studies pointed out that dosage (and with it, selection for dosage)  is  an  important  part  of  the  equation  that  might  have  been  missed  by  Ohno.

Your points are well taken. To clarify the insights from previous experiments and the aims of our experiments we rewrote this passage in question as follows.

“These studies underline the importance of gene duplication in providing fast adaptation under changing environmental conditions. In some studies one copy was lost6, 25, while in others, additional copies were gained8, 26, 27. Together these studies highlight that gene dosage and selection for dosage can play an important role during the evolution of duplicated genes6, 8, 25-28.

These studies also raise the question whether gene duplication can provide an advantage beyond its effects on gene dosage. To find out it is necessary to study the evolution of gene duplicates while keeping the copy number of the duplicated gene exactly at two. This is challenging because gene duplication causes recombinational instability and high variability in copy number. No previous experimental studies were designed to control copy number. Here, we present an experimental system that allowed us to keep the copy number fixed at one or two genes, and to follow the evolution of each gene copy in the absence of any dosage increase.”

(3)  "Such models are also easier to test experimentally, because they do not require precise control of gene copy number. The necessary tests can even benefit from massive gene amplifications8. Although Ohno's hypothesis is more difficult to test experimentally (...)" - again, I feel the wording is slightly misleading. The point is not that IAD is easier to test and Ohno's model is harder to test in laboratory experiments, rather, experiments (and some more limited observations of naturally evolving populations) seem to suggest that in reality evolution proceeds (more often?) according to IAD rather than Ohno's neofunctionalization hypothesis. However, as the authors point out, it will be exciting to see their clever experimental system used to test other genes and conditions to get a more comprehensive understanding of what gene- and selection- parameter values would overcome Ohno's dilemma.

We agree and in response rewrote the paragraph in question to read:

“The challenge that a duplicated gene copy must remain free of frequent deleterious mutations long enough to acquire beneficial mutations that provide a new selectable phenotype is known as Ohno’s dilemma13. Our experiments confirm that this challenge is highly relevant for post-duplication evolution. Other models such as the innovation-amplification-divergence (IAD) model8, 13 postulate that this dilemma can be resolved through an increase in gene dosage that allows latent pre-duplication phenotypes to come under the influence of selection. To distinguish between the effects of gene dosage and other benefits of gene duplication, we prevented recombination and gene amplification to prevent copy number increases beyond two copies. We are aware that our experimental design does not reflect how evolution may occur in the wild. However, this design allowed us to study evolutionary forces separately that are otherwise difficult to disentangle. “

Finally, we also made two changes in the abstract (highlighted in red) to take your feedback into account.

Reviewer #2 (Recommendations For The Authors):

The paper is very well written, with a lot of emphasis put on explaining every step and every finding. It was a joy to read.

Thanks!

Full stop missing in line 5 of abstract.

Corrected.

Author response:

The following is the authors’ response to the original reviews.

Reviewer 1 (Public Review):

Summary: Wilmes and colleagues present a computational model of a cortical circuit for predictive processing which tackles the issue of how to learn predictions when different levels of uncertainty are present for the predicted sensory stimulus. When a predicted sensory outcome is highly variable, deviations from the average expected stimulus should evoke prediction errors that have less impact on updating the prediction of the mean stimulus. In the presented model, layer 2/3 pyramidal neurons represent either positive or negative prediction errors, SST neurons mediate the subtractive comparison between prediction and sensory input, and PV neurons represent the expected variance of sensory outcomes. PVs therefore can control the learning rate by divisively inhibiting prediction error neurons such that they are activated less, and exert less influence on updating predictions, under conditions of high uncertainty.

Strengths: The presented model is a very nice solution to altering the learning rate in a modality and context-specific way according to expected uncertainty and, importantly, the model makes clear, experimentally testable predictions for interneuron and pyramidal neuron activity. This is therefore an important piece of modelling work for those working on cortical and/or predictive processing and learning. The model is largely well-grounded in what we know of the cortical circuit.

Weaknesses: Currently, the model has not been challenged with experimental data, presumably because data from an ad- equate paradigm is not yet available. I therefore only have minor comments regarding the biological plausibility of the model:

Beyond the fact that some papers show SSTs mediate subtractive inhibition and PVs mediate divisive inhibition, the selection of interneuron types for the different roles could be argued further, given existing knowledge of their properties. For instance, is a high PV baseline firing rate, or broad sensory tuning that is often interpreted as a ’pooling’ of pyramidal inputs, compatible with or predicted by the model?

Thank you for this nice suggestion. We added a section to the discussion expanding on this: “The model predicts that the divisive interneuron type, which we here suggest to be the PVs, receive a representation of the stimulus as an input. PVs could be pooling the inputs from stimulus-responsive layer 2/3 neurons to estimate uncertainty. The more the stimulus varies, the larger the variability of the pyramidal neuron responses and, hence, the variability of the PV activity. The broader sensory tuning of PVs (Cottam et al. 2013) is in line with the model insofar as uncertainty modulation could be more general than the specific feature, which is more likely for low-level features processed in primary sensory cortices. PVs were shown to connect more to pyramidal cells with similar feature-tuning (Znamenskyiy et al. 2024); this would be in line with the model, as uncertainty modulation should be feature-related. In our model, some SSTs deliver the prediction to the positive prediction error neurons. SSTs are already known to be involved in spatial prediction, as they underlie the effect of surround suppression (Adesnik et al. 2012), in which SSTs suppress the local activity dependent on a predictive surround.”

On a related note, SSTs are thought to primarily target the apical dendrite, while PVs mediate perisomatic inhibition, so the different roles of the interneurons in the model make sense, particularly for negative PE neurons, where a top-down excitatory predicted mean is first subtractively compared with the sensory input, s, prior to division by the variance. However, sensory input is typically thought of as arising ’bottom-up’, via layer 4, so the model may match the circuit anatomy less in the case of positive PE neurons, where the diagram shows ’s’ arising in a top-down manner. Do the authors have a justification for this choice?

We agree that ‘s’ is a bottom-up input and should have been more clear about that we do not consider ‘s’ to be a top-down input like the prediction. We hence adjusted the figure correspondingly and added a few clarifying sentences to the manuscript. The reviewer, however, raises an important point, which is not talked about enough. Namely, that if the bottom-up input ‘s’ comes from L4, how can it be compared in a subtractive manner with the top-down prediction arriving in the superficial layers? In Attinger et al. it was shown that the visual stimulus had subtractive effects on SST neurons. The axonal fibers delivering the stimulus information are hence likely to arrive in the vicinity of the apical dendrites, where SSTs target pyramidal cells. Hence, those axons delivering stimulus information could also target the apical dendrites of pyramidal cells. As the reviewer probably had in mind, L4 input tends to arrive in the somatic layer. However, there are also stimulus-responsive cells in layer 2/3, such that the stimulus information does not need to come directly from L4, it could be relayed via those stimulus-responsive layer 2/3 cells. It has been shown that L2/3→L3 axons are mostly located in the upper basal dendrites and the apical oblique dendrites, above the input from L4 (Petreanu et al. The subcellular organization of neocortical excitatory connections). Hence, stimulus information could arrive on the apical dendrites, and be subtractively modulated by SSTs. We would also like to note that the model does not take into account the precise dendritic location of the inputs. The model only assumes that the difference between stimulus and prediction is calculated before the divisive modulation by the variance.

In cortical circuits, assuming a 2:8 ratio of inhibitory to excitatory neurons, there are at least 10 pyramidal neurons to each SST and PV neuron. Pyramidal neurons are also typically much more selective about the type of sensory stimuli they respond to compared to these interneuron classes (e.g., Kerlin et al., 2012, Neuron). A nice feature of the proposed model is that the same interneurons can provide predictions of the mean and variance of the stimulus in a predictor-dependent manner. However, in a scenario where you have two types of sensory stimulus to predict (e.g., two different whiskers stimulated), with pyramidal neurons selective for prediction errors in one or the other, what does the model predict? Would you need specific SST and PV circuits for each type of predicted stimulus?

If we understand correctly, this would be a scenario in which the same context (e.g., sound) is predicting two types of sensory stimulus. In that case, one may need specific SST and PV circuits for the different error neurons selective for prediction errors in these stimuli, depending on how different the predictions are for the two stimuli as we elaborate in the following. The reviewer is raising an important point here and that is why we added a section to the discussion elaborating on it.

We think that there is a reason why interneurons are less selective than pyramidal cells and that this is also a feature in prediction error circuits. Similarly-tuned cells are more connected to each other, because they tend to be activated together as the stimuli they encode tend to be present in the environment together. Also, error neurons selective to nearby whiskers are more likely to receive similar stimulus information, and hence similar predictions. Hence, because nearby whiskers are more likely to be deflected similarly, a circuit structure may have developed during development such that neurons selective for prediction errors of nearby whiskers, may receive inputs from the same inhibitory interneurons. In that case, the same SST and PV cells could innervate those different neurons. If, however, the sensory stimuli to be predicted are very different, such that their representations are likely to be located far away from each other, then it also makes sense that the predictions for those stimuli are more diverse, and hence the error neurons selective to these are unlikely to be innervated by the same interneurons.

We added a shorter version of this to the discussion: “The lower selectivity of interneurons in comparison to pyramidal cells could be a feature in prediction error circuits. Error neurons selective to similar stimuli are more likely to receive similar stimulus information, and hence similar predictions. Therefore, a circuit structure may have developed such that prediction error neurons with similar selectivity may receive inputs from the same inhibitory interneurons.”

Reviewer 2 (Public Review):

Summary: This computational modeling study addresses the observation that variable observations are interpreted differently depending on how much uncertainty an agent expects from its environment. That is, the same mismatch between a stimulus and an expected stimulus would be less significant, and specifically would represent a smaller prediction error, in an environment with a high degree of variability than in one where observations have historically been similar to each other. The authors show that if two different classes of inhibitory interneurons, the PV and SST cells, (1) encode different aspects of a stimulus distribution and (2) act in different (divisive vs. subtractive) ways, and if (3) synaptic weights evolve in a way that causes the impact of certain inputs to balance the firing rates of the targets of those inputs, then pyramidal neurons in layer 2/3 of canonical cortical circuits can indeed encode uncertainty-modulated prediction errors. To achieve this result, SST neurons learn to represent the mean of a stimulus distribution and PV neurons its variance.

The impact of uncertainty on prediction errors is an understudied topic, and this study provides an intriguing and elegant new framework for how this impact could be achieved and what effects it could produce. The ideas here differ from past proposals about how neuronal firing represents uncertainty. The developed theory is accompanied by several predictions for future experimental testing, including the existence of different forms of coding by different subclasses of PV interneurons, which target different sets of SST interneurons (as well as pyramidal cells). The authors are able to point to some experimental observations that are at least consistent with their computational results. The simulations shown demonstrate that if we accept its assumptions, then the authors’ theory works very well: SSTs learn to represent the mean of a stimulus distribution, PVs learn to estimate its variance, firing rates of other model neurons scale as they should, and the level of un- certainty automatically tunes the learning rate, so that variable observations are less impactful in a high uncertainty setting.

Strengths: The ideas in this work are novel and elegant, and they are instantiated in a progression of simulations that demonstrate the behavior of the circuit. The framework used by the authors is biologically plausible and matches some known biological data. The results attained, as well as the assumptions that go into the theory, provide several predictions for future experimental testing.

Weaknesses: Overall, I found this manuscript to be frustrating to read and to try to understand in detail, especially the Results section from the UPE/Figure 4 part to the end and parts of the Methods section. I don’t think the main ideas are so complicated, and it should be possible to provide a much clearer presentation.

For me, one source of confusion is the comparison across Figure 1EF, Figure 2A, Figure 3A, Figure 4AB, and Figure 5A. All of these are meant to be schematics of the same circuit (although with an extra neuron in Figure 5), yet other than Figures 1EF and 4AB, no two are the same! There should be a clear, consistent schematic used, with identical labeling of input sources, neuron types, etc. across all of these panels.

We changed all figures to make them more consistent and pointed out that we consider subparts of the circuit.

The flow of the Results section overall is clear until the “Calculation of the UPE in Layer 2/3 error neurons” and Figure 4, where I find that things become significantly more confusing. The mention of NMDA and calcium spikes comes out of the blue, and it’s not clear to me how this fits into the authors’ theory. Moreover: Why would this property of pyramidal cells cause the PV firing rate to increase as stated? The authors refer to one set of weights (from SSTs to UPE) needing to match two targets (weights from s to UPE and weights from mean representation to UPE); how can one set of weights match two targets? Why do the authors mention “out-of-distribution detection’ here when that property is not explored later in the paper? (see also below for other comments on Figure 4)

We agree that the introduction of NMDA and calcium spikes was too short and understand that it was confusing. We therefore modified and expanded the section. To answer the two specific questions: First, Why would this property of pyramidal cells cause the PV firing rate to increase as stated? This property of pyramidal cells does not cause the PV firing rate to increase. When for example in positive error neurons, the mean input increases, then the PVs receive higher stimulus input on average, which is not compensated by the inhibitory prediction (which is still at the old mean), such that the PV firing rate increases. Due to the nonlinear integration in PVs, the firing rate can increase a lot and inhibit the error neurons strongly. If the error neurons integrate the difference nonlinearly, they compensate for the increased inhibition by PVs. In Figure 5, we show that a circuit in which error neurons exhibit a dendritic nonlinearity matches an idealised circuit in which the PVs perfectly represent the variance. We modified the text to clarify this.

Second, how can one set of weights match two targets? In our model, one set of weights does not need to match two targets. We apologise that this was written in such a confusing way. In positive error neurons, the inhibitory weights from the SSTs need to match the excitatory weights from the stimulus, and in negative error neurons, the inhibitory weights from the SSTs need to match the excitatory weights from the prediction. The weights in positive and negative circuits do not need to be the same. So, on a particular error neuron, the inhibition needs to match the excitation to maintain EI balance. Given experimental evidence for EI balance and heterosynaptic plasticity, we think that this constraint is biologically achievable. The inhibitory and excitatory synapses that need to match are targeting the same postsynaptic neuron and could hence have access to their postsynaptic effect. We modified the text to be more clear. Finally, we omitted the mentioning of out-of-distribution detection, see our reply below.

Coming back to one of the points in the previous paragraph: How realistic is this exact matching of weights, as well as the weight matching that the theory requires in terms of the weights from the SSTs to the PVs and the weights from the stimuli to the PVs? This point should receive significant elaboration in the discussion, with biological evidence provided. I would not advocate for the authors’ uncertainty prediction theory, despite its elegant aspects, without some evidence that this weight matching occurs in the brain. Also, the authors point out on page 3 that unlike their theory, “...SSTs can also have divisive effects, and PVs can have subtractive effects, dependent on circuit and postsynaptic properties”. This should be revisited in the Discussion, and the authors should explain why these effects are not problematic for their theory. In a similar vein, this work assumes the existence of two different populations of SST neurons with distinct UPE (pyramidal) targets. The Discussion doesn’t say much about any evidence for this assumption, which should be more thoroughly discussed and justified.

These are very important points, we agree that the biological plausibility of the model’s predictions should be discussed and hence expanded the discussion with three new paragraphs:

To enable the comparison between predictions and sensory information via subtractive inhibition, we pointed out that the weights of those inputs on the postsynaptic neuron need to match. This essentially means that there needs to be a balance of excitatory and inhibitory inputs. Such an EI balance has been observed experimentally (Tan and Wehr, 2009). And it has previously been suggested that error responses are the result of breaking this EI balance (Hertäg und Sprekeler, 2020, Barry and Gerstner, 2024). Heterosynaptic plasticity is a possible mechanism to achieve EI balance (Field et al. 2020). For example, spike pairing in pre- and postsynaptic neurons induces long-term potentiation at co-activated excitatory and inhibitory synapses with the degree of inhibitory potentiation depending on the evoked excitation (D’amour and Froemke, 2015), which can normalise EI balance (Field et al. 2020).

In the model we propose, SSTs should be subtractive and PVs divisive. However, SSTs can also be divisive, and PVs subtractive dependent on circuit and postsynaptic properties (Seybold et al. 2015, Lee et al. 2012, Dorsett et al. 2021). This does not necessarily contradict our model, as circuits in which SSTs are divisive and PVs subtractive could implement a different function, as not all pyramidal cells are error neurons. Hence, our model suggests that error neurons which can calculate UPEs should have similar physiological properties to the layer 2/3 cells observed in the study by Wilson et al. 2012.

Our model further posits the existence of two distinct subtypes of SSTs in positive and negative error circuits. Indeed, there are many different subtypes of SSTs. SST is expressed by a large population of interneurons, which can be further subdivided. There is e.g. a type called SST44, which was shown to specifically respond when the animal corrects a movement (Green et al. 2023). Our proposal is hence aligned with the observation of functionally specialised subtypes of SSTs.

Finally, I think this is a paper that would have been clearer if the equations had been interspersed within the results. Within the given format, I think the authors should include many more references to the Methods section, with specific equation numbers, where they are relevant throughout the Results section. The lack of clarity is certainly made worse by the current state of the Methods section, where there is far too much repetition and poor ordering of material throughout.

We implemented the reviewer’s detailed and helpful suggestions on how to improve the ordering and other aspects of the methods section and now either intersperse the equations within the results or refer to the relevant equation number from the Methods section within the Results section.

Reviewer 3 (Public Review):

Summary: The authors proposed a normative principle for how the brain’s internal estimate of an observed sensory variable should be updated during each individual observation. In particular, they propose that the update size should be inversely proportional to the variance of the variable. They then proposed a microcircuit model of how such an update can be implemented, in particularly incorporating two types of interneurons and their subtractive and divisive inhibition onto pyramidal neurons. One type should represent the estimated mean while another represents the estimated variance. The authors used simulations to show that the model works as expected.

Strengths: The paper addresses two important issues: how uncertainty is represented and used in the brain, and the role of inhibitory neurons in neural computation. The proposed circuit and learning rules are simple enough to be plausible. They also work well for the designated purposes. The paper is also well-written and easy to follow.

Weaknesses: I have concerns with two aspects of this work.

(1) The optimality analysis leading to Eq (1) appears simplistic. The learning setting the authors describe (estimating the mean of a stationary Gaussian variable from a stream of observations) is a very basic problem in online learning/streaming algorithm literature. In this setting, the real “optimal” estimate is simply the arithmetic average of all samples seen so far. This can be implemented in an online manner with µˆt = µˆt−1 +(st −µˆt−1)/t. This is optimal in the sense that the estimator is always the maximum likelihood estimator given the samples seen up to time t. On the other hand, doing gradient descent only converges towards the MLE estimator after a large number of updates. Another critique is that while Eq (1) assumes an estimator of the mean (mˆu), it assumes that the variance is already known. However, in the actual model, the variance also needs to be estimated, and a more sophisticated analysis thus needs to take into account the uncertainty of the variance estimate and so on. Finally, the idea that the update should be inverse to the variance is connected to the well-established idea in neuroscience that more evidence should be integrated over when uncertainty is high. For example, in models of two-alternative forced choices it is known to be optimal to have a longer reaction time when the evidence is noisier.

We agree with the reviewer that the simple example we gave was not ideal, as it could have been solved much more elegantly without gradient descent. And the reviewer correctly pointed out that our solution was not even optimal. We now present a better example in Figure 7, where the mean of the Gaussian variable is not stationary. Indeed, we did not intend to assume that the Gaussian variable is stationary, as we had in mind that the environment can change and hence also the Gaussian variable. If the mean is constant over time, it is indeed optimal to use the arithmetic mean. However, if the mean changes after many samples, then the maximum likelihood estimator model would be very slow to adapt to the new mean, because t is large and each new stimulus only has a small impact on the estimate. If the mean changes, uncertainty modulation may be useful: if the variance was small before, and the mean changes, then the resulting big error will influence the change in the estimate much more, such that we can more quickly learn the new mean. A combination of the two mechanisms would probably be ideal. We use gradient descent here, because not all optimisation problems the brain needs to solve are that simple. The problem with converging only after a large number of updates is a general problem of the algorithm. Here, we propose how the brain could estimate uncertainty to achieve the uncertainty-modulation observed in inference and learning tasks observed in behavioural studies. To give a more complex example, we present in a new Figure 8 how a hierarchy of UPE circuits can be used for uncertainty-based integration of prior and sensory information, similar to Bayes-optimal integration.

Yes, indeed, there is well-known behavioural evidence, we would like to thank the reviewer for pointing out this connection to two-alternative forced choice tasks. We now cite this work. Our contribution is not on the already established computational or algorithmic level, but the proposal of a neural implementation of how uncertainty could modulate learning. The variance indeed needs to be estimated for optimal mean updating. That means that in the beginning, there will be non-optimal updating until the variance is learned. However, once the variance is learned, mean-updating can use the learned variance. There may be few variance contexts but many means to be learned, such that variance contexts can be reused. In any case, this is a problem on the algorithmic level, and not so much on the implementational level we are concerned with.

(2) While the incorporation of different inhibitory cell types into the model is appreciated, it appears to me that the computation performed by the circuit is not novel. Essentially the model implements a running average of the mean and a running average of the variance, and gates updates to the mean with the inverse variance estimate. I am not sure about how much new insight the proposed model adds to our understanding of cortical microcircuits.

We here suggest an implementation for how uncertainty could modulate learning via influencing prediction error com- putation. Our model can explain how humans could estimate uncertainty and weight prior versus sensory information accordingly. The focus of our work was not to design a better algorithm for mean and variance estimation, but rather to investigate how specialised prediction error circuits in the brain can implement these operations to provide new experimental hypotheses and predictions.

Reviewer 1 (Recommendations For The Authors):

Clarity and conciseness are a strength of this manuscript, but a more comprehensive explanation could improve the reader’s understanding in some instances. This includes the NMDA-based nonlinearity of pyramidal neuron activation - I am a little unclear exactly what problem this solves and how (alongside the significance of 5D and E).

We agree that the introduction of the NMDA-based nonlinearity was too short and understand that it was confusing. We therefore modified and expanded the section, where we introduce the dendritic nonlinearity of the error neurons.

Page 5: I think there is a ’positive’ and ’negative’ missing from the following sentence: ’the weights from the SSTs to the UPE neurons need to match the weights from the stimulus s to the UPE neuron and from the mean representation to the UPE neuron, respectively.’

Thanks for pointing that out! We changed the sentence to be more clear to the following: “To ensure a comparison between the stimulus and the prediction, the inhibition from the SSTs needs to match the excitation it is compared to in the UPE neurons: In the positive PE circuit, the weights from the SSTs representing the prediction to the UPE neurons need to match the weights from the stimulus s to the UPE neurons. In the negative PE circuit, the weights from SSTs representing the stimulus to the negative UPE neurons need to match the weights from the mean representation to the UPE neurons, respectively.”

Reviewer 2 (Recommendations For The Authors):

Related to the first point above: I don’t feel that the authors adequately explained what the “s” and “a” information (e.g., in Figures 2A, 3A) represent, where they are coming from, what neurons they impact and in what way (and I believe Fig. 3A is missing one “a” label). I think they should elaborate more fully on these key, foundational details for their theory. To me, the idea of starting from the PV, SST, and pyramidal circuit, and then suddenly introducing the extra R neuron in Figure 5, just adds confusion. If the R neuron is meant to be the source, in practice, of certain inputs to some of the other cell types, then I think that should be included in the circuit from the start. Perhaps a good idea would be to start with two schematics, one in the form of Figure 5A (but with additional labeling for PV, SST) and one like Figure 1EF (but with auditory inputs as well), with a clear indication that the latter is meant to represent a preliminary, reduced form of the former that will be used in some initial tests of the performance of the PV, SST, UPE part of the circuit. Related to the Methods, I also can give a list of some specific complaints (in latex):

(1) φ, φP V are used in equations (10), (11), so they should be defined there, not many equations later.

Thank you, we changed that.

(2) β, 1 − β appear without justification or explanation in (11). That is finally defined and derived several pages later.

Thank you, we now define it right at the beginning.

(3) Equations (10)-(12) should be immediately followed by information about plasticity, rather than deferring that.

That’s a great idea. We changed it. Now the synaptic dynamics are explained together with the firing rate dynamics.

(4) After the rate equations (10)-(12) and weight change equations (23)-(25) are presented, the same equations are simply repeated in the “Explanation of the synaptic dynamics” subsection.

We agree that this was suboptimal. We moved the explanation of the synaptic dynamics up and removed the repetition.

(5) In the circuit model (13)-(19), it’s not clear why rR shows up in the SST+ and PV− equations vs. rs in PV+ and SST−. Moreover, rs is not even defined! Also, I don’t see why wP V +,R shows up in the equation for rP V − .

We added more explanation to the Methods section as to why the neurons receive these inputs and renamed rs to s, which is defined. The “+” in wP V +,R was a typo. Thank you for spotting that.

(6) The authors should only number those equations that they will reference by number. Even more importantly, there are many numbers such as (20), (26), (32), (39) that are just floating there without referring to an equation at all.

Thank you for spotting that. We corrected this.

(7) The authors fail to specify what is ra in Figure 8. Moreover, it seems strange to me that wP V,a approaches σ rather than wP V,ara approaching σ, since φP V is a function of wP V,ara.

You are right, wP V,ara should approach σ, but since ra is either 1 or 0 to indicate the presence of absence of the cue, and only wP V,a is plastic and changing„ wP V,a approaches σ.

(8) I don’t understand the rationale for the authors to introduce equation. (30) when they already had plasticity equations earlier. What is the relation of (30), (31) to (24)?

It is the same equation. In 30 we introduce simpler symbols for a better overview of the equations. 31 is equal to 30, with rP V replaced by it’s steady state.

(9) η is omitted from (33) - it won’t affect the final result but should be there.

We fixed this.

I have many additional specific comments and suggestions, some related to errors that really should have been caught before manuscript submission. I will present these based on the order in which they arise in the manuscript.

(1) In the abstract, the mention of layer 2/3 comes out of nowhere. Why this layer specifically? Is this meant to be an abstract/general cortical circuit model or to relate to a specific brain area? (Also watch for several minor grammatical issues in the abstract and later.)

Thank you for pointing this out. We now mention that the observed error neurons can be found in layer 2/3 of diverse brain areas. It is meant to be a general cortical circuit model independent of brain area.

(2) In par. 2 of the introduction, I find sentences 3-4 to be confusing and vague. Please rewrite what is meant more directly and clearly.

We tried to improve those sentences.

(3) Results subtitle 1: “suggests” → “suggest”

Thank you.

(4) Be careful to use math font whenever variables, such as a and N, are referenced (e.g., use of a instead of a bottom pg. 2).

We agree and checked the entire manuscript.

(5) Ref. to Fig. 1B bottom pg. 2 should be Fig. 1CD. The panel order in the figure should then be changed to match how it is referenced.

We fixed it and matched the ordering of the text with the ordering of the figure.

(6) Fig. 2C and 3E captions mention std but this is not shown in the figures - should be added.

It is there, it is just very small.

(7) Please clarify the relation of Figure 2C to 2F, and Figure 3F to 3H.

We colour-coded the points in 2F that correspond to the bars in 2C. We did the same for 3F and 3H.

(8) Figures 3E,3F appear to be identical except for the y-axis label and inclusion of std in 3F. Either more explanation is needed of how these relate or one should be cut.

The difference is that 3E shows the activity of PVs based on only the sound cue in the absence of a whisker stimulus. And 3F shows the activity of PVs based on both the sound cue and whisker stimuli. We state this more clearly now.

(9) Bottom of pg. 4: clarify that a quadratic φP V is a model assumption, not derived from results in the figure.

We added that we assume this.

(10) When k is referenced in the caption of Figure 4, the reader has no idea what it is. More substantially, most panels of Figure 4 are not referenced in the paper. I don’t understand what point the authors are trying to make here with much of this figure. Indeed, since the claim is that the uncertainy prediction should be based on division by σ2, why aren’t the numerical values for UPE rates much larger, since σ gets so small? The authors also fail to give enough details about the simulations done to obtain these plots; presumably these are after some sort of (unspecified) convergence, and in response to some sort of (unspecified) stimulus? Coming back to k, I don’t understand why k > 2 is used in addition to k = 2. The text mentions – even italicizes – “out-of-distribution dectection’, but this is never mentioned elsewhere in the paper and seems to be outside the true scope of the work (and not demonstrated in Figure 4). Sticking with k = 2 would also allow authors to simply use (·)k below (10), rather than the awkward positive part function that they have used now.

We now introduce the equation for the error neurons in Eq. 3 within the text, such that k is introduced before the caption. It also explains why the numerical values do not become much larger. Divisive inhibition, unlike mathematical division, cannot lead to multiplication in neurons. To ensure this, we add 1 to the denominator.

We show the error neuron responses to stimuli deviating from the learned mean after learning the mean and variance. The deviation is indicated either on the x-axis or in the legend depending on the plot. We now more explicitly state that these plots are obtained after learning the mean and the variance.

We removed the mentioning of the “out-of-distribution detection” as a detailed treatment would indeed be outside of the scope.

(11) Page 5, please clarify what is meant by “weights from the sound...”. You have introduced mathematical notation - use it so that you can be precise.

We added the mathematical notation, thank you!

(12) Figure 5D: legend has 5 entries but the figure panel only plots 4 quantities.

The SST firing rate was below the R firing rate. We hence omitted the SST firing rate and its legend.

(13) Figure 5: I don’t understand what point is being made about NMDA spikes. The text for Figure 5 refers to NMDA spikes in Figure 4, but nothing was said about NMDA spikes in the text for Figure 4 nor shown in Figure 4 itself.

We were referring to the nonlinearity in the activation function of UPEs in Figure 4. We changed the text to clarify this point.

(14) Figure 6: It is too difficult to distinguish the black and purple curves even on a large monitor. Also, the authors fail to define what they mean by “MM” and also do not define the quantities Y+ and Y− that they show. Another confusing aspect is that the model has PV+ and PV− neurons, so why doesn’t the figure?

Thank you for the comment. We changed the colour for better visibility, replaced the Upsilons with UPE (we changed the notation at some point and forgot to change it in the figure), and defined MM, which is the mismatch stimulus that causes error activity. We did not distinguish between PV+ and PV− in the plot as their activity is the same on average. We plotted the activity of the PV+. We now mention that we show the activity of PV+ as the representative.

(15) Also Figure 6: The authors do not make it clear in the text whether these are simulation results or cartoons. If the latter, please replace this with actual simulation results.

They are actual simulation results. We clarified this in the text.

(16) This work assumes the existence of two different populations of SST neurons with distinct UPE (pyramidal) targets. The Discussion doesn’t say much about any evidence for this assumption, which should be more thoroughly discussed and justified.

We now discuss this in more detail in the discussion as mentioned in our response to the public review.

(17) Par. 2 of the discussion refers to “Bayesian” and “Bayes-optimal” several times. Nothing was said earlier in the paper about a Bayesian framework for these results and it’s not clear what the authors mean by referring to Bayes here. This paragraph needs editing so that it clearly relates to the material of the results section and its implications.

We added an additional results section (the last section with Figure 8) on integrating prior and sensory information based on their uncertainties, which is also the case for Bayes-optimal integration, and show that our model can reproduce the central tendency effect, which is a hallmark of Bayes-optimal behaviour.

Reviewer 3 (Recommendations For The Authors):

See public review. I think the gradient-descent type of update the authors do in Equation (1) could be more useful in a more complicated learning scenario where the MLE has no closed form and has to be computed with gradient-based algorithms.

We responded in detail to your points in our point-by-point response to the public review.

Author response:

Reviewer #1 (Public review):

This manuscript from Schwintek and coworkers describes a system in which gas flow across a small channel (10^-4-10^-3 m scale) enables the accumulation of reactants and convective flow. The authors go on to show that this can be used to perform PCR as a model of prebiotic replication.

Strengths:

The manuscript nicely extends the authors' prior work in thermophoresis and convection to gas flows. The demonstration of nucleic acid replication is an exciting one, and an enzyme-catalyzed proof-of-concept is a great first step towards a novel geochemical scenario for prebiotic replication reactions and other prebiotic chemistry.

The manuscript nicely combines theory and experiment, which generally agree well with one another, and it convincingly shows that accumulation can be achieved with gas flows and that it can also be utilized in the same system for what one hopes is a precursor to a model prebiotic reaction. This continues efforts from Braun and Mast over the last 10-15 years extending a phenomenon that was appreciated by physicists and perhaps underappreciated in prebiotic chemistry to increasingly chemically relevant systems and, here, a pilot experiment with a simple biochemical system as a prebiotic model.

I think this is exciting work and will be of broad interest to the prebiotic chemistry community.

Weaknesses:

The manuscript states: "The micro scale gas-water evaporation interface consisted of a 1.5 mm wide and 250 µm thick channel that carried an upward pure water flow of 4 nl/s ≈ 10 µm/s perpendicular to an air flow of about 250 ml/min ≈ 10 m/s." This was a bit confusing on first read because Figure 2 appears to show a larger channel - based on the scale bar, it appears to be about 2 mm across on the short axis and 5 mm across on the long axis. From reading the methods, one understands the thickness is associated with the Teflon, but the 1.5 mm dimension is still a bit confusing (and what is the dimension in the long axis?) It is a little hard to tell which portion (perhaps all?) of the image is the channel. This is because discontinuities are present on the left and right sides of the experimental panels (consistent with the image showing material beyond the channel), but not the simulated panels. Based on the authors' description of the apparatus (sapphire/CNC machined Teflon/sapphire) it sounds like the geometry is well-known to them. Clarifying what is going on here (and perhaps supplying the source images for the machined Teflon) would be helpful.

We understand. We will update the figures to better show dimensions of the experimental chamber. We will also add a more complete Figure in the supplementary information. Part of the complexity of the chamber however stems from the fact that the same chamber design has also been used to create defined temperature gradients which are not necessary and thus the chamber is much more complex than necessary.

The data shown in Figure 2d nicely shows nonrandom residuals (for experimental values vs. simulated) that are most pronounced at t~12 m and t~40-60m. It seems like this is (1) because some symmetry-breaking occurs that isn't accounted for by the model, and perhaps (2) because of the fact that these data are n=1. I think discussing what's going on with (1) would greatly improve the paper, and performing additional replicates to address (2) would be very informative and enhance the paper. Perhaps the negative and positive residuals would change sign in some, but not all, additional replicates?

To address this, we will show two more replicates of the experiment and include them in Figure 2.

We are seeing two effects when we compare fluorescence measurements of the experiments.

Firstly, degassing of water causes the formation of air-bubbles, which are then transported upwards to the interface, disrupting fluorescence measurements. This, however, mostly occurs in experiments with elevated temperatures for PCR reactions, such as displayed in Figure 4.

Secondly, due to the high surface tension of water, the interface is quite flexible. As the inflow and evaporation work to balance each other, the shape of the interface adjusts, leading to alterations in the circular flow fields below.

Thus the conditions, while overall being in steady state, show some fluctuations. The strong dependence on interface shape is also seen in the simulation. However, modeling a dynamic interface shape is not so easy to accomplish, so we had to stick to one geometry setting. Again here, the added movies of two more experiments should clarify this issue.

The authors will most likely be familiar with the work of Victor Ugaz and colleagues, in which they demonstrated Rayleigh-Bénard-driven PCR in convection cells (10.1126/science.298.5594.793, 10.1002/anie.200700306). Not including some discussion of this work is an unfortunate oversight, and addressing it would significantly improve the manuscript and provide some valuable context to readers. Something of particular interest would be their observation that wide circular cells gave chaotic temperature profiles relative to narrow ones and that these improved PCR amplification (10.1002/anie.201004217). I think contextualizing the results shown here in light of this paper would be helpful.

Thanks for pointing this out and reminding us. We apologize. We agree that the chaotic trajectories within Rayleigh-Bénard convection cells lead to temperature oscillations similar to the salt variations in our gas-flux system. Although the convection-driven PCR in Rayleigh-Bénard is not isothermal like our system, it provides a useful point of comparison and context for understanding environments that can support full replication cycles. We will add a section comparing approaches and giving some comparison into the history of convective PCR and how these relate to the new isothermal implementation.

Again, it appears n=1 is shown for Figure 4a-c - the source of the title claim of the paper - and showing some replicates and perhaps discussing them in the context of prior work would enhance the manuscript.

We appreciate the reviewer for bringing this to our attention. We will now include the two additional repeats for the data shown in Figure 4c, while the repeats of the PAGE measurements are already displayed in Supplementary Fig. IX.2. Initially, we chose not to show the repeats in Figure 4c due to the dynamic and variable nature of the system. These variations are primarily caused by differences at the water-air interface, attributed to the high surface tension of water. Additionally, the stochastic formation of air bubbles in the inflow—despite our best efforts to avoid them—led to fluctuations in the fluorescence measurements across experiments. These bubbles cause a significant drop in fluorescence in a region of interest (ROI) until the area is refilled with the sample.

Unlike our RNA-focused experiments, PCR requires high temperatures and degassing a PCR master mix effectively is challenging in this context. While we believe our chamber design is sufficiently gas-tight to prevent air from diffusing in, the high surface-to-volume ratio in microfluidics makes degassing highly effective, particularly at elevated temperatures. We anticipate that switching to RNA experiments at lower temperatures will mitigate this issue, which is also relevant in a prebiotic context.

The reviewer’s comments are valid and prompt us to fully display these aspects of the system. We will now include these repeats in Figure 4c to give readers a deeper understanding of the experiment's dynamics. Additionally, we will provide videos of all three repeats, allowing readers to better grasp the nature of the fluctuations in SYBR Green fluorescence depicted in Figure 4c.

I think some caution is warranted in interpreting the PCR results because a primer-dimer would be of essentially the same length as the product. It appears as though the experiment has worked as described, but it's very difficult to be certain of this given this limitation. Doing the PCR with a significantly longer amplicon would be ideal, or alternately discussing this possible limitation would be helpful to the readers in managing expectations.

This is a good point and should be discussed more in the manuscript. Our gel electrophoresis is capable of distinguishing between replicate and primer dimers. We know this since we were optimizing the primers and template sequences to minimize primer dimers, making it distinguishable from the desired 61mer product. That said, all of the experiments performed without a template strand added did not show any band in the vicinity of the product band after 4h of reaction, in contrast to the experiments with template, presenting a strong argument against the presence of primer dimers.

Reviewer #2 (Public review):

Schwintek et al. investigated whether a geological setting of a rock pore with water inflow on one end and gas passing over the opening of the pore on the other end could create a non-equilibrium system that sustains nucleic acid reactions under mild conditions. The evaporation of water as the gas passes over it concentrates the solutes at the boundary of evaporation, while the gas flux induces momentum transfer that creates currents in the water that push the concentrated molecules back into the bulk solution. This leads to the creation of steady-state regions of differential salt and macromolecule concentrations that can be used to manipulate nucleic acids. First, the authors showed that fluorescent bead behavior in this system closely matched their fluid dynamic simulations. With that validation in hand, the authors next showed that fluorescently labeled DNA behaved according to their theory as well. Using these insights, the authors performed a FRET experiment that clearly demonstrated the hybridization of two DNA strands as they passed through the high Mg++ concentration zone, and, conversely, the dissociation of the strands as they passed through the low Mg++ concentration zone. This isothermal hybridization and dissociation of DNA strands allowed the authors to perform an isothermal DNA amplification using a DNA polymerase enzyme. Crucially, the isothermal DNA amplification required the presence of the gas flux and could not be recapitulated using a system that was at equilibrium. These experiments advance our understanding of the geological settings that could support nucleic acid reactions that were key to the origin of life.

The presented data compellingly supports the conclusions made by the authors. To increase the relevance of the work for the origin of life field, the following experiments are suggested:

(1) While the central premise of this work is that RNA degradation presents a risk for strand separation strategies relying on elevated temperatures, all of the work is performed using DNA as the nucleic acid model. I understand the convenience of using DNA, especially in the latter replication experiment, but I think that at least the FRET experiments could be performed using RNA instead of DNA.

We understand the request only partially. The modification brought about by the two dye molecules in the FRET probe to be able to probe salt concentrations by melting is of course much larger than the change of the backbone from RNA to DNA. This was the reason why we rather used the much more stable DNA construct which is also manufactured at a lower cost and in much higher purity also with the modifications. But we think the melting temperature characteristics of RNA and DNA in this range is enough known that we can use DNA instead of RNA for probing the salt concentration in our flow cycling.

Only at extreme conditions of pH and salt, RNA degradation through transesterification, especially under alkaline conditions is at least several orders of magnitude faster than spontaneous degradative mechanisms acting upon DNA [Li, Y., & Breaker, R. R. (1999). Kinetics of RNA degradation by specific base catalysis of transesterification involving the 2 ‘-hydroxyl group. Journal of the American Chemical Society, 121(23), 5364-5372.]. The work presented in this article is however focussed on hybridization dynamics of nucleic acids. Here, RNA and DNA share similar properties regarding the formation of double strands and their respective melting temperatures. While RNA has been shown to form more stable duplex structures exhibiting higher melting temperatures compared to DNA [Dimitrov, R. A., & Zuker, M. (2004). Prediction of hybridization and melting for double-stranded nucleic acids. Biophysical Journal, 87(1), 215-226.], the general impact of changes in salt, temperature and pH [Mariani, A., Bonfio, C., Johnson, C. M., & Sutherland, J. D. (2018). pH-Driven RNA strand separation under prebiotically plausible conditions. Biochemistry, 57(45), 6382-6386.] on respective melting temperatures follows the same trend for both nucleic acid types. Also the diffusive properties of RNA and DNA are very similar [Baaske, P., Weinert, F. M., Duhr, S., Lemke, K. H., Russell, M. J., & Braun, D. (2007). Extreme accumulation of nucleotides in simulated hydrothermal pore systems. Proceedings of the National Academy of Sciences, 104(22), 9346-9351.].

Since this work is a proof of principle for the discussed environment being able to host nucleic acid replication, we aimed to avoid second order effects such as degradation by hydrolysis by using DNA as a proxy polymer. This enabled us to focus on the physical effects of the environment on local salt and nucleic acid concentration. The experiments performed with FRET are used to visualize local salt concentration changes and their impact on the melting temperature of dissolved nucleic acids.  While performing these experiments with RNA would without doubt cover a broader application within the field of origin of life, we aimed at a step-by-step / proof of principle approach, especially since the environmental phenomena studied here have not been previously investigated in the OOL context. Incorporating RNA-related complexity into this system should however be addressed in future studies. This will likely require modifications to the experimental boundary conditions, such as adjusting pH, temperature, and salt concentration, to account for the greater duplex stability of RNA. For instance, lowering the pH would reduce the RNA melting temperature [Ianeselli, A., Atienza, M., Kudella, P. W., Gerland, U., Mast, C. B., & Braun, D. (2022). Water cycles in a Hadean CO2 atmosphere drive the evolution of long DNA. Nature Physics, 18(5), 579-585.].

(2) Additionally, showing that RNA does not degrade under the conditions employed by the authors (I am particularly worried about the high Mg++ zones created by the flux) would further strengthen the already very strong and compelling work.

Based on literature values for hydrolysis rates of RNA [Li, Y., & Breaker, R. R. (1999). Kinetics of RNA degradation by specific base catalysis of transesterification involving the 2 ‘-hydroxyl group. Journal of the American Chemical Society, 121(23), 5364-5372.], we estimate RNA to have a halflife of multiple months under the deployed conditions in the FRET experiment (High concentration zones contain <1mM of Mg2+). Additionally, dsRNA is multiple orders of magnitude more stable than ssRNA with regards to degradation through hydrolysis [Zhang, K., Hodge, J., Chatterjee, A., Moon, T. S., & Parker, K. M. (2021). Duplex structure of double-stranded RNA provides stability against hydrolysis relative to single-stranded RNA. Environmental Science & Technology, 55(12), 8045-8053.], improving RNA stability especially in zones of high FRET signal. Furthermore, at the neutral pH deployed in this work, RNA does not readily degrade. In previous work from our lab [Salditt, A., Karr, L., Salibi, E., Le Vay, K., Braun, D., & Mutschler, H. (2023). Ribozyme-mediated RNA synthesis and replication in a model Hadean microenvironment. Nature Communications, 14(1), 1495.], we showed that the lifetime of RNA under conditions reaching 40mM Mg2+ at the air-water interface at 45°C was sufficient to support ribozymatically mediated ligation reactions in experiments lasting multiple hours.

With that in mind, gaining insight into the median Mg2+ concentration across multiple averaged nucleic acid trajectories in our system (see Fig. 3c&d) and numerically convoluting this with hydrolysis dynamics from literature would be highly valuable. We anticipate that longer residence times in trajectories distant from the interface will improve RNA stability compared to a system with uniformly high Mg2+ concentrations.

(3) Finally, I am curious whether the authors have considered designing a simulation or experiment that uses the imidazole- or 2′,3′-cyclic phosphate-activated ribonucleotides. For instance, a fully paired RNA duplex and a fluorescently-labeled primer could be incubated in the presence of activated ribonucleotides +/- flux and subsequently analyzed by gel electrophoresis to determine how much primer extension has occurred. The reason for this suggestion is that, due to the slow kinetics of chemical primer extension, the reannealing of the fully complementary strands as they pass through the high Mg++ zone, which is required for primer extension, may outcompete the primer extension reaction. In the case of the DNA polymerase, the enzymatic catalysis likely outcompetes the reannealing, but this may not recapitulate the uncatalyzed chemical reaction.

This is certainly on our to-do list. Our current focus is on templated ligation rather than templated polymerization and we are working hard to implement RNA-only enzyme-free ligation chain reaction, based on more optimized parameters for the templated ligation from 2’3’-cyclic phosphate activation that was just published [High-Fidelity RNA Copying via 2′,3′-Cyclic Phosphate Ligation, Adriana C. Serrão, Sreekar Wunnava, Avinash V. Dass, Lennard Ufer, Philipp Schwintek, Christof B. Mast, and Dieter Braun, JACS doi.org/10.1021/jacs.3c10813 (2024)]. But we first would try this at an air-water interface which was shown to work with RNA in a temperature gradient [Ribozyme-mediated RNA synthesis and replication in a model Hadean microenvironment, Annalena Salditt, Leonie Karr, Elia Salibi, Kristian Le Vay, Dieter Braun & Hannes Mutschler, Nature Communications doi.org/10.1038/s41467-023-37206-4 (2023)] before making the jump to the isothermal setting we describe here. So we can understand the question, but it was good practice also in the past to first get to know the setting with PCR, then jump to RNA.

Reviewer #2 (Recommendations for the authors):

(1) Could the authors comment on the likelihood of the geological environments where the water inflow velocity equals the evaporation velocity?

This is an important point to mention in the manuscript, thank you for pointing that out. To produce a defined experiment, we were pushing the water out with a syringe pump, but regulated in a way that the evaporation was matching our flow rate. We imagine that a real system will self-regulate the inflow of the water column on the one hand side by a more complex geometry of the gas flow, matching the evaporation with the reflow of water automatically. The interface would either recede or move closer to the gas flux, depending on whether the inflow exceeds or falls short of the evaporation rate. As the interface moves closer, evaporation speeds up, while moving away slows it down. This dynamic process stabilizes the system, with surface tension ultimately fixing the interface in place.

We have seen a bit of this dynamic already in the experiments, could however so far not yet find a good geometry within our 2-dimensional constant thickness geometry to make it work for a longer time. Very likely having a 3-dimensional reservoir of water with less frictional forces would be able to do this, but this would require a full redesign of a multi-thickness microfluidics. The more we think about it, the more we envisage to make the next implementation of the experiment with a real porous volcanic rock inside a humidity chamber that simulates a full 6h prebiotic day. But then we would lose the whole reproducibility of the experiment, but likely gain a way that recondensation of water by dew in a cold morning is refilling the water reservoirs in the rocks again. Sorry that I am regressing towards experiments in the future.

(2) Could the authors speculate on using gases other than ambient air to provide the flux and possibly even chemical energy? For example, using carbonyl sulfide or vaporized methyl isocyanide could drive amino acid and nucleotide activation, respectively, at the gas-water interface.

This is an interesting prospect for future work with this system. We thought also about introducing ammonia for pH control and possible reactions. We were amazed in the past that having CO2 instead of air had a profound impact on the replication and the strand separation [Water cycles in a Hadean CO2 atmosphere drive the evolution of long DNA, Alan Ianeselli, Miguel Atienza, Patrick Kudella, Ulrich Gerland, Christof Mast & Dieter Braun, Nature Physics doi.org/10.1038/s41567-022-01516-z (2022)]. So going more in this direction absolutely makes sense and as it acts mostly on the length-selectively accumulated molecules at the interface, only the selected molecules will be affected, which adds to the selection pressure of early evolutionary scenarios.

Of course, in the manuscript, we use ambient air as a proxy for any gas, focusing primarily on the energy introduced through momentum transfer and evaporation. We speculate that soluble gasses could establish chemical gradients, such as pH or redox potential, from the bulk solution to the interface, similar to the Mg2+ accumulation shown in Figure 3c. The nature of these gradients would depend on each gas's solubility and diffusivity. We have already observed such effects in thermal gradients [Keil, L. M., Möller, F. M., Kieß, M., Kudella, P. W., & Mast, C. B. (2017). Proton gradients and pH oscillations emerge from heat flow at the microscale. Nature communications, 8(1), 1897.] and finding similar behavior in an isothermal environment would be a significant discovery.

(3) Line 162: Instead of "risk," I suggest using "rate".

Oh well - thanks for pointing this out! Will be changed.

(4) Using FRET of a DNA duplex as an indicator of salt concentration is a decent proxy, but a more direct measurement of salt concentration would provide further merit to the explicit statement that it is the salt concentration that is changing in the system and not another hidden parameter.

Directly observing salt concentration using microscopy is a difficult task. While there are dyes that change their fluorescence depending on the local Na+ or Mg2+ concentration, they are not operating differentially, i.e. by making a ratio between two color channels. Only then we are not running into artifacts from the dye molecules being accumulated by the non-equilibrium settings. We were able to do this for pH in the past, but did not find comparable optical salt sensors. This is the reason we ended up with a FRET pair, with the advantage that we actually probe the strand separation that we are interested in anyhow. Using such a dye in future work would however without a doubt enhance the understanding of not only this system, but also our thermal gradient environments.

(5) Figure 3a: Could the authors add information on "Dried DNA" to the caption? I am assuming this is the DNA that dried off on the sides of the vessel but cannot be sure.

Thanks to the reviewer for pointing this out. This is correct and we will describe this better in the revised manuscript.

(6) Figure 4b and c: How reproducible is this data? Have the authors performed this reaction multiple independent times? If so, this data should be added to the manuscript.

The data from the gel electrophoresis was performed in triplicates and is shown in full in supplementary information. The data in c is hard to reproduce, as the interface is not static and thus ROI measurements are difficult to perform as an average of repeats. Including the data from the independent repeats will however give the reader insight into some of the experimental difficulties, such as air bubbles, which form from degassing as the liquid heats up, that travel upwards to the interface, disrupting the ongoing fluorescence measurements.

(7) Line 256: "shielding from harmful UV" statement only applies to RNA oligomers as UV light may actually be beneficial for earlier steps during ribonucleoside synthesis. I suggest rephrasing to "shielding nucleic acid oligomers from UV damage.".

Will be adjusted as mentioned.

(8) The final paragraph in the Results and Discussion section would flow better if placed in the Conclusion section.

This is a good point and we will merge results and discussion closer together.

(9) Line 262, "...of early Life" is slightly overstating the conclusions of the study. I suggest rephrasing to "...of nucleic acids that could have supported early life."

This is a fair comment. We thank the reviewer for his detailed analysis of the manuscript!

(10) In references, some of the journal names are in sentence case while others are in title case (see references 23 and 26 for example).

Thanks - this will be fixed.

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Reply to the reviewers

Response to Reviewer Comments:

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

*Glaucoma-associated optineurin mutations increase transmitophagy in vertebrate optic nerve.

Summary In Jeong et al., the authors perform live imaging of the X. laevis optic nerve to track neuronal mitochondrial movement and expulsion in an intact nervous system. The authors observe similar mitochondrial dynamics in vivo as previously described in other systems. They find that stationary mitochondria are more likely to be associated with OPTN, suggestive of mitochondria undergoing mitophagy. Forced expression of OPTN mutations results in a larger pool of stationary mitochondria that colocalize withLC3B, and OPTN. Finally, the authors argue that extra-axonal mitochondria are observed more frequently in OPTN mutants, suggesting that mutations in OPTN that are associated with disease can lead to an increase in the expulsion of mitochondria through exopher-like structures.

Major Findings and impact: • The authors establish that mitochondria dynamics can be tracked in the X. laevis optic nerve. • OPTN mutations increase the stationary pool of mitochondria and likely result in increased rates of mitophagy. • Exopher-like structures containing mitochondria and LC3 can be expelled from the optic nerve and increase in the presence of OPTN mutations. These structures were observed in a living system and have interesting implications in the context of disease.

Concerns: • The authors state in their results that the secreted blebs are exophers. While these initial observations are consistent with exophers, additional data are needed to strengthen this claim. For example: what are the sizes of secreted vesicles? Do all express LC3? How frequently do these occur? From where are they expelling? Alternatively, the discussion of exophers could be moved to the discussion.*

We agree that calling the axon shedding intermediates “exophers” was an overreach on our part. While we believe that in all probability time will demonstrate this to be the case, reviewers are correct in stating that putting our work in the context of exophers is best left to the discussion. We have removed all mention of exophers from the results and graphical abstract and now use the term only once in the discussion. We do provide detail as to the frequency of the structures, what fraction contain mitochondria, and morphological parameters of the contained mitochondria. And while all of these new data support them being exophers, the point remains that the use of the nomenclature “exopher” in the results section was inappropriate.

• Quantifications in sparse labeling experiments seem quite surprising and concerns related to these findings should be addressed. As the authors used LC3b expression to represent axonal volume, the authors should demonstrate that this is the case using an axonal fill or membrane marker in both the wt and E50K conditions. This is important as it is unclear whether LC3b expression is consistent between the wild type and the E50K conditions. Lower expression of LC3b in E50K could account for the large changes in axonal width that seem to be observed and could confound the measured amount of expelled mitochondria.*
• *

We agree that using EGFP-LC3b as a “cell fill” was problematic in a situation where the interventions likely perturb autophagy/mitophagy and therefore might have also perturbed LC3b. We do provide some axon width and LC3b-EGFP intensity data for a partial dataset that had been imaged side-by-side, showing that expression of LC3b is not different in the two conditions. We also provide independent measures of extra-axonal mitochondria based on a membrane-GFP reporter. While in principle there would be value to repeat the studies of Wt vs. E50K in the context of the membrane-GFP reporter, these experiments would involve new constructs and new breedings, and would likely take months to years to complete.

• • Could large amounts of exogenous mitochondria in explant experiments be from cells that died during the plantation?* The concern that some of the exogenous mitochondria signal might derive from degenerating axons is one that we worry much about, and not only in the transplantation experiments. In our sparse labeling experiments we do occasionally see axons undergoing Wallerian degeneration, but it is rare and does not appear to be more common in the expression of the mutated OPTN, at least not at the stage after transgene expression that the analyses were performed. We do provide new data that expression of E50K OPTN does not compromise vision at the time that experiments were carried out, ruling out that extra-axonal mitochondria are the result of large-scale degeneration. However, from other data we know that axon loss would likely need to be very extensive to manifest itself in functional vision loss in our behavioral assay, so milder axon loss contributing some noise to the measures cannot be excluded. But, the point raised is heard, and now we include a sentence in the discussion acknowledging that some of the signal outside of axons could have been due to degenerating axons, but still contend that our documentation of shedding intermediates support the view that many of the axonal mitochondria outside of axons were shed from otherwise intact axons.

Suggested experiments/quantifications: • In OPTN/MITO/LC3b trafficking experiments, does flux/number of events change? Representative kymograph in Figure 2D seems to show far more OPTN-positive mitochondria which is opposite of what is shown in Figure 2C.

Multiple reviewers rightfully point out that we did not carry out the flux experiments which would be necessary to make definitive statements regarding the amount of mitophagy. New experiments show that inhibiting lysosomal activity through chloroquine does increase the amount of astrocytic autophagosomes not yet acidified as expected, and that they contain axonal mitochondria signal, supporting the idea that astrocytes are involved in the degradation of axonal mitochondria. However, they did not show changes in the amount of stopped mitochondria, supporting the view that the co-localization of OPTN and mitochondria in axons is not conventional autophagy. This is a very important point that affects the interpretation of our results, and we thank reviewers for suggesting this experiment.

• Demonstrate that axonal width measured with LC3B is representative of axonal fill/membrane marker in wt and E50K. Axonal area appears to change, is this accurate? This appears to be the case for both figure 3 and figure 4.* Addressed above.

• Raw images in addition to the reconstruction would be beneficial.* Now include raw images beside the reconstruction at the first use of reconstructions.

• Further characterization of exopher-like structures.**

* Addressed above.

***Referees cross-commenting**

I agree with the concerns of the other reviewers, and perhaps was over-optimistic about a timeline for revision. However, I do think the work is worth the effort, and I hope to see a revised manuscript published somewhere, as these observations are novel

Reviewer #1 (Significance (Required)):

This work reports potentially novel biology, and thus will be of interest to the field. The strength of the study is that it is an initial description of this biology, rather than a complete analysis. The work raises many more questions than it answers, and much further work on this topic is required to support these initial findings, but the manuscript will likely be of interest to many. Revisions are required to improve the rigor and clarity of the work, but following these revisions we recommend publication to facilitate follow-up work.*

Fully agree that our study raises far more questions than it answers. Believe that the revisions made to address reviewer comments go a long way to improve rigor and clarity of the work. We hope that the reviewers agree and deem the changes sufficient.

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

Summary: This article studied transmitophagy in xenopus optic nerves in the context of overexpressing glaucoma-associated optineurin mutations. Using a series of labeling, imaging and transplantation techniques, the authors found that overexpressing mutated optineurins stops mitochondria movements and potentially induces transmitophagy, and that astrocytes are responsible for taking up the extra-axonal mitochondria. Below are my comments on this article.

Major comments: 1. Identifying extra-axonal mitochondria is key to this research. In Figure 3, the authors used EGFP-LC3B as a marker for RGC boundaries. However, it is unconvincing how perfect LC3B is as a cell membrane marker. Particularly in the case of OPTN E50K OE, it seems that the optic nerve is thinner than the WT condition, which makes the quantification of extra-axonal OPTN less convincing. The authors should detect extra-axonal mitochondria with an RGC membrane marker or cytosolic marker. In addition, in Figure 3, the extra-axonal mitochondria seem to localize mostly on the dorsal surface. Why is there such a polarity?*

As stated above, we acknowledge that the use of LC3b as both an autophagosome marker and a cell fill was somewhat problematic and now provide additional experiments ruling out that the LC3b expression or axon thickness in our sparse axon labeling experiments, or that E50K might affect the thickness of the optic nerve. In addition, we also provide additional new data using a bona fide membrane marker together a transgenic labeling or RGC mitochondria that also shows under the “baseline state” extensive mitochondria signal outside the axons on the surface of the optic nerve (New Fig. 6A and new Suppl Fig. 3D). All the new data are consistent with the previous data and support the view that using LC3b potentially could have been problematic, for the reasons reviewers state, but in practice it was not.

The reviewer observes that the E50K optic nerve appears thinner--this observation is not a consistent difference in optic nerves across the experimental groups. The images we show are always near the mean values for the quantitative results presented, and we rather not include prettier nerves that are not representative of the whole datasets.

As for why the extra-axonal mitochondria localize mostly to the dorsal surface, it remains undetermined. There are dorsoventral differences in the optic nerve established during development, as developmental Sonic hedgehog signaling emanating from the midline appears to affect dorsoventral aspects of the optic nerve differentially. Early axon loss in humans and some models of glaucoma do show a dorsal bias, and there may be optic nerve lymphatic structure reported in mice that also may be preferentially dorsal. However, it is not known whether any of these observations are connected, so we did not want to speculate beyond what the data say. We do now explicitly mention the dorsoventral difference in the discussion, and state why we think it may be worth further study.

• The experiment in Figure 5 is very important as it gives direct evidence of transmitophagy. However, one caveat is that the mitotracker injection is done after the transplantation. If in rare cases the dye is leaky after injection and is taken up by astrocytes directly, then the conclusion that mitochondria from RGCs are phagocytosed by astrocytes will be flawed. The authors should either use a transgene in the donor to label mitochondria or inject mitotracker into the donor before the transplantation and repeat the experiments. In addition, in Figure 5E, what is the large membranous structure inside the highlighted astrocyte? Is it associated with phagocytosis?*

We fully agree that MitoTracker is an imperfect tool, both for the reason stated here that the dye may get into the astrocytes directly (or may label astrocyte mitochondria after it is released from degrading RGC mitochondria), and, also as stated by reviewer 3, that it requires healthy mitochondria for labeling. For this reason, we have added new datasets that rely on RGC mitochondria labeling not by Mitotracker but through a genetic reporter. As to identity of the conspicuous structure shown inside the astrocytes, it remains an open question, and we are avidly pursuing what astrocytic organelles are involved through additional transgenic reporters and correlated-light-EM studies, but those are complicated experiments that are beyond the scope of the current manuscript.

• This research is entirely based on overexpression of OPTN. Since overexpressing WT OPTN does seem to affect mito trafficking (Figure S2G, and the description in the manuscript is often inconsistent with this result), it is unclear what the increased stalled mitochondria really mean when overexpressing mutated OPTN. Similarly, the authors examined extra-axonal mitochondria in Figures 3 and 4 all in overexpressing conditions, and made the connection that increased stalled mitochondria lead to transmitophagy. However, this conclusion will be better supported by using mutant animals rather than overexpression. The authors should consider using OPTN mutant xenopus if available or using CRISPR to introduce the specific mutations and repeat mitochondria trafficking and transmitophagy.*

• *

We thank this reviewer by pointing out an important detail that we failed to highlight, namely that transgenic overexpression of Wt OPTN (and/or Wt LC3B) does have a small but significant effect on mitochondria trafficking. Interestingly, it is affecting just the speed of retrogradely transported mitochondria, which based on the elegant work of Holzbaur and colleagues, include mitochondria destined for degradation. So, we now acknowledge more explicitly that, since our studies involve expression of OPTN and LC3b transgenes (fluorophore tagged human genes, no less), that some caution should be exercised in not overinterpreting the results. Nonetheless, since we show that expression of Wt OPTN behaves similarly to expression of a mitochondria reporter (Tom20-mCherry) in not affecting either stopped mitochondria or extra-axonal mitochondria, we believe that our results still stand. Nonetheless, we now make mention of the effect Wt OPTN on retrograde mitochondria movement. We have embarked on OPTN loss-of-function studies and have some founder animals carrying CRISPR-generated mutations; however, these experiments will take additional time, and based on the results in mammals may or may not show any measurable effects in our assays, not only because of possible redundancy by the other damaged mitochondria adaptors that we mention in the introduction, but also because the mutations that affect the shedding process (as well as cause glaucoma) are thought to be gain-of-function mutations. However, we decided not to dwell on these complexities in the discussion, as the discussion was previously quite extensive and now is even moreso with the added discussion on how our studies relate to those of exophers.

• On Page 12, the authors claim that even overexpressing WT OPTN causes extra-axonal mitochondria in the optic nerve. However, there is no control condition without OE to support this conclusion. It is thus unclear to what extent extra-axonal mitochondria occur at baseline and how many extra-axonal mitochondria can be induced by overexpression. The authors should include, in Figure 3 and 4, controls without overexpression.*

We acknowledge that our language was confusing and somewhat misleading on this point. With the caveat mentioned above that WT OPTN expression does perturb the system somewhat (by increasing the speed of mitochondria retrograde transport, perhaps by increasing the proportion of retrograde moving mitochondria tagged for degradation), we still contend that the state observed after WT OPTN expression is close to the “baseline” state. In support of that, in the new data included in response to the LC3b concern, we observe plentiful shedding events in the absence of any OPTN or LC3b transgenes. Indeed, what may be the most surprising finding of our studies is that in the absence of any significant perturbation of OPTN, there is already a large fraction of axonal mitochondria that are outside of axons and inside of astrocytes, which is consistent with what we previously observed in the optic nerve head of mice; however, the current studies provide much more rigorous quantification of the process and live imaging of intermediates, but also provide for an intervention that increases the process. While there are many more questions to answer, we do believe our studies contribute mechanistic insights.

• A technical question regarding kymographs: Based on Figure 2C, it looks that OPTN and LC3B labeling are pretty diffuse in axons and this makes sense since they may only be associated with damaged mitos. But this raises a question about how accurate the kymograph assay is. It may significantly underestimate the fraction of OPTN/LC3B that is stationary since they appeared diffusedon the kymograph. This may explain why the percentage of stationary OPTN/LC3B is so small when the authors OE WT OPTN in Figure 2E and 2E', compared to the percentage of moving mitochondria shown in Figure 1E.*

We fully agree that the kymograph studies likely underestimate the amounts of stationary mitochondria for the reasons stated. However, we interpret the discrepancy between Figure 1E and 2E and 2E’ differently. We believe that the value of stopped mitochondria in the sparse labeling experiments are actually more accurate, as the value of stopped mitochondria in the whole nerve experiments likely include mitochondria stopped within the axons, but also mitochondria recently shed either by those or nearby axons which are perceived to be in axons due to limitations of imaging resolution. In the discussion we now make very explicit that all the measures we provide need should be interpreted as estimates, as every experiment relies on assumptions and is subject to technical limitations.

Minor: 1. Figure 2E and 2E' do not agree with the text on page 7 and page 8. Not only F178A, but also H486R and D474N have no effect on OPTN trafficking. The authors should make their conclusions more accurate.

F178 was the only mutation that had no effect on either OPTN or LC3b in either F0 or F1 experiments. However, we agree that our language should have been clearer, and now we have made our description of the results (and conclusions) more accurate.

• Figure S2E-F: why does OE of mutated OPTN in F1s but not in F0s reduce trafficking speed compared to WT?*

We do not know the reason for this discrepancy. Though it does not wholly agree with the rest of the story, we felt it important to include all relevant data, not only that which perfectly fit our interpretation. One possible reason may be that the F1 data derives from a single integration event, which is the reason why we trust more the F0 data that derive from multiple integrations, in what are essentially outbred animals, which is the reason we present the F0 data as the primary results where possible.

* In movie 5, fusion of exopher with other structures is not clear and also the GFP signal does not disappear, which is in contrast to the statement in the text that the GFP signal is quenched in acidified environment. To confirm that LC3B leaves RGC axons in exophers, the authors should consider switching the fluorophores and examine LC3B localization during exopher formation.*

This too is a valid point, and we have amended our description of these results. While swapping fluorophores between OPTN and LC3b is a highly worthy experiment, for technical reasons it likely would take many months to carry out just because of how involved it is to make the relevant constructs (recombineering details provided in the methods section).

• In figure 6, to better show exopher formation and the pinching-off step, the authors should consider labeling the membrane and mitochondria instead of using the LC3B and OPTN marker.*

This arguably was the biggest weakness of our initial submission, and now provide new experiments using a bona fide membrane marker. We have not yet captured a pinching-off event with these better reporters, but that is not surprising given how rare they are, which we now quantify. Indeed, a membrane reporter and a mitochondria transgene in sparsely labeled axons are the ideal tool for figuring out the frequency of these structures and what fraction contain mitochondria, data which we now provide.

***Referees cross-commenting**

Generally agree with the criticisms voiced by the other reviewers; in aggregate the reviews indicate the manuscript needs more than just a quick fix.

Reviewer #2 (Significance (Required)):

Previous literature has already described the transmitophagy process in the optic nerve. The significance of this paper lies in the observation that overexpressing glaucoma-associated OPTN mutants can induce increased transmitophagy through astrocytes, which points to a potential role of OPTN in glaucoma. A highlight of this paper is the use of correlated light SBEM to directly show transmitophagy in astrocytes. However, the significance of this paper may be limited for the following reasons: 1. everything is based on overexpression of mutated OPTN, which makes it hard to translate the results to real disease conditions; 2. The consequence of increased transmitophagy on RGC survival or visual functions is unclear.

*

While we agree that much of the paper is based on OPTN overexpression, we did have experiments and now provide more that that were not based on OPTN overexpression. Some of these still involve expression of a different transgene (Tom20-mCherry) that might in principle perturb the system, though we show that expression of Tom20-mCherry does not affect mitochondria movement parameters as measured by Mitotracker. As to “the consequence of increased transmitophagy”, we do now provide data showing that there is no vision loss suggestive of axon loss or severe dysfunction at the time that the imaging studies were carried out. Whether longer term expression of these OPTN transgenes lead to axon degeneration and visual dysfunction are studies that are ongoing, but those studies involve extensive characterizations and controls that are beyond what could be included in this study.

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

Summary In this work, Jeong et al describe the effect of Optineurin (OPTN) mutations in the transcellular degradation of retinal ganglion cell (RGC) mitochondria by astrocytes at the Optic Nerve (ON), a process previously described this group and referred as "transmitophagy" (Davis et al 2014). Here, authors use Xenopus laevis animal model to image the optic nerve of animals carrying different OPTN mutations associated to disease or with compromised function and explore its effect in mitochondria dynamics at the RGC axons. They find that OPTN mutants lead to increased stationary mitochondria in the nerve and affect their co-localization with mitophagy-related markers, suggesting alterations in this pathway. Finally, they found that mitochondria co-localizing with OPTN can be found in the periphery of the ON under different conditions and this is particularly increased in glaucoma-associated E50K mutation. This extracellular mitochondria are transferred in vesicles to astrocytes, as they previously described in mice (Davis 2014), where they are presumably degraded. Major comments - OPTN levels at a given time point cannot be used as readout for mitophagy level/flux. Both OPTN and LC3b are degraded upon fusion with acidic compartment (i.e. lysosomes, PMID: 33783320, 33634751) and that is the reason why the field of autophagy /mitophagy blocks lysosomal activity to measure autophagy/mitophagy flux (PMID: 33634751). In this document, authors claim that there is low levels of mitophagy in RGC axons at baseline and increased levels of mitophagy in glaucoma associated perturbations just based on increased presence of OPTN+ mitochondria in this condition. This could be also interpreted as an accumulation of non-degraded defective mitochondria due to a mitophagy block in neurons carrying the glaucoma associated mutation, which is the opposite of what they propose. If authors want to evaluate mitophagy levels in this system, mitophagy/autophagy flux experiments should be performed.*

In response to reviewers, we do now include “lysosome inhibition” experiment, using chloroquine at doses modestly above those used in aquaculture as an anti-parasitic. After testing various chemical means to inhibit lysosome activity, it was the only one that did not adversely affect the animals. We know the chloroquine intervention works because we see the expected increase in autophagosomes using the standard LC3b-tandem reporter, and in those unacidified astrocytic autophagosomes we do indeed find axonal mitochondria signal. However, since the amount of mitochondria signal there is small relative to the total amount of axonal mitochondria in the astrocytes, we do not feel it would be appropriate to make mechanistic claims, for example claiming this to be related to LC3b associated phagocytosis; much more work would be needed to make that claim. However, we were surprised to find no alteration in either stopped mitochondria in axons or axonal mitochondria material within the astrocytes. There are technical reasons why this result might be difficult to interpret, but now having done it (as we should have before), we are even more careful in describing the process as transcellular degradation rather than transmitophagy. We elaborate further on this point in the next response.

- I find inappropriate the use of the term "transmitophagy". Although this term transmits very well the message that the authors try to strength, the term "mitophagy" refers to the specific elimination of mitochondria through autophagy (PMID: 21179058). There are many reasons why I think that "transmitophagy" is not adequate to describe this phenomena but I will just refer to these three: First, authors do not provide data showing that this mechanism is specific for mitochondria as they have never checked for the presence of other type of cargo in the vesicles produced by RGCs. If these are related to exophers as they suggest in the document, is very probable that they contain other type of cargo; Second, if the final destiny for those particles is the acidic compartment of astrocytes, this process may have nothing to do with autophagy/mitophagy and just share some molecular mediators with those pathways; Third, they should explore if other canonical mitophagy molecular mediators (i.e. Parkin/Pink) are regulating the production or the mitochondria recruitment to this extracellular particles.

We too struggle with our own “transmitophagy” term, for the very reasons stated. To address this concern, we now refer to the process as “transcellular degradation of mitochondria”, which is how we described it initially in mice as well. We do present new data that show that while the majority of axonal outpocketings contain mitochondria, not all do. This suggests that the others may contain other cargo, which supports the view that what we are dealing with in axons are indeed exophers. And yet, since what we measure is mitochondria, we think most appropriate to describe the process narrowly and not extrapolate to other types of exophers. We agree that what we originally discovered in mice and now live image and perturb in frog, may not be “autophagy” according to the strict definition of the term, but rather a process that uses some of the same molecular machinery, which given the evolutionary link between autophagy and phagocytosis that should be no surprise. Terminology can be tricky, and we thank the reviewer for calling us out on this point. We now use the term “transmitophagy” only once in the discussion section making the link between our work and the emerging field of exopher biology, and use that occasion to elaborate the point that the more descriptive term “transcellular degradation of mitochondria” is more appropriate in our case.

*- In several experiments, authors use Mitotracker instead of genetic tools to quantify the amount of mitochondria co-localizing with OPTN (Fig2, Fig3) or being transferred to astrocytes (Fig4). A problem here is that Mitotracker needs the mitochondria to be active at the time of injection in order to label them (PMID: 21807856) and it has a clear effect in mitochondria dynamics in their setting, as pointed by the authors. Since most mitochondria transferred to astrocytes would be presumably damaged and not able to import Mitotracker, I am concern about how this is affecting their quantifications and the conclusions.

*

We agree. The use of Mitotracker to label the RGC mitochondria can be problematic for the reasons stated by reviewers 1 and 3. Indeed, our opinion is that many of the studies out there that claim to demonstrate transfer of mitochondria between cells likely are just showing the transfer of the dye rather than the mitochondria. While the previous submission included a number of controls to address this concern, we now provide multiple new experiments that measure the transfer of mitochondria through a transgene rather than Mitotracker. The provided experiments use a new Tom20-mCherry transgene which is highly specific to mitochondria due to the use of an SOD2 UTR. We have similar data using RGC-expressed Mito-mCherry and Mito-EGFP-mCherry (using the commonly used Cox8 mitochondria matrix targeting sequence); we do not include such data because we find the provided data sufficiently compelling, and the story is already sufficiently long and complicated.

- Some conclusions are based on single images with no quantifications or statistics. This is the case for: 1) Page 6) "Most of the mCherry and Mitotracker objects colocalized with each other both in the merged images (Fig. S1C) and kymographs (Fig. S1D), indicating that the mitochondria-targeted transgene and Mitotracker similarly label the RGC axonal mitochondria".

That is a fair comment. After reanalyzing the original dataset used, it would be very difficult to quantify that statement, largely because the Tom20-mCherry expression was relatively weak in those particular animals. We are confident that we could generate a new dataset to provide support for this statement, but instead chose to just provide side-by-side movies of mitochondria labeled by Mitotracker or the Tom20-mCherry transgenes, which we believe is far more compelling than any quantification we could provide.

2) Page 8) "In the nerves labeled by Mitotracker, visual inspection of the raw images (Fig. 2C) and the derived kymographs (Fig. 2D) showed that OPTN and the Mitotracker labeled mitochondria often co-localized, particularly in the stopped populations, and more so in the animals expressing E50K OPTN, further suggesting that at least a fraction of the stopped LC3b, OPTN and mitochondria might represent mitophagy occurring in the axons".

While we have made a minor change to this sentence, we feel that it is appropriate given that it serves just as a justification to carry out the quantitative studies that follow. We would not have quantified the process had it not been obvious to the eye. However, we do not interpret the results as supporting that mitophagy occurs in axons, for the reasons explained above.

3) Page 14) "We also observed similar axonal dystrophies and exopher-like structures in E50K OPTN under similar imaging settings, but with 2-min intervals and additional Mitotracker labeling (Mov. 6), demonstrating that these structures not only contain OPTN but also mitochondria or mitochondria remnants". Image in video is not clear and there is not quantification for OPTN or OPTN+ mitochondria.*

*

We have removed Mov. 6.

*Minor comments

• In Figures showing the reconstruction of OPTN+ mitochondria outside nerve (Fig.3 and Fig.4), those seem to be present only in one lateral of the nerve. Is this process polarized in any way (i.e. faced to astrocytes) or is the result of a technical issue (i.e. difference in laser penetration for blue vs Yellow lasers)? I think it will be important to include this in the discussion.*

This was also pointed out by reviewer 1, and we agree that it is worth including in the discussion, which we now do. While we do not believe it to be a light penetration issue (based on fluorescence intensities and apparent spatial resolution), we also do not yet have an explanation. Having studied dorsoventral differences in the visual pathway both during my graduate and post-doctoral years, I am very interested in this asymmetry, and we have some theories that might explain it, mentioned above. The asymmetry is obvious and thus we think it would have been inappropriate not to show, but it also be inappropriate to be overly speculative.

- In Pag.13 authors claim "OPTN and mitochondria leave RGC axons in the form of exophers". After "exophers" were coined by the Driscoll lab in 2017, too few people has adopted this terminology and the molecular machinery involved in this process is still under research. It is clear that the particles described here share some similarities with exophers like size (in the range of microns) and cargo (mitochondria), but you have not demonstrated if they share the same origin or are part of the same phenomena. For that reason, I recommend to be more cautious with this statement and point these limitations in the discussion. Additionally, since Exophers are not a consensus or well defined particles, authors should include an introductory paragraph at the beginning of this section for readers to understand what they are talking about.

We wholly agree with all points. We now have moved all mention of exophers to just the discussion.

- Exophers described by Monica Driscoll and Andres Hidalgo laboratories are presented as "garbage bags" that help cells to stay fit through elimination of unwanted material. If the extracellular vesicles presented here are part of the same mechanism and potentially beneficial for the RGCs, why are they increased in OPTN mutants? Is it part of RGCs response to a proteomic stress generated by malfunctioning OPTN? I think that is critical to understand this to figure out the relevance of your findings.

• *

Our personal opinion is that the OPTN mutants most likely lead to stress focally in the axons, thus triggering exopher generation. We are carrying additional experiments to determine whether too much exopher generation or their insufficient degradation by astrocytes might be deleterious (by causing inflammation). However, those are big stories that would not stand on their own were we not able to first rigorously demonstrate that certain OPTN mutants increase exopher generation, which I believe our study demonstrates, albeit now without calling them exophers.

- Related to Fig.5G, authors say "The soma of the astrocytes were located at the optic nerve periphery but had processes that extended deep into the parenchyma". This is very interesting and opens the possibility that many mitochondria are directly transferred to astrocytes through that processes instead of the lateral of the nerve, meaning that your quantifications of "transmitophagy" may be underestimated.

* *We also agree that this. Our limited optical resolution, and limitations intrinsic to carrying out quantifications with Imaris software, are likely the main reasons for the discrepancy between the whole nerve and sparse-labelled-axon estimates of how much axonal material is outside of axons. Our view is that most of the transcellular degradation occurs within fine astrocyte processes, and that only in the case of failure to degrade material in these fine processes that significant amounts accumulate in the cell body (optic nerve periphery), and that in the cell body additional or different degradative pathways are utilized. Experiments using various transgenes and correlated EM as well as perturbation experiments are ongoing attempting to firmly establish what organelles are used in processes versus soma. However, we believe that such studies are well beyond the scope of this manuscript..

- Reference to Fig. S2G is missing. Now mentioned twice. Thank you.

- I cannot find in Fig.5 E-I legends what are the cells/structures labelled in Green and Red. Thank you.

***Referees cross-commenting**

In agreement with my colleagues, I think that a revision is needed to support some important points of the paper. The the work is interesting and I think it deserves a chance for revision. Having that said, I am not familiar with the breeding and experimental times when working with Xenopus but, considering the amount of work requested, it may require more than 3 months to have the work done.

*

*Reviewer #3 (Significance (Required)):

Until not very long ago, it was thought that mitochondria could not cross cell barriers. In recent years however, there has been an explosion in the number of works showing mitochondria transfer between different cell types in vivo. This may happen either as an organelle donation to improve energy production or as a quality control mechanism to get rid of damaged mitochondria, as it is the case in this work. The laboratory of Nicholas Marsh-Armstrong was pioneer in this field with a foundational work in 2014 where they show how RGC-derived mitochondria are captured and eliminated by astrocytes in mice (PMID: 24979790). This work was particularly relevant because it proposed for the first time that mitochondrial degradation can occur in RGC axons far from the cell soma, and surrogated in a different cell type, something that changed completely the view of how quality control is maintained in neurons and other cell types. In the present study, Jeong and collaborators explore how Glaucoma-associated Optineurin mutations affect this process, which is of potential interest for the broad cell biologist community due to its possible implications in other tissues and cell types (OPTN is broadly expressed), but especially for those researchers interested in neurobiology, quality control mechanisms and mitochondria biology. Since some OPTN mutations studied here cause disease, they are also relevant for the clinic. This work provides a thorough characterization of how relevant Optineurin mutations affect mitochondria dynamics in RGCs and their transference to astrocytes, as fairly claimed in the title. However, the mechanism by which they result in pathology is not either explored or carefully discussed, making this a descriptive work with no much conceptual insight. In addition, conclusions are often not unambiguously stated and the results part contains a lot of large sentences and unnecessary technical data that hinders reading and difficult the transmission of the key messages. Even if it stands as a descriptive work, the physiological and clinical relevance of these findings is not clear. There are some claims related with mitophagy activity that may require more sophisticated experiments (mitophagy flux with lysosomal inhibitors). Please see comments above. A critical point to understand the relevance of this work would be to demonstrate if alterations in transmitophagy are either causing or involved in the disease generated by these OPTN mutations in any way, or just a correlative phenomenon. To help authors contextualize my point of view, my field of expertise includes cell biology, imaging, quality control pathways, mitochondria biology and phagocytosis, among others. I am not familiar with Xenopus Laevis genetics or the limitations to work with this animal model.*

• *

We appreciate both the complements and the critiques. To a fault, we rather undersell than oversell. We are actively pursuing the possibility that dysregulation of this process is disease causing, and not just for glaucoma. However, those studies will not stand without a strong foundation, which we believe this study provides.

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Referee #3

Evidence, reproducibility and clarity

Summary

In this work, Jeong et al describe the effect of Optineurin (OPTN) mutations in the transcellular degradation of retinal ganglion cell (RGC) mitochondria by astrocytes at the Optic Nerve (ON), a process previously described this group and referred as "transmitophagy" (Davis et al 2014). Here, authors use Xenopus laevis animal model to image the optic nerve of animals carrying different OPTN mutations associated to disease or with compromised function and explore its effect in mitochondria dynamics at the RGC axons. They find that OPTN mutants lead to increased stationary mitochondria in the nerve and affect their co-localization with mitophagy-related markers, suggesting alterations in this pathway. Finally, they found that mitochondria co-localizing with OPTN can be found in the periphery of the ON under different conditions and this is particularly increased in glaucoma-associated E50K mutation. This extracellular mitochondria are transferred in vesicles to astrocytes, as they previously described in mice (Davis 2014), where they are presumably degraded.

Major comments

• OPTN levels at a given time point cannot be used as readout for mitophagy level/flux. Both OPTN and LC3b are degraded upon fusion with acidic compartment (i.e. lysosomes, PMID: 33783320, 33634751) and that is the reason why the field of autophagy /mitophagy blocks lysosomal activity to measure autophagy/mitophagy flux (PMID: 33634751). In this document, authors claim that there is low levels of mitophagy in RGC axons at baseline and increased levels of mitophagy in glaucoma associated perturbations just based on increased presence of OPTN+ mitochondria in this condition. This could be also interpreted as an accumulation of non-degraded defective mitochondria due to a mitophagy block in neurons carrying the glaucoma associated mutation, which is the opposite of what they propose. If authors want to evaluate mitophagy levels in this system, mitophagy/autophagy flux experiments should be performed.
• I find inappropriate the use of the term "transmitophagy". Although this term transmits very well the message that the authors try to strength, the term "mitophagy" refers to the specific elimination of mitochondria through autophagy (PMID: 21179058). There are many reasons why I think that "transmitophagy" is not adequate to describe this phenomena but I will just refer to these three: First, authors do not provide data showing that this mechanism is specific for mitochondria as they have never checked for the presence of other type of cargo in the vesicles produced by RGCs. If these are related to exophers as they suggest in the document, is very probable that they contain other type of cargo; Second, if the final destiny for those particles is the acidic compartment of astrocytes, this process may have nothing to do with autophagy/mitophagy and just share some molecular mediators with those pathways; Third, they should explore if other canonical mitophagy molecular mediators (i.e. Parkin/Pink) are regulating the production or the mitochondria recruitment to this extracellular particles.
• In several experiments, authors use Mitotracker instead of genetic tools to quantify the amount of mitochondria co-localizing with OPTN (Fig2, Fig3) or being transferred to astrocytes (Fig4). A problem here is that Mitotracker needs the mitochondria to be active at the time of injection in order to label them (PMID: 21807856) and it has a clear effect in mitochondria dynamics in their setting, as pointed by the authors. Since most mitochondria transferred to astrocytes would be presumably damaged and not able to import Mitotracker, I am concern about how this is affecting their quantifications and the conclusions.
• Some conclusions are based on single images with no quantifications or statistics. This is the case for:
  1. Page 6) "Most of the mCherry and Mitotracker objects colocalized with each other both in the merged images (Fig. S1C) and kymographs (Fig. S1D), indicating that the mitochondria-targeted transgene and Mitotracker similarly label the RGC axonal mitochondria".
  2. Page 8) "In the nerves labeled by Mitotracker, visual inspection of the raw images (Fig. 2C) and the derived kymographs (Fig. 2D) showed that OPTN and the Mitotracker labeled mitochondria often co-localized, particularly in the stopped populations, and more so in the animals expressing E50K OPTN, further suggesting that at least a fraction of the stopped LC3b, OPTN and mitochondria might represent mitophagy occurring in the axons".
  3. Page 14) "We also observed similar axonal dystrophies and exopher-like structures in E50K OPTN under similar imaging settings, but with 2-min intervals and additional Mitotracker labeling (Mov. 6), demonstrating that these structures not only contain OPTN but also mitochondria or mitochondria remnants". Image in video is not clear and there is not quantification for OPTN or OPTN+ mitochondria.

Minor comments

• In Figures showing the reconstruction of OPTN+ mitochondria outside nerve (Fig.3 and Fig.4), those seem to be present only in one lateral of the nerve. Is this process polarized in any way (i.e. faced to astrocytes) or is the result of a technical issue (i.e. difference in laser penetration for blue vs Yellow lasers)? I think it will be important to include this in the discussion.
• In Pag.13 authors claim "OPTN and mitochondria leave RGC axons in the form of exophers". After "exophers" were coined by the Driscoll lab in 2017, too few people has adopted this terminology and the molecular machinery involved in this process is still under research. It is clear that the particles described here share some similarities with exophers like size (in the range of microns) and cargo (mitochondria), but you have not demonstrated if they share the same origin or are part of the same phenomena. For that reason, I recommend to be more cautious with this statement and point these limitations in the discussion. Additionally, since Exophers are not a consensus or well defined particles, authors should include an introductory paragraph at the beginning of this section for readers to understand what they are talking about.
• Exophers described by Monica Driscoll and Andres Hidalgo laboratories are presented as "garbage bags" that help cells to stay fit through elimination of unwanted material. If the extracellular vesicles presented here are part of the same mechanism and potentially beneficial for the RGCs, why are they increased in OPTN mutants? Is it part of RGCs response to a proteomic stress generated by malfunctioning OPTN? I think that is critical to understand this to figure out the relevance of your findings.
• Related to Fig.5G, authors say "The soma of the astrocytes were located at the optic nerve periphery but had processes that extended deep into the parenchyma". This is very interesting and opens the possibility that many mitochondria are directly transferred to astrocytes through that processes instead of the lateral of the nerve, meaning that your quantifications of "transmitophagy" may be underestimated.
• Reference to Fig. S2G is missing.
• I cannot find in Fig.5 E-I legends what are the cells/structures labelled in Green and Red.

Referees cross-commenting

In agreement with my colleagues, I think that a revision is needed to support some important points of the paper. The the work is interesting and I think it deserves a chance for revision. Having that said, I am not familiar with the breeding and experimental times when working with Xenopus but, considering the amount of work requested, it may require more than 3 months to have the work done.

Significance

Until not very long ago, it was thought that mitochondria could not cross cell barriers. In recent years however, there has been an explosion in the number of works showing mitochondria transfer between different cell types in vivo. This may happen either as an organelle donation to improve energy production or as a quality control mechanism to get rid of damaged mitochondria, as it is the case in this work. The laboratory of Nicholas Marsh-Armstrong was pioneer in this field with a foundational work in 2014 where they show how RGC-derived mitochondria are captured and eliminated by astrocytes in mice (PMID: 24979790). This work was particularly relevant because it proposed for the first time that mitochondrial degradation can occur in RGC axons far from the cell soma, and surrogated in a different cell type, something that changed completely the view of how quality control is maintained in neurons and other cell types.

In the present study, Jeong and collaborators explore how Glaucoma-associated Optineurin mutations affect this process, which is of potential interest for the broad cell biologist community due to its possible implications in other tissues and cell types (OPTN is broadly expressed), but especially for those researchers interested in neurobiology, quality control mechanisms and mitochondria biology. Since some OPTN mutations studied here cause disease, they are also relevant for the clinic.

This work provides a thorough characterization of how relevant Optineurin mutations affect mitochondria dynamics in RGCs and their transference to astrocytes, as fairly claimed in the title. However, the mechanism by which they result in pathology is not either explored or carefully discussed, making this a descriptive work with no much conceptual insight. In addition, conclusions are often not unambiguously stated and the results part contains a lot of large sentences and unnecessary technical data that hinders reading and difficult the transmission of the key messages.

Even if it stands as a descriptive work, the physiological and clinical relevance of these findings is not clear. There are some claims related with mitophagy activity that may require more sophisticated experiments (mitophagy flux with lysosomal inhibitors). Please see comments above. A critical point to understand the relevance of this work would be to demonstrate if alterations in transmitophagy are either causing or involved in the disease generated by these OPTN mutations in any way, or just a correlative phenomenon. To help authors contextualize my point of view, my field of expertise includes cell biology, imaging, quality control pathways, mitochondria biology and phagocytosis, among others. I am not familiar with Xenopus Laevis genetics or the limitations to work with this animal model.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

SUMO proteins are processed and then conjugated to other proteins via a C-terminal di-glycine motif. In contrast, the N-terminus of some SUMO proteins (SUMO2/3) contains lysine residues that are important for the formation of SUMO chains. Using NMR studies, the N-terminus of SUMO was previously reported to be flexible (Bayer et al., 1998). The authors are investigating the role of the flexible (referred to as intrinsically disordered) N-terminus of several SUMO proteins. They report their findings and modeling data that this intrinsically disordered N-terminus of SUMO1 (and the C. elegans Smo1) regulates the interaction of SUMO with SUMO interacting motifs (SIMs).

Strengths:

Among the strongest experimental data suggesting that the N-terminus plays an inhibitory function are their observations that

(1) SUMO1∆N19 binds more efficiently to SIM-containing Usp25, Tdp2, and RanBp2,<br /> (2) SUMO1∆N19 shows improved sumoylation of Usp25,<br /> (3) changing negatively-charged residues, ED11,12KK in the SUMO1 N-terminus increased the interaction and sumoylation with/of USP25.

The paper is very well-organized, clearly written, and the experimental data are of high quality. There is good evidence that the N-terminus of SUMO1 plays a role in regulating its binding and conjugation to SIM-containing proteins. Therefore, the authors are presenting a new twist in the ever-evolving saga of SUMO, SIMs, and sumoylation.

Weaknesses:

Much has been learned about SUMO through structure-function analyses and this study is another excellent example. I would like to suggest that the authors take some extra time to place their findings into the context of previous SUMO structure-function analyses. Furthermore, it would be fitting to place their finding of a potential role of N-terminally truncated Smo1 into the context of the many prior findings that have been made with regard to the C. elegans SUMO field. Finally, regarding their data modeling/simulation, there are questions regarding the data comparisons and whether manipulations of the N-terminus also have an effect on the 70/80 region of the core.

We thank the reviewer for insightful and constructive comments to improve our manuscript. We have now placed our findings in the context of previous structure-function analyses at several occasions, details of which can be found in our replies to the detailed comments.

We are also placing the C. elegans data into context of previously published findings on the various functions of SMO-1 in controlling development and maintaining genomic stability (lines 510ff). Finally, we addressed all questions and suggestions regarding comparison of MD simulation and NMR data, and addressed the question whether mutations in the N-terminus affected the 70/80 region. We have now clarified in the manuscript that the sum of MD and NMR data does not allow a clear-cut conclusion on the 70/80 interactions. 

Reviewer #2 (Public Review):

Summary:

This very interesting study originated from a serendipitous observation that the deletion of the disordered N-terminal tail of human SUMO1 enhances its binding to its interaction partners. This suggested that the N terminus of SUMO1 might be an intrinsic competitive inhibitor of SUMO-interacting motif (SIM) binding to SUMO1. Subsequent experiments support this mechanism, showing that in humans it is specific to SUMO1 and does not extend to SUMO2 or SUMO3 (except, perhaps, when the N terminus of SUMO2 becomes phosphorylated, as the authors intriguingly suggest - and partially demonstrate). The auto-inhibition of SUMO1 via its N-terminal tail apparently explains the lower binding of SUMO1 compared to SUMO2 to some SIMs and lower SIM-dependent SUMOylation of some substrates with SUMO1 compared to SUMO2, thus adding an important element to the puzzle of SUMO paralogue preference. In line with this explanation, N-terminally truncated SUMO1 was equally efficient to SUMO2 in the studied cases. The inhibitory role of SUMO1's N terminus appears conserved in other species including S. cerevisiae and C. elegans, both of which contain only one SUMO. The study also elucidates the molecular mechanism by which the disordered N-terminal region of SUMO1 can exert this auto-inhibitory effect. This appears to depend on the transient, very highly dynamic physical interaction between the N terminus and the surroundings of the SIM-binding groove based mostly on electrostatic interactions between acidic residues in the N terminus and basic residues around the groove.

Strengths:

A key strength of this study is the interplay of different techniques, including biochemical experiments, NMR, molecular dynamics simulations, and, at the end, in vivo experiments. The experiments performed with these different techniques inform each other in a productive way and strengthen each others' conclusions. A further strength is the detailed and clear text, which patiently introduces, describes, and discusses the study. Finally, in terms of the message, the study has a clear, mechanistic message of fundamental importance for various aspects of the SUMO field, and also more generally for protein biochemists interested in the functional importance of intrinsically disordered regions.

Weaknesses:

Some of the authors' conclusions are similar to those from a recent study by Lussier-Price et al. (NAR, 2022), the two studies likely representing independent inquiries into a similar topic. I don't see it as a weakness by itself (on the contrary), but it seems like a lost opportunity not to discuss at more length the congruence between these two studies in the discussion (Lussier-Price is only very briefly cited). Another point that can be raised concerns the wording of conclusions from molecular dynamics. The use of molecular dynamics simulations in this study has been rigorous and fruitful - indeed, it can be a model for such studies. Nonetheless, parameters derived from molecular dynamics simulations, including kon and koff values, could be more clearly described as coming from simulations and not experiments. Lastly, some of the conclusions - such as enhanced binding to SIM-containing proteins upon N-terminal deletion - could be additionally addressed with a biophysical technique (e.g. ITC) that is more quantitative than gel-based pull-down assays - but I don't think it is a must.

Thank you very much for pointing towards the study of Lussier-Price. We now point out congruent findings in more detail in the discussion.

We also thank the reviewer for the advice to present and discuss the MD findings more clearly, and more explicitly specify which parameters were obtained from MD. We have made changes throughout the Results and Discussion sections.

We agree that it would be a nice addition to use ITC measurements as a more quantitative method to assess differences in binding affinities upon deletion of the SUMO N-terminus. We had tried to measure affinities between SUMO and SIM-containing binding partners by ITC but in our hand, this failed. In the study of Lussier-Price et al., the authors were able to measure differences in SIM binding upon deleting the N-terminus but only when they used phosphorylated SIM peptides. Follow-up studies, e.g., on the effect of SUMO’s N-terminal modifications should certainly include more quantitative measurement such as ITCs, however these studies will have to be picked up by others. The main PI Frauke Melchior and most contributing authors moved on to new challenges.

Reviewing Editor (Recommendations For The Authors):

Both reviewers agreed that your manuscript presents novel results and the key findings including the self-inhibitory role of the N-terminal tail of SUMO proteins in their interaction with SIM are overall well supported by the data. The reviewers also provided constructive suggestions. They pointed out that some simulation results are not clear, which could be strengthened by control analysis and by toning down the related descriptions. In addition, Reviewer 2 suggested that the conclusions from the current biochemical and simulation studies could be further reinforced by more quantitative binding measurements. We hope that these points can be addressed in the revision.

We thank both reviewers for their insightful and constructive comments and the appreciative tone. In our replies above and below we address most of the raised concerns.

We strongly recommend the change of the current title. eLife advises that the authors avoid unfamiliar abbreviations or acronyms, or spell out in full or provide a brief explanation for any acronyms in the title.

We changed the title to “The intrinsically disordered N-terminus of SUMO1 is an intramolecular inhibitor of SUMO1 interactions” to avoid acronyms in the title.

Reviewer #1 (Recommendations For The Authors):

Major:

Lines 190-262: The authors use NMR experiments and all-atom molecular dynamics (MD) simulations. They state that this approach reveals a highly dynamic interaction of the SUMO1 N-terminus with the core and that the SIM binding groove and the 70/80 region are temporarily occupied by the SUMO1 N-terminus (Fig. 3C). After comparing SUMO1, Smt3, SUMO2, and Smo1 by this approach they state that the most striking differences exist for the interaction with the SIM-binding groove, while interactions with the 70/80 region are rather comparable.

The authors then compare the average binding time data of Figure 3C, D, E, F in Figure 3G.

It is not clear which data points are included in the bar graphs of Figure 3G and how the individual data points (there are maybe 8 shown in each bar) correspond to the data shown in 3C, D, E, and F or if they are iterations (n?) of the modeled data. This should be clarified. Also, for comparison, the authors should also graph the average data of the 70/80 region.

We clarified the data shown in Figure 3G as well as 3C-F, and how It relates to each other. Indeed, Figure 3G shows 8 data points for 8 trajectories, and their average. Figure 3C-F are based on the same 8 trajectories, in this case broken down per residue of the protein. The average data of the 70/80 region does not show any significant differences across the proteins, as already pretty well visible from panels 3C-F.

Line 322: More concerning, in Figure 5, the authors model how a ED11,12KK mutations disrupt the interaction between the N-terminus and the SIM-binding groove and state that this mutation leaves interactions with the 70/80 region largely untouched. Again, it is not clear which data points are included in the bar graph 5D and 5G and how many iterations. Furthermore, data of 5B, C (SUMO1) and 5 E, F (smo1) do show clear differences between the WT and mutants affecting both the SIM binding groove and the 70/80 region. The double mutation clearly seems to affect the 70/80 region when comparing 5B, C (SUMO1) and 5 E, F (smo1), but this result is not mentioned. Indeed, the authors state that the double mutants leave the interactions with the 70/80 region largely untouched, but this is not borne out by the data presented.

We improved the clarity of the legend of Figure 5 as suggested. We also thank the reviewer for the comment on the changes in the 70/80 region, to which we point the reader explicitly now in the corresponding Results section. We, however, refrain from drawing conclusions from the MD in this case, as this change is not supported by the NMR measurements (Fig 5a). Charge-charge interactions in the charge-rich double mutants might be overstabilized in the MD simulations, a problem known for the canonical force fields used here, albeit tailoring it for IDPs. We now cite a corresponding reference. Another potential explanation for that the CMPs do not take this change up upon mutation could be a pronounced fuzziness in this region, which however, in turn, is not apparent from the simulations. We would therefore not overinterpret these differences in the 70/80 region. Our key conclusion is the loss of interactions with the SIM-binding groove – and thus of cis-inhibition – by mutations, which is supported by both, MD and NMR.  

341: In their N-termini substitution experiments, the authors show that the SUMO1 core that carries the SUMO2 N-terminus (S2N-S1C) binds USP25 more efficiently than wt SUMO1. However, the SUMO1 core that carries the SUMO2 N-terminus is also reduced in its interaction with Usp25. This is concerning as the SUMO2 N-terminus was not predicted to interfere with SIM binding.

We were excited to see that the inhibitory potential could be partially transplanted by swapping the N-termini of SUMO1 and SUMO2 demonstrating that some important determinants are contained within the N-terminal tail of SUMO proteins. However, the observed effects were partial indicating that also other determinants contribute and that we do not yet understand all aspects. Obviously, the SUMO1 and SUMO2 cores are similar (also in the area comprising the SIM binding groove) but not identical, and as the inhibition arises from dynamic interactions of the N-terminus with the SIM binding area, differences in the SUMO cores and in residues flanking SUMO’s N-terminus are likely to influence the inhibitory potential as well.

Blue bars in 3G, 5D, and 6A look surprisingly similar down to the individual data points - does that mean that the same SUMO1 WT data was recycled for these different experiments? This is concerning to me.

The data displayed in the figures listed above are derived from in silico simulations and indeed display the same data set for the case of SUMO1 WT repeatedly, as we also state in the figure legends (we had done so for 5D “(identical to Fig. 3C)”, and now added the same comment to 6A, thanks for pointing this out). We show the SUMO1 WT data again to facilitate comparing the different SUMO variants in MD simulations.

Line 352 and 496: The authors used phosphomimetic mutants to assess the effect of SUMO2 N-term phosphorylation on interaction with Usp25. The data suggest a mild phenotype (6G) which is borne out by the quantization in 6H. In contrast, the effect of an array of modifications for SUMO1 (Figures 6A - C) was solely analyzed by MD simulation. If possible, this data should be confirmed, at least by using a phosphomimetic at the Ser9 position of SUMO1. Alternatively, a caveat explaining the need to confirm these predictions by actual experiments should be added to the text.

Already now we state in “Limitations of the study” that “While our MD simulations and in vitro studies with selected mutants point in this direction, we have not been able to generate quantitatively acetylated and/or phosphorylated SUMO variants to test this hypothesis.”

We agree that the hypothesis needs experimental validation. Phosphomimetic amino acids can be a useful tool in some cases but fail to mimic a phosphor group in other cases. In the past we had tested whether replacing Ser9 by a potentially phospho-mimicking amino acid (Glu) would further diminish binding of SIM-containing proteins compared to already strongly reduced binding to wt SUMO1 but the effect was too mild to yield a significant difference, at least in our assay. Whether this is due to a lack of Glu in mimicking phosphorylation of Ser9, due to limited sensitivity of our pulldown assay combined with the challenge to detect inhibition compared to an already inhibited state, or a failure in our hypothesis we were not able to clarify so far. We therefore now also added a sentence to the paragraph introducing phosphoSer9 MD simulations (now line 367) stating that this hypothesis needs to be tested experimentally.

Minor:

Line 110: the authors should include references for their summary statement that "A defining feature of SUMO proteins is the intrinsically disordered N-terminus, whose function is only partly understood." Also cite in line 119.

Thank you, we now included some references.

Line 75: Please indicate early on that the N-terminus of some SUMO proteins contains lysines for the formation of SUMO chains. Please list them.

We now list, which of the SUMO proteins used in this study contain lysine residues in their N-termini.

Line 113: Please cite studies that elucidated the sumoylation of lysines in the N-terminus of SUMO2/3 proteins.

Thank you, we now included some references.

Line 153: The authors should include additional references on Smt3 structure function analyses to provide better context. One important detail, for example, is the important finding that Yeast SUMO (Smt3) deletion can be complemented by hsSUMO1 but not hsSUMO2 and hsSUMO3. Additionally, in yeast the entire Smt3 N-terminus can be deleted without detectable effects on growth, underscoring the enigmatic role of the N-terminus (Newman et al., 2017). Caveat also applies to line 266.

Thank you, we now included some additional information and references around line 153 and below.

164: The hypothesis that the SUMO1 N-terminus interferes with SIM binding groove ignores the previous observation that deletion of the SUMO2 N-terminus does not have an effect on binding (in vitro). While this is addressed later, the authors should clarify this e.g. by stating "a unique feature of the SUMO1 N-terminus".
>

We now explicitly mention that this feature appears to be unique to SUMO1.

374 and 499: The authors should discuss the caveat that the deletion of the N-terminus of Smt3 does not have a phenotype in yeast in vivo (Newman et al., 2017).

We now discuss that Smt3’s N-terminus can be deleted without detectable phenotype, both in the results as well as in “Limitations of the study”.

Line 367: I feel this is overstated and I do not see any evidence that post translation modifications of the SUMO core plays a role. Therefore, I suggest: Our data and modeling are consistent with an interpretation that the N-termini of human and C. elegans SUMO1 proteins are inhibitory and that other SUMO N-termini may acquire such a function upon posttranslational modification of the N-terminus.

We agree that this is pure speculation and therefore restrict our hypothesis to modifications of the N-terminus.

Line 374 ff: Since Smo-∆N12 increases sumoylation (Fig. 2I), it is likely that the in vivo defect is due to over-sumoylation in C. elegans. The authors should discuss this possibility and quote appropriate literature e.g.: Rytinki et al., Overexpression of SUMO perturbs the growth and development of Caenorhabditis elegans. Cell Mol Life Sci. 2011 Oct;68(19):3219-32. PMID: 21253676.

In our study, we employ in vitro SUMOylation as a means to assess the SIM binding capability in an in-solution assay. For this, we use USP25 as a specific substrate known to depend on a SIM for its SUMOylation. We cannot exclude that some specific substrates depending on this same mechanism for their modification may be upregulated in modification also in the Smo-1∆N12 worms. In vivo however, the majority of SUMO substrates is not subject to SIM-dependent SUMOylation. We now added a control experiment showing that we neither observe significantly increased SUMO levels nor upregulated steady state levels of SUMOylation in these worms (Supplemental figure 8).

The phenotypes shown in the paper by Rytinki et al. do not resemble the smo-1∆N12 mutants. Rather, we observed a specific defect in the meiotic germ cells at the pachytene stage causing increased apoptosis Moreover, we show by western blot analysis that there is no global over-sumoylation occurring in smo-1∆N12 mutants (Fig. s8). Together, our data point to a germline-specific function of the SMO-1 N-terminus in maintaining genome stability (lines 510ff).

Reviewer #2 (Recommendations For The Authors):

Page2 - "Small Ubiquitin-related modifiers of the SUMO family regulate thousands of proteins in eukaryotic cells" - The authors could consider a more precise statement, e.g. that SUMO modifiers have been detected on thousands of proteins and their regulatory effect on many proteins have been demonstrated.

To be a bit more precise, the sentence now reads: “Ubiquitin-related proteins of the SUMO family are reversibly attached to thousands of proteins”. The summary has a word limit, hence we did not expand further at this place.

Page 4 - "Both events require SUMO-binding motifs (reviewed, e.g. in 7 ." - The end bracket is missing. Also, isn't it too strong a statement that paralogue specificity always requires a SIM? I don't know all the literature sufficiently well, but the authors could double-check if it is correct to say that paralogue-specific SUMOylation always depends on a SIM.

Thank you, we added the missing bracket. We agree that it would not be correct to say that paralogue-specificity always depends on a SIM. One alternative example is Dpp9, which shows a clear preference for SUMO1 without owning a SIM. Instead, Dpp9 harbors an alternative SUMO-binding motif, the E67-interacting loop, with a strong paralogue-preference (Pilla et al., 2012). We never intended to imply that a SIM is required for paralogue preference and we also rather generically wrote “SUMO binding motif” instead of “SIM”. However, in the subsequent paragraph about SUMO binding motifs we only go into details of SIMs as one of three classes of SUMO binding motifs not even mentioning the alternative classes. To make this more obvious, we now list the two other known classes of SUMO binding motifs hoping that it will shed the correct light onto our previous statement about paralogue preference.

Page 4 - In the nice discussion of different types of SIMs, the authors could consider mentioning also the special case of TDP2, which is used later by them as a model binding protein. This could provide an occasion to explain what the unusual "split SIM", mentioned on page 6, but not discussed, is, and what its relation to a normal SIM is. Also, it can perhaps be mentioned that TDP2 contacts SUMO2 not only through the two hydrophobic elements contiguous in space that mimic a SIM but also through a slightly larger interface around these regions on the surface of a folded domain.

Thank you for pointing this out. In the introduction, we extended our section on SUMO binding and now also included TDP2’s “split SIM”.

Page 11-12 - In the section "Interaction between SUMO's disordered N-termini and the SIM binding groove is highly dynamic" (and corresponding figures), it should be stated that the discussed kinetic parameters are derived from molecular dynamics simulations and not experimental measurements. It was not very clear to me. This also applies to this sentence on page 17: "First, we observed a very fast (ns) rate of the binding/unbinding process", which in its current form suggests direct observation rather than simulation.

We thank the reviewer for pointing this out, and in fact, Rev #1 made the same comment. We specified now clearly that the rates were calculated from MD simulations, in the Results and Discussion sections (on page 11-12 and 18 (previously 17)).

Page 16 - The authors could briefly mention that this relatively long disordered N-terminal tail is a specific feature of SUMO proteins that distinguishes them from ubiquitin. I guess it is obvious to people from the SUMO field, but I don't think it is explicitly stated anywhere in the text and it could be interesting for readers who are less familiar with SUMO/ubiquitin differences.

Thank you, we added a short half-sentence pointing out this difference.

Page 17 - "The N-terminal region remains fully disordered in the bound state and is thus a classic example of intrinsic disorder irrespective of the binding state." - it could be added to this sentence that this is suggested by molecular dynamics simulations and not directly observed.

We added the information that this finding is based on the MD simulations.

Page 18 - "(e.g., 41,53 or flanking the SIM binding groove24,42" - the end bracket is missing.

Thanks, we added it.

Page 19 - "Our analysis in C. elegans (Fig. 7) suggests that this N-terminal function is particularly important in DNA damage response, a pathway that is strongly dependent on the SUMO system." - this brief description of the in vivo data seems to overgeneralise them a little bit. Perhaps one can describe what was observed with slightly more nuance.

See changes on p.19, lines 510ff.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

Summary:

This manuscript by Xu, Hörner, Schüle and colleagues is an RNA-seq study focusing characterization of axonal transcriptomes from human iPSC-derived cortical neurons. The authors have differentiated iPSC into neurons, cultured them in microfluidic devices and isolated axonal RNA, comparing this to corresponding cell soma transcriptomes. Second, axonal transcriptomes are compared between wild type and Kif1c knockout axons to determine Kif1c-dependently localized transcripts. Characterization of the latter allows the authors to suggest differentially expressed transcripts in Kif1c-KO axons can be mRNAs relevant for motor neuron degeneration owing to Kif1c mutations in hereditary spastic paraplegias.

Major comments: Overall, his manuscript reads like work in (early) progress. This manuscript provides an interesting dataset, but needs substantial additional experimental and/or bioinformatic work to merit publication. The technical complexity of steps that have led to obtaining axonal transcriptomes can be appreciated, the soundness of generating these data is beyond doubt. However, the study stops at the point of generating axonal transcriptomes from wild type and Kif1c axons. No follow-up experiments are performed to study genes of interest found in RNA-seq. This could be compensated by in-depth bioinformatic analysis (e.g. comparisons with the many different datasets in known in the field), but this is clearly lacking as well. The results section only contains minimal bioinformatic analysis and nothing else. Introduction and discussion are well, clearly written and are in good dialogue with the existing body of work. To improve the manuscript, at minimum these two aspects should be addressed: 1. Characterization of the iPSC-derived neurons is missing (immunostaining with neuronal markers, e.g. Tau, MAP2, exclusion of glial markers, and lack of stem cell markers) 2. Validation of candidates of interest (e.g. FISH analysis in axons vs somata, Kif1c vs wt). Very specific requests from the review are useless at this point, as the authors should have the liberty to focus.

Thank you for the review of our manuscript. We appreciate your recognition of the technical complexity involved in generating axonal transcriptomes and the clarity of our introduction and discussion sections.

__Characterization of iPSC-derived neurons: __We acknowledge the importance of immunostaining with neuronal markers to ensure the purity of our neuronal population. We included this characterization in our revised manuscript and added it into the results and methods section of the paper (Supplementary Figure S1). Additionally, we included RT-qPCR analysis that confirmed the presence of cortical markers and added these to the results and method section of the paper (Supplementary Figure S2).

Additional bioinformatic work: We agree that additional bioinformatic work will greatly benefit this paper. Therefore, we compared our datasets to all additional datasets that we were able to retrieve. This was added to the main text (results and discussion) and supplementary material (Supplementary Figure S5 and S6). We believe this strengthens the merit of our paper, and adds a lot of new unpublished information to the manuscript

__Validation of candidates of interest: __We understand the necessity of validating our RNA-seq findings through experimental approaches such as FISH analysis and comparisons between KIF1C knockout and wild-type neurons. While we appreciate the comment and agree on the importance of high-resolution RNA FISH, we believe it is beyond the scope of this manuscript due to the considerable complexity of these experiments in human iPSC-derived cortical neurons. We will focus on incorporating this aspect into future studies and added a corresponding statement outlining the limitations of our study in the discussion stressing the importance of this.

Minor comments: 1. Details of RNA seq technicalities are redundant in the results section, e.g. „Our RNA-seq pipeline encompassed read quality control (QC), RNA-seq mapping, and gene quantification" (p. 7) is a trivial description - this and similar details should be skipped or described in methods.

We will ensure that technical details are appropriately placed in the methods section and avoid redundancy in the results. Technical details included in the results section have been moved to the methods.

1. Fig1A: Y axis should start from 0

We adjusted Figure 1A to start the Y-axis from 0.

1. Too much interpretational voice in figure legends (e.g. see Fig. 1, „PC1 clearly distinguishes the soma (blue)"

We revised the interpretational voice in the figure legends to maintain objectivity.

1. PCA analysis seems redundant in Fig. 2C

We removed the PCA analysis in Fig. 2A (2C corresponds to Gene ontology term enrichment analysis).

1. Subheading „Human motor axons show a unique transcription factor profile" is misleading - you are not dealing with motor iPS-derived motoneurons (Isl-1 positive), but cortical neurons (again, no marker information provided to assess this!)

The subheading „Human motor axons show a unique transcription factor profile" was adjusted. Furthermore, validation of neuronal identity has been added to the supplementary figures (Supplementary Figure S1 and S2), as well as main text and methods section.

1. Fig. 3: Just by comparing top expressed factors in axonal samples is not informative - overall high expression of a certain transcript likely makes it easier for it to be picked up in the axonal compartment. Axon/soma ratios would perhaps be more appropriate.

After careful consideration, we decided that we will not change the data presentation in Figure 3. Our aim in this figure was not to compare axon and soma but to see highly expressed transcripts in the axon, regardless of whether they are highly expressed in the soma as well. We think that looking at transcripts present in the axon can give information about axonal function, that we might lose when we only consider transcripts that are upregulated compared to the soma. The fact that 25 out of 50 transcription factor RNAs detected in the axon are actually specific to the axons supports this point of view. The comparison between transcripts expressed in axon and soma are presented in Figure 2.

1. Figure 4 (KIF1C modulates the axonal transcriptome): you should show also data for the same genes in the soma, axonal data only is misleading (is overall expression changed?)

We appreciate your suggestion. This data was already included in Supplementary Figure S6 (now Supplementary Figure S9). To make this easier to find, we've added a section to the results part to more clearly state how transcript expression changes in the soma.

Significance

Axonal transcriptomes have been studied since early 2010s by a number of groups and several datasets exist from different model systems. The authors know these studies well, address their findings and cite them appropriately. Is the dataset in this manuscript novel? Does it contribute to the field? Several axonal transcriptomes have been characterized in thorough studies, and even in the specific niche (human IPS-derived motoneurons) a point of reference exists - as the authors themselves point out, it is the Nijssen 2018 study. With appropriate presentation and follow-up experiments this material could have merit as a replication study.

Audience: specialized

We appreciate the reviewer's suggestion to clarify the differences between our findings and previously published data. In response, we have added a dedicated section to the discussion, where we provide a more detailed comparison of our results with existing research. This includes an in-depth examination of the methodologies, experimental conditions, and biological contexts that may explain the observed discrepancies (e.g., variations in methods, neuronal types, and disease contexts). As prior studies primarily focused on mouse-derived neurons, we have included a new section in both the results (Supplementary Figure S6) and the discussion to highlight the limited overlap in gene expression between the axons of mouse- and human-derived neurons. Furthermore, previous studies on human-derived cells either investigated i3 neurons -induced by transcription factors but not fully representative of human-derived CNS-resident neurons - or neurons of the peripheral nervous system (lower motor neurons). In contrast, our study focuses on human-derived CNS-resident cortical neurons (Supplementary Figure S1, S2; comparison shown in Supplementary Figure S5), emphasizing the greater translatability of our findings.

Moreover, we have expanded our bioinformatic analyses and compared our dataset with additional datasets to further substantiate our conclusions (Supplementary Figure S5, S6)

We believe that these revisions significantly enhance the clarity, quality, and impact of our manuscript. We sincerely thank the reviewer for their constructive feedback.

Reviewer #2

Evidence, reproducibility and clarity

This study seeks to identify axonal transcriptome by RNA-sequencing of the iPSC-derived cortical neuron axons. This is achieved by comparing the RNA expressions between the axonal and soma compartments using microfluid system. The specific expression of axon specific RNAs in the axonal compartment validate the specificity of the approach. Some unique RNAs including TF specific RNAs are identified. Furthermore, this study compared the KIF1C-knockout neurons (which models hereditary spastic paraplegia characterized by axonal degeneration) with wildtype (WT) control neurons, which led to the identification of specific down-regulated RNAs involved in axonal development and guidance, neurotransmission, and synaptic formation.

The data of this study are interesting and clearly presented. The major concerns are the lack of characterization of the neuron identities and the examination of functional deficits in the KIF1C-knockout neurons. For example: 1) are these neurons express layer V/VI markers at protein levels, and the proportion of positive neurons (efficiency of cortical neuron differentiation); 2) What are the phenotypic changes in the KIF1C-knockout neurons; are there change sin axonal growth or transport? 3) Day 58 was selected for collecting RNA for sequencing study: how this time point is selected? And are there phenotypic differences between the WT and knockout neurons at this time point?

We appreciate the favorable review of our manuscript and the insightful comments:

Characterization of neuron identities: We agree on the importance of validating neuron identities and included protein-level characterization of layer V/VI markers and efficiency of cortical neuron differentiation in our revised manuscript: We conducted immunohistochemical staining for layer V/VI and other neuronal markers, as well as qRT-PCR to validate the identity of the neurons, ensuring a comprehensive characterization of our neuronal population.

Functional deficits in KIF1C-knockout neurons: We have conducted phenotypic examinations of the neurons but did not observe gross differences in differentiation, axon growth or axon length. We added a corresponding statement to the results section. Neurons were harvested at DAI 58 because at this time we achieved a nearly confluent chamber that yielded enough material for in-depth RNA-sequencing. We did not observe phenotypic differences between wt and KIF1C-KO neurons at this time point. We added a statement to the method section outlining this.

Some minor comments:1. The protein levels of some critical factors needs to be validated.

We validated neuronal identities on qRT-PCR level (Supplementary Figure S2). While we understand the necessity of validating our RNA-seq findings on protein level, we believe it is beyond the scope of this manuscript. However, we will focus on incorporating this aspect into future studies and added a corresponding statement outlining the limitations of our study in the discussion stressing the importance of this.

1. Figure 4C, for the list genes, statistical analyses between WT and knockout groups are required.

In Figure 4C we only included differentially expressed genes with a p-value We added a corresponding statement in the main text and figure legend.

1. Page 15, the 5th to last sentence: "nucleus nucleus" (repeat)

The repeat word on page 15 was deleted.

1. The sequencing data requires public links to the deposited library

We will provide public links to the deposited library for the sequencing data once the data is submitted to a journal (depending on journal guidelines).

Significance

The strength of this study is the combinations of iPSC differentiation, gene editing (KIF1C knockout iPSC) and microfluidic system. This allows the identification of specific axonal transcriptomes. Moreover, the comparisons of control and KIF1C knockout neurons at both axon and soma compartments enables the identification of RNAs and pathways caused by the loss of KIF1C.

The limitation is the lack of functional assessment of the iPSC-derived neurons, especially phenotypic changes in the KIF1C-knockout neurons. Only one time point is selected for comparing the WT and KIF1C knockout neurons, and the relationship between this time point and disease phenotypes is unclear.

This study will be of interest to researchers from both basic and translational fields, and in the fields of stem cells, neuroscience, neurology and genetics.

My expertise includes stem cells, iPSC modeling, motor neuron diseases, and nerve degeneration.

We appreciate the favorable significance statement and believe addressing these points will strengthen the scientific rigor and impact of our study. Thank you for your valuable feedback.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):  Using microfluidics chambers and RNA sequencing (RNA-seq) of axons from iPSC-derived human cortical neurons, authors use RNA profiling to investigate the RNAs present in the soma and axons and the impact of KIF1C molecular motor downregulation (KIF1CKO) on the axonal transcriptome. The rationale is that mutations in KIF1C are associated with an autosomal recessive form of hereditary spastic paraplegia, and KIF1C is implicated in the long-range directional transport of APC-dependent mRNAs and RNA-dependent transport of the exon junction complex into neurites.  Employing a well-defined RNA-seq pipeline for analysis, they obtained RNA sequences particular to axonal samples, outperforming previous studies. They detected over 16,000 genes in the soma (which includes axons) and RNA for more than 5,000 genes in axons. A comparison of the list of axonal genes revealed a strong correlation with previous publications, but they detected more genes overall. They identified transcripts enriched in axons compared to somas, notably those for ribosomal and mitochondrial proteins. Indeed, they observed enrichment for ribosomal subunits, respiratory chain complexes, ion transport, and mRNA splicing.  The study also found that human axons exhibit a unique RNA transcription profile of transcription factors (TFs), with TFs such as GTF3A and ATF4 predominant in axons. At the same time, CREB3 was highly expressed in the soma.  Upon analyzing the soma and axon transcriptomes from KIF1CKO cultures, they identified 189 differentially regulated transcripts: 89 downregulated and 100 upregulated in the KIF1CKO condition. Some of these transcripts are critical for synaptic growth and neurotransmission. Notably, only two targets of APC-target RNAs were downregulated, contrary to their expectation. Their data indicates that KIF1C downregulation significantly alters the axonal transcriptome landscape.  Reviewer #3 (Significance (Required)):  The study is well-performed and informative, particularly for researchers interested in the local translation of axonal proteins and the axonal transcriptome. However, the authors did not validate their findings for any transcripts and did not perform any functional assays, so the manuscript lacks mechanistic insight. Interestingly, GTF3A is a transcription factor that stimulates polymerase III transcription of ribosomal proteins, and mRNAs for ribosomal proteins are enriched in human axons. Maybe there is an interesting story there. 

We appreciate the favorable significance statement and the valuable feedback. We have conducted phenotypic examinations of the neurons but did not observe gross differences in differentiation, axon growth or axon length. We added a corresponding statement to the results section. While we understand the necessity of validating our RNA-seq findings on protein level, we believe it is beyond the scope of this manuscript. However, we will focus on incorporating this aspect into future studies and added a corresponding statement outlining the limitations of our study in the discussion stressing the importance of this.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

This important research uses an elegant combination of protein-protein biochemistry, genetics, and microscopy to demonstrate that the novel bacterial protein FipA is required for polar flagella synthesis and binds to FlhF in multiple bacterial species. This manuscript is convincing, providing evidence for the early stages of flagellar synthesis at a cell pole; however, the protein biochemistry is incomplete and would benefit from additional rigorous experiments. This paper could be of significant interest to microbiologists studying bacterial motility, appendages, and cellular biology.

We are very grateful for the very positive and helpful evaluation.

Joint Public Review:

Bacteria exhibit species-specific numbers and localization patterns of flagella. How specificity in number and pattern is achieved in Gamma-proteobacteria needs to be better understood but often depends on a soluble GTPase called FlhF. Here, the authors take an unbiased protein-pulldown approach with FlhF, resulting in identifying the protein FipA in V. parahaemolyticus. They convincingly demonstrate that FipA interacts genetically and biochemically with previously known spatial regulators HubP and FlhF. FipA is a membrane protein with a cytoplasmic DUF2802; it co-localizes to the flagellated pole with HubP and FlhF. The DUF2802 mediates the interaction between FipA and FlhF, and this interaction is required for FipA function. Altogether, the authors show that FipA likely facilitates the recruitment of FlhF to the membrane at the cell pole together with the known recruitment factor HupB. This finding is crucial in understanding the mechanism of polar localization. The authors show that FipA co-occurs with FlhF in the genomes of bacteria with polarly-localized flagella and study the role of FipA in three of these organisms: V. parahaemolyticus, S. purtefaciens, and P. putida. In each case, they show that FipA contributes to FlhF polar localization, flagellar assembly, flagellar patterning, and motility, though the details differ among the species. By comparing the role of FipA in polar flagellum assembly in three different species, they discover that, while FipA is required in all three systems, evolution has brought different nuances that open avenues for further discoveries.

Strengths:

The discovery of a novel factor for polar flagellum development. The solid nature and flow of the experimental work.

The authors perform a comprehensive analysis of FipA, including phenotyping of mutants, protein localization, localization dependence, and domains of FipA necessary for each. Moreover, they perform a time-series analysis indicating that FipA localizes to the cell pole likely before, or at least coincident with, flagellar assembly. They also show that the role of FipA appears to differ between organisms in detail, but the overarching idea that it is a flagellar assembly/localization factor remains convincing.

The work is well-executed, relying on bacterial genetics, cell biology, and protein interaction studies. The analysis is deep, beginning with discovering a new and conserved factor, then the molecular dissection of the protein, and finally, probing localization and interaction determinants. Finally, the authors show that these determinants are important for function; they perform these studies in parallel in three model systems.

Weaknesses:

The comparative analysis in the different organisms was on balance, a weakness. Mixing the data for the organisms together made the text difficult to read and took away key points from the results. The individual details crowded out the model in its current form. Indeed, because some of the phenotypes and localization dependencies differ between model systems, the comparison is challenging to the reader. The authors could more clearly state what these differences mean, why they arise, and (in the discussion) how they might relate to the organism's lifestyle.

More experiments would be needed to fully analyze the effects of interacting proteins on individual protein stability; this absence slightly detracted from the conclusions.

We have tried our best to improve the manuscript according to the insightful suggestions of the reviewers. Please find our answers to the raised issues below.

Reviewer #1 (Recommendations For The Authors):

We are very grateful to this reviewer for the very positive evaluation and the great suggestions to improve the manuscript.

I think there is value to the comparative analysis but how to present it in such a way that the key similarities and differences stand out is the challenge. Perhaps a table that compares the three datasets is sufficient. Or tell the story of V. parahaemolyticus first to establish the model, followed by comparative analysis of the other two organisms highlighting differences and relegating similarities to supplemental?

We agree that the our previous presentation of our comparative analysis made it very hard to follow the major findings and the general role(s) of FipA, and we are very grateful for the suggestions on how to improve this. We have decided to change the presentation as the reviewer recommended. We used V. parahaemolyticus as a ‚lead model‘ to describe the role of FipA, and we then compared the major findings to the other two species. We hope that the story is now easier to follow.

This is not something that needs to be addressed in the text but I wanted to bring the protein SwrB to the authors' attention which may further expand FipA relevance. Bacillus subtilis uses FlhFG to somehow pattern flagella in a peritrichous arrangement and there are a number of striking similarities, in my opinion, between FipA and SwrB. The two proteins have very similar domain architecture/topology, both proteins promote flagellar assembly, and the genetic neighborhood/operon organization is uncannily similar. There are other more minor similarities dependent on the organism in this paper.

Phillips, Kearns. 2021. Molecular and cell biological analysis of SwrB in Bacillus subtilis. J Bacteriol 203:e0022721

Phillips, Kearns. 2015. Functional activation of the flagellar type III secretion export apparatus. PLoS Genet 11:e1005443.

We thank this reviewer for pointing out these intriguing similarities. For this study we have decided to exclusively concentrate on polarly flagellated bacteria. FlhF und FlhG are also present in B. subtilis where they play a role in organizing flagellation, but we feel that this would be out of scope for this manuscript.

Reviewer #2 (Recommendations For The Authors):

We would like to thank this reviewer for the very positive evaluation and for pointing out several issues to strengthen the story.

Figure 3A data are problematic since everything is too small to visualize. Since these are functional GFP fusions (or mCherry for 2E data), why are they not presented in color?

Again - why are color figures not used to help the reader in Fig 4A and 5F & 5G to confirm what is asserted?

Again, it is difficult to see the images presented. It is asserted that FipA is recruited to the cell pole after cell division and before flagellum assembly, but one has to take their word for it.

We fully agree that in some case the localization pattern is hard to see on the micrographs presented. We have, therefore, provided enlarged micrographs in the supplemental part which allow to better see the fluorescent foci within the cells. With respect to presentations in color – we found that this did not improve the visibility of localizations and therefore have decided to use the grayscale images.

Here, what is missing are turnover assays. Do FipA, FlhF, and HubP all co-localize as complex or is the absence of one leading to the protein turnover of other partners? I think this needs to be sorted out before final conclusions can be made.

Thanks for pointing out this important point. We have now provided western analysis which demonstrate that FipA and FlhF are produced and stable in the absence of the other partners (see Supplemental Figure 5). Stability of HubP as a general polar marker not only required for flagellation was not determined.

Minor comments:

Line 58: change "around" to "in timing with"

Line 79: what "signal" is transferred from the C-ring to the MS-ring. Are they not fully connected such that rotation is the entire structure - C-ring-MS-ring-Rod-Hook-Filament. Is it not the change in the relationship to the stator complex where the signal is transferred?

Line 85: change "counting" to "control of flagellar numbers per cell"

Line 110: change "is (co-)responsible for recruiting" to "facilitates recruitment of"

Thanks for pointing this out. We have adjusted the wording according to the reviewer’s suggestions.

Given that motility phenotypes vary on individual plates (volumes and dryness vary), why in Figure 2C are the motility assays for fipA and flhF mutants of P. putida done on different plates?

For better visualisation, we have rearranged the spreading halos for the figure. All strain spreading comparisons on soft agar were always conducted on the same plate due to the reasons this reviewer mentioned.

Reviewer #3 (Recommendations For The Authors):

We thank this reviewer for the very positive evalution and the great suggestions.

One possibility is to describe first all the results relating to FipA in Vibrio and then add the result sections at the end to illustrate the differences between Vibrio and Shewanella, and then Vibrio and Pseudomonas. This may make it easier to follow for the reader.

We agree that the our previous presentation of our comparative analysis made it very hard to follow the major findings and the general role(s) of FipA, and we are very grateful for the suggestions on how to improve this. We have decided to change the presentation as the reviewer recommended. We used V. parahaemolyticus as a ‚lead model‘ to describe the role of FipA, and we then compared the major findings to the other two species. We hope that the story is now easier to follow.

I would have liked to see some TEM analysis of flagella in fipA/hubP double mutants strains and was also wondering if FipA/FlhF/HubP colocalization had been studied in E. coli when all proteins are expressed together, at least with two bearing fluorescent tags.

Thanks for these great suggestions. In this study, we have concentrated on the localization of FlhF by FipA and HubP. HubP has multiple functions in the cell and may also affect flagellar synthesis to some extent in a species-specific fashion. Therefore, any findings would have to be discussed very carefully, so we have decided to leave that out for the time being.

With respect to the FipA/HubP/FlhF production in a heterologous host such as E. coli, this has been partly done (without FipA) in a second parallel story (see reference to Dornes et al (2024) in this manuscript). Rebuilding larger parts of the system in a heterologous host is currently done in an independent study. Therefore, we have decided not to include this already here.

From the Reviewing Editor:

We are grateful for handling the fair reviewing process, for the positive evaluation and the helpful hints.

The microscopy was inconsistent (DIC versus phase) for unclear reasons. Did using different microscopes impact the ability to acquire low-intensity fluorescence signals? Please add a sentence in the Methods section to clarify.

We are sorry for this inconsistency. As the imaging was carried out by different labs (to some part before the projects were joined), the corresponding preferred microscopy settings were used. We have added an explaining sentence to the Methods section.

Also, some subcellular fluorescence localizations were not visible in the selected images (e.g., Figures 3 and 5). The reader had to rely on the authors' statements and analyses. The conclusions could be more robust with fluorescence measurements across the cell body for a subset of cells. The authors could provide this data analysis in the Supplemental; this measurement would more clearly show an accumulation of fluorescence at the cell pole, particularly in low-intensity images.

We fully agree that in some case the localization pattern is hard to see on the micrographs presented. Unfortunately, often the signal is not sufficiently strong to provied proper demographs. We have, therefore, provided enlarged micrographs in the supplemental part, which allow to better see the fluorescent foci within the cells.

Author response:

We sincerely thank the reviewers for their thoughtful, critical, and constructive comments, which will help us in further exploring the mechanisms by which LDH regulates glycolysis, the tricarboxylic acid cycle, and oxidative phosphorylation future studies. The following is our responses to the reviewers' comments.

Reviewer #1 (Public Review):

Summary:

Zeng et al. have investigated the impact of inhibiting lactate dehydrogenase (LDH) on glycolysis and the tricarboxylic acid cycle. LDH is the terminal enzyme of aerobic glycolysis or fermentation that converts pyruvate and NADH to lactate and NAD+ and is essential for the fermentation pathway as it recycles NAD+ needed by upstream glyceraldehyde-3-phosphate dehydrogenase. As the authors point out in the introduction, multiple published reports have shown that inhibition of LDH in cancer cells typically leads to a switch from fermentative ATP production to respiratory ATP production (i.e., glucose uptake and lactate secretion are decreased, and oxygen consumption is increased). The presumed logic of this metabolic rearrangement is that when glycolytic ATP production is inhibited due to LDH inhibition, the cell switches to producing more ATP using respiration. This observation is similar to the well-established Crabtree and Pasteur effects, where cells switch between fermentation and respiration due to the availability of glucose and oxygen. Unexpectedly, the authors observed that inhibition of LDH led to inhibition of respiration and not activation as previously observed. The authors perform rigorous measurements of glycolysis and TCA cycle activity, demonstrating that under their experimental conditions, respiration is indeed inhibited. Given the large body of work reporting the opposite result, it is difficult to reconcile the reasons for the discrepancy. In this reviewer's opinion, a reason for the discrepancy may be that the authors performed their measurements 6 hours after inhibiting LDH. Six hours is a very long time for assessing the direct impact of a perturbation on metabolic pathway activity, which is regulated on a timescale of seconds to minutes. The observed effects are likely the result of a combination of many downstream responses that happen within 6 hours of inhibiting LDH that causes a large decrease in ATP production, inhibition of cell proliferation, and likely a range of stress responses, including gene expression changes.

Strengths:

The regulation of metabolic pathways is incompletely understood, and more research is needed, such as the one conducted here. The authors performed an impressive set of measurements of metabolite levels in response to inhibition of LDH using a combination of rigorous approaches.

Weaknesses:

Glycolysis, TCA cycle, and respiration are regulated on a timescale of seconds to minutes. The main weakness of this study is the long drug treatment time of 6 hours, which was chosen for all the experiments. In this reviewer's opinion, if the goal was to investigate the direct impact of LDH inhibition on glycolysis and the TCA cycle, most of the experiments should have been performed immediately after or within minutes of LDH inhibition. After 6 hours of inhibiting LDH and ATP production, cells undergo a whole range of responses, and most of the observed effects are likely indirect due to the many downstream effects of LDH and ATP production inhibition, such as decreased cell proliferation, decreased energy demand, activation of stress response pathways, etc.

We appreciate the reviewer’s critical comments. The main argument is whether the inhibition of LDH induces a temporal perturbation in glycolysis, the TCA cycle, and OXPHOS, or if it leads to a shift to a new steady state. We argue that this shift represents a transition between two steady states; specifically, GNE-140 treatment drives metabolism from one steady state to another.

Before conducting the experiment, we performed a time course experiment, measuring glucose consumption and lactate production in cells treated with GNE-140. The results demonstrated a very good linearity, indicating that the glycolytic rate remained constant—thus confirming that glycolysis was at steady state. Given the tight coupling between glycolysis, the TCA cycle, and OXPHOS, we infer that the TCA cycle and OXPHOS were also at steady state. However, this ‘infer’ requires further confirmation.

Multiple published reports have shown that LDH inhibition in cancer cells causes a shift from fermentative ATP production to respiratory ATP production. This notion persists because it is often compared to the well-established Crabtree and Pasteur effects, where cells toggle between fermentation and respiration based on glucose and oxygen availability. However, in the Pasteur or Crabtree effects, the deprivation of oxygen—the terminal electron acceptor—drives the switch, which is fundamentally different from LDH inhibition.

Reviewer #2 (Public Review):

Summary:

Zeng et al. investigated the role of LDH in determining the metabolic fate of pyruvate in HeLa and 4T1 cells. To do this, three broad perturbations were applied: knockout of two LDH isoforms (LDH-A and LDH-B), titration with a non-competitive LDH inhibitor (GNE-140), and exposure to either normoxic (21% O2) or hypoxic (1% O2) conditions. They show that knockout of either LDH isoform alone, though reducing both protein level and enzyme activity, has virtually no effect on either the incorporation of a stable 13C-label from a 13C6-glucose into any glycolytic or TCA cycle intermediate, nor on the measured intracellular concentrations of any glycolytic intermediate (Figure 2). The only apparent exception to this was the NADH/NAD+ ratio, measured as the ratio of F420/F480 emitted from a fluorescent tag (SoNar).

The addition of a chemical inhibitor, on the other hand, did lead to changes in glycolytic flux, the concentrations of glycolytic intermediates, and in the NADH/NAD+ ratio (Figure 3). Notably, this was most evident in the LDH-B-knockout, in agreement with the increased sensitivity of LDH-A to GNE-140 (Figure 2). In the LDH-B-knockout, increasing concentrations of GNE-140 increased the NADH/NAD+ ratio, reduced glucose uptake, and lactate production, and led to an accumulation of glycolytic intermediates immediately upstream of GAPDH (GA3P, DHAP, and FBP) and a decrease in the product of GAPDH (3PG). They continue to show that this effect is even stronger in cells exposed to hypoxic conditions (Figure 4). They propose that a shift to thermodynamic unfavourability, initiated by an increased NADH/NAD+ ratio inhibiting GAPDH explains the cascade, calculating ΔG values that become progressively more endergonic at increasing inhibitor concentrations.

Then - in two separate experiments - the authors track the incorporation of 13C into the intermediates of the TCA cycle from a 13C6-glucose and a 13C5-glutamine. They use the proportion of labelled intermediates as a proxy for how much pyruvate enters the TCA cycle (Figure 5). They conclude that the inhibition of LDH decreases fermentation, but also the TCA cycle and OXPHOS flux - and hence the flux of pyruvate to all of those pathways. Finally, they characterise the production of ATP from respiratory or fermentative routes, the concentration of a number of cofactors (ATP, ADP, AMP, NAD(P)H, NAD(P)+, and GSH/GSSG), the cell count, and cell viability under four conditions: with and without the highest inhibitor concentration, and at norm- and hypoxia. From this, they conclude that the inhibition of LDH inhibits the glycolysis, the TCA cycle, and OXPHOS simultaneously (Figure 7).

Strengths:

The authors present an impressively detailed set of measurements under a variety of conditions. It is clear that a huge effort was made to characterise the steady-state properties (metabolite concentrations, fluxes) as well as the partitioning of pyruvate between fermentation as opposed to the TCA cycle and OXPHOS.

A couple of intermediary conclusions are well supported, with the hypothesis underlying the next measurement clearly following. For instance, the authors refer to literature reports that LDH activity is highly redundant in cancer cells (lines 108 - 144). They prove this point convincingly in Figure 1, showing that both the A- and B-isoforms of LDH can be knocked out without any noticeable changes in specific glucose consumption or lactate production flux, or, for that matter, in the rate at which any of the pathway intermediates are produced. Pyruvate incorporation into the TCA cycle and the oxygen consumption rate are also shown to be unaffected.

They checked the specificity of the inhibitor and found good agreement between the inhibitory capacity of GNE-140 on the two isoforms of LDH and the glycolytic flux (lines 229 - 243). The authors also provide a logical interpretation of the first couple of consequences following LDH inhibition: an increased NADH/NAD+ ratio leading to the inhibition of GAPDH, causing upstream accumulations and downstream metabolite decreases (lines 348 - 355).

Weaknesses:

Despite the inarguable comprehensiveness of the data set, a number of conceptual shortcomings afflict the manuscript. First and foremost, reasoning is often not pursued to a logical conclusion. For instance, the accumulation of intermediates upstream of GAPDH is proffered as an explanation for the decreased flux through glycolysis. However, in Figure 3C it is clear that there is no accumulation of the intermediates upstream of PFK. It is unclear, therefore, how this traffic jam is propagated back to a decrease in glucose uptake. A possible explanation might lie with hexokinase and the decrease in ATP (and constant ADP) demonstrated in Figure 6B, but this link is not made.

We appreciate the reviewer's critical comment. In Figure 3C, there is no accumulation of F6P or G6P, which are upstream of PFK1. This is because the PFK1-catalyzed reaction sets a significant thermodynamic barrier. Even with treatment using 30 μM GNE-140, the ∆GPFK1 (Gibbs free energy of the PFK1-catalyzed reaction) remains -9.455 kJ/mol (Figure 3D), indicating that the reaction is still far from thermodynamic equilibrium, thereby preventing the accumulation of F6P and G6P.

We agree with the reviewer that hexokinase inhibition may play a role, this requires further investigation.

The obvious link between the NADH/NAD+ ratio and pyruvate dehydrogenase (PDH) is also never addressed, a mechanism that might explain how the pyruvate incorporation into the TCA cycle is impaired by the inhibition of LDH (the observation with which they start their discussion, lines 511 - 514).

We agree with the reviewer’s comment. In this study, we did not explore how the inhibition of LDH affects pyruvate incorporation into the TCA cycle. As this mechanism was not investigated, we have titled the study: "Elucidating the Kinetic and Thermodynamic Insights into the Regulation of Glycolysis by Lactate Dehydrogenase and Its Impact on the Tricarboxylic Acid Cycle and Oxidative Phosphorylation in Cancer Cells."

It was furthermore puzzling how the ΔG, calculated with intracellular metabolite concentrations (Figures 3 and 4) could be endergonic (positive) for PGAM at all conditions (also normoxic and without inhibitor). This would mean that under the conditions assayed, glycolysis would never flow completely forward. How any lactate or pyruvate is produced from glucose, is then unexplained.

This issue also concerned me during the study. However, given the high reproducibility of the data, we consider it is true, but requires explanation.

The PGAM-catalyzed reaction is tightly linked to both upstream and downstream reactions in the glycolytic pathway. In glycolysis, three key reactions catalyzed by HK2, PFK1, and PK are highly exergonic, providing the driving force for the conversion of glucose to pyruvate. The other reactions, including the one catalyzed by PGAM, operate near thermodynamic equilibrium and primarily serve to equilibrate glycolytic intermediates rather than control the overall direction of glycolysis, as previously described by us (J Biol Chem. 2024 Aug 8;300(9):107648).

The endergonic nature of the PGAM-catalyzed reaction does not prevent it from proceeding in the forward direction. Instead, the directionality of the pathway is dictated by the exergonic reaction of PFK1 upstream, which pushes the flux forward, and by PK downstream, which pulls the flux through the pathway. The combined effects of PFK1 and PK may account for the observed endergonic state of the PGAM reaction.

However, if the PGAM-catalyzed reaction were isolated from the glycolytic pathway, it would tend toward equilibrium and never surpass it, as there would be no driving force to move the reaction forward.

Finally, the interpretation of the label incorporation data is rather unconvincing. The authors observe an increasing labelled fraction of TCA cycle intermediates as a function of increasing inhibitor concentration. Strangely, they conclude that less labelled pyruvate enters the TCA cycle while simultaneously less labelled intermediates exit the TCA cycle pool, leading to increased labelling of this pool. The reasoning that they present for this (decreased m2 fraction as a function of DHE-140 concentration) is by no means a consistent or striking feature of their titration data and comes across as rather unconvincing. Yet they treat this anomaly as resolved in the discussion that follows.

GNE-140 treatment increased the labeling of TCA cycle intermediates by [13C6]glucose but decreased the OXPHOS rate, we consider the conflicting results as an 'anomaly' that warrants further explanation. To address this, we analyzed the labeling pattern of TCA cycle intermediates using both [13C6]glucose and  [13C5]glutamine. Tracing the incorporation of glucose- and glutamine-derived carbons into the TCA cycle suggests that LDH inhibition leads to a reduced flux of glucose-derived acetyl-CoA into the TCA cycle, coupled with a decreased flux of glutamine-derived α-KG, and a reduction in the efflux of intermediates from the cycle. These results align with theoretical predictions. Under any condition, the reactions that distribute TCA cycle intermediates to other pathways must be balanced by those that replenish them. In the GNE-140 treatment group, the entry of glutamine-derived carbon into the TCA cycle was reduced, implying that glucose-derived carbon (as acetyl-CoA) entering the TCA cycle must also be reduced, or vice versa.

This step-by-step investigation is detailed under the subheading "The Effect of LDHB KO and GNE-140 on the Contribution of Glucose Carbon to the TCA Cycle and OXPHOS" in the Results section in the manuscript.

In the Discussion, we emphasize that caution should be exercised when interpreting isotope tracing data. In this study, treatment of cells with GNE-140 led to an increase labeling percentage of TCAC intermediates by [13C6]glucose (Figure 5A-E). However, this does not necessarily imply an increase in glucose carbon flux into TCAC; rather, it indicates a reduction in both the flux of glucose carbon into TCAC and the flux of intermediates leaving TCAC. When interpreting the data, multiple factors must be considered, including the carbon-13 labeling pattern of the intermediates (m1, m2, m3, ---) (Figure 5G-K), replenishment of intermediates by glutamine (Figure 5M-V), and mitochondrial oxygen consumption rate (Figure 5W). All these factors should be taken into account to derive a proper interpretation of the data. 

Reviewer #3 (Public Review):

Hu et al in their manuscript attempt to interrogate the interplay between glycolysis, TCA activity, and OXPHOS using LDHA/B knockouts as well as LDH-specific inhibitors. Before I discuss the specifics, I have a few issues with the overall manuscript. First of all, based on numerous previous studies it is well established that glycolysis inhibition or forcing pyruvate into the TCA cycle (studies with PDKs inhibitors) leads to upregulation of TCA cycle activity, and OXPHOS, activation of glutaminolysis, etc (in this work authors claim that lowered glycolysis leads to lower levels of TCA activity/OXPHOS). The authors in the current work completely ignore recent studies that suggest that lactate itself is an important signaling metabolite that can modulate metabolism (actual mechanistic insights were recently presented by at least two groups (Thompson, Chouchani labs). In addition, extensive effort was dedicated to understanding the crosstalk between glycolysis/TCA cycle/OXPHOS using metabolic models (Titov, Rabinowitz labs). I have several comments on how experiments were performed. In the Methods section, it is stated that both HeLa and 4T1 cells were grown in RPMI-1640 medium with regular serum - but under these conditions, pyruvate is certainly present in the medium - this can easily complicate/invalidate some findings presented in this manuscript. In LDH enzymatic assays as described with cell homogenates controls were not explained or presented (a lot of enzymes in the homogenate can react with NADH!). One of the major issues I have is that glycolytic intermediates were measured in multiple enzyme-coupled assays. Although one might think it is a good approach to have quantitative numbers for each metabolite, the way it was done is that cell homogenates (potentially with still traces of activity of multiple glycolytic enzymes) were incubated with various combinations of the SAME enzymes and substrates they were supposed to measure as a part of the enzyme-based cycling reaction. I would prefer to see a comparison between numbers obtained in enzyme-based assays with GC-MS/LC-MS experiments (using calibration curves for respective metabolites, of course). Correct measurements of these metabolites are crucial especially when thermodynamic parameters for respective reactions are calculated. Concentrations of multiple graphs (Figure 1g etc.) are in "mM", I do not think that this is correct.

While the roles of lactate as a signaling metabolite and metabolic models are important areas of research, our work focuses on different aspects.

It is true that cell homogenates contain many enzymes that use NAD as a hydride acceptor or NADH as a hydride donor. However, in our assay system, the substrates are pyruvate and NADH, meaning only enzymes that catalyze the conversion of pyruvate + NADH to NAD + lactate can utilize NADH. Other enzymes do not interfere with this reaction. Although some enzymes may also catalyze this reaction, their catalytic efficiency is markedly lower than that of LDH, ensuring the validity of this assay.

Similarly, the assays for glycolytic intermediates are validated by the substrate specificity.

We have developed an LC-MS methodology for some glycolytic intermediates, but the accuracy of quantification remains unsatisfactory due to inherent limitations of this methodology.

Article review: This article discusses the idea of "learning styles," disputes their standing as legitimate in educational circles, and offers alternative options. Overall, I think this article presents a solid argument for why, while we put lots of stock in the idea of them, learning styles may not be accurate or helpful in the long run.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors use microscopy experiments to track the gliding motion of filaments of the cyanobacteria Fluctiforma draycotensis. They find that filament motion consists of back-and-forth trajectories along a "track", interspersed with reversals of movement direction, with no clear dependence between filament speed and length. It is also observed that longer filaments can buckle and form plectonemes. A computational model is used to rationalize these findings.

We thank the reviewer for this accurate summary of the presented work.

Strengths:

Much work in this field focuses on molecular mechanisms of motility; by tracking filament dynamics this work helps to connect molecular mechanisms to environmentally and industrially relevant ecological behavior such as aggregate formation.

The observation that filaments move on tracks is interesting and potentially ecologically significant.

The observation of rotating membrane-bound protein complexes and tubular arrangement of slime around the filament provides important clues to the mechanism of motion.

The observation that long filaments buckle has the potential to shed light on the nature of mechanical forces in the filaments, e.g. through the study of the length dependence of buckling.

We thank the reviewer for listing these positive aspects of the presented work.

Weaknesses:

The manuscript makes the interesting statement that the distribution of speed vs filament length is uniform, which would constrain the possibilities for mechanical coupling between the filaments. However, Figure 1C does not show a uniform distribution but rather an apparent lack of correlation between speed and filament length, while Figure S3 shows a dependence that is clearly increasing with filament length. Also, although it is claimed that the computational model reproduces the key features of the experiments, no data is shown for the dependence of speed on filament length in the computational model. The statement that is made about the model "all or most cells contribute to propulsive force generation, as seen from a uniform distribution of mean speed across different filament lengths", seems to be contradictory, since if each cell contributes to the force one might expect that speed would increase with filament length.

We agree that the data shows in general a lack of correlation, rather than strictly being uniform. In the revised manuscript, we intend to collect more data from observations on glass to better understand the relation between filament length and speed. 

In considering longer filaments, one also needs to consider the increased drag created by each additional cell - in other words, overall friction will either increase or be constant as filament length increases. Therefore, if only one cell (or few cells) are generating motility forces, then adding more cells in longer filaments would decrease speed.

Since the current data does not show any decrease in speed with increasing filament length, we stand by the argument that the data supports that all (or most) cells in a filament are involved in force generation for motility. We would revise the manuscript to make this point - and our arguments about assuming multiple / most cells in a filament contributing to motility - clear.

The computational model misses perhaps the most interesting aspect of the experimental results which is the coupling between rotation, slime generation, and motion. While the dependence of synchronization and reversal efficiency on internal model parameters are explored (Figure 2D), these model parameters cannot be connected with biological reality. The model predictions seem somewhat simplistic: that less coupling leads to more erratic reversal and that the number of reversals matches the expected number (which appears to be simply consistent with a filament moving backwards and forwards on a track at constant speed).

We agree that the coupling between rotation, slime generation and motion is interesting and important when studying the specific mechanism leading to filament motion. However, we believe it even more fundamental to consider the intercellular coordination that is needed to realise this motion. Individual filaments are a collection of independent cells. This raises the question of how they can coordinate their thrust generation in such a way that the whole filament can both move and reverse direction of motion as a single unit. With the presented model, we want to start addressing precisely this point.

The model allows us to qualitatively understand the relation between coupling strength and reversals (erratic vs. coordinated motion of the filament). It also provides a hint about the possibility of de-coordination, which we then look for and identify in longer filaments.

While the model results seem obvious in hindsight, the analysis of the model allows phrasing the question of cell-to-cell coordination, which has not been brought up previously when considering the inherently multi-cell process of filament motility.

Filament buckling is not analysed in quantitative detail, which seems to be a missed opportunity to connect with the computational model, eg by predicting the length dependence of buckling.

Please note that Figure S10 provides an analysis of filament length and number of buckling instances observed. This suggests that buckling happens only in filaments above a certain length.

We do agree that further analyses of buckling - both experimentally and through modelling would be interesting.  This study, however,  focussed on cell-to-cell coupling / coordination during filament motility. We have identified the possibility of de-coordination through the use of a simple 1D model of motion, and found evidence of such de-coordination in experiments. Notice that the buckling we report does not depend on the filament hitting an external object. It is a direct result of a filament activity which, in this context, serves as evidence of cellular de-coordination.

Now that we have observed buckling and plectoneme formation, these processes need to be analysed with additional experiments and modelling. The appropriate model for this process needs to be 3D, and should ideally include torques arising from filament rotation. Experimentally, we need to identify means of influencing filament length and motion and see if we can measure buckling frequency and position across different filament lengths. These works are ongoing and will have to be summarised in a separate, future publication.

Reviewer #2 (Public review):

Summary:

The authors combined time-lapse microscopy with biophysical modeling to study the mechanisms and timescales of gliding and reversals in filamentous cyanobacterium Fluctiforma draycotensis. They observed the highly coordinated behavior of protein complexes moving in a helical fashion on cells' surfaces and along individual filaments as well as their de-coordination, which induces buckling in long filaments.

We thank the reviewer for this accurate summary of the presented work.

Strengths:

The authors provided concrete experimental evidence of cellular coordination and de-coordination of motility between cells along individual filaments. The evidence is comprised of individual trajectories of filaments that glide and reverse on surfaces as well as the helical trajectories of membrane-bound protein complexes that move on individual filaments and are implicated in generating propulsive forces.

We thank the reviewer for listing these positive aspects of the presented work.

Limitations:

The biophysical model is one-dimensional and thus does not capture the buckling observed in long filaments. I expect that the buckling contains useful information since it reflects the competition between bending rigidity, the speed at which cell synchronization occurs, and the strength of the propulsion forces.

Cell-to-cell coordination is a more fundamental phenomenon than the buckling and twisting of longer filaments, in that the latter is a consequence of limits of the former. In this sense, we are focussing here on something that we think is the necessary first step to understand filament gliding. The 3D motion of filaments (bending, plectoneme formation) is fascinating and can have important consequences for collective behaviour and macroscopic structure formation. As a consequence of cellular coupling, however, it is beyond the scope of the present paper.

Please also see our response above. We believe that the detailed analysis of buckling and plectoneme formation requires (and merits) dedicated experiments and modelling which go beyond the focus of the current study (on cellular coordination) and will constitute a separate analysis that stands on its own. We are currently working in that direction.

Future directions:

The study highlights the need to identify molecular and mechanical signaling pathways of cellular coordination. In analogy to the many works on the mechanisms and functions of multi-ciliary coordination, elucidating coordination in cyanobacteria may reveal a variety of dynamic strategies in different filamentous cyanobacteria.

We thank the reviewer for highlighting this point again and seeing the value in combining molecular and dynamical approaches.

Reviewer #3 (Public review):

Summary:

The authors present new observations related to the gliding motility of the multicellular filamentous cyanobacteria Fluctiforma draycotensis. The bacteria move forward by rotating their about their long axis, which causes points on the cell surface to move along helical paths. As filaments glide forward they form visible tracks. Filaments preferentially move within the tracks. The authors devise a simple model in which each cell in a filament exerts a force that either pushes forward or backwards. Mechanical interactions between cells cause neighboring cells to align the forces they exert. The model qualitatively reproduces the tendency of filaments to move in a concerted direction and reverse at the end of tracks.

We thank the reviewer for this accurate summary of the presented work.

Strengths:

The observations of the helical motion of the filament are compelling.

The biophysical model used to describe cell-cell coordination of locomotion is clear and reasonable. The qualitative consistency between theory and observation suggests that this model captures some essential qualities of the true system.

The authors suggest that molecular studies should be directly coupled to the analysis and modeling of motion. I agree.

We thank the reviewer for listing these positive aspects of the presented work and highlighting the need for combining molecular and biophysical approaches.

Weaknesses:

There is very little quantitative comparison between theory and experiment. It seems plausible that mechanisms other than mechano-sensing could lead to equations similar to those in the proposed model. As there is no comparison of model parameters to measurements or similar experiments, it is not certain that the mechanisms proposed here are an accurate description of reality. Rather the model appears to be a promising hypothesis.

We agree with the referee that the model we put forward is one of several possible. We note, however, that the assumption of mechanosensing by each cell - as done in this model - results in capturing both the alignment of cells within a filament (with some flexibility) and reversal dynamics. We have explored an even more minimal 1D model, where the cell’s direction of force generation is treated as an Ising-like spin and coupled between nearest neighbours (without assuming any specific physico-chemical basis). We found that this model was not fully able to capture both phenomena. In that model, we found that alignment required high levels of coupling (which is hard to justify except for mechanical coupling) and reversals were not readily explainable (and required additional assumptions). These points led us to the current, mechanically motivated model.

The parameterisation of the current model would require measuring cellular forces. To this end, a recent study has attempted to measure some of the physical parameters in a different filamentous cyanobacteria [1] and in our revision we will re-evaluate model parameters and dynamics in light of that study. We will also attempt to directly verify the presence of mechano-sensing by obstructing the movement of filaments.

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

The authors present valuable findings on how to determine the genetic architecture of extreme phenotype values by using data on sibling pairs. While the authors' derivations of the method are correct, the scenarios considered are incomplete, making it difficult to have confidence in the interpretation of the results as demonstrating the influence of de-novo or Mendelian (rare, penetrant-variant) architectures. The method nevertheless shows promise and will be of interest to researchers studying complex trait genetics. 

A.1: We have now expanded our consideration of the scenarios and we have ensured that we do not over-interpret our results as being due to de novo or Mendelian architectures. Instead, we make clear that our statistical tests are powered to identify these architectures but that there are other potential causes of significant results (e.g. measurement error or uncontrolled environmental factors from heavy-tailed distributions), making follow-up validation studies necessary before underlying architectures can be confirmed. We consider this to be typical of observational research, in which significant results may indicate causal effects unless uncontrolled confounding factors explain the observed associations, requiring experimental/trial follow-up for validation. We believe that our tests are useful for providing initial inference, and that in some settings – e.g. prioritising samples for sequencing to identify rare variants – could be useful as an initial screening step to increase the efficacy of a planned analysis or study.

Additionally, we have now developed “SibArc”, an openly available software tool that takes input sibling trait data and estimates conditional sibling heritability across the trait distribution. Then - based on our theoretical framework developed and described in the paper - for each tail of the trait distribution, estimates effect sizes and generates P-values corresponding to our de novo and Mendelian tests, and performs a Kolmogorov-Smirnov test to identify general departures from our null model. Furthermore, SibArc also provides additional functionality for users under preliminary beta form, for example, running an iterative optimisation routine to infer approximate relative degrees of polygenic, de novo, and Mendelian architectures prevailing in each trait tail. We have made this software tool, Quick Start tutorial, and sample data available online at Github and are hosting these on a dedicated website: www.sibarc.net.

Reviewer #1 (Public Review):

This is a clever and well-done paper that should be published. The authors sought to craft a method, applicable to biobank-scale data but without necessarily using genotyping or sequencing, to detect the presence of de novo mutations and rare variants that stand out from the polygenic background of a given trait. Their method depends essentially on sibling pairs where one sibling is in an extreme tail of the phenotypic distribution and whether the other sibling's regression to the mean shows a systematic deviation from what is expected under a simple polygenic architecture. 

Their method is successful in that it builds on a compelling intuition, rests on a rigorous derivation, and seems to show reasonable statistical power in the UK Biobank. (More biobanks of this size will probably become available in the near future.)  It is somewhat unsuccessful in that rejection of the null hypothesis does not necessarily point to the favored hypothesis of de novo or rare variants. The authors discuss the alternative possibility of rare environmental events of large effect. Maybe attention should be drawn to this in the abstract or the introduction of the paper. Nevertheless, since either of these possibilities is interesting, the method remains valuable. 

A.2: We agree with the reviewer that we should have made it clearer that - while our statistical tests are powered to identify de novo and Mendelian architectures – significant findings from our tests could also be explained by rare environmental events of large effect (specifically by uncontrolled environmental factors with heavy-tailed distributions). We have now made this clear throughout the manuscript (see A.1).

Moreover, we agree with the reviewer that whether the cause of deviations from expectations are due to de novo or rare variants, or environmental factors, either possibility is interesting. For example, in either scenario, our results can highlight inaccuracy in PRS prediction of extreme trait values for certain traits, and also provides a relative measure across different traits of large effects impacting on the trait tails, irrespective of whether genetic or environmental. We now place more emphasis on this point throughout the manuscript.

Reviewer #2 (Public Review):

Souaiaia et al. attempt to use sibling phenotype data to infer aspects of genetic architecture affecting the extremes of the trait distribution. They do this by considering deviations from the expected joint distribution of siblings' phenotypes under the standard additive genetic model, which forms their null model. They ascribe excess similarity compared to the null as due to rare variants shared between siblings (which they term 'Mendelian') and excess dissimilarity as due to de-novo variants. While this is a nice idea, there can be many explanations for rejection of their null model, which clouds interpretation of Souaiaia et al.'s empirical results.

A.3: We agree with the reviewer that we should have made clearer that there are other explanations for significant results from our tests and we have now fully addressed this point – (see A.1, A.2, A.4, A.5 for more detail).  In addition, we now elaborate on exactly what our null hypothesis is: which is not only that the expected joint distribution of siblings’ phenotypes is governed by the standard additive genetic model, but that environmental effects are either controlled for or else their combined effect is approximately Gaussian. Furthermore, by selecting only those traits whose raw trait distribution most closely corresponds to a Gaussian distribution from the UK Biobank, we increase the probability that significant results from our tests are due to rare variants (shared or unshared among siblings).

The authors present their method as detecting aspects of genetic architecture affecting the extremes of the trait distribution. However, I think it would be better to characterize the method as detecting whether siblings are more or less likely to be aggregated in the extremes of the phenotype distribution than would be predicted under a common variant, additive genetic model.

A.4: As discussed above we should have stated more clearly that significant results could be due to non-genetic factors, we have now addressed this.

However, we do not think that it would be appropriate to characterise our tests as merely corresponding to over and under aggregation of siblings in the tails. Firstly, environmental factors should be controlled for as part of our testing, increasing the probability that significant results are due to genetic, and not environmental factors. Secondly, tests for identifying broad over and under aggregation of siblings in the tails should be designed differently and, accordingly, the tests that we have developed here would not be optimal to detect over/under aggregation of siblings in trait tails. Our test for inference of de novo variants, for example, exploits the fact that de novo alleles of large effect result in one sibling being extreme and all others being drawn from the background distribution, so that the mean of other siblings is relatively low – not merely that other siblings are less likely to be found in the tail. For more discussion on this issue in relation to one of reviewer 1’s points, see A.9.

Exactly how the rareness and penetrance of a genetic variant influence the conditional sibling phenotype distribution at the extremes is not made clear. The contrast between de-novo and 'Mendelian' architectures is somewhat odd since these are highly related phenomena: a 'Mendelian' architecture could be due to a de-novo variant of the previous generation. The fact that these two phenomena are surmised to give opposing signatures in the authors' statistical tests seems suboptimal to me: would it not be better to specify a parameter that characterizes the degree or sharing between siblings of rare factors of large effect? This could be related to the mixture components in the bimodal distribution displayed in Fig 1. In fact, won't the extremes of all phenotypes be influenced by all three types of variants (common, rare, de-novo) to greater or lesser degree? By framing the problem as a hypothesis testing problem, I think the authors are obscuring the fact that the extremes of real phenotypes likely reflect a mixture of causes: common, de-novo, and rare variants (and shared and non-shared environmental factors). 

A.5: We absolutely recognise that there will typically be a complex and continuous mix of genetic architectures underlying complex traits in their tails, dictated by the 2-dimensional relationship between allele frequency and effect size. We did consider developing a fully Bayesian statistical framework to model this, but soon realised that doing this properly would require a substantial amount of model development, accounting for multiple factors in ways that would require a great deal of further investigation; for example, performing a range of complex simulations to investigate the effects of different selective pressures over time, different patterns of assortative mating, and effect size generating distributions. We are in the process of applying for funding for a multi-year project that will perform exactly these investigations as a step towards developing more sophisticated models of inference. In the meantime, we do believe that the simpler hypothesis-testing framework that we have developed here does have important value. Assuming that environmental factors are accounted for, or that any that are not accounted for have combined Gaussian effects, then our tests will indeed infer enrichments of de novo and ‘Mendelian’ rare alleles of large effect in the tails of complex traits. Results from these tests can also be compared within and across traits to compare the relative degree of such enrichments among traits. For some traits we observe significant results from both tests, and for other traits we observe highly significant results from one of our tests but not the other. Thus, while our tests do not provide a complete picture about the genetic architecture in the tails of complex traits, they do offer some intriguing initial insights into tail architecture, important given the enrichment of disease in trait tails.

To better enable interpretation of the results of this method, a more comprehensive set of simulations is needed. Factors that may influence the conditional distribution of siblings' phenotypes beyond those considered include: non-normal distribution, assortative mating, shared environment, interactions between genetic and shared environmental factors, and genetic interactions. 

A.6: As described above (see A.5) we do agree that a more comprehensive set of simulations is exactly what is needed to further extend this work. However, we believe that the tests that we have developed so far, which make some simplifying assumptions that we think would often hold in practice, is a useful start to what is an entirely novel approach to inferring genetic architecture from family trait-only (non-genetic) data. Our work could already be useful for method developers who may wish to extend our approach in ways that we may not think of. It could also be useful for applied scientists focusing on specific traits who will be able to gain initial, inference-level, insights by applying our tests to their data, while the results of applying our tests may even guide study design of rare variant mapping studies.

In summary, I think this is a promising method that is revealing something interesting about extreme values of phenotypes. Determining exactly what is being revealed is going to take a lot more work, however. 

A.7: We thank the reviewer for highlighting the promise in our approach and agree that it is revealing something interesting about complex traits. We also agree that it is going to take a lot more work to reveal exactly what that is for different traits, which we plan to work on ourselves and hope that this paper will help other interested scientists to follow-up on and extend as well.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

R.1.1: Why these particular traits (body fat, mean corpuscular haemoglobin, neuroticism, heel bone mineral density, monocyte count, sitting height)? 

A.8: Traits were initially selected to cover a variety of traits (anthropometric, metabolic, personality..) and to illustrate different examples of tail architecture. However, in response to a point from reviewer 2 (see A.17), we have now overhauled our quality control of traits to ensure that only traits closely matching Gaussian distributions are included. In total, 18 traits were selected, with detailed results presented in Appendix 4 and results corresponding to 6 of the traits presented in the main text (Figure 6) to show examples of different types of tail architecture.

R.1.2: Why are there separate tests for de novo and Mendelian architectures? It seems that one could use either of the derived tests for both purposes, simply by switching to a two-sided test for each tail. My guess is that the score test of whether alpha is zero would be the more statistically powerful test. 

A.9: The score test of whether alpha is zero has limited power to detect Mendelian architectures. This is because under Mendelian effects, half the siblings in a family have trait values reflecting the background distribution, such that the mean of sibling trait values is not so different from the polygenic expectation (i.e. alpha close to 0). The Mendelian score test that we developed is substantially more powerful because it evaluates co-occurrence of siblings in the tails, which is far higher under Mendelian architecture in the tail than compared to polygenic architecture.

However, in order test for general departures from our null model, including those of non-Gaussian environmental factors, we now include results from performing a Kolmogorov-Smirnoff test of difference from the expected distribution, and also provide this test as an option in our ‘SibArc’ software tool.

R.1.3: This method assumes that assortative mating is absent. I worry that sitting height might not be a good trait to analyze, since there is some assortative mating (~0.3) for height (e.g., Yengo et al., 2018). Perhaps this trait should not be included among those that are analyzed in this paper. Then again, it is possible that there is less assortative mating for sitting height than total height (i.e., leg length) (Jensen & Sinha, 1993). 

A.10:  It is true that our method assumes random mating. We note that while  assortative mating increases sibling similarity relative to expectation, if it is stable across the trait distribution it will also bias heritability estimation upward which is likely it’s potential impact in our framework.  However, if assortative mating is more prevalent in the tails of the distribution, it can result in excess kurtosis – an impact that can increase false positive Mendelian tests and false negative de novo tests.  Given that the trait distribution for Sitting Height has only moderate excess Kurtosis (~0.4, see Fig 9, Appendix 4) and we inferred de novo architecture only for this trait, we feel that including it in the paper is appropriate. 

R.1.4: I wonder if it's possible to discuss the impact of non-additive genetic variance on the method. How does this affect the estimation of heritability, which calibrates the expectation for regression to the mean? Can non-additive genetic deviations explain a rejection of the null hypothesis of simple polygenicity? 

A.11: Yes, the heritability estimation, which calibrates expectation for regression to the mean, assumes additivity of effects, as do the most popular estimators of heritability from GWAS data in the field: GCTA-GREML, LD Score regression and LDAK. Accordingly, non-additive genetic effects could result in rejection of the null hypothesis. We have highlighted this point in the Discussion. However, we also point out that current evidence suggests that the contribution of non-additive genetic effects to complex trait variation is relatively small (Hivert 2021) and that non-additive genetic effects that have a similar impact across the trait distribution should not be a problem for our approach (only those that have an increasing effect towards the tails would be).

R.1.5: p.5: Maybe a more realistic way to simulate a genetic architecture is to draw the MAF from the distribution [MAF(1 - MAF)]^{-1} and then an effect of the minor allele from some mound-shaped distribution (e.g., mixture of normals). The absolute or squared effect of the minor allele should increases as the MAF decreases, and there have been some papers trying to estimate this relationship (e.g., Zeng et al., 2021). Maybe make the number of causal SNPs 10,000. I don't rate this as an urgent suggestion because my sense is that the method should be robust, making adequate even a fairly minimal simulation confirming its accuracy. 

A.11: In separate work, we have performed a comprehensive simulation study using the forward-in-time population genetic simulator SLIM-3 (Haller and Messer, 2019), which generates genetic effects according to Gaussian and Gamma distributions and models different selective pressures on complex traits. We plan to publish this work shortly and also extend the simulations to family data, from which we will be able to test the performance of our methods here under a range of different scenarios of genetic variation generation, including a variety of relationships between allele frequency and effect sizes. We agree with the reviewer that at this point, however, our minimal simulation should be sufficient to confirm our tests’ general robustness and so we will perform further testing once we have extended our more sophisticated simulation study.

R.1.6: p.6: Step D seems to leave out a normalization of G to have unit variance. Also, the last part should say "the square of the correlation between the genetic liability and the trait is equal to the heritability." 

A.12: Corrected – we thank the reviewer for spotting this.

R.1.7: Figure 5: The power being adequate if roughly 1 of a 1000 index siblings with an extreme trait value owes their values to de novo mutations makes me think that there should be a discussion of the prior probability. The average person carries about 80 de novo mutations. How many of these are likely to affect, e.g., height? Zeng et al. (2021) gave estimates of mutational targets. Given that a mutation affects height, will its likely effect size be large enough to be detected with the method? Kemper et al. (2012) discussed this point in a perhaps useful way. 

A.13: We find the work investigating mutational target sizes and generating effect sizes of different mutations (de novo or rare) to be extremely interesting and critical for understanding the causes of observed genetic variation. However, we think that this work is insufficiently progressed at this point to build on directly here for making more nuanced interpretation of our results. We are, however, exploring the impact of mutational target sizes, effect size distributions and selection effects, on the genetic architecture of complex traits via population genetic simulations (see A.11), and so we hope to be able to provide more in-depth interpretation of our results in the future.

R.1.8: Figure 6: The number in the tables for Mendelian architecture are presumably observed and expected counts. But what about the numbers for de novo architecture? Those don't look like counts. Maybe they are conditional expectations of standardized trait values. Whatever the case may be, the caption should provide an explanation. 

A.14: The observed and expected values for the de novo statistical test represent the expected and observed mean standardized trait values for siblings of individuals in the bottom and top 1% of the distribution. We have now made this clear in our updated figure.

R.1.9: p. 16: Element (2,1) in the precision matrix after Equation 15 is missing a negative sign. 

A.15: Corrected – we thank the reviewer for spotting this.

R.1.10: p. 20: Shouldn't Equation 20 place an exponent of n on the factor outside of the exponential? 

A.16: Corrected – we thank the reviewer for spotting this.

Reviewer #2 (Recommendations For The Authors):

R.2.1: The first concern that I have is that their statistical tests rely heavily on an assumption of bivariate normal distribution for sibling pair's phenotypes. Real phenotypes do not have such a distribution in general. The authors rely upon an inverse-normal transform when applying their method to real data. While the inverse-normal transform will ensure that the siblings' phenotypes have a marginal normal distribution, such a transform does not ensure that the joint distribution is bivariate normal. The authors should examine their procedure for simulated phenotypes with a non-normal distribution to see if their statistical tests remain properly calibrated. Related to this, I am concerned about applying an inverse normal transform to the neuroticism phenotype that contains only 13 unique values in UKB. How does the transform deal with tied values? Can we sensibly talk about extreme trait values for such a set of observations? 

A.17: The reviewer is correct that a bivariate normal distribution for sibling pairs’ trait values does not necessarily hold, and only does so if the assumptions of our null model are met (polygenic effects, Gaussian environmental effects, random mating..). We have now more clearly described the assumptions of our null model, and to increase the matching of our selected traits to those assumptions we have expanded our analyses and now present results on traits that are close to Gaussian. As part of this more strict quality control, only traits with more than 50 unique values are included, meaning that neuroticism is excluded in our final analysis. We also now note that performing an inverse normal transformation on the traits only increases the robustness of the tests to some of our modelling assumptions. In future work we plan to investigate how best to model the conditional sibling distribution under a variety of non-Gaussian environmental effects and different non-random patterns of mating.

R.2.2: The joint sibling phenotype distribution (Equation 4) can be derived by applying the formula for the conditional distribution of a multivariate Gaussian to the standard additive genetic model. The authors' derivation is unnecessarily complex. Furthermore, many of the formulae have been used in Shai Carmi's work on embryo screening, but this work is not cited. 

A.18: We now state in the text that the conditional sibling distribution can also be derived from the joint trait distribution of related individuals, which we use in our extension to the 3-sibling scenario, and cite Shai Carmi’s work where this is used. The joint distribution is a more straightforward way to derive the conditional sibling distribution, but our derivation based on considering mid-parents is generalisable to cases where assumptions of random mating, Gaussian population trait distribution and no selection do not hold. We also think that our mid-parent based derivation will be more intuitive to many readers, leading to greater understanding and potential for extension. Therefore, overall we believe that its presentation is worthwhile and we have now elaborated on this in the Methods.

R.2.3: Equation 8: this probability should be conditional on s1 

A.19: Corrected – we thank the reviewer for spotting this.

R.2.4: The empirical application to UKB data is lacking methodological details. Also, the number of siblings used is low compared to the number of available sibling pairs. Around 19k sibling pairs are available in the UKB white British subsample, but only 10k were used for height. Why? Also, why are extreme values excluded? Isn't this removing the signal the authors are looking to explain?

A.20: We have now provided more methodological details throughout the Methods section, in particular in relation to the samples used and quality control performed. The removal of individuals with extreme values, in particular, is because unusually low/high trait values are more likely to be due to measurement error (e.g. due to imperfect measuring device, or storage/assaying) than for typical values, and so while this may also result in some loss in power (albeit small due to few individuals having values +/- 8 s.d. trait means) we consider it worth it for the potential reduction in type I error. In performing our newly expanded analysis (described above), and accounting for the reviewer’s point here about sample size, we did find a bug in our pipeline that meant that we did not include as many sibling pairs as available. We thank the reviewer for spotting this, since this contributed to our new analysis being substantially more powerful than the original (including up to ~17k sibling pairs depending on completeness of trait data).

Benjamin C Haller, Phillip W Messer. SLiM 3: Forward Genetic Simulations Beyond the Wright–Fisher Model. Molecular Biology and Evolution. 2019. 36(3): 632-637.

SD Whiteman, SM McHale, A Soli. Theoretical Perspectives on Sibling Relationships. J Fam Theory Rev. 2011 Jun 1;3(2):124-139.

Nicholas H Barton, Alison M Etheridge, and Amandine Véber. The infinitesimal model: Definition, derivation, and implications. Theoretical population biology, 118:50–73, 2017.

Valentin Hivert et al. “Estimation of non-additive genetic variance in human complex traits from a large sample of unrelated individuals.” American journal of human genetics vol. 108,5 (2021)

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors demonstrate that it is possible to carry out eQTL experiments for the model eukaryote S. cerevisiae, in "one pot" preparations, by using single-cell sequencing technologies to simultaneously genotype and measure expression. This is a very appealing approach for investigators studying genetic variation in single-celled and other microbial systems, and will likely inspire similar approaches in non-microbial systems where comparable cell mixtures of genetically heterogeneous individuals could be achieved.

Strengths:

While eQTL experiments have been done for nearly two decades (the corresponding author's lab are pioneers in this field), this single-cell approach creates the possibility for new insights about cell biology that would be extremely challenging to infer using bulk sequencing approaches. The major motivating application shown here is to discover cell occupancy QTL, i.e. loci where genetic variation contributes to differences in the relative occupancy of different cell cycle stages. The authors dissect and validate one such cell cycle occupancy QTL, involving the gene GPA1, a G-protein subunit that plays a role in regulating the mating response MAPK pathway. They show that variation at GPA1 is associated with proportional differences in the fraction of cells in the G1 stage of the cell cycle. Furthermore, they show that this bias is associated with differences in mating efficiency.

Weaknesses:

While the experimental validation of the role of GPA1 variation is well done, the novel cell cycle occupancy QTL aspect of the study is somewhat underexploited. The cell occupancy QTLs that are mentioned all involve loci that the authors have identified in prior studies that involved the same yeast crosses used here. It would be interesting to know what new insights, besides the "usual suspects", the analysis reveals. For example, in Cross B there is another large effect cell occupancy QTL on Chr XI that affects the G1/S stage. What candidate genes and alleles are at this locus? And since cell cycle stages are not biologically independent (a delay in G1, could have a knock-on effect on the frequency of cells with that genotype in G1/S), it would seem important to consider the set of QTLs in concert.

We thank the reviewer for this suggested clarification. We have modified the text to make it clear that cell cycle occupancy is a compositional phenotype. Like the reviewer, we also noticed the distal trans eQTL hotspot on Chr XI in Cross B, but we were not able to identify compelling candidate gene(s) or variant(s) despite extensive effort.

Reviewer #2 (Public Review):

Boocock and colleagues present an approach whereby eQTL analysis can be carried out by scRNA-Seq alone, in a one-pot-shot experiment, due to genotypes being able to be inferred from SNPs identified in RNA-Seq reads. This approach obviates the need to isolate individual spores, genotype them separately by low-coverage sequencing, and then perform RNA-Seq on each spore separately. This is a substantial advance and opens up the possibility to straightforwardly identify eQTLs over many conditions in a cost-efficient manner. Overall, I found the paper to be well-written and well-motivated, and have no issues with either the methodological/analytical approach (though eQTL analysis is not my expertise), or with the manuscript's conclusions.

I do have several questions/comments.

393 segregant experiment:

For the experiment with the 393 previously genotyped segregants, did the authors examine whether averaging the expression by genotype for single cells gave expression profiles similar to the bulk RNA-Seq data generated from those genotypes? Also, is it possible (and maybe not, due to the asynchronous nature of the cell culture) to use the expression data to aid in genotyping for those cells whose genotypes are ambiguous? I presume it might be if one has a sufficient number of cells for each genotype, though, for the subsequent one-pot experiments, this is a moot point.

As mentioned in our preliminary response, while it is possible to expand the analysis along these lines, this is not relevant for the subsequent one-pot experiments. We have made all the data available so that anyone interested can try these analyses.

Figure 1B:

Is UMAP necessary to observe an ellipse/circle - I wouldn't be surprised if a simple PCA would have sufficed, and given the current discussion about whether UMAP is ever appropriate for interpreting scRNA-Seq (or ancestry) data, it seems the PCA would be a preferable approach. I would expect that the periodic elements are contained in 2 of the first 3 principal components. Also, it would be nice if there were a supplementary figure similar to Figure 4 of Macosko et al (PMID 26000488) to indeed show the cell cycle dependent expression.

We have added two new figures (S2 and S3) that represent alternative visualizations of the cell-cycle that are not dependent on UMAP. Figure S2 shows plots of different pairs of principal components, with each cell colored by its assigned cell-cycle stage. We do not observe a periodic pattern in the first 3 principal components as the reviewer expected, but when we explore the first 6 principal components, we see combinations of components that clearly separate the cell cycle clusters. We emphasize that the clusters were generated using the Louvain algorithm and assigned to cell-cycle stages using marker genes, and that UMAP was used only for visualization.

We could not create a figure similar to Macosko et al. because of differences between the cell cycle categories we used and those of Spellman et al (PMID 9843569). We instead created Figure S3 to address the reviewer's comment. This figure uses a heatmap in a style similar to that of Macosko et al. to display cell-cycle-dependent expression of the 22 genes we used as cell cycle markers across each of the five cell cycle stages (M/G1, G1, G1/S, S, G2/M).

We have renumbered the supplementary figures after incorporating these two additional supplementary figures into the manuscript.

Aging, growth rate, and bet-hedging:

The mention of bet-hedging reminded me of Levy et al (PMID 22589700), where they saw that Tsl1 expression changed as cells aged and that this impacted a cell's ability to survive heat stress. This bet-hedging strategy meant that the older, slower-growing cells were more likely to survive, so I wondered a couple of things. It is possible from single-cell data to identify either an aging, or a growth rate signature? A number of papers from David Botstein's group culminated in a paper that showed that they could use a gene expression signature to predict instantaneous growth rate (PMID 19119411) and I wondered if a) this is possible from single-cell data, and b) whether in the slower growing cells, they see markers of aging, whether these two signatures might impact the ability to detect eQTLs, and if they are detected, whether they could in some way be accounted for to improve detection.

As mentioned in our preliminary response, we are not sure how to look for gene expression signatures of aging in yeast scRNA-seq data. We believe that the proposed analyses are beyond the scope of the current paper. As noted above, we have made all the data available so that anyone interested can explore these hypotheses.

AIL vs. F2 segregants:

I'm curious if the authors have given thought to the trade-offs of developing advanced intercross lines for scRNA-Seq eQTL analysis. My impression is that AIL provides better mapping resolution, but at the expense of having to generate the lines. It might be useful to see some discussion on that.

We thank the reviewer for the comments. We believe that a discussion of trade-offs between different approaches for constructing mapping populations, such as AIL and F2 segregants, is beyond the scope of this paper.

10x vs SPLit-Seq

10x is a well established, but fairly expensive approach for scRNA-Seq - I wondered how the cost of the 10x approach compares to the previously used approach of genotyping segregants and performing bulk RNA-Seq, and how those costs would change if one used SPLiT-Seq (see PMID 38282330).

We thank the reviewer for the comments. We believe that a discussion of cost trade-offs between 10x and other approaches is beyond the scope of this paper, especially given the rapidly evolving costs of different technologies.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Throughout the results section the authors point to File S1 for additional information. This file is a tarball with about 20 Excel documents in it, each with several sheets embedded. The authors should provide a detailed README describing how to understand the organizations of the files in File S1 and the many embedded sheets in each file. Statements made in the manuscript about File S1 should explicitly direct the reader to a specific spreadsheet and table to refer to.

We have added an additional README file to the tarball that explains the organization of File S1 and describes the data contained in each sheet. Throughout the text, we now reference specific spreadsheets to assist the reader. In addition, these spreadsheets have been added to a github repository https://github.com/theboocock/finemapping_spreadsheets_single_cell

Neither of the two GitHub repositories referenced under "Code availability" has adequate documentation that would allow a reader to try and reproduce the analyses presented here. The one entitled https://github.com/joshsbloom/single_cell_eQTL has no functional README, while https://github.com/theboocock/yeast_single_cell_post_analysis is somewhat better but still hard to navigate. Basic information on expected inputs, file formats, file organization, output types, and formats, etc. is required to get any of these pipelines to run and should be provided at a minimum.

We thank the reviewer for the comment. In response, we have refactored both GitHub repositories and added extensive documentation to improve usability. We updated the versions of software and packages, this has been reflected in the methods section.

S. cerevisiae strains are preferentially diploid in nature and many genes involved in the mating pathway are differentially regulated in diploids vs haploids. Have the authors explored the fitness effects of the GPA1 82R allele in diploids? What is the dominance relationship between 82W and 82R?

We thank the reviewer for the comment. In diploid yeast, the mating pathway is repressed, and thus we would not expect there to be any fitness consequences due to the presence of different alleles of GPA1.

The diploid expression profiling (page 5 and Table S9) doesn't implicate GPA1; can you the authors comment on this in light of their finding in haploids?

The mating pathway, including GPA1, is repressed in diploids, and hence the expression of GPA1 cannot be studied in these strains (PMID: 3113739). In addition, allele-specific expression differences only identify cis-regulatory effects. We know that the GPA1 variant results in a protein-coding change, which may or may not influence the levels of mRNA in cis, so that even if GPA1 were expressed in diploids, there would be no expectation of an allele-specific difference in expression.

With respect to the candidate CYR1 QTL -- note that strains with compromised Cyr1 function also generally show increased sporulation rates and/or sporulation in rich media conditions (cAMP-PKA signaling represses sporulation). Is this the case in diploids with the CBS2888 allele at CYR1? If the CBS2888 allele is a CYR1 defect one might expect reduced cAMP levels. It is possible to estimate adenylate cyclase levels using a fairly straightforward ELISA assay. This would provide more convincing evidence of the causal mechanism of the alleles identified.

We thank the reviewer for the comment, and we agree that a functional study of the CYR1 alleles would provide more convincing evidence for the causal mechanism of the connection between cell cycle occupancy, cAMP levels, and growth. However, we believe that the proposed experiments are beyond the scope of our current study. The evidence we provide is sufficient to establish that CYR1 is a strong candidate gene for the eQTL hotspot.

Re: CYR1 candidate QTL -- The authors should reference the work of [Patrick Van Dijck] (https://pubmed.ncbi.nlm.nih.gov/?sort=date&term=Van+Dijck+P&cauthor_id= 20924200) and [Johan M Thevelein] (https://pubmed.ncbi.nlm.nih.gov/?sort=date&term=Thevelein+JM&cauth or_id=20924200) on CYR1 allelic variation, and other papers besides the Matsumoto/ Ishikawa papers, as the effects of cAMP-PKA signaling on stress can be quite variable. cAMP pathway variants, including in CYR1, have popped up in quite a few other yeast QTL mapping and experimental evolution papers. These should be referenced as well.

We thank the reviewer for these references; we have added a comment about the relationship between stress tolerance and CYR1 variation, and cited the relevant references accordingly.

Figure S10 - the subfigure showing the frequency of the GPA 82R compared to 82W suggests a fairly large and deleterious fitness effect of this allele; on the order of 7-8% fewer cells per cell cycle stage than the 82W allele. Can the authors reconcile this with the more modest growth rate effect they report on page 8?

Figure S12C displays the allele frequency of the 82R allele across the cell cycle in the single-cell data from allele-replacement strains. These strains were grown separately and processed using two individual 10x chromium runs. The resulting sequenced library had 11,695 cells with the 82R allele and 14,894 cells with the 82W allele. The 7-8% difference in the number of cells is due to slight differences in the number of captured cells per run, not due to growth differences, because we attempted to pool cells in equal numbers from separate mid-log cultures.

The proportion of cells in G1 increases by ~3% in strains with the 82R allele relative to the baseline proportion of cells in the experiment, which, to the reviewers point, is still larger than the ~1% growth difference we observed. Cell cycle occupancy is a compositional phenotype. As shown in figure S12C, the 82R variant increases the fraction of cells in G1 and slightly decreases the fraction of cells in M/G1. There is no obvious expectation for quantitatively translating a change in cell cycle occupancy to a change in growth rate.

The authors refer to the Lang et al. 2009 paper w/respect to GPA1 variant S469I but that paper seems to have explored a different GPA1 allele, GPA1-G1406T, with respect to growth rates.

We thank the reviewer for their comment. The S469I variant is the same as the G1406T variant, one denoting the amino acid change at position 469 in the protein and the other denoting the corresponding nucleotide change at position 1406 in the DNA coding sequence. We have altered the text to make this clear to the reader.

Reviewer #2 (Recommendations For The Authors):

I make no recommendations as to additional work for the authors. The manuscript is complete. I suggested some things I would like to see in my review, but it's up to them to decide whether they think any of those would further enhance the manuscript.

However, I do have I have some pedantic formatting notes:

- Microliters are variously presented as uL, ul, and µl - it should be µL

- Similarly, milliliters are presented as ml and ML - it should be mL

- Also, there should be a space between the number and the unit, e.g. 10 µL

- Some gene names in the manuscript are not italicized in all instances, e.g., GPA1

We thank the reviewer for these formatting suggestions, we have made these changes throughout the text.

Author response:

The following is the authors’ response to the original reviews.

Response to Public Reviews:

We thank the reviewers for their kind comments have implemented many of the suggestion their suggestions. Our paper has greatly benefited from their advice.  Like Reviewer 1, we acknowledge that while the exact involvement of Ih in allowing smooth transitions is likely not universal across all systems, our demonstration of the ways in which such currents can affect the dynamics of the response of complex rhythmic motor networks provides valuable insight. To address the concerns of Reviewer 2, we included a sentence in the discussion to highlight the fact that cesium neither increased the pyloric frequency nor caused consistent depolarization in intracellular recordings. We also highlighted that these observations suggest both that cesium is not indirectly raising [K+]outside and support the conclusion that the effects of cesium are primarily through blockade of Ih rather than other potassium channels.

Reviewer 3 raised some important points about modeling. While the lab has models that explore the effects of temperature on artificial triphasic rhythms, these models do not account for all the biophysical nuances of the full biological system. We have limited data about the exact nature of temperature-induced parameter changes and the extent to which these changes are mediated by intrinsic effects of temperature on protein structure versus protein interactions/modification by processes such as phosphorylation. With respects to the A current, Tang et al., 2010 reported that the activation and inactivation rates are differentially temperature sensitive but we do not have the data to suggest whether or not the time courses of such sensitivities are different. As such, we focus our discussion on the properties we know are modulated by temperature, i.e. activation rates. Within the discussion we now include the suggestion that future, more comprehensive modeling may be appropriate to further elucidate the ways in which reducing Ih may produce the here reported experimentally observed effects.

Reviewer #1 (Recommendations For The Authors):

Suggested revisions:

A figure showing examples of the voltage-clamp traces for the critical measurements of the extent of Ih block by 5 mM CsCl in PD and LP neurons at the temperature extremes in these preparations is not shown, and the authors should consider including such a figure, perhaps as a supplemental figure.

We have added Supplemental Figure 1 containing voltage-clamp traces demonstrating the extent of Ih block by 5mM CsCl in PD and LP neurons at 11 and 21°C.  Due to technical concerns, different preparations were used in the measurements at 11°C and 21°C, but the point that the H-current is reduced is demonstrated in all cases.

Reviewer #2 (Recommendations for The Authors):

Specific (Minor) Comments:

(1) Line 83: In Cs+ "at 11°C, the pyloric frequency was significantly decreased compared to control conditions (Saline: 1.2± 0.2 Hz; Cs+ 0.9± 0.2 Hz)".

As above, the authors often report that cesium generally reduces pyloric frequency. Figure 5A demonstrates this action quite nicely. However, cesium's effect on pyloric frequency at 11°C seems less robust in Figure 1C. Why the discrepancy?

There is variability in the effects of Cs+ on the pyloric frequency.  As noted, the standard deviation in frequency in both conditions is 0.2Hz.  As such, there are some cases in which the initial frequency drop in Cs+ compared to control was relatively small.  1C is one such case, but was selected as an example because of its clear reduction in temperature sensitivity. 

(2) I don't understand what the arrows/dashed lines are trying to convey in Figure 3C.

The arrows/dashed lines represent the criteria used to define a cycle as “decreasing in frequency” (Temperature Increasing) or “increasing in frequency” (Temperature Stable).  We have amended lines 130 and 137 in the text to hopefully clarify this point, as well as the figure legend.

(3) Lines 118/168. The description of cesium's specific action on the depolarizing portion of PD activity is a bit confusing. In my mind, "depolarization phase" refers to the point at which PD is most depolarized. Perhaps restating the phrase to "elongation of the depolarizing trajectory" is less confusing. The authors may also want to consider labeling this trajectory in Figure 2C.

We have changed “depolarization phase” to “depolarizing phase” to highlight that this is the period during which the cell is depolarizing, rather than at its most depolarized.  We consider the plateau of the slow wave and spiking (the point at which PD is most depolarized) to be the “bursting phase”.  We have labeled these phases in Figure 2C as suggested.

(4) Figure 3C legend: a few words seem to be missing. I suggest "the change in mean frequency was more likely TO decrease IN Cs+ than in saline".

Thank you for catching this typo, it has been corrected.

(5) Line 165: Awkward phrasing. “In one experiment, the decrease in frequency while temperature increased and subsequent increase in frequency after temperature stabilized was particularly apparent in Cs+ PTX”.

How about: “One Cs+ PTX experiment wherein elevating the temperature transiently decreased pyloric frequency is shown in Figure 4F.”

We have amended this sentence to read, “One Cs++PTX experiment in which elevating the temperature produced a particularly pronounced transient decrease in frequency is shown in Figure 4F.”

(6) Line 186: Awkward phrasing. "LP OFF was also significantly advanced in Cs+, although duty cycle (percent of the period a neuron is firing) was preserved".

The use of the word "although" seems a bit strange. If both LP onset and LP offset phase advance by the same amount, then isn't an unchanged duty cycle expected?

“Although” has been changed to “and subsequently”.

Reviewer #3 (Recommendations For The Authors):

Major comments:

(1) I know the Marder lab has detailed models of the pyloric rhythm. I am not saying they have to add modeling to this already extensive and detailed paper, but it would be useful to know how much of these temperature effects have been modeled, for example in the following locations.

(2) Line 259 - "Mathematically..." - Is there a computational model of H current that has shown this decrease in frequency in pyloric neurons? If you are working on one for the future, you could mention this.

There is not currently a model in which the reduction of the H-current results in the non-minimum phase dynamics in the frequency response to temperature seen experimentally. It should be noted that our existing models of pyloric activity responses to temperature are not well suited to investigate such dynamics in their current iterations.  Further work is necessary to demonstrate the principles observed experimentally in computational modeling, and we have added a sentence to the paper to reflect this point (Line 268).

(3) Line 318 - "therefore it remains unclear" - I thought they had models of the circuit rhythmicity. Do these models include temperature effects? Can they comment on whether their models of the circuit show an opposite effect to what they see in the experiment? I'm not saying they have to model these new effects as that is probably an entirely different paper, but it would be interesting to know whether current models show a different effect.

We have some models of the pyloric response to temperature, but these models were specifically selected to maintain phase across the range of temperature.  When Ih was reduced in these models, a variety of effects on phase and duty cycle were seen.  These models were selected to have the same key features of behavior as the pyloric rhythm, but do not capture all the biophysical nuances of the complete system, and therefore should not necessarily be expected to reflect the experimental findings in their current iterations.  Furthermore, these models are meant to have temperature as a static, rather than dynamic input, and thus are ill-suited to examine the conditions of our experiments.  The models in their current state are not sufficiently relevant to these experimental findings that we they can illuminate the present paper `2.

(4) "If deinactivation is more accelerated or altered by temperature than inactivation...While temperature continued to change, the difference in parameters would continue to grow" - This is described as a difference in temperature sensitivity, but it seems like it is also a function of the time course of the response to change in temperature (i.e. the different components could have the same final effect of temperature but show a different time course of the change).

We know from Tang et al, 2010, that activation and inactivation rates of the A current are differentially temperature sensitive. We have no evidence to suggest that the time course of the response to temperature of various parameters differ.  The physical actions of temperature on proteins are likely to be extremely rapid, making a time course difference on the order of tens of seconds less unlikely, though not impossible. Modeling of the biophysics might illuminate the relative plausibility of these different mechanisms of action, but we feel that our current suggested explanation is reasonable based on existing information.

(5) Is it known how temperature is altering these channel kinetics? Is it via an intrinsic rearrangement of the protein structure, or is it a process that involves phosphorylation (that could explain differences in time course?). Some mention of the mechanism of temperature changes would be useful to readers outside this field.

It is not known exactly how temperature alters channel parameters.  Invariably some, if not all, of it is due to an intrinsic rearrangement of protein structure, and our current models treat all parameter changes as an instantaneous consequence.  However, it is possible that some effects of temperature are due to longer timescale processes such as phosphorylation or cAMP interactions.  Current work in the lab is actively exploring these questions, but there is no definitive answer. Given that this paper focuses on the phenomenon and plausible biomolecular explanations based on existing data, we have not altered the paper to include more exhaustive  coverage of all the possible avenues by which temperature may alter channel properties.

Specific comments:

Title: misspelling of "Cancer" ?

We are unsure how that extra “w” got into the earliest version of the manuscript and have removed it.

Line 66 "We used 5mM CsCl" - might mention right up front that this was a bath application of the substance.

We have altered this line to read “used bath application of 5mM CsCl”.  

Figure 4 - "The only feedback synapse to the pacemaker kernel neurons, LP to PD, and is blocked by picrotoxin" - I think the word "and" should be removed from this phrase in the figure legend.

Fixed

Figure 4 legend - "Reds denote temperature...yellows denote..." - I think it should be "Red dots denote temperature...yellow dots denote...".

Done

Figure 4B - Why does the change in frequency in cesium look so different in Figure 4B compared to Figure 1C or Figure 3B? In the earlier figures, the increase of frequency is smaller but still present in cesium, whereas, in Figure 4B, cesium seems to completely block the increase in frequency. I'm not sure why this is different, but I guess it's because 3B and 4B are just mean traces from single experiments. Presumably, 4B is showing an experiment in which the cesium was subsequently combined with picrotoxin?

Figures 1C, 3B, and 4B are indeed all from different single experiments. As acknowledged in our concluding paragraph, there was substantial variability in the exact response of the pyloric rhythm to temperature while in cesium.  The most consistent effect was that the difference in frequency between cesium and saline at a particular temperature increased, as demonstrated across 21 preparations in Figure 1D. It may be noted in Figure 1E that the Q10 was not infrequently <1, meaning that there was a net decrease in frequency as temperature increased in some experiments such as seen in the example of Figure 4B.  The “fold over” (initial increase in steady-state frequency with temperature, then decrease at higher temperatures) has been observed at higher temperatures (typically around 23-30 degrees C) even under control conditions but has not been highlighted in previous publications.  The example in 4B was chosen because it demonstrated both the similarity in jags between Cs+ and Cs++PTX and an overall decrease in temperature sensitivity, even though in this instance the steady-state change in frequency with temperature was not monotonic. 

Figure 6A - "Phase 0 to 1.0" - The y-axis should provide units of phase. Presumably, these are units of radians so 1.0=2*pi radians (or 360 degrees, but probably best to avoid using degrees of phase due to confusion with degrees of temperature).

Phase, with respect to pyloric rhythm cycles, does not traditionally have units as it is a proportion rather than an angle. As such, we have not changed the figure.

Line 275 - "the pacemaker neuron can increase" - Does this indicate that the main effects of H current are in the follower neurons (i.e. LP and PY versus the driver neuron PD)?

Not necessarily.  We posit in the next paragraph that the effect of the H current on the temperature sensitivity could be due to its phase advance of LP, but that phase advance of LP is not particularly expected to increase frequency.  We favor the possibility that temperature increases Ih in the pacemaker, which in turn advances the PRC of the rhythm, allowing the frequency increase seen under normal conditions.  In Cs+, this advance does not occur, resulting in the lower temperature sensitivity.  In Cs++PTX, the lack of inhibition from LP means compensatory advance of the pacemaker PRC by Ih is unnecessary to allow increased frequency.

Line 285 - "either increase frequency have no effect" - Is there a missing "or" in this phrase?

Thank you, we have added the “or”.

Author response:

The following is the authors’ response to the current reviews.

Reviewer 2:

In addition, it is still unacceptable for me that the number of ovulated oocytes in mice at 6 months of age is only one third of young mice (10 vs 30; Fig. S1E). The most of published literature show that mice at 12 months of age still have ~10 ovulated oocytes.

We disagree with the reviewer’s comment, and the concerns raised were not shared by the other reviewers.  We have reported our data with full transparency (each data point is plotted). In the current study, we observed an intermediate phenotype in gamete number (assessed by both ovarian follicle counts and ovulated eggs) when comparing 6 month old mice to 6 week or 10 month old mice; this is as expected. It is well accepted that follicle counts are highly mouse strain dependent.  Although the reviewer mentions that mice at 12 months have ~10 ovulated oocytes, no actual references are provided nor are the mouse strain or other relevant experimental details mentioned.  Therefore, we do not know how these quoted metrics relate to the female FVB mice used in our current study.   As clearly explained and justified in our manuscript, we used mice at 6 months and 10 months to represent a physiologic aging continuum. 

Moreover, based on the follicle counting method used in the present study (Fig. S1D), there are no antral follicles observed in mice at 6 months and 10 months of age, which is not reasonable.

This statement is incorrect. Antral follicles were present at 6 and 10 months of age, but due to the scale of the y-axis and the normalization of follicle number/area in Fig. S1D, the values are small.  The absolute number of antral follicles per ovary (counted in every 5th section) was 31.3 ± 3.8 follicles for 6-week old mice, 9.3 ± 2.3 follicles for 6-month old mice, and 5.3 ± 1.8 follicles for 10-month old mice.  Moreover, it is important to note that these ovaries were not collected in a specific stage of the estrous cycle, so the number of antral follicles may not be maximal.  In addition, as described in the Materials and Methods, antral follicles were only counted when the oocyte nucleus was present in a section to avoid double counting.  Therefore, this approach (which was applied consistently across samples) could potentially underestimate the total number.

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript by Bomba-Warczak describes a comprehensive evaluation of long-lived proteins in the ovary using transgenerational radioactive labelled 15N pulse-chase in mice. The transgenerational labeling of proteins (and nucleic acids) with 15N allowed the authors to identify regions enriched in long-lived macromolecules at the 6 and 10-month chase time points. The authors also identify the retained proteins in the ovary and oocyte using MS. Key findings include the relative enrichment in long-lived macromolecules in oocytes, pregranulosa cells, CL, stroma, and surprisingly OSE. Gene ontology analysis of these proteins revealed enrichment for nucleosome, myosin complex, mitochondria, and other matrix-type protein functions. Interestingly, compared to other post-mitotic tissues where such analyses have been previously performed such as the brain and heart, they find a higher fractional abundance of labeled proteins related to the mitochondria and myosin respectively.

Response: We thank the reviewer for this thoughtful summary of our work.  We want to clarify that our pulse-chase strategy relied on a two-generation stable isotope-based metabolic labelling of mice using 15N from spirulina algae (for reference, please see (Fornasiero & Savas, 2023; Hark & Savas, 2021; Savas et al., 2012; Toyama et al., 2013)).  We did not utilize any radioactive isotopes.

Strengths:

A major strength of the study is the combined spatial analyses of LLPs using histological sections with MS analysis to identify retained proteins.

Another major strength is the use of two chase time points allowing assessment of temporal changes in LLPs associated with aging.

The major claims such as an enrichment of LLPs in pregranulosa cells, GCs of primary follicles, CL, stroma, and OSE are soundly supported by the analyses, and the caveat that nucleic acids might differentially contribute to this signal is well presented.

The claims that nucleosomes, myosin complex, and mitochondrial proteins are enriched for LLPs are well supported by GO enrichment analysis and well described within the known body of evidence that these proteins are generally long-lived in other tissues.

Weaknesses:

Comment 1: One small potential weakness is the lack of a mechanistic explanation of if/why turnover may be accelerating at the 6-10 month interval compared to 1-6.

Response 1: At the 6-month time point, we detected more long lived proteins than the 10 month time point in both the ovary and the oocyte.  We anticipated this because proteins are degraded over time, and substantially more time has elapsed at the later time point.  Moreover, at the 6–10-month time point, age-related tissue dysfunction is already evident in the ovary.  For example, in 6-9 month old mice, there is already a deterioration of chromosome cohesion in the egg which results in increased interkinetochore distances (Chiang et al., 2010), and by 10 months, there are multinucleated giant cells present in the ovarian stroma which is consistent with chronic inflammation (Briley et al., 2016).  Thus, the observed changes in protein dynamics may be another early feature of aging progression in the ovary.  

Comment 2: A mild weakness is the open-ended explanation of OSE label retention. This is a very interesting finding, and the claims in the paper are nuanced and perfectly reflect the current understanding of OSE repair. However, if the sections are available and one could look at the spatial distribution of OSE signal across the ovarian surface it would interesting to note if label retention varied by regions such as the CLs or hilum where more/less OSE division may be expected. 

Response 2: We agree that the enrichment of long-lived molecules in the OSE is interesting. To make interpretable conclusions about the dynamics of long-lived molecules in the OSE, we would need to generate a series of samples at precise stages of the estrous cycle or ideally across a timecourse of ovulation to capture follicular rupture and repair.  These samples do not currently exist and are beyond the scope of this study. However, this idea is an important future direction and it has been added to the discussion (lines 221-223). Furthermore, from a practical standpoint, MIMS imaging is resource and time intensive. Thus, we are not able to readily image entire ovarian sections.  Instead, we focused on structures within the ovary and took select images of follicles, stroma, and OSE.  We, therefore, do not have a comprehensive series of images of the OSE from the entire ovarian section for each mouse analyzed.

Reviewer #2 (Public Review):

Summary:

The manuscript by Bomba-Warczak et al. applied multi-isotope imaging mass spectrometry (MIMS) analysis to identify the long-lived proteins in mouse ovaries during reproductive aging, and found some proteins related to cytoskeletal and mitochondrial dynamics persisting for 10 months.

Response: We thank the reviewer for their summary and feedback.

Strengths:

The manuscript provides a useful dataset about protein turnover during ovarian aging in mice.

Weaknesses:

Comment 1: The study is pretty descriptive and short of further new findings based on the dataset. In addition, some results such as the numbers of follicles and ovulated oocytes in aged mice are not consistent with the published literature, and the method for follicle counting is not accurate. The conclusions are not fully supported by the presented evidence.

Response 1: We agree with the reviewer that this study is descriptive. Our goal, as stated, was to use a discovery-based approach to define the long-lived proteome of the ovary and oocyte across a reproductive aging continuum.  As the prominent aging researcher, Dr. James Kirkland, stated: “although ‘descriptive’ is sometimes used as a pejorative term…descriptive or discovery research leading to hypothesis generation has become highly sophisticated and of great relevance to the aging field (Kirkland, 2013).”  We respectfully disagree with the reviewer that our study is short of new findings. In fact, this is the first time that a stable two-generation stable isotope-based metabolic labelling of mice in combination with two different state-of-the-art mass spectrometry methods has been used to identify and localize long lived molecules in the ovary and oocyte along this particular reproductive aging continuum in an unbiased manner.  We have identified proteins groups that were previously not known to be long lived in the ovary and oocyte.  Our hope is that this long-lived proteome will become an important hypothesis-generating resource for the field of reproductive aging.

The age-dependent decline in number of follicles and eggs ovulated in mice has been well established by our group as well as others (Duncan et al., 2017; Mara et al., 2020).  Thus, we are unclear about the reviewer’s comments that our results are not consistent with the published literature.  The absolute numbers of follicles and eggs ovulated as well as the rate of decline with age are highly strain dependent.  Moreover, mice can have a very small ovarian reserve and still maintain fertility (Kerr et al., 2012).  In our study, we saw a consistent age-dependent decrease in the ovarian reserve (Figure 1 – figure supplement 1 D), the number of oocytes collected from large antral follicles following hyperstimulation with PMSG (used for LC-MS/MS), and the number of eggs collected from the oviduct following hyperstimulation and superovulation with PMSG and hCG (Figure 1 – figure supplement 1 E and F).  In all cases, the decline was greater in 10 month old compared to 6 month old mice demonstrating a relative reproductive aging continuum even at these time points.

Our research team has significant expertise in follicle classification and counting as evidenced by our publication record (Duncan et al., 2017; Kimler et al., 2018; Perrone et al., 2023; Quan et al., 2020).  We used our established methods which we have further clarified in the manuscript text (lines 395-397).  Follicle counts were performed on every 5th tissue section of serial sectioned ovaries, and 1 ovary from 3 mice per timepoint were counted. Therefore, follicle counts were performed on an average of 48-62 total sections per ovary. The number of follicles was then normalized per total area (mm2) of the tissue section, and the counts were averaged. Figure 1 – figure supplement 1 C and D represents data averaged from all ovarian sections counted per mouse.   It is important to note that the same criteria were applied consistently to all ovaries across the study, and thus regardless of the technique used, the relative number of follicles or oocytes across ages can be compared.

Reviewer #3 (Public Review):

Summary:

In this study, Bomba-Warczak et al focused on reproductive aging, and they presented a map for long-lived proteins that were stable during reproductive lifespan. The authors used MIMS to examine and show distinct molecules in different cell types in the ovary and tissue regions in a 6 month mice group, and they also used proteomic analysis to present different LLPs in ovaries between these two timepoints in 6-month and 10-month mice. The authors also examined the LLPs in oocytes in the 6-months mice group and indicated that these were nuclear, cytoskeleton, and mitochondria proteins.

Response: We thank the reviewer for their summary and feedback.

Strengths:

Overall, this study provided basic information or a 'map' of the pattern of long-lived proteins during aging, which will contribute to the understanding of the defects caused by reproductive aging.

Weaknesses:

Comment 1: The 6-month mice were used as an aged model; no validation experiments were performed with proteomics analysis only.  

Response 1:  We did not select the 6-month time point to be representative of the “aged model” but rather one of two timepoints on the reproductive aging continuum – 6 and 10 months.  In the manuscript (Figure 1 – figure supplement 1) we have demonstrated the relevance of the two timepoints by illustrating a decrease in follicle counts, number of fully grown oocytes collected, and number of eggs ovulated as well as a tendency towards increased stromal fibrosis (highlighted in the main text lines 78-85).  Inclusion of the 6-month timepoint ultimately turned out to be informative and essential as many long-lived proteins were absent by the 10 month timepoint. These results suggest that important shifts in the proteome occur during mid to advanced reproductive age.  The relevance of these timepoints is mentioned in the discussion (lines 247-270).

Two independent mass spectrometry approaches (MIMS and LC-MS/MS) were used to validate the presence of long-lived macromolecules in the ovary and oocyte. Studies focused on the role of specific long-lived proteins in oocyte and ovarian biology as well as how they change with age in terms of function, turnover, and modification are beyond the scope of the current study but are ongoing.  We have acknowledged these important next steps in the manuscript text (lines 286-288, 311-312).

It is important to note, that oocytes are biomass limited cells, and their numbers decrease with age.  Thus, we had to select ages where we could still collect enough from the mice available to perform LC-MS/MS. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Comment 1: The writing and figures are beautiful - it would be hard to improve this manuscript.

Response 1: We greatly appreciate this enthusiastic evaluation of our work.

Comment 2: In Fig S1E/F it would help to list the N number here. Why are there 2 groups at 6-12 wk?

Response 2:  We did not have 6 month and 10-month-old mice available at the same time to be able to run the hyperstimulation and superovulation experiment in parallel.  Therefore, we performed independent experiments comparing the number of eggs collected from either 6-month-old or 10 month old mice relative to 6-12 week old controls.  In each trial, eggs were collected from pooled oviducts from between 3-4 mice per age group, and the average total number of eggs per mouse was reported.  Each point on the graph corresponds to the data from an individual trial, and two trials were performed.  This has been clarified in the figure legend (lines 395-397).  Of note, while addressing this reviewer’s comments, we noticed that we were missing Materials and Methods regarding the collection of eggs from the oviduct following hyperstimulation and superovulation with PMSG and hCG.  This information has now been added in Methods Section, lines 477-481.

Comment 3: The manuscript would benefit from an explanation of why the pups were kept on a 1-month N15 diet after birth, since the oocytes are already labeled before birth, and granulosa at most by day 3-4. Would ZP3 have not been identified otherwise?

Response 3:   The pups used in this study were obtained from fully labeled female dams that were maintained on an15N diet.  These pups had to be kept with their mothers through weaning.  To limit the pulse period only through birth, the pups would have had to be transferred to unlabeled foster mothers.  However, this would have risked pup loss which would have significantly impacted our ability to conduct the studies given that we only had 19 labeled female pups from three breeding pairs.  We have clarified this in the manuscript text in lines 78-80.  It is hard to know, without doing the experiment, whether we would have detected ZP3 if we only labeled through birth.  The expression of ZP3 in primordial follicles, albeit in human, would suggest that this protein is expressed quite early in development.

Comment 4: What is happening to the mitochondria at 6-10 months? Does their number change in the oocyte? Is there a change in the rate of fission? Any chance to take a stab at it with these or other age-matched slides?

Response 4:  The reviewer raises an excellent point.  As mentioned previously in the Discussion (lines 290-301), there are well documented changes in mitochondrial structure and function in the oocyte in mice of advanced reproductive age.  However, there is a paucity of data on the changes that may happen at earlier mid-reproductive age time points.  From the oocyte mitochondrial proteome perspective, our data demonstrate a prominent decline in the persistence of long-lived proteins between 6 and 10 months, and this occurs in the absence of a change in the total pool of mitochondrial proteins (both long and short lived populations) as assessed by spectral counts or protein IDs (figure below).  These data, which we have added into Figure 3 – figure supplement 1 and in the manuscript text (lines 164-170) are suggestive of similar numbers of mitochondria at these two timepoints. It would be informative to do a detailed characterization of oocyte mitochondrial structure and function within this window to see if there is a correlation with this shift in long lived mitochondrial proteins.  Although this analysis is beyond the scope of the current manuscript, it is an important next line of inquiry which we have highlighted in the manuscript text (lines 255-257 and 311-312).

Reviewer #2 (Recommendations For The Authors):

Several concerns are raised as shown below.

Comment 1: In Fig. 2F, it is surprising that ZP3 disappeared in the ovary from mice at the age of 10 months by MIMS analysis, because quite a few oocytes with intact zona pellucida can still be obtained from mice at this age. Notably, ZP would not be renewed once formed.

Response 1: To clarify, Figure 2F shows LC-MS/MS data and not MIMS data.  As mentioned in the Discussion, the detection of long-lived pools of ZP3 at 6 months cannot be derived from newly synthesized zona pellucidae in growing follicles because they would not have been present during the pulse period.  The only way we could detect ZP3 at 6 months is if it forms a primitive zona scaffold in the primordial follicle or if ZPs from atretic follicles of the first couple of waves of folliculogenesis incorporate into the extracellular matrix of the ovary.  The lack of persistence of ZP3 at 10 months could be due to protein degradation. Should ZP3 indeed form a primitive zona, its loss at 10 months would be predicted to result in poor formation of a bona fide zona pellucida upon follicle growth.  Interestingly, aging has been associated with alterations in zona pellucida structure and function.   These data open novel hypotheses regarding the zona pellucida (e.g. a primitive zona scaffold and part of the extracellular matrix) and will require significant further investigation to test. These points are highlighted in the Discussion lines 227-245.

Comment 2: To determine whether those proteins that can not be identified by MIMS at the time point of 10 months are degraded or renewed, the authors should randomly select some of them to examine their protein expression levels in the ovary by immunoblotting analysis.

Response 2: To clarify, proteins were identified by LC-MS/MS and not MIMS which was used to visualize long lived macromolecules.   Each protein will be comprised of old pools (15N containing) and newly synthesized pools (14N containing).  Degradation of the old pool of protein does not mean that there will be a loss of total protein.  Moreover, immunoblotting cannot distinguish old and newly synthesized pools of protein. Where overall peptide counts are listed for each protein identified at both time points.  As peptides derive from proteins, the table provided with the manuscript reflects what immunoblotting would, but on a larger and more precise scale.

Comment 3: I think those proteins that can be identified by MIMS at the time point of 6 months but not 10 months deserve more analyses as they might be the key molecules that drive ovarian aging.

Response 3:  This comment conflicts with comment 2 from Reviewer #3 (Recommendations For The Authors).  This underscores that different researchers will prioritize the value and follow up of such rich datasets differently.  We agree that the LLP identified at 6 months are of particular interest to reproductive aging, and we are planning to follow up on these in future studies.

Comment 4:  Figure 1 – figure supplement 1 C-F, compared with the published literature, the numbers of follicles at different developmental stages and ovulated oocytes at both ages of 6 months and 10 months were dramatically low in this study. For 6-month-old female mice, the reproductive aging just begins, thus these numbers should not be expected to decrease too much. In addition, follicle counting was carried out only in an area of a single section, which is an inaccurate way, because the numbers and types of follicles in various sections differ greatly. Also, the data from a single section could not represent the changes in total follicle counts.

Response 4: We have addressed these points in response to Comment 1 in the Reviewer #2 Public Review, and corresponding changes in the text have been noted.    

Comment 5:  The study lacks follow-up verification experiments to validate their MIMS data.

Response 5: Two independent mass spectrometry approaches (MIMS and LC-MS/MS) were used to validate the presence of long-lived macromolecules in the ovary and oocyte. Studies focused on the role of specific long-lived proteins in oocyte and ovarian biology as well as how they change with age in terms of function, turnover, and modification are beyond the scope of the current study but ongoing.  We have acknowledged these important next steps in the manuscript text (lines 286-288 and 311-312).

Reviewer #3 (Recommendations For The Authors):

Comment 1: The authors used the 6-month mice group to represent the aged model, and examined the LLPs from 1 month to 6 months. Indeed, 6-month-old mice start to show age-related changes; however, for the reproductive aging model, the most widely accepted model is that 10-month-old age mice start to show reproductive-related changes and 12-month-old mice (corresponding to 35-40 year-old women) exhibit the representative reproductive aging phenotypes. Therefore, the data may not present the typical situation of LLPs during reproductive aging.

Response 1: As described in the response to Comment 1 in the Reviewer #3 Public Review, there were clear logistical and technical feasibility reasons why the 6 month and 10-month timepoints were selected for this study.  Importantly, however, these timepoints do represent a reproductive aging continuum as evidenced by age-related changes in multiple parameters.  Furthermore, there were ultimately very few LLPs that remained at 10 months in both the oocyte and ovary, so inclusion of the 6-month time point was an important intermediate.  Whether the LLPs at the 6-month timepoint serve as a protective mechanism in maintaining gamete quality or whether they contribute to decreased quality associated with reproductive aging is an intriguing dichotomy which will require further investigation.  This has been added to the discussion (lines 247-257).

Comment 2:  Following the point above, the authors examined the ovaries in 6 months and 10 months mice by proteomics, and found that 6 months LLPs were not identical compared with 10 months, while there were Tubb5, Tubb4a/b, Tubb2a/b, Hist2h2 were both expressed at these two time points (Fig 2B), why the authors did not explore these proteins since they expressed from 1 month to 10 months, which are more interesting.

Response 2:  The objective of this study was to profile the long-lived proteome in the ovary and oocyte as a resource for the field rather than delving into specific LLPs at a mechanistic level.  That being said, we wholeheartedly agree with the reviewer that the proteins that were identified at both 6 month and 10 months are the most robust and long lived and worthy of prioritizing for further study.  Interestingly, Tubb5 and Tubb4a have high homology to primate-specific Tubb8, and Tubb8 mutations in women are associated with meiosis I arrest in oocytes and infertility (Dong et al., 2023; Feng et al., 2016).  Thus, perturbation of these specific proteins by virtue of their long-lived nature may be associated with impaired function and poor reproductive outcomes.  We have highlighted the importance of these LLPs which are present at both timepoints and persist to at least 10 months in the manuscript text (lines 259-270).

Comment 3:  The authors also need to provide a hypothesis or explanation as to why LLDs from 6 months LLPs were not identical compared with 10 months.

Response 3:  We agree that LLDs identified at 10 months should be also identified as long-lived at 6 months. This is a common limitation of mass spectrometry-based proteomics where each sample is prepared and run individually, which introduces variability between biological replicates, especially when it comes to low abundant proteins. It is key to note that just because we do not identify a protein, it does not mean the protein is not there – it merely means that we were not able to detect it in this particular experiment, but low levels of the protein may still be there. To compensate for this known and inherent variability, we have applied stringent filtering criteria where we required long-lived peptides to be identified in an independent MS scan (alternative is to identify peptide in either heavy or light scan and use modeling to infer FA value based on m/z shift), which gave us peptides of highest confidence. Ideally, these experiments would be done using TMT (tandem mass tag) approach. However, TMT-based experiments typically require substantial amount of input (80-100ug per sample) which unfortunately is not feasible with oocytes obtained from a limited number of pulse-chased animals.  We have added this explanation to the discussion (lines 265-270).

Comment 4:  The reviewer thinks that LLPs from 6 months to 10 months may more closely represent the long-lived proteins during reproductive aging.

Response 4:  We fully agree that understanding the identity of LLPs between the 6 month and 10 month period will be quite informative given that this is a dynamic period when many of LLPs get degraded and thus might be key to the observed decline in reproductive aging. This is a very important point that we hope to explore in future follow-up studies.

Comment 5: The authors used proteomics for the detection of ovaries and oocytes, however, there are no validation experiments at all. Since proteomics is mainly for screening and prediction, the authors should examine at least some typical proteins to confirm the validity of proteomics. For example, the authors specifically emphasized the finding of ZP3, a protein that is critical for fertilization.

Response 5:  Thank you, we agree that closer examination of proteins relevant and critical for fertilization is of importance.  However, a detailed analysis of specific proteins fell outside of the scope of this study which aimed at unbiased identification of long-lived macromolecules in ovaries and oocytes. We hope to continue this important work in near future.

Comment 6: For the oocytes, the authors indicated that cytoskeleton, mitochondria-related proteins were the main LLPs, however, previous studies reported the changes of the expression of many cytoskeleton and mitochondria-related proteins during oocyte aging. How do the authors explain this contrary finding?   

Response 6:  Our findings are not contrary to the studies reporting changes in protein expression levels during oocyte aging – the two concepts are not mutually exclusive. The average FA value at 6-month chase for oocyte proteins is 41.3 %, which means that while 41.3% of long-lived proteins pool persisted for 6 months, the other 58.7% has in fact been renewed. With the exception of few mitochondrial proteins (Cmkt2 and Apt5l), and myosins (Myl2 and Myh7), which had FA values close to 100% (no turnover), most of the LLPs had a portion of protein pools that were indeed turned over. Moreover, we included new data analysis illustrating that we identify comparable number of mitochondrial proteins between the two time points, indicating that while the long-lived pools are changing over time, the total content remains stable (Figure 3 – figure supplement 1E-G).

Comment 7:  The authors also should provide in-depth discussion about the findings of the current study for long-lived proteins. In this study, the authors reported the relationship between these "long-lived" proteins with aging, a process with multiple "changes". Do long-lived proteins (which are related to the cytoskeleton and mitochondria) contribute to the aging defects of reproduction? or protect against aging?

Response 7: This is a very important comment and one that needs further exploration. The fact is – we do not know at this moment whether these proteins are protective or deleterious, and such a statement would be speculative at this stage of research into LLPs in ovaries and oocytes. Future work is needed to address this question in detail.

Briley, S. M., Jasti, S., McCracken, J. M., Hornick, J. E., Fegley, B., Pritchard, M. T., & Duncan, F. E. (2016). Reproductive age-associated fibrosis in the stroma of the mammalian ovary. Reproduction, 152(3), 245-260. https://doi.org/10.1530/REP-16-0129

Chiang, T., Duncan, F. E., Schindler, K., Schultz, R. M., & Lampson, M. A. (2010). Evidence that Weakened Centromere Cohesion Is a Leading Cause of Age-Related Aneuploidy in Oocytes. Current Biology, 20(17), 1522-1528. https://doi.org/10.1016/j.cub.2010.06.069

Dong, J., Jin, L., Bao, S., Chen, B., Zeng, Y., Luo, Y., Du, X., Sang, Q., Wu, T., & Wang, L. (2023). Ectopic expression of human TUBB8 leads to increased aneuploidy in mouse oocytes. Cell Discov, 9(1), 105. https://doi.org/10.1038/s41421-023-00599-z

Duncan, F. E., Jasti, S., Paulson, A., Kelsh, J. M., Fegley, B., & Gerton, J. L. (2017). Age-associated dysregulation of protein metabolism in the mammalian oocyte. Aging Cell, 16(6), 1381-1393. https://doi.org/10.1111/acel.12676

Feng, R., Sang, Q., Kuang, Y., Sun, X., Yan, Z., Zhang, S., Shi, J., Tian, G., Luchniak, A., Fukuda, Y., Li, B., Yu, M., Chen, J., Xu, Y., Guo, L., Qu, R., Wang, X., Sun, Z., Liu, M., . . . Wang, L. (2016). Mutations in TUBB8 and Human Oocyte Meiotic Arrest. N Engl J Med, 374(3), 223-232. https://doi.org/10.1056/NEJMoa1510791

Fornasiero, E. F., & Savas, J. N. (2023). Determining and interpreting protein lifetimes in mammalian tissues. Trends Biochem Sci, 48(2), 106-118. https://doi.org/10.1016/j.tibs.2022.08.011

Hark, T. J., & Savas, J. N. (2021). Using stable isotope labeling to advance our understanding of Alzheimer's disease etiology and pathology. J Neurochem, 159(2), 318-329. https://doi.org/10.1111/jnc.15298

Kerr, J. B., Hutt, K. J., Michalak, E. M., Cook, M., Vandenberg, C. J., Liew, S. H., Bouillet, P., Mills, A., Scott, C. L., Findlay, J. K., & Strasser, A. (2012). DNA damage-induced primordial follicle oocyte apoptosis and loss of fertility require TAp63-mediated induction of Puma and Noxa. Mol Cell, 48(3), 343-352. https://doi.org/10.1016/j.molcel.2012.08.017

Kimler, B. F., Briley, S. M., Johnson, B. W., Armstrong, A. G., Jasti, S., & Duncan, F. E. (2018). Radiation-induced ovarian follicle loss occurs without overt stromal changes. Reproduction, 155(6), 553-562. https://doi.org/10.1530/REP-18-0089

Kirkland, J. L. (2013). Translating advances from the basic biology of aging into clinical application. Exp Gerontol, 48(1), 1-5. https://doi.org/10.1016/j.exger.2012.11.014

Mara, J. N., Zhou, L. T., Larmore, M., Johnson, B., Ayiku, R., Amargant, F., Pritchard, M. T., & Duncan, F. E. (2020). Ovulation and ovarian wound healing are impaired with advanced reproductive age. Aging (Albany NY), 12(10), 9686-9713. https://doi.org/10.18632/aging.103237

Perrone, R., Ashok Kumaar, P. V., Haky, L., Hahn, C., Riley, R., Balough, J., Zaza, G., Soygur, B., Hung, K., Prado, L., Kasler, H. G., Tiwari, R., Matsui, H., Hormazabal, G. V., Heckenbach, I., Scheibye-Knudsen, M., Duncan, F. E., & Verdin, E. (2023). CD38 regulates ovarian function and fecundity via NAD(+) metabolism. iScience, 26(10), 107949. https://doi.org/10.1016/j.isci.2023.107949

Quan, N., Harris, L. R., Halder, R., Trinidad, C. V., Johnson, B. W., Horton, S., Kimler, B. F., Pritchard, M. T., & Duncan, F. E. (2020). Differential sensitivity of inbred mouse strains to ovarian damage in response to low-dose total body irradiationdagger. Biol Reprod, 102(1), 133-144. https://doi.org/10.1093/biolre/ioz164

Savas, J. N., Toyama, B. H., Xu, T., Yates, J. R., 3rd, & Hetzer, M. W. (2012). Extremely long-lived nuclear pore proteins in the rat brain. Science, 335(6071), 942. https://doi.org/10.1126/science.1217421

Toyama, B. H., Savas, J. N., Park, S. K., Harris, M. S., Ingolia, N. T., Yates, J. R., 3rd, & Hetzer, M. W. (2013). Identification of long-lived proteins reveals exceptional stability of essential cellular structures. Cell, 154(5), 971-982. https://doi.org/10.1016/j.cell.2013.07.037

Author response:

The following is the authors’ response to the original reviews.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

This is a fine paper that serves the purpose to show that the use of light sheet imaging may be used to provide whole brain imaging of axonal projections. The data provided suggest that at this point the technique provides lower resolution than with other techniques. Nonetheless, the technique does provide useful, if not novel, information about particular brain systems. 

Strengths: 

The manuscript is well written. In the introduction a clear description of the functional organization of the barrel cortex is provided provides the context for applying the use of specific Cre-driver lines to map the projections of the main cortical projection types using whole brain neuroanatomical tracing techniques. The results provided are also well written, with sufficient detail describing the specifics of how techniques were used to obtain relevant data. Appropriate controls were done, including the identification of whisker fields for viral injections and determination of the laminar pattern of Cre expression. The mapping of the data provides a good way to visualize low resolution patterns of projections. 

Weaknesses: 

(1) The results provided are, as stated in the discussion, "largely in agreement with previously reported studies of the major projection targets". However it must be stated that the study does not "extend current knowledge through the high sensitivity for detecting sparse axons, the high specificity of labeling of genetically defined classes of neurons and the brain wide analysis for assigning axons to detailed brain regions" which have all been published in numerous other studies. ( the allen connectivity project and related papers, along with others). If anything the labeling of axons obtained with light sheet imaging in this study does not provide as detailed mapping obtained with other techniques. Some detail is provided of how the raw images are processed to resolve labeled axons, but the images shown in the figures do not demonstrate how well individual axons may be resolved, of particular interest would be to see labeling in terminal areas such as other cortical areas, striatum and thalamus. As presented the light sheet imaging appears to be rather low resolution compared to the many studies that have used viral tracing to look at cortical projections from genetically identified cortical neurons. 

We agree with the reviewer that the resolution of imaging should be further improved in future studies, as also mentioned in the original manuscript. On P. 17 of the revised manuscript we write “Probably most important for future studies is the need to increase the light-sheet imaging resolution perhaps combined with the use of expansion microscopy to provide brain-wide micron-resolution data (Glaser et al., 2023; Wassie et al., 2019).” However, even at somewhat lower resolution, through bright sparse labelling, individual axonal segments can nonetheless be traced through machine learning to define axonal skeletons, whose length can be quantified as we do in this study. This methodology highlights sparse wS1 and wS2 innervation of a large number of brain areas, some of which are not typically considered, and our anatomical results might therefore help the neuronal circuit analysis underlying various aspects of whisker sensorimotor processing. Despite impressive large-scale projection mapping projects such as the Allen connectivity atlas, there remains relatively sparse cell typespecific projection map data for the representations of the large posterior whiskers in wS1 and wS2, and our data in this study thus adds to a growing body of cell-type specific projection mapping with the specific focus on the output connectivity of these whisker-related neocortical regions of sensory cortex.

In the revised manuscript, we now provide an additional supplementary figure (Figure 1 – figure supplement 2) showing examples of the axonal segmentation from further additional image planes including branching axons in the key innervation regions mentioned by the reviewer, namely “other cortical areas, striatum and thalamus”.

(2) Amongst the limitations of this study is the inability to resolve axons of passage and terminal fields. This has been done in other studies with viral constructs labeling synaptophysin. This should be mentioned. 

The reviewer brings up another important point for future methodological improvements to enhance connectivity mapping. Indeed, we already mentioned this in our original submission near the end of the first paragraph under the Limitations and future perspectives section. In the revised manuscript on P. 17, we write “Future studies should also aim to identify neurotransmitter release sites along the axon, which could be achieved by fluorescent labeling of prominent synaptic components, such as synaptophysin-GFP (Li et al., 2010).”

(3) There is no quantitative analysis of differences between the genetically defined neurons projecting to the striatum, what is the relative area innervated by, density of terminals, other measures. 

The reviewer raises an interesting question, and in the revised manuscript, we now present a more detailed analysis of cell class-specific axonal projections focusing specifically on the striatum. Following the reviewer’s suggestion, in a new supplementary figure (Figure 7 – figure supplement 1), we now report spatial axonal density maps in the striatum from SSp-bfd and SSs, finding potentially interesting differences comparing the projections of Rasgrf2-L2/3, Scnn1a-L4 and Tlx3-L5IT neurons. On P. 12 of the revised manuscript, we now write “We also investigated the spatial innervation pattern of Rasgrf2-L2/3, Scnn1a-L4 and Tlx3-L5IT neurons in the striatum (Figure 7 – figure supplement 1), where we found that axonal density from Rasgrf2-L2/3 neurons in both SSp-bfd and SSs was concentrated in a posterior dorsolateral part of the ipsilateral striatum, whereas Tlx3-L5IT neurons had extensive axonal density across a much larger region of the striatum, including bilateral innervation by SSp-bfd neurons. Striatal innervation by Scnn1a-L4 neurons was intermediate between Rasgrf2-L2/3 and Tlx3-L5IT neurons.” We think the reviewer’s comment has helped reveal further interesting aspects of our data set, and we thank the reviewer.

(4) Figure 5 is an example of the type of large sets of data that can be generated with whole brain mapping and registration to the Allen CCF that provides information of questionable value. Ordering the 50 plus structures by the density of labeling does not provide much in terms of relative input to different types of areas. There are multiple subregions for different functional types ( ie, different visual areas and different motor subregions are scattered not grouped together. Makes it difficult to understand any organizing principles.

We agree with the reviewer, and fully support the importance of considering subregions within the relatively coarse compartmentalization of the current Allen CCF. In order to provide some further information about connectivity that may help give the reader further insights into the data, we have now added further quantification of cortex-specific axonal density ranked according to functional subregions in a new supplementary figure (Figure 5 – figure supplement 2). 

(5) The GENSAT Cre driver lines used must have the specific line name used, not just the gene name as the GENSAT BAC-Cre lines had multiple lines for each gene and often with very different expression patterns. Rbp4_KL100, Tlx3_PL56, Sim1_KJ18, Ntsr1_ GN220. 

In the revised manuscript, we now write out a fuller description of the mouse lines the first time they are mentioned in the Results section on P. 7. The full mouse line names, accession numbers and references were of course already described in the methods section, which remains the case in the revised manuscript.

Reviewer #2 (Public Review): 

Summary: 

This study takes advantage of multiple methodological advances to perform layer-specific staining of cortical neurons and tracking of their axons to identify the pattern of their projections. This publication offers a mesoscale view of the projection patterns of neurons in the whisker primary and secondary somatosensory cortex. The authors report that, consistent with the literature, the pattern of projection is highly different across cortical layers and subtype, with targets being located around the whole brain. This was tested across 6 different mouse types that expressed a marker in layer 2/3, layer 4, layer 5 (3 sub-types) and layer 6.  Looking more closely at the projections from primary somatosensory cortex into the primary motor cortex, they found that there was a significant spatial clustering of projections from topographically separated neurons across the primary somatosensory cortex. This was true for neurons with cell bodies located across all tested layers/types. 

Strengths: 

This study successfully looks at the relevant scale to study projection patterns, which is the whole brain. This is achieved thanks to an ambitious combination of mouse lines, immunohistochemistry, imaging and image processing, which results in a standardized histological pipeline that processes the whole-brain projection patterns of layer-selected neurons of the primary and secondary somatosensory cortex. 

This standardization means that comparisons between cell-types projection patterns are possible and that both the large-scale structure of the pattern and the minute details of the intra-areas pattern are available. 

This reference dataset and the corresponding analysis code are made available to the research community. 

Weaknesses: 

One major question raised by this dataset is the risk of missing axons during the postprocessing step. Indeed, it appears that the control and training efforts have focused on the risk of false positives (see Figure 1 supplementary panels). And indeed, the risk of overlooking existing axons in the raw fluorescence data id discussed in the article. 

Based on the data reported in the article, this is more than a risk. In particular, Figure 2 shows an example Rbp4-L5 mouse where axonal spread seems massive in Hippocampus, while there is no mention of this area in the processed projection data for this mouse line. 

In Figure 2, we show the expression of tdTomato in double-transgenic mice in which the Cre-driver lines were crossed with a Cre-dependent reporter mouse expressing cytosolic tdTomato. In addition to the specific labelling of L5PT neurons in the somatosensory cortex, Rbp4-Cre mice also express Cre-recombinase in other brain regions including the hippocampus. In the reporter mice crossed with Rbp4-Cre mice, tdTomato is expressed in neurons with cell bodies in the hippocampus which is clearly visualized in Figure 2. Because our axonal labelling is based on localized viral vector expression of tdTomato in SSp-bfd and SSs, the expression of Cre in hippocampus does not affect our analysis. In order to clarify to the reader, in the legend to Figure 2D, we now specifically write “As for panel A, but for Rbp4-L5 neurons. Note strong expression of Cre in neurons with cell bodies located in the hippocampus, which does not affect our analysis of axonal density based on virus injected locally into the neocortex.” Consistent with this observation, the Allen Institute’s ISH data support

expression of Rbp4 in neurons of the hippocampus e.g. https://mouse.brainmap.org/gene/show/19425 and https://mouse.brainmap.org/experiment/show/68632655.

Similarily, the Ntsr1-L6CT example shows a striking level of fluorescence in Striatum, that does not reflect in the amount of axons that are detected by the algorithms in the next figures.  These apparent discrepancies may be due to non axonal-specific fluorescence in the samples. In any case, further analysis of such anatomical areas would be useful to consolidate the valuable dataset provided by the article. 

As pointed out above, Figure 2 shows cytosolic tdTomato fluorescence in transgenic crosses of the Cre-driver mice with Cre-dependent tdTomato reporter mice. For the Ntsr1-Cre x LSL-tdTomato mice, all corticothalamic L6CT neurons from across the entire cortex drive tdTomato expression. The axon of each neuron must traverse the striatum giving rise to fluorescence in the striatum. As discussed above, labelling of synaptic specialisations will be important in future studies to separate travelling axon from innervating axon. However, the overall impact of the axons traversing the striatum is again mitigated in our study by considering the axonal projections from local sparse infections in SSp-bfd and SSs rather than from cortex-wide tdTomato expression.

Reviewer #3 (Public Review): 

Summary: 

The paper offers a systematic and rigorous description of the layer-and sublayer specific outputs of the somatosensory cortex using a modern toolbox for the analysis of brain connectivity which combines: 1) Layer-specific genetic drivers for conditional viral tracing; 2) whole brain analyses of axon tracts using tissue clearing and imaging; 3) Segmentation and quantification of axons with normalization to the number of transduced neurons; 4) registration of connectivity to a widely used anatomical reference atlas; 5) functional validation of the connectivity using optogenetic approaches in vivo. 

Strengths: 

Although the connectivity of the somatosensory cortex is already known, precise data are dispersed in different accounts (papers, online resources,) using different methods. So the present account has the merit of condensing this information in one very precisely documented report. It also brings new insights on the connectivity, such as the precise comparison of layer specific outputs, and of the primary and secondary somatosensory areas. It also shows a topographic organization of the circuits linking the somatosensory and motor cortices. The paper also offers a clear description of the methodology and of a rigorous approach to quantitative anatomy. 

Weaknesses: 

The weakness relates to the intrinsic limitations of the in toto approaches, that currently lack the precision and resolution allowing to identify single axons, axon branching or synaptic connectivity. These limitations are identified and discussed by the authors. 

We agree with the reviewer.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

No additional comment 

OK

Reviewer #2 (Recommendations For The Authors): 

In Figure 8, we don't get to see much raw data, while the diversity of functional responses pattern to the primary and supplementary S1 activations is highly intriguing (and this diversity exists as suggested by the results in Figure 8E, LRPT). 

Can Figure 8C be less blurred? Maybe give more space to individual examples, such as an overlay of the delineations of the activated area across the tested mice? 

Also, can we have a view on the time dynamics of the functional activation and integration window? 

Raw data - We have now added a new supplementary figure (Figure 8 – figure supplement 1) to show data from individual mice, as well as plotting the time-course of the evoked jRGECO fluorescence signals in the frontal cortex hotspot. 

Image blur - Each pixel represents 62.5 x 62.5 um on the cortical surface. The images in Figure 8B&C were averaged across mice, which causes some additional spatial blurring. However, the most likely explanation for the ‘blurred’ impression, is the overall large horizontal extent of the axonal innervation as well as likely rapid lateral spread of excitation both at the stimulation area and in the target region, as for example also indicated in rapid voltage-sensitive imaging experiments (Ferezou et al., 2007).  

Reviewer #3 (Recommendations For The Authors): 

At the time being, the abstract is really centred on the methodology which is no longer very novel as it has actually been already been described previously by other groups. In my view the paper would gain visibility, and be a useful tool for the community if amended to better point out the significant results of the study, for instance, i) the layer and sub-layer specificity of the outputs, using the listed genetic drivers; ii) the comparison of primary and secondary somatosensory areas, iii) the functional validation. The layer specificity of each cre- line should be indicated in the abstract. 

We have tried to improve the writing of the abstract along the lines suggested by the reviewer. Specifically, we have now added layer and projection class of the various Cre-lines, and we now also highlight the most obvious differences in the innervation patterns.

There is some degree of redundancy in the description in the result section. One suggestion, for an easier flow of reading, would be to join the paragraphs " Laminar characterization of the Cre-lines.." and: "Axonal projections...". Start for each Cre-line with a description of the laminar localisation of recombination in the somatosensory cortices, followed therefrom by the description of outputs from SSp-bfd and SSs; Then the general description/overview of the outputs can be summarized as a legend to Figure 5-supplementary 2, which could appear as a main figure. 

Although we agree with the reviewer that there is some level of redundancy in the text, the results of the characterization of the Cre-line (Figure 2) is quite a different experiment compared to the viral injections described in other figures, and we therefore prefer to keep these sections separate.

Other minor points: 

In the text; Indicate the genetic background of the transgenic mouse lines. 

On P. 18, we now indicate that all mice were “back-crossed with C57BL/6 mice”.

Keep consistency in the designation of the areas, S1 appears sometimes as SSp-bfd or as SSp 

We thank the reviewer for pointing out the inconsistent nomenclature, which we have now corrected in the revised manuscript. ‘SSp’ remains used on P. 9 and P. 16 of the revised manuscript to indicate a region including SSp-bfd but also extending beyond.

Figure 1 supplement 2 is not really necessary to show (as the viral tools have previously been validated) can just be stated in the text. Conversely one would like to see a higher resolution image of the injection sites that allowed to do the cell counts used for normalization, as this can be pretty tricky. 

In response to the reviewer’s suggestion, we have now added a new supplemental figure to show an example of how cells in the injection site were counted (Figure 1 – figure supplement 3).

Figure 2: the most important here is the higher magnification to show the precise laminar localisation of the recombination, rather than the atlas landmarks that is already shown in Figure 1. This would allow more space for clearer higher magnification panels comparing SSs and SSp. The present image hints to some real differences, but difficult to appreciate with the current resolution. The legend should also comment on the labelling seen in layer 1, in the Tlx2 and Rbp4 lines. Could be dendritic labelling, but this needs a word of clarification.

We think both the overview images as well as the high-resolution images are of value to the reader. Following the reviewer’s comment, in the legends to Figure 2C&D, we have now added text suggesting that the layer 1 fluorescence is likely axonal or dendritic in origin : “Labelling in layer 1 is likely of axonal or dendritic origin, and no cell bodies were labelled in this layer.” In addition, we have added a new supplemental figure which shows the cortical labelling in SSp and SSS in a more magnified view (Figure 2 – figure supplement 1).

Figure 3: the comparison of the 3 transgenic lines labelling layer 5 and showing sublaminar identities is really interesting in showing the heterogeneity of this layer and possible regional differences. However, the cases shown for illustration for Rbp4 and Tlx3 seem pretty massive in comparison with the other drivers. Maybe cases with smaller injections could be chosen for illustration. 

Figure 3 shows grand average axonal density maps across different mice normalized to the number of neurons in the injection site. The large amount of axon per neuron observed in Rbp4 and Tlx3 mice therefore shows their long, wide-ranging axons compared to other neuronal classes.

Figure 6A could be a supplementary figure in my view; 6B is clearer. 

We think both representations are useful, and we think different readers might better appreciate either of the two analyses.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Jang et al. describes the application of new methods to measure the localization of GTP-binding signaling proteins (G proteins) on different membrane structures in a model mammalian cell line (HEK293). G proteins mediate signaling by receptors found at the cell surface (GPCRs), with evidence from the last 15 years suggesting that GPCRs can induce G-protein mediated signaling from different membrane structures within the cell, with variation in signal localization leading to different cellular outcomes. While it has been clearly shown that different GPCRs efficiently traffic to various intracellular compartments, it is less clear whether G proteins traffic in the same manner, and whether GPCR trafficking facilitates "passenger" G protein trafficking. This question was a blind spot in the burgeoning field of GPCR localized signaling in need of careful study, and the results obtained will serve as an important guidepost for further work in this field. The extent to which G proteins localize to different membranes within the cell is the main experimental question tested in this manuscript. This question is pursued through two distinct methods, both relying on genetic modification of the G-beta subunit with a tag. In one method, G-beta is modified with a small fragment of the fluorescent protein mNG, which combines with the larger mNG fragment to form a fully functional fluorescent protein to facilitate protein trafficking by fluorescent microscopy. This approach was combined with the expression of fluorescent proteins directed to various intracellular compartments (different types of endosomes, lysosome, endoplasmic reticulum, Golgi, mitochondria) to look for colocalization of G-beta with these markers. These experiments showed compelling evidence that G-beta co-localizes with markers at the plasma membrane and the lysosome, with weak or absent co-localization for other markers. A second method for measuring localization relied on fusing G-beta with a small fragment from a miniature luciferase (HiBit) that combines with a larger luciferase fragment (LgBit) to form an active luciferase enzyme. Localization of Gbeta (and luciferase signal) was measured using a method known as bystander BRET, which relies on the expression of a fluorescent protein BRET acceptor in different cellular compartments. Results using bystander BRET supported findings from fluorescence microscopy experiments. These methods for tracking G protein localization were also used to probe other questions. The activation of GPCRs from different classes had virtually no impact on the localization of G-beta, suggesting that GPCR activation does not result in the shuttling of G proteins through the endosomal pathway with activated receptors.

Strengths:

The question probed in this study is quite important and, in my opinion, understudied by the pharmacology community. The results presented here are an important call to be cognizant of the localization of GPCR coupling partners in different cellular compartments. Abundant reports of endosomal GPCR signaling need to consider how the impact of lower G protein abundance on endosomal membranes will affect the signaling responses under study.

The work presented is carefully executed, with seemingly high levels of technical rigor. These studies benefit from probing the experimental questions at hand using two different methods of measurement (fluorescent microscopy and bystander BRET). The observation that both methods arrive at the same (or a very similar) answer inspires confidence about the validity of these findings.

Weaknesses:

The rationale for fusing G-beta with either mNG2(11) or SmBit could benefit from some expansion. I understand the speculation that using the smallest tag possible may have the smallest impact on protein performance and localization, but plenty of researchers have fused proteins with whole fluorescent proteins to provide conclusions that have been confirmed by other methods. Many studies even use G proteins fused with fluorescent proteins or luciferases. Is there an important advantage to tagging G-beta with small tags? Is there evidence that G proteins with full-size protein tags behave aberrantly? If the studies presented here would not have been possible without these CRISPR-based tagging approaches, it would be helpful to provide more context to make this clearer. Perhaps one factor would be interference from newly synthesized G proteins-fluorescent protein fusions en route to the plasma membrane (in the ER and Golgi).

There are several advantages to using small peptide tags that we did not fully explain. From a practical standpoint the most important advantage of using the HiBit tag instead of full-length Nanoluc is that it allows us to restrict luminescence output to cells transiently transfected with LgBit. In this way untransfected cells contribute no background signal. Although we did not take advantage of it here, this also applies to fluorescent protein complementation, and will be useful for visualizing proteins in individual cells within tissues. The HiBit tag also allows PAGE analysis by probing membranes with LgBit (as in Fig. 1). We are not aware of evidence that tagging Gb or Gg subunits on the N terminus results in aberrant behavior, while there is some evidence that Ga subunits tagged with full-size protein tags (in some positions) have altered functional properties (PMID: 16371464). We do think that editing endogenous genes is critical, as studies using transient overexpression (usually driven by strong promoters) have sometimes reported accumulation of tagged G proteins in the biosynthetic pathway (e.g., PMID: 17576765), as the reviewer suggests. Ga and Gbg appear to be mutually dependent on each other for appropriate trafficking to the plasma membrane (reviewed in PMID: 23161140), therefore the native (presumably matched) stoichiometry is likely to be critical.

To clarify this context the revised manuscript includes the following:

“For bioluminescence experiments we added the HiBit tag (Schwinn et al., 2018) and isolated clonal “HiBit-b1“ cell lines. An advantage of this approach over adding a full-length Nanoluc luciferase is that it requires coexpression of LgBit to produce a complemented luciferase. This limits luminescence to cotransfected cells and thus eliminates background from untransfected cells.”

“Some studies using overexpressed G protein subunits have suggested that a large pool of G proteins is located on intracellular membranes, including the Golgi apparatus (Chisari et al., 2007; Saini et al., 2007; Tsutsumi et al., 2009), whereas others have indicated a distribution that is dominated by the plasma membrane (Crouthamel et al., 2008; Evanko, Thiyagarajan, & Wedegaertner, 2000; Marrari et al., 2007; Takida & Wedegaertner, 2003). A likely factor contributing to these discrepant results is the stoichiometry of overexpressed subunits, as neither Ga nor Gbg traffic appropriately to the plasma membrane as free subunits (Wedegaertner, 2012). Our gene-editing approach presumably maintains the native subunit stoichiometry, providing a more accurate representation of native G protein distribution.”

As noted by the authors, they do not demonstrate that the tagged G-beta is predominantly found within heterotrimeric G protein complexes. If there is substantial free G-beta, then many of the conclusions need to be reconsidered. Perhaps a comparison of immunoprecipitated tagged G beta vs immunoprecipitated supernatant, with blotting for other G protein subunits would be informative.

We do think that HiBit-b1 exists predominantly within heterotrimeric complexes, for several reasons. First, overexpression studies have shown that Gbg requires association with Ga to traffic to the plasma membrane, and that by itself Gbg is retained on the endoplasmic reticulum

(PMID: 12609996; PMID: 12221133). We find almost no endogenous Gb1 on the endoplasmic reticulum, and a high density on the plasma membrane. Second, we are able to detect large increases in free HiBit-Gbg after G protein activation using free Gbg sensors (e.g. Fig. 1). Third, many proteins that bind to free Gbg are found entirely in the cytosol of HEK 293 cells (e.g. PMID: 10066824), suggesting there is not a large population of free Gbg. We have added discussion of these points to the revised manuscript as follows:

“Endogenous Ga and Gb subunits are expressed at approximately a 1:1 ratio, and Gb subunits are tightly associated with Gg and inactive Ga subunits (Cho et al., 2022; Gilman, 1987; Krumins & Gilman, 2006). Moreover, proteins that bind to free Gbg dimers are found in the cytosol of unstimulated HEK 293 cells, suggesting at most only a small population of free Gbg in these cells. Therefore, we assume that the large majority of mNG-b1 and HiBit-b1 subunits in unstimulated cells are part of heterotrimers.”

“Notably, when Gbg dimers are expressed alone they accumulate on the endoplasmic reticulum

(Michaelson et al., 2002; Takida & Wedegaertner, 2003). That we detect almost no endogenous Gbg on the endoplasmic reticulum supports our conclusion that the large majority of Gbg in unstimulated HEK 293 cells is associated with Ga, although we cannot rule out a small population of free Gbg.”

We do not entirely understand the suggested experiment, as free Gbg will still be largely associated with the membrane fraction. Notably, we find almost no HiBit-b1 in the supernatant after lysis in hypotonic buffer and preparation of membrane fractions, and the small amount that we do find does not change if Ga is overexpressed.

Additional context and questions:

(1) There exists some evidence that certain GPCRs can form enduring complexes with G-betagamma (PubMed: 23297229, 27499021). That would seem to offer a mechanism that would enable receptor-mediated transport of G protein subunits. It would be helpful for the authors to place the findings of this manuscript in the context of these previous findings since they seem somewhat contradictory.

We agree. In our original submission we noted “It is possible that other receptors will influence G protein distribution using mechanisms not shared by the receptors we studied.” In the revised manuscript we have added:

“For example, a few receptors are thought to form relatively stable complexes with Gbg, which could provide a mechanism of trafficking to endosomes (Thomsen et al., 2016; Wehbi et al., 2013).”

(2) There is some evidence that GaS undergoes measurable dissociation from the plasma membrane upon activation (see the mechanism of the assay in PubMed: 35302493). It seems possible that G-alpha (and in particular GaS) might behave differently than the G-beta subunit studied here. This is not entirely clear from the discussion as it now stands.

Indeed, there is abundant evidence that some Gas translocates away from the plasma membrane upon activation. We referred to translocation of “some Ga subunits” in the introduction, although we did not specify that Gas is by far the most studied example. In a previous study (PMID: 27528603) we found that overexpressed Gas samples many intracellular membranes upon activation and returns to the plasma membrane when activation ceases. This is similar to activation-dependent translocation of free Gbg dimers. Because these translocation mechanisms depend on activation and are reversible they are unlikely to be a major source of inactive heterotrimers for intracellular membranes.

We did a poor job of making it clear that we intentionally avoided translocation mechanisms that operate only during receptor and G protein stimulation. In the revised manuscript we have added new data showing reversible activation-dependent translocation of endogenous HiBitGb1.

(3) The authors say "The presence of mNG-b1 on late endosomes suggested that some G proteins may be degraded by lysosomes". The mechanism of lysosomal degradation by proteins on the outside of the lysosome is not clear. It would be helpful for the authors to clarify.

We agree we didn’t connect the dots here. Our initial idea was that G proteins on the surface of late endosomes might reach the interior of late endosomes and then lysosomes by involution into multivesicular bodies. However, the reviewer correctly points out that much of the G protein associated with lysosomes still appears to be on the cytosolic surface, where it would not be subject to degradation. In fact, since lysosomes can fuse with the plasma membrane under certain circumstances, this could even represent a pathway for recycling G proteins to the plasma membrane.

We have revised the text to avoid giving the impression that lysosomes degrade G proteins, since we have scant evidence that this occurs. In the revised discussion we point out that we do not know the fate of G proteins located on the surface of lysosomes and speculate that these could be returned to the plasma membrane:

“We do not know the fate of G proteins located on the surface of lysosomes. Since lysosomes may fuse with the plasma membrane under certain circumstances (Xu & Ren, 2015), it is possible that this represents a route of G protein recycling to the plasma membrane.”

(4) Although the authors do a good job of assessing G protein dilution in endosomal membranes, it is unclear how this behavior compares to the measurement of other lipidanchored proteins using the same approach. Is the dilution of G proteins what we would expect for any lipid-anchored protein at the inner leaflet of the plasma membrane?

This is a great question. To begin to address it we have studied a model lipid-anchored protein consisting of mNeongreen2 anchored to the plasma membrane by the C terminus of HRas, which is palmitoylated and prenylated. We find that this protein is also diluted on endocytic vesicles, although to a lesser degree than heterotrimeric G proteins. We have added a section to the results and a new figure supplement describing these results:

“To test if other peripheral membrane proteins are similarly depleted from endocytic vesicles, we performed analogous experiments by overexpressing mNG bearing the C-terminal membrane anchor of HRas (mNG-HRas ct). We found that mNG-HRas ct was also less abundant on FM464-positive endocytic vesicles than expected based on plasma membrane abundance, although not to the same extent as mNG-b1 (Figure 4 - figure supplement 2); mNG-HRas ct density on FM4-64-positive vesicles was 64 ± 17% (mean ± 95% CI; n=78) of the nearby plasma membrane.”

Reviewer #2 (Public Review):

This is an interesting method that addresses the important problem of assessing G protein localization at endogenous levels. The data are generally convincing.

Specific comments

Methods:

The description of the gene editing method is unclear. There are two different CRISPR cell lines made in two different cell backgrounds. The methods should clearly state which CRISPR guides were used on which cell line. It is also not clear why HiBit is included in the mNG-β1 construct. Presumably, this is not critical but it would be helpful to explicitly note. In general, the Methods could be more complete.

We have added the following to the methods to clarify that the same gRNA was used to produce both cell lines:

“The human GNB1 gene was targeted at a site corresponding to the N-terminus of the Gb1 protein; the sequence 5’-TGAGTGAGCTTGACCAGTTA-3’ was incorporated into the crRNA, and the same gRNA was used to produce both HiBit-b1 and mNG-b1 cell lines.”

We have added the following to the methods to clarify why HiBit is included in the mNG-b1 construct:

“HiBit was included in the repair template for producing mNG-b1 cells to enable screening for edited clones using luminescence.”

Results:

The explanation of validation experiments in Figures 1 C and D is incomplete and difficult to follow. The rationale and explanation of the experiments could be expanded. In addition, because this is an interesting method, it would be helpful to know if the endogenous editing affects normal GPCR signaling. For example, the authors could include data showing an Isoinduced cAMP response. This is not critical to the present interpretation but is relevant as a general point regarding the method. Also, it may be relevant to the interpretation of receptor effects on G protein localization.

We have expanded the rationale and explanation of experiments in Figures 1C and D by adding:

“For example, we observed agonist-induced BRET between the D2 dopamine receptor and mNG-b1, an interaction that requires association with endogenous Ga subunits (Figure 1C). Similarly, we observed BRET between HiBit-b1 and the free Gbg sensor memGRKct-Venus after activation of receptors that couple Gi/o, Gs, and Gq heterotrimers, indicating that HiBit-b1 associated with endogenous Ga subunits from these three families (Figure 1D).”

We have done the suggested cAMP experiment and provide the data in a new figure supplement:

“We also found that cyclic AMP accumulation in response to stimulation of endogenous b adrenergic receptors was similar in edited cell lines and their unedited parent lines (Figure 1 - figure supplement 1).”

Discussion:

The conclusion that beta-gamma subunits do not redistribute after GPCR activation seems new and different from previous reports. Is this correct? Can the authors elaborate on how the results compare to previous literature?

Many previous studies have indeed shown that free Gbg dimers can redistribute after GPCR activation and sample intracellular membranes. Our initial focus was on possible changes in heterotrimer distribution after GPCR activation, but in retrospect we should have directly addressed free Gbg translocation and made the distinction clear. 

In the revised manuscript we show that during stimulation we observe changes consistent with modest translocation of endogenous Gbg from the plasma membrane and sampling of intracellular compartments. To our knowledge this is the first demonstration of endogenous Gbg translocation.

We have added:

“With overexpressed G proteins free Gbg dimers translocate from the plasma membrane and sample intracellular membrane compartments after activation-induced dissociation from Ga subunits. Consistent with this, we observed small decreases in bystander BRET at the plasma membrane and small increases in bystander BRET at intracellular compartments during activation of GPCRs, suggesting that endogenous Gbg subunits undergo similar translocation (Figure 5- figure supplement 1). Notably, these changes occurred at room temperature, suggesting that endocytosis was not involved, and developed over the course of minutes. The latter observation and the small magnitude of agonist-induced changes are both consistent with expression of primarily slowly-translocating endogenous Gg subtypes in HEK 293 cells. Moreover, as shown previously for overexpressed Gbg, the changes we observed with endogenous Gbg were readily reversible (Figure 5- figure supplement 1), suggesting that most heterotrimers reassemble at the plasma membrane after activation ceases.”

Can the authors note that OpenCell has endogenously tagged Gβ1 and reports more obvious internal localization? Can the authors comment on this point?

OpenCell has tagged GNB1 and the Leonetti group kindly provided a parent cell line we used to add a slightly different tag. Although their study did not identify any specific intracellular compartments, our impression is that most of the internal structures visible in their images are likely to be lysosomes, as they are large, round and often have a clear lumen. Overall their images and ours are comfortingly similar. We have added:

“Unsurprisingly, our images are quite similar to those made as part of previous study that labeled Gb1 subunits with mNG2 (Cho et al., 2022).”

Notably, the Leonetti group has recently reported the subcellular distribution of many untagged proteins using a proteomic approach. They find that Gb1 is enriched on the plasma membrane and lysosomes but is not enriched on endosomes, the Golgi apparatus, endoplasmic reticulum or mitochondria (https://www.biorxiv.org/content/10.1101/2023.12.18.572249v1). We have cited this work in the revised manuscript.

Is this the first use of CRISPR / HiBit for BRET assay? It would be helpful to know this or cite previous work if not. Also, as this is submitted as a tools piece, the authors might say a little more about the potential application to other questions.

The only previous study we are aware of utilizing a similar combination of methods is a 2020 report from the group of Dr. Stephen Hill, in which the authors studied binding of fluorescent ligands to HiBit-tagged GPCRs. This work is now cited.

We have also added the following to our previous brief statement about potential applications:

“In addition, it may also be possible to use these cells in combination with targeted sensors to study endogenous G protein activation in different subcellular compartments. More broadly, our results show that subcellular localization of endogenous membrane proteins can be studied in living cells by adding a HiBit tag and performing bystander BRET mapping. Applied at large scale this approach would have some advantages over fluorescent protein complementation, most notably the ability to localize endogenous membrane proteins that are expressed at levels that are too low to permit fluorescence microscopy.”

Reviewer #3 (Public Review):

Summary:

This article addresses an important and interesting question concerning intracellular localization and dynamics of endogenous G proteins. The fate and trafficking of G protein-coupled receptors (GPCRs) have been extensively studied but so far little is known about the trafficking routes of their partner G proteins that are known to dissociate from their respective receptors upon activation of the signaling pathway. The authors utilize modern cell biology tools including genome editing and bystander bioluminescence resonance energy transfer (BRET) to probe intracellular localization of G proteins in various membrane compartments in steady state and also upon receptor activation. Data presented in this manuscript shows that while G proteins are mostly present on the plasma membrane, they can be also detected in endosomal compartments, especially in late endosomes and lysosomes. This distribution, according to data presented in this study, seems not to be affected by receptor activation. These findings will have implications in further studies addressing GPCR signaling mechanisms from intracellular compartments.

Strengths:

The methods used in this study are adequate for the question asked. Especially, the use of genome-edited cells (for the addition of the tag on one of the G proteins) is a great choice to prevent the effects of overexpression. Moreover, the use of bystander BRET allowed authors to probe the intracellular localization of G proteins in a very high-throughput fashion. By combining imaging and BRET authors convincingly show that G proteins are very low abundant on early endosomes (also ER, mitochondria, and medial Golgi), however seem to accumulate on membranes of late endosomal compartments.

Weaknesses:

While the authors provide a novel dataset, many questions regarding G protein trafficking remain open. For example, it is not entirely clear which pathway is utilized to traffic G proteins from the plasma membrane to intracellular compartments. Additionally, future studies should also address the dynamics of G protein trafficking, for example by tracking them over multiple time points.

We agree, there is much more to do.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

On page 7 the text says "the difference did reach significance (Figure 5D)". It looks like the difference did not reach significance. Please check on this.

Thank you, this was an unfortunately significant typo.

Reviewer #3 (Recommendations For The Authors):

This article addresses an important and interesting question concerning intracellular localization and dynamics of endogenous G proteins. While the posed question is indeed a grand one and the methods used by the authors are novel, I believe that the data presented in this manuscript are still insufficient to support all claims posed by the authors. Below I list my major concerns:

(1) The authors claim that they provide a "detailed subcellular map of endogenous G protein distribution", however, the map is in my opinion not sufficiently detailed (e.g. trans-Golgi network is not included) and not quantitative enough (e.g. % of proteins present on one compartment vs. the other as authors claim that BRET signals "cannot be directly compared between different compartments"). To strengthen this statement, except for providing more extensive and quantitative data, it would be beneficial to provide such a "map" as an illustration based on the findings presented in this article.

“Detailed” is certainly a subjective term. While we maintain that our description of endogenous G protein distribution is far more detailed than any previous study, we now simply claim to provide a “subcellular map”. We have added images of TGNP (TGN46; TGOLN2), showing that endogenous G proteins are readily detectable on the structures labeled by this marker. These data are now provided in Figure 3 – figure supplement 7.

We did not claim that our study was quantitative- we did not try to count G proteins. However, if we use published estimates of total G proteins and surface area for HEK 293 cells we estimate that there are roughly 2,500 G proteins µm-2 on the plasma membrane and 500 G proteins µm-2 on endocytic vesicles. For other intracellular compartments relative density can be approximated by inspecting images, but a truly quantitative estimate would require a surface area standard analogous to FM4-64 for each compartment. The percentage of the total G protein pool on a given compartment is, in our opinion, less important than the density of G proteins on that compartment, as the latter is more likely to affect the efficiency of local signal transduction. Since we do not claim to have accurate G protein density estimates for many intracellular compartments, we prefer to provide several raw images for each compartment rather than a schematized map.

Bystander BRET values cannot be compared directly across compartments due to differences in expression and energy transfer efficiency of different markers and compartment surface area. This method is well suited for following changes in distribution as a function of time or after perturbations and for sensitive detection of weak colocalization but can only provide approximate “maps” of absolute distribution.

(2) Probing of the intracellular distribution of these proteins, especially after GPCR activation, includes a single chosen timepoint. I believe that the manuscript would greatly benefit from including some dynamic data on internalization and intracellular trafficking kinetics. What is the turnover of tested G proteins? What is the fraction that is going to recycling compartments and/or lysosomes? Authors could perhaps turn to other methods to be able to dynamically track proteins over time e.g. via photoconversion techniques.

Because G protein trafficking appears to be largely constitutive there is no easy way for us to assess how long it takes G proteins to transit various intracellular compartments, although we agree this would be interesting. As the reviewer suggests, dynamic data on constitutive trafficking would require methods (such as photoconversion) not currently available to us for endogenous G proteins. Accordingly, we have made no claims regarding the kinetics of G protein trafficking. As for possible redistribution after GPCR activation, in the revised manuscript we have added 5- and 15-minute timepoints after agonist stimulation for our bystander BRET mapping (Figure 5- figure supplement 2). These timepoints were chosen to correspond to persistent signaling mediated by internalized receptors. 

(3) Exemplary images with cells showing significant colocalization with lysosomal compartments seem to contain more intracellular vesicles visible in the mNG channel than in the case of the other compartment. Is it an effect of the treatment to stain lysosomes? It would be beneficial to compare it with some endogenous marker e.g. LAMP1 without additional treatments.

The visibility of intracellular vesicles in our lysosome images likely reflects our selection of cells and regions with visible and abundant lysosomes, specifically peripheral regions directly adhered to the coverslip, rather than treatment with lysosomal stains (LV 633 and dextran). As suggested, we now include images of cells expressing LAMP1 as an alternative lysosome marker (Figure 3 - figure supplement 6).

(4) The authors probe an abundance of G proteins along the constitutive endocytic pathway. However, to prove that G proteins are not de-palmitoylated rather than endocytosed authors should perform control experiments where endocytosis is blocked e.g. pharmacologically or via a knockdown approach. Additionally, various endocytic pathways can be probed.

We did not claim that depalmitoylation plays no role in delivery of G proteins to internal compartments. In fact, we pointed out that we cannot at present rule out other pathways and delivery mechanisms. Importantly, if some of the G proteins that we detect along the endocytic pathway do arrive there by trafficking through the cytosol this would only strengthen our major conclusion that endocytosis is inefficient.

Having said this, we have now conducted extensive experiments investigating the role of palmitate cycling in the trafficking of heterotrimeric G proteins and the small G protein H-Ras. Our results suggest that a depalmitoylation-repalmitoylation cycle is not important for the distribution of heterotrimers, but these findings will be the subject of a separate publication focused on this specific question for both large and small G proteins.

We agree that it will be interesting to probe different endocytic pathways, as suggested using a genetic approach. Our main interest here was in endocytic membranes that were defined functionally (with FM4-64 or internalized receptors) rather than biochemically.

Minor comments:

(5) "Imaging" paragraph in the Methods section refers to a non-existent figure called "SI Appendix S9".

Thank you.

(6) It is not clear what was used as a "control" in Figure 5E.

“Control” refers to DPBS vehicle alone. This information is now added to the legend for Figure 5E.

Author response:

The following is the authors’ response to the previous reviews.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Line 127. Provide a few more words describing the voltage protocol. To the uninitiated, panels A and B will be difficult to understand. "The large negative step is used to first close all channels, then probe the activation function with a series of depolarizing steps to re-open them and obtain the max conductance from the peak tail current at -36 mV. "

We have revised the text as suggested (revision lines 127 to Line 131): “From a holding potential within the gK,L activation range (here –74 mV), the cell is hyperpolarized to –124 mV, negative to EK and the activation range, producing a large inward current through open gK,L channels that rapidly decays as the channels deactivate. We use the large transient inward current as a hallmark of gK,L. The hyperpolarization closes all channels, and then the activation function is probed with a series of depolarizing steps, obtaining the max conductance from the peak tail current at –44 mV (Fig. 1A).”

Incidentally, why does the peak tail current decay? 

We added this text to the figure legend to explain this: “For steps positive to the midpoint voltage, tail currents are very large. As a result, K+ accumulation in the calyceal cleft reduces driving force on K+, causing currents to decay rapidly, as seen in A (Lim et al., 2011).”

The decay of the peak tail current is a feature of gK,L (large K+ conductance) and the large enclosed synaptic cleft (which concentrates K+ that effluxes from the HC). See Govindaraju et al. (2023) and Lim et al. (2011) for modeling and experiments around this phenomenon.

Line 217-218. For some reason, I stumbled over this wording. Perhaps rearrange as "In type II HCs absence of Kv1.8 significantly increased Rin and tauRC. There was no effect on Vrest because the conductances to which Kv1.8 contributes, gA and gDR activate positive to the resting potential. (so which K conductances establish Vrest???). 

We kept our original wording because we wanted to discuss the baseline (Vrest) before describing responses to current injection.

->Vrest is presumably maintained by ATP-dependent Na/K exchangers (ATP1a1), HCN, Kir, and mechanotransduction currents. Repolarization is achieved by delayed rectifier and A-type K+ conductances in type II HCs.

Figure 4, panel C - provides absolute membrane potential for voltage responses. Presumably, these were the most 'ringy' responses. Were they obtained at similar Vm in all cells (i.e., comparisons of Q values in lines 229-230). 

We added the absolute membrane potential scale. Type II HC protocols all started with 0 pA current injection at baseline, so they were at their natural Vrest, which did not differ by genotype or zone. Consistent with Q depending on expression of conductances that activate positive to Vrest, Q did not co-vary with Vrest (Pearson’s correlation coefficient = 0.08, p = 0.47, n= 85).

Lines 254. Staining is non-specific? Rather than non-selective? 

Yes, thanks - Corrected (Line 264).

Figure 6. Do you have a negative control image for Kv1.4 immuno? Is it surprising that this label is all over the cell, but Kv1.8 is restricted to the synaptic pole? 

We don’t have a null-animal control because this immunoreactivity was done in rat. While the cuticular plate staining was most likely nonspecific because we see that with many different antibodies, it’s harder to judge the background staining in the hair cell body layer. After feedback from the reviewers, we decided to pull the KV1.4 immunostaining from the paper because of the lack of null control, high background, and inability to reproduce these results in mouse tissue. In our hands, in mouse tissue, both mouse and rabbit anti-KV1.4 antibodies failed to localize to the hair cell membrane. Further optimization or another method could improve that, but for now the single-cell expression data (McInturff et al., 2018) remain the strongest evidence for KV1.4 expression in murine type II hair cells.

Lines 400-404. Whew, this is pretty cryptic. Expand a bit? 

We simplified this paragraph (revision lines 411-413): “We speculate that gA and gDR(KV1.8) have different subunit composition: gA may include heteromers of KV1.8 with other subunits that confer rapid inactivation, while gDR(KV1.8) may comprise homomeric KV1.8 channels, given that they do not have N-type inactivation .”

Line 428. 'importantly different ion channels'. I think I understand what is meant but perhaps say a bit more. 

Revised (Line 438): “biophysically distinct and functionally different ion channels”.

Random thought. In addition to impacting Rin and TauRC, do you think the more negative Vrest might also provide a selective advantage by increasing the driving force on K entry from endolymph? 

When the calyx is perfectly intact, gK,L is predicted to make Vrest less negative than the values we report in our paper, where we have disturbed the calyx to access the hair cell (–80, Govindaraju et al., 2023, vs. –87 mV, here). By enhancing K+ accumulation in the calyceal cleft, the intact calyx shifts EK—and Vrest—positively (Lim et al., 2011), so the effect on driving force may not be as drastic as what you are thinking.

Reviewer #2 (Recommendations For The Authors): 

(1) Introduction: wouldn't the small initial paragraph stating the main conclusion of the study fit better at the end of the background section, instead of at the beginning? 

Thank you for this idea, we have tried that and settled on this direct approach to let people know in advance what the goals of the paper are.

(2) Pg.4: The following sentence is rather confusing "Between P5 and P10, we detected no evidence of a non-gK,L KV1.8-dependent.....". Also, Suppl. Fig 1A seems to show that between P5 and P10 hair cells can display a potassium current having either a hyperpolarised or depolarised Vhalf. Thus, I am not sure I understand the above statement. 

Thank you for pointing out unclear wording. We used the more common “delayed rectifier” term in our revision (Lines 144-147): “Between P5 and P10, some type I HCs have not yet acquired the physiologically defined conductance, gK,L.. N effects of KV1.8 deletion were seen in the delayed rectifier currents of immature type I HCs (Suppl. Fig. 1B), showing that they are not immature forms of the Kv1.8-dependent gK,L channels. ”

(3) For the reduced Cm of hair cells from Kv1.8 knockout mice, could another reason be simply the immature state of the hair cells (i.e. lack of normal growth), rather than less channels in the membrane? 

There were no other signs to suggest immaturity or abnormal growth in KV1.8–/– hair cells or mice. Importantly, type II HCs did not show the same Cm effect.

We further discussed the capacitance effect in lines 160-167: “Cm scales with surface area, but soma sizes were unchanged by deletion of KV1.8 (Suppl. Table 2). Instead, Cm may be higher in KV1.8+/+ cells because of gK,L for two reasons. First, highly expressed trans-membrane proteins (see discussion of gK,L channel density in Chen and Eatock, 2000) can affect membrane thickness (Mitra et al., 2004), which is inversely proportional to specific Cm. Second, gK,L could contaminate estimations of capacitive current, which is calculated from the decay time constant of transient current evoked by small voltage steps outside the operating range of any ion channels. gK,L has such a negative operating range that, even for Vm negative to –90 mV, some gK,L channels are voltage-sensitive and could add to capacitive current.”

(4) Methods: The electrophysiological part states that "For most recordings, we used .....". However, it is not clear what has been used for the other recordings.

Thanks for catching this error, a holdover from an earlier ms. version.  We have deleted “For most recordings” (revision line 466).

Also, please provide the sign for the calculated 4 mV liquid junction potential. 

Done (revision line 476).

Reviewer #3 (Recommendations For The Authors): 

(1) Some of the data in panels in Fig. 1 are hard to match up. The voltage protocols shown in A and B show steps from hyperpolarized values to -71mV (A) and -32 mV (B). However, the value from A doesn't seem to correspond with the activation curve in C.

Thank you for catching this.  We accidentally showed the control I-X curve from a different cell than that in A. We now show the G-V relation for the cell in A.

Also the Vhalf in D for -/- animals is ~-38 mV, which is similar to the most positive step shown in the protocol.

The most positive step in Figure 1B is actually –25 mV. The uneven tick labels might have been confusing, so we re-labeled them to be more conventional.

Were type I cells stepped to more positive potentials to test for the presence of voltage-activated currents at greater depolarizations? This is needed to support the statement on lines 147-148. 

We added “no additional K+ conductance activated up to +40 mV” (revision line 149-150).  Our standard voltage-clamp protocol iterates up to ~+40 mV in KV1.8–/– hair cells, but in Figure 1 we only showed steps up to –25 mV because K+ accumulation in the synaptic cleft with the calyx distorts the current waveform even for the small residual conductances of the knockouts. KV1.8–/– hair cells have a main KV conductance with a Vhalf of ~–38 mV, as shown in Figure 1, and we did not see an additional KV conductance that activated with a more positive Vhalf up to +40 mV.

(2) Line 151 states "While the cells of Kv1.8-/- appeared healthy..." how were epithelia assessed for health? Hair cells arise from support cells and it would be interesting to know if Kv1.8 absence influences supporting cells or neurons. 

We added our criteria for cell health to lines 477-479: “KV1.8–/– hair cells appeared healthy in that cells had resting potentials negative to –50 mV, cells lasted a long time (20-30 minutes) in ruptured patch recordings, membranes were not fragile, and extensive blebbing was not seen.”

Supporting cells were not routinely investigated. We characterized calyx electrical activity (passive membrane properties, voltage-gated currents, firing pattern) and didn’t detect differences between +/+, +/–, and –/– recordings (data not shown). KV1.8 was not detected in neural tissue (Lee et al., 2013). 

(3) Several different K+ channel subtypes were found to contribute to inner hair cell K+ conductances (Dierich et al. 2020) but few additional K+ channel subtypes are considered here in vestibular hair cells. Further comments on calcium-activated conductances (lines 310-317) would be helpful since apamin-sensitive SK conductances are reported in type II hair cells (Poppi et al. 2018) and large iberiotoxin-sensitive BK conductances in type I hair cells (Contini et al. 2020). Were iberiotoxin effects studied at a range of voltages and might calcium-dependent conductances contribute to the enhanced resonance responses shown in Fig. 4? 

We refer you to lines 310-317 in the original ms (lines 322-329 in the revised ms), where we explain possible reasons for not observing IK(Ca) in this study.

(4) Similar to GK,L erg (Kv11) channels show significant Cs+-permeability. Were experiments using Cs+ and/or Kv11 antagonists performed to test for Kv11? 

No. Hurley et al. (2006) used Kv11 antagonists to reveal Kv11 currents in rat utricular type I hair cells with perforated patch, which were also detected in rats with single-cell RT-PCR (Hurley et al. 2006) and in mice with single-cell RNAseq (McInturff et al., 2018).  They likely contribute to hair cell currents, alongside Kv7, Kv1.8, HCN1, and Kir. 

(5) Mechanosensitive ("MET") channels in hair cells are mentioned on lines 234 and 472 (towards the end of the Discussion), but a sentence or two describing the sensory function of hair cells in terms of MET channels and K+ fluxes would help in the Introduction too. 

Following this suggestion we have expanded the introduction with the following lines  (78-87): “Hair cells are known for their large outwardly rectifying K+ conductances, which repolarize membrane voltage following a mechanically evoked perturbation and in some cases contribute to sharp electrical tuning of the hair cell membrane.  Because gK,L is unusually large and unusually negatively activated, it strongly attenuates and speeds up the receptor potentials of type I HCs (Correia et al., 1996; Rüsch and Eatock, 1996b). In addition, gK,L augments a novel non-quantal transmission from type I hair cell to afferent calyx by providing open channels for K+ flow into the synaptic cleft (Contini et al., 2012, 2017, 2020; Govindaraju et al., 2023), increasing the speed and linearity of the transmitted signal (Songer and Eatock, 2013).”

(6) Lines 258-260 state that GKL does not inactivate, but previous literature has documented a slow type of inactivation in mouse crista and utricle type I hair cells (Lim et al. 2011, Rusch and Eatock 1996) which should be considered. 

Lim et al. (2011) concluded that K+ accumulation in the synaptic cleft can explain much of the apparent inactivation of gK,L. In our paper, we were referring to fast, N-type inactivation. We changed that line to be more specific; new revision lines 269-271: “KV1.8, like most KV1 subunits, does not show fast inactivation as a heterologously expressed homomer (Lang et al., 2000; Ranjan et al., 2019; Dierich et al., 2020), nor do the KV1.8-dependent channels in type I HCs, as we show, and in cochlear inner hair cells (Dierich et al., 2020).”

(7) Lines 320-321 Zonal differences in inward rectifier conductances were reported previously in bird hair cells (Masetto and Correia 1997) and should be referenced here.

Zonal differences were reported by Masetto and Correia for type II but not type I avian hair cells, which is why we emphasize that we found a zonal difference in I-H in type I hair cells. We added two citations to direct readers to type II hair cell results (lines 333-334): “The gK,L knockout allowed identification of zonal differences in IH and IKir in type I HCs, previously examined in type II HCs (Masetto and Correia, 1997; Levin and Holt, 2012).”

Also, Horwitz et al. (2011) showed HCN channels in utricles are needed for normal balance function, so please include this reference (see line 171). 

Done (line 184).

(8) Fig 6A. Shows Kv1.4 staining in rat utricle but procedures for rat experiments are not described. These should be added. Also, indicate striola or extrastriola regions (if known). 

We removed KV1.4 immunostaining from the paper, see above.

(9) Table 6, ZD7288 is listed -was this reagent used in experiments to block Gh? If not please omit. 

ZD7288 was used to block gH to produce a clean h-infinity curve in Figure 6, which is described in the legend.

(10) In supplementary Fig. 5A make clear if the currents are from XE991 subtraction. Also, is the G-V data for single cell or multiple cells in B? It appears to be from 1 cell but ages P11-505 are given in legend. 

The G-V curve in B is from XE991 subtraction, and average parameters in the figure caption are for all the KV1.8–/–  striolar type I hair cells where we observed this double Boltzmann tail G-V curve. I added detail to the figure caption to explain this better.

(11) Supplementary Fig. 6A claims a fast activation of inward rectifier K+ channels in type II but not type I cells-not clear what exactly is measured here.

We use “fast inward rectifier” to indicate the inward current that increases within the first 20 ms after hyperpolarization from rest (IKir, characterized in Levin & Holt, 2012) in contrast to HCN channels, which open over ~100 ms. We added panel C to show that the activation of IKir is visible in type II hair cells but not in the knockout type I hair cells that lack gK,L. IKir was a reliable cue to distinguish type I and type II hair cells in the knockout.

For our actual measurements in Fig 6B, we quantified the current flowing after 250 ms at –124 mV because we did not pharmacologically separate IKir and IH.

Could the XE991-sensitive current be activated and contributing?

The XE991-sensitive current could decay (rapidly) at the onset of the hyperpolarizing step, but was not contributing to our measurement of IKir­ and IH, made after 250 ms at –124 mV, at which point any low-voltage-activated (LVA) outward rectifiers have deactivated. Additionally, the LVA XE991-sensitive currents were rare (only detected in some striolar type I hair cells) and when present did not compete with fast IKir, which is only found in type II hair cells.

Also, did the inward rectifier conductances sustain any outward conductance at more depolarized voltage steps? 

For the KV1.8-null mice specifically, we cannot answer the question because we did not use specific blocking agents for inward rectifiers.  However, we expect that there would only be sustained outward IR currents at voltages between EK and ~-60 mV: the foot of IKir’s I-V relation according to published data from mouse utricular hair cells – e.g., Holt and Eatock 1995, Rusch and Eatock 1996, Rusch et al. 1998, Horwitz et al., 2011, etc.  Thus, any such current would be unlikely to contaminate the residual outward rectifiers in Kv1.8-null animals, which activate positive to ~-60 mV. 

(I-HCN is also not a problem, because it could only be outward positive to its reversal potential at ~-40 mV, which is significantly positive to its voltage activation range.)

Author response:

The following is the authors’ response to the original reviews.

We edited the manuscript for clarity, added information described in new figure panels (below) and corrected typos.

In figure 1 we corrected a typo.

In figure 2, panel 2H, and Figure S2E, we included a new statistical analysis (mixed effect linear regression) to compare mutational burden in controls and AD patients.

In figure 3, and Figure S4B, we revised the western blots panels in Panel 3E,F, to improve presentation of controls and quantification.

we corrected typos.

In figure 5 we removed a panel (former 5D) which did not add useful information.

In Figure S1A we included information about sex and age from the control and patients analyzed. In Figure S2B, we added an analysis of the mutational burden in controls, distinguishing controls with and without cancer.

We modified Table S1 for completeness of information for all samples analyzed.

Reviewer #1:

Weaknesses: 

Even though the study is overall very convincing, several points could help to connect the seen somatic variants in microglia more with a potential role in disease progression. The connection of P-SNVs in the genes chosen from neurological disorders was not further highlighted by the authors. 

All P-SNVs are reported in Table S3.

We observed only two P-SNVs within genes associated to neurological disorders (brain panel in Table S2). - SQSTM1 (p.P392L) was identified in blood but not in brain from the patient AD48A.

- OPTN was identified (p.Q467P) in PU.1 from control 25.   

To highlight this point, we modified the first paragraph of the discussion as follow:

“We report here that microglia from a cohort of 45 AD patients with intermediate-onset sporadic AD (mean age 65 y.o) is enriched for clones carrying pathogenic/oncogenic variants in genes associated with clonal proliferative disorders (Supplementary Table 2) in comparison to 44 controls. Of note we did not observe microglia P-SNVs within genes reported to be associated with neurological disorders (Supplementary Table 2) in patients, and one such variant was identified in a control (Supplementary Table 3) “.

The authors show in snRNA-seq data that a disease-associated microglia state seems to be enriched in patients with somatic variants in the CBL ring domain, however, this analysis could be deepened. For example, how this knowledge may translate to patient benefits when the relevant cell populations appear concentrated in a single patient sample (Figure 5; AD52) is unclear; increasing the analyzed patient pool for Figure 5 and showcasing the presence of this microglia state of interest in a few more patients with driving mutations for CBL or other MAPK pathway associated mutations would lend their hypotheses further credibility. 

We acknowledge this limitation, but we respectfully submit that the analysis was performed in 2 patients. AD 53 also show a MAPK-associated inflammatory signature in the microglia clusters associated with mutations.

We performed the analysis on all FACS-purified PU.1+ nuclei samples that passed QC for single nuclei RNAseq. It should be noted that this analysis is extremely difficult with current technologies because microglia nuclei need to be fixed for PU.1 staining and FACS purification and the clones are small (~1% of microglia).

A potential connection between P-SNVs in microglia and disease pathology and symptoms was not further explored by the authors. 

At the population level, Braak/CERAD scores, the presence of Lewy bodies, amyloid angiopathy, tauopathy, or alpha synucleinopathy were not different between AD patients with or without pathogenic microglial clones (Figure S3 and Table S1). Of note, we studied here a homogenous population of AD patients.

At the tissue level, the roles of mutant microglia in plaques for example is being investigated, but we do not have results to present at this time.

A recent preprint (Huang et al., 2024) connected the occurrence of somatic variants in genes associated with clonal hematopoiesis in microglia in a large cohort of AD patients, this study is not further discussed or compared to the data in this manuscript. 

This pre-print supports the high frequency of detection of oncogenic variants associated with clonal proliferative disorders, they hypothesize that the mutations may be associated with microglia, but they only check a few mutations in purified microglia. Most of the study is performed in whole brain tissue. It does not really bring new information as compared to other study we cite in the introduction (and to our manuscript).

Reviewer #2 (Recommendations For The Authors): 

Suggestions for improved or additional experiments, data, or analyses: 

The authors can demonstrate that identified pathological SNVs from their AD cohort also lead to the activation of human microglia-like cells in vitro, but do not provide any data from histological examination of the patient cohort (e.g. accumulation at the plaque site, microglia distribution, and cell number). The study could be further supported by providing a histological examination of patients with and without P-SNVs to identify if microglia response to pathology, microglia accumulation, or phagocytic capacity are altered in these patients. 

We performed IBA1 staining in brain samples from control and from AD patients, with or without microglial clones and microglia density was not different between patient with and without mutations. In addition, histological reports from the brain bank (Braak/CERAD scores, Lewis bodies, amyloid angiopathy, tauopathy, or alpha synucleinopathy did not suggest differences between patient with and without mutations (Figure S3). These results are preliminary and further investigations are ongoing.

It would have been interesting to see if for example, transgenic AD mice with an introduced somatic mutation in microglia show an altered disease progression with alterations in amyloid pathology or cognition. 

We agree with the reviewer. We performed an in vivo study with mice expressing a  5xFAD transgene, an inducible microglia Cx3cr1CreERt2 BrafLSL-V600E transgene, or both, and performed survival, behavioral (Y-Maze and Novel Object Recognition), and histological analyses for β-Amyloid, p-Tau and Iba1 staining.

Microgliosis was increased in the group with the 2 transgenes, however the phenotype associated with the expression of a BrafV600E allele in microglia (Mass et al Nature 2017) was strongly dominant over the phenotype of 5xFAD mice, which did not allow us to conclude on survival and behavioral analyses.

Other studies with different transgenes are in progress but we have no results yet to include in this revised manuscript.

To connect the somatic mutations in microglia better to a potential contribution in neurodegeneration or neurotoxicity, the authors could provide further details on how to demonstrate if human microglia-like cells respond differentially to amyloid or induce neurotoxicity in a co-culture or slice culture model. 

These studies are undertaken in the laboratory, but unfortunately, we have no results as yet to include in this revised manuscript.

The number of samples analyzed for hippocampi, especially in the age-matched controls might be underpowered. 

Unfortunately, despite our best efforts, we were not able to analyze more hippocampus from control individuals. To control for bias in sampling as well as to other potential bias in our analysis, we investigated the statistical analysis of the cohorts for inclusion of age as a criterion (age matched controls), inclusion of a random effect structure, and possible confounding factor such as sex, brain bank site, and samples’ anatomical location (see revised Methods and revised Fig. 2C, F, and H, and S2B).

We first tested whether the inclusion of age is appropriate in a fixed-effects linear regression using a generalized linear model (GLM) with gaussian distribution. Compared to the baseline model, the model with age had significantly low AIC (from -66.6 to -71.9, P = 0.0067 by chi-square test). Therefore, the inclusion of age as a fixed effect is appropriate. We next tested multiple structures of mixed-effects linear modeling. We used donors as random effects, while utilizing age, disease status (neurotypical control vs. AD), or both as fixed effects. Fitting was performed using the lme function implemented in the nlme package with the maximum likelihood (ML) method. The incorporation of age and disease status significantly improved overall model fitting. Both age and AD are associated with a significant increase in SNV burden in this model (P<1x10^-4 and P=1x10^-4, respectively, by likelihood ratio test). The model's total explanatory power is substantial (conditional R^2=0.48). We also asked if the addition of potential confounding factors to the model is justified. Three factors were tested via the two above-mentioned methods: sex, brain bank site, and the anatomical location of the samples. In all cases, the AIC increased, and the P values by likelihood ratio tests were higher than 0.99. Therefore, from a statistical standpoint, the inclusion of these potential confounding factors does not seem to improve overall model fitting.

Minor corrections to the text and figures: 

The authors made a great effort to analyze various samples from one individual donor. One can get a bit confused by the sentence that "an average of 2.5 brains samples were analyzed for each donor". Maybe the authors could highlight more in the first paragraph of the results section and in Figure 1A, that there are multiple samples ("technical replicates") from one individual patient across different brain regions used. 

We removed the ‘2.5’ sentence and rewrote the paragraph for clarity. Samples information’s are now displayed in Table S1.

In the method section is a part included "Expression of target genes in microglia", it was very hard to allocate where these data from public data sets were actually used and for which analysis. Maybe the authors could clarify this again. 

AU response: we apologize and corrected the paragraph in the methods (page 6) as follow: “ Expression of target genes in microglia. To evaluate the expression levels of the genes identified in this study as target of somatic variants, we consulted a publicly available database (https://www.proteinatlas.org/), and also plotted their expression as determined by RNAseq in 2 studies (Galatro et al. GSE99074 33, and Gosselin et al. 34) (Table S3 and Figure S2). For data from Galatro et al. (GSE99074) 33, normalized gene expression data and associated clinical information of isolated human microglia (N = 39) and whole brain (N = 16) from healthy controls were downloaded from GEO. For data from Gosselin et al. 34, raw gene expression ­data and associated clinical information of isolated microglia (N = 3) and whole brain (N = 1) from healthy controls were extracted from the original dataset. Raw counts were normalized using the DESeq2 package in R 35.”

Table S3 is very informative, but also very complex. The reader could maybe benefit a lot from this table if it can be structured a bit easier especially when it comes to identifying P-SNVs and in which tissue sample they were found and if this was the same patient. The sorting function on top of the columns helps, but the color coding is a bit unclear. 

Despite our best efforts we agree that the table, which contain all sequencing data for all samples, is complex. The color coding (red) only highlights the presence of pathogenic mutation.

Reviewer #3 (Recommendations For The Authors): 

This is a well-done study of an important problem. I present the following minor critiques: 

At the bottom of Page 4 and into the top of Page 5, the authors state that 66 of the 826 variants identified in their panel sequencing experiment were found in multiple donors. Then the authors proceed to analyze the remaining 760 variants. It seems that the authors concluded that these multi-donor mosaics were artifacts, which is why they were excluded from further analysis. I think this is a reasonable assumption, but it should be stated explicitly so it is clear to the reader. Complicating this assumption, however, the authors later state that one of their CBL variants was found in two donors, and it is treated as a true mosaic. The authors should make it clear whether recurrent variants were filtered out of any given analysis. It remains possible that all recurrent variants are true mosaics that occurred in multiple donors. The authors should do a bit more to characterize these recurrent variants. Are they observed in the human population using a database like gnomAD, which, together with their recurrence, would strongly suggest they are germline variants? Are they in MAPK genes, or otherwise relevant to the study?

We apologize for the confusion. Our original intent for the ddPCR validation of variants (Figure 1E) was to count only 1 ‘unique’ variant for variants found for example in 1 brain sample and in the blood from the same patient, or in 2 brain regions from one patient, in order to avoid the criticism of overinflating our validation rate. This was notably the case for TET2 and DNMT3 variants. For example, validation of a TET2 variant found in 2 different brain areas and blood of the same donor is counted as 1 and not 3. We did not eliminate these variants from the analysis as they passed the criteria for somatic variants as presented in Methods.

In contrast, when a specific variant was found and validated in two different donors, we counted it as 2.

The characterization of variants included multiple parameters and databases, including for example AF and gnomAD, as indicated in Methods and reported in Table S3.

All ddPCR results can be found at the end of Table S3.

Figure 2B labels age-matched controls as "C", but Figure 2C labels age-matched controls as AM-C. Labels should be consistent throughout the manuscript. 

We corrected this in the revised version.

It is not clear if the "p:0.02" label in Figure 2F is referring to AM-C Cx vs. AD-Cx or AM-C vs. AD. Please clarify. 

We apologize for the confusion, and we corrected the legend. The calculated p value is for the comparison between Cortex from Controls (age-matched) and the Cortex from AD.

On Page 7, the authors state, "The allelic frequencies at which MAPK activating variants are detected in brain samples from AD patients range from ~1-6% of microglia (Fig. 3G), which correspond to clones representing 2 to 12% of mutant microglia in these samples, assuming heterozygosity." I understand what the authors mean here but I think it's a bit confusingly stated. I suggest something like "The allelic frequencies at which MAPK activating variants are detected in brain samples from AD patients range from ~1-6% in microglia (Figure 3G), which correspond to mutant clones representing 2 to 12% of all microglia in these samples, assuming heterozygosity." 

We thank the reviewer for this suggestion and re-wrote that sentence.

Is there any evidence that the transcriptional regulators mutated in AD microglia (MED12, SETD2, MLL3, DNMT3A, ASXL1, etc.) are involved in regulating MAPK genes? This would tie these mutations into the broader conclusions of the paper. 

This is a very interesting question, and indeed published studies indicate that some of the transcriptional /epigenetic regulators regulate expression of MAPK genes. However, in the absence of experimental evidence in microglia and patients, the argument may be too speculative to be included.

Do the authors have any thoughts as to whether germline variants in CBL are linked to AD? If not, why do they think germline mutations in CBL are not relevant to AD? 

This is also a very interesting question. As indicated in our manuscript, germline mutations in CBL (and other member of the classical MAPK genes, see Figure 3C) cause early onset (pediatric) and severe developmental diseases known as RASopathies, characterized by multiple developmental defects, and associated with frequent neurological and cognitive deficits.

It is possible that some other (and more frequent?) germline variants may be associated with a late-onset brain restricted phenotype, but we did not find germline pSNV in our patients. GWAS studies may be more appropriate to test this hypothesis.

Do any donors show multiple variants? I don't think this is addressed in the text. 

We do find donors with multiple variants (see Figure 3D and Figure S3), however at this stage, we did not perform single nuclei genotyping to investigate whether they are part of the same clone.

Figure S3 appears to be upside down. 

This was corrected

Figure 5C should have some kind of label telling the reader what gene set is being depicted. 

We added this information above the panel (it was in the corresponding legend).

At the top of Page 12, Lewy bodies are written as Lewis bodies. 

This was corrected

Many control donors died of cancer (Table S1). Is there any information on which, if any, chemotherapeutics or radiation these patients received? Might this impact the somatic mutation burden? The authors should compare controls with and without cancer or with and without cancer treatments to rule this out. 

As suggested by the reviewer, we analyzed the mutational load of age-matched controls with and without cancer (revised Figure S2B). As expected, we saw an increase in the mutational load in controls with cancer, particularly in their blood. This information was added in the result section.

This is most likely associated with the treatments received as well as possible cancer clones.

The formatting for Table S3 is odd. Multiple different fonts are used (this is also seen in Table S5). Column Q has no column ID. The word "panel" is spelled "pannel." The word "expressed" is spelled "expressd" in one of the worksheet labels. Columns BG-BN in the ALL-SNV worksheet are blank but seemingly part of the table. 

We fixed this error in Table S3.

Author response:

The following is the authors’ response to the original reviews.

We thank the reviewers for their constructive reviews.  Taken together, the comments and suggestions from reviewers made it clear that we needed to focus on improving the clarity of the methods and results.  We have revised the manuscript with that in mind.  In particular, we have restructured the results to make the logic of the manuscript clearer and we have added details to the methods section.

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The work of Muller and colleagues concerns the question of where we place our feet when passing uneven terrain, in particular how we trade-off path length against the steepness of each single step. The authors find that paths are chosen that are consistently less steep and deviate from the straight line more than an average random path, suggesting that participants indeed trade-off steepness for path length. They show that this might be related to biomechanical properties, specifically the leg length of the walkers. In addition, they show using a neural network model that participants could choose the footholds based on their sensory (visual) information about depth. 

Strengths: 

The work is a natural continuation of some of the researchers' earlier work that related the immediately following steps to gaze [17]. Methodologically, the work is very impressive and presents a further step forward towards understanding real-world locomotion and its interaction with sampling visual information. While some of the results may seem somewhat trivial in hindsight (as always in this kind of study), I still think this is a very important approach to understanding locomotion in the wild better. 

Weaknesses: 

The manuscript as it stands has several issues with the reporting of the results and the statistics. In particular, it is hard to assess the inter-individual variability, as some of the data are aggregated across individuals, while in other cases only central tendencies (means or medians) are reported without providing measures of variability; this is critical, in particular as N=9 is a rather small sample size. It would also be helpful to see the actual data for some of the information merely described in the text (e.g., the dependence of \Delta H on path length). When reporting statistical analyses, test statistics and degrees of freedom should be given (or other variants that unambiguously describe the analysis).

There is only one figure (Figure 6) that shows data pooled over subjects and this is simply to illustrate how the random paths were calculated. The actual paths generated used individual subject data. We don’t draw our conclusions from these histograms – they are instead used to generate bounds for the simulated paths.  We have made clear both in the text and in the figure legends when we have plotted an example subject. Other plots show the individual subject data. We have given the range of subject medians as well as the standard deviation for data illustrated in Figure (random vs chosen), we have also given the details of the statistical test comparing the flatness of the chosen paths versus the randomly generated paths.  We have added two supplemental figures to show individual walker data more directly: (Fig. 14) the per subject histograms of step parameters, (Fig. 18) the individual subject distributions for straight path slopes and tortuosity.

The CNN analysis chosen to link the step data to visual sampling (gaze and depth features) should be motivated more clearly, and it should describe how training and test sets were generated and separated for this analysis.

We have motivated the CNN analysis and moved it earlier in the manuscript to help clarify the logic the manuscript. Details of the training and test are now provided, and the data have been replotted. The values are a little different from the original plot after making a correction in the code, but the conclusions drawn from this analysis are unchanged. This analysis simply shows that there is information in the depth images from the subject’s perspective that a network can use to learn likely footholds. This motivates the subsequent analysis of path flatness.

There are also some parts of figures, where it is unclear what is shown or where units are missing. The details are listed in the private review section, as I believe that all of these issues can be fixed in principle without additional experiments. 

Several of the Figures have been replotted to fix these issues.

Reviewer #2 (Public Review): 

Summary: 

This manuscript examines how humans walk over uneven terrain using vision to decide where to step. There is a huge lack of evidence about this because the vast majority of locomotion studies have focused on steady, well-controlled conditions, and not on decisions made in the real world. The author team has already made great advances in this topic, but there has been no practical way to map 3D terrain features in naturalistic environments. They have now developed a way to integrate such measurements along with gaze and step tracking, which allows quantitative evaluation of the proposed trade-offs between stepping vertically onto vs. stepping around obstacles, along with how far people look to decide where to step. 

Strengths: 

(1) I am impressed by the overarching outlook of the researchers. They seek to understand human decision-making in real-world locomotion tasks, a topic of obvious relevance to the human condition but not often examined in research. The field has been biased toward well-controlled studies, which have scientific advantages but also serious limitations. A well-controlled study may eliminate human decisions and favor steady or periodic motions in laboratory conditions that facilitate reliable and repeatable data collection. The present study discards all of these usually-favorable factors for rather uncontrolled conditions, yet still finds a way to explore real-world behaviors in a quantitative manner. It is an ambitious and forward-thinking approach, used to tackle an ecologically relevant question. 

(2) There are serious technical challenges to a study of this kind. It is true that there are existing solutions for motion tracking, eye tracking, and most recently, 3D terrain mapping. However most of the solutions do not have turn-key simplicity and require significant technical expertise. To integrate multiple such solutions together is even more challenging. The authors are to be commended on the technical integration here.

(3) In the absence of prior studies on this issue, it was necessary to invent new analysis methods to go with the new experimental measures. This is non-trivial and places an added burden on the authors to communicate the new methods. It's harder to be at the forefront in the choice of topic, technical experimental techniques, and analysis methods all at once. 

Weaknesses: 

(1) I am predisposed to agree with all of the major conclusions, which seem reasonable and likely to be correct. Ignoring that bias, I was confused by much of the analysis. There is an argument that the chosen paths were not random, based on a comparison of probability distributions that I could not understand. There are plots described as "turn probability vs. X" where the axes are unlabeled and the data range above 1. I hope the authors can provide a clearer description to support the findings. This manuscript stands to be cited well as THE evidence for looking ahead to plan steps, but that is only meaningful if others can understand (and ultimately replicate) the evidence. 

We have rewritten the manuscript with the goal of clarifying the analyses, and we have re-labelled the offending figure.

(2) I wish a bit more and simpler data could be provided. It is great that step parameter distributions are shown, but I am left wondering how this compares to level walking.  The distributions also seem to use absolute values for slope and direction, for understandable reasons, but that also probably skews the actual distribution. Presumably, there should be (and is) a peak at zero slope and zero direction, but absolute values mean that non-zero steps may appear approximately doubled in frequency, compared to separate positive and negative. I would hope to see actual distributions, which moreover are likely not independent and probably have a covariance structure. The covariance might help with the argument that steps are not random, and might even be an easy way to suggest the trade-off between turning and stepping vertically. This is not to disregard the present use of absolute values but to suggest some basic summary of the data before taking that step. 

We have replotted the step parameter distributions without absolute values. Unfortunately, the covariation of step parameters (step direction and step slope) is unlikely to help establish this tradeoff.  Note that the primary conclusion of the manuscript is that works make turns to keep step slope low (when possible). Thus, any correlation that might exist between goal direction and step slope would be difficult to interpret without a direct comparison to possible alternative paths (as we have done in this paper). As such we do not draw our conclusions from them.  We use them primarily to generate plausible random paths for comparison with the chosen paths.  We have added two supplementary figures including distributions (Fig 15) and covariation of all the step parameters discussed in the methods (Fig 16).

(3) Along these same lines, the manuscript could do more to enable others to digest and go further with the approach, and to facilitate interpretability of results. I like the use of a neural network to demonstrate the predictiveness of stepping, but aside from above-chance probability, what else can inform us about what visual data drives that?

The CNN analysis simply shows that the information is there in the image from the subject’s viewpoint and is used to motivate the subsequent analysis.  As noted above, we have generally tried to improve the clarity of the methods.

Similarly, the step distributions and height-turn trade-off curves are somewhat opaque and do not make it easy to envision further efforts by others, for example, people who want to model locomotion. For that, clearer (and perhaps) simpler measures would be helpful. 

We have clarified the description of these plots in the main text and in the methods.  We have also tried to clarify why we made the choices that we did in measuring the height-turn trade-off and why it is necessary in order to make a fair comparison.

I am absolutely in support of this manuscript and expect it to have a high impact. I do feel that it could benefit from clarification of the analysis and how it supports the conclusions. 

Reviewer #3 (Public Review): 

Summary: 

The systematic way in which path selection is parametrically investigated is the main contribution. 

Strengths: 

The authors have developed an impressive workflow to study gait and gaze in natural terrain. 

Weaknesses: 

(1) The training and validation data of the CNN are not explained fully making it unclear if the data tells us anything about the visual features used to guide steering. It is not clear how or on what data the network was trained (training vs. validation vs. un-peeked test data), and justification of the choices made. There is no discussion of possible overfitting. The network could be learning just e.g. specific rock arrangements. If the network is overfitting the "features" it uses could be very artefactual, pixel-level patterns and not the kinds of "features" the human reader immediately has in mind. 

The CNN analysis has now been moved earlier in the manuscript to help clarify its significance and we have expanded the description of the methods. Briefly, it simply indicates that there is information in the depth structure of the terrain that can be learned by a network. This helps justify the subsequent analyses.  Importantly, the network training and testing sets were separated by terrain to ensure that the model was being tested on “unseen” terrain and avoid the model learning specific arrangements.  This is now clarified in the text.