eLife Assessment

By combining the 'pinging' technique with fMRI-based multivariate pattern analysis, this important study provides convincing evidence for a dual-format of attentional representation during preparatory period. The result reconciles the competing views between the sensory-like versus non-sensory accounts of attentional template and advances our understanding of how the brain flexibly utilizes different versions of template to guide attention. This work will be of interest to researchers in psychology, vision science, and cognitive science.

Reviewer #1 (Public review):

Summary:

The aim of the experiment reported in this paper is to examine the nature of the representation of a template of an upcoming target. To this end, participants were presented with compound gratings (consisting of tilted to the right and tilted to the left lines) and were cued to a particular orientation - red left tilt or blue right tilt (counterbalanced across participants). There are two directly compared conditions: (i) no ping: where there was a cue, that was followed by a 5.5-7.5s delay, then followed by a target grating in which the cued orientation deviated from the standard 45 degrees; and (ii) ping condition in which all aspects were the same with the only difference that a ping (visual impulse presented for 100ms) was presented after the 2.5 seconds following the cue. There was also a perception task in which only the 45 degrees to the right or to the left lines were presented. It was observed that during the delay, only in the ping condition, were the authors able to decode the orientation of the to-be-reported target using the cross-task generalization. Attention decoding, on the other hand, was decoded in both ping and non-ping conditions. It is concluded that the visual system has two different functional states associated with a template during preparation: a predominantly non-sensory representation for guidance and a latent sensory-like for prospective stimulus processing.

Strengths:

There is so much to be impressed with in this report. The writing of the manuscript is incredibly clear. The experimental design is clever and innovative. The analysis is sophisticated and also innovative - the cross-task decoding, the use of Mahalanobis distance as a function of representational similarity, the fact that the question is theoretically interesting, and the excellent figures.

Weaknesses:

While I think that this is an interesting study that addresses an important theoretical question, I have several concerns about the experimental paradigm and the subsequent conclusions that can be drawn.

(1) Why was V1 separated from the rest of the visual cortex, and why the rest of the areas were simply lumped into an EVC ROI? It would be helpful to understand the separation into ROIs.

(2) It would have been helpful to have a behavioral measure of the "attended" orientation to show that participants in fact attended to a particular orientation and were faster in the cued condition. The cue here was 100% valid, so no such behavioral measure of attention is available here.

(3) As I was reading the manuscript I kept thinking that the word attention in this manuscript can be easily replaced with visual working memory. Have the authors considered what it is about their task or cognitive demand that makes this investigation about attention or working memory?

(4) If I understand correctly, the only ROI that showed a significant difference for the cross-task generalization is V1. Was it predicted that only V1 would have two functional states? It should also be made clear that the only difference where the two states differ is V1.

(5) My primary concern about the interpretation of the finding is that the result, differences in cross-task decoding within V1 between the ping and no-ping condition might simply be explained by the fact that the ping condition refocuses attention during the long delay thus "resharpening" the template. In the no-ping condition during the 5.5 to 7.5 seconds long delay, attention for orientation might start getting less "crisp." In the ping condition, however, the ping itself might simply serve to refocus attention. So, the result is not showing the difference between the latent and non-latent stages, rather it is the difference between a decaying template representation and a representation during the refocused attentional state. It is important to address this point. Would a simple tone during the delay do the same? If so, the interpretation of the results will be different.

(6) The neural pattern distances measured using Mahalanobis values are really great! Have the authors tried to use all of the data, rather than the high AMI and low AMI to possibly show a linear relationship between response times and AMI?

(7) After reading the whole manuscript I still don't understand what the authors think the ping is actually doing, mechanistically. I would have liked a more thorough discussion, rather than referencing previous papers (all by the co-author).

Comments on revisions:

I am impressed with the thoroughness with which the authors addressed my concerns. I don't have any further concerns and think that this paper makes an interesting and significant contribution to our understanding of VWM. I would only suggest adding citations to the newly added paragraph where the authors state "It could be argued that preparatory attention relies on the same mechanisms as working memory maintenance." They could cite work by Bettencourt and Xu, 2016; and Sheremata, Somers, and Shomstein (2018).

Reviewer #2 (Public review):

Summary:

In the present study, the authors investigated the nature of attentional templates during preparatory period of goal-directed attention. By combing the use of 'pinging' the neural activity with a visual impulse and fMRI-based multivariate decoding, the authors found that the nature of the neural representations of the prospective feature target during preparatory period was contingent on the presence of the 'pinging' impulse. While the preparatory representations contained highly similar information content as the perceptual representations when the pinging impulse was introduced, they fundamentally differed from perceptual representations in the absence of the pinging impulse. Based on these findings, the authors proposed a dual-format mechanism in which both a "non-sensory" template and a latent "sensory" template coexisted during attentional preparation. The former actively guides activity in the preparatory state, and the latter is utilized for future stimulus processing.

Strengths:

Overall, I think that the authors' revision has addressed most, if not all, of my major concerns noted in my previous comments.

Weaknesses:

The results appear convincing and I do not have additional comments.

Reviewer #3 (Public review):

This paper discusses how non-sensory and latent, sensory-like attentional templates are represented during attentional preparation. Using multivariate pattern analysis, they found that visual impulses can enhance the decoding generalization from perception to attention tasks in the preparatory stage in the visual cortex. Furthermore, the emergence of the sensory-like template coincided with enhanced information connectivity between V1 and frontoparietal areas and was associated with improved behavioral performance. It is an interesting paper with supporting evidence for the latent, sensory-like attentional template.

(1) The authors addressed most of my previous concerns and provided additional data analysis. They conducted further analyses to demonstrate that the observed changes in network communication are associated with behavioral RTs, supporting the idea that the impulse-driven sensory-like template enhances informational connectivity between sensory and frontoparietal areas, and relates to behavior.

(2) I would like to further clarify my previous points regarding the definition of the two types of templates and the evidence for their coexistence. The authors stated that the sensory-like template likely existed in a latent state and was reactivated by visual pings, proposing that sensory and non-sensory templates coexist. However, it remains unclear whether this reflects a dynamic switch between formats or true coexistence. If the templates are non-sensory in nature, what exactly do they represent? Are they meant to be abstract or conceptual representations, or, put simply, just "top-down attentional information"? If so, why did the generalization analyses-training classifiers on activity during the stimulus selection period and testing on preparatory activity-fail to yield significant results? While the stimulus selection period necessarily encodes both target and distractor information, it should still contain attentional information. I would appreciate more discussion from this perspective.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) Why was V1 separated from the rest of the visual cortex, and why the rest of the areas were simply lumped into an EVC ROI? It would be helpful to understand the separation into ROIs.

We thank the reviewer for raising the concerns regarding the definition of ROI. Our approach to analyze V1 separately was based on two key considerations. First, previous studies consistently identify V1 as the main locus of sensory-like templates during featurespecific preparatory attention (Kok et al., 2014; Aitken et al., 2020). Second, V1 shows the strongest orientation selectivity within the visual hierarchy (Priebe, 2016). In contrast, the extrastriate visual cortex (EVC; comprising V2, V2, V3AB and V4) demonstrates broader selectivity, such as complex features like contour and texture (Grill-Spector & Malach, 2004). Thus, we think it would be particularly informative to analyze V1 data separately as our experiment examines orientation-based attention. We should also note that we conducted MVPA separately for each visual ROIs (V2, V3, V3AB and V4). After observing similar patterns of results across these regions, we averaged the decoding accuracies into a single value and labeled it as EVC. This approach allowed us to simplify data presentation while preserving the overall data pattern in decoding performance. We now added the related explanations on the ROI definition in the revised texts (Page 26; Line 576-581).

(2) It would have been helpful to have a behavioral measure of the "attended" orientation to show that participants in fact attended to a particular orientation and were faster in the cued condition. The cue here was 100% valid, so no such behavioral measure of attention is available here.

We thank the reviewer for the comments. We agree that including valid and neutral cue trials would have provided valuable behavioral measures of attention; Yet, our current design was aimed at maximizing the number of trials for decoding analysis due to fMRI time constraints. Thus, we could not fit additional conditions to measure the behavioral effects of attention. However, we note that in our previous studies using a similar feature cueing paradigm, we observed benefits of attentional cueing on behavioral performance when comparing valid and neutral conditions (Liu et al., 2007; Jigo et al., 2018). Furthermore, our neural data indeed demonstrated attention-related modulation (as indicated by MVPA results, Fig. 2 in the main texts) so we are confident that on average participants followed the instruction and deployed their attention accordingly. We now added the related explanations on this point in the revised texts (Page 23; Line 492-498).

(3) As I was reading the manuscript I kept thinking that the word attention in this manuscript can be easily replaced with visual working memory. Have the authors considered what it is about their task or cognitive demand that makes this investigation about attention or working memory?

We thank the reviewer for this comment. We added the following extensive discussion on this point in the revised texts (Page 18; Line 363-381).

“It could be argued that preparatory attention relies on the same mechanisms as working memory maintenance. While these functions are intuitively similar and likely overlap, there is also evidence indicating that they can be dissociated (Battistoni et al., 2017). In particular, we note that in our task, attention is guided by symbolic cues (color-orientation associations), while working memory tasks typically present the actual visual stimulus as the memorandum. A central finding in working memory studies is that neural signals during WM maintenance are sensory in nature, as demonstrated by generalizable neural activity patterns from stimulus encoding to maintenance in visual cortex (Harrison & Tong, 2009; Serences et al., 2009; Rademaker et al., 2019). However, in our task, neural signals during preparation were nonsensory, as demonstrated by a lack of such generalization in the No-Ping session (see also Gong et al., 2022). We believe that the differences in cue format and task demand in these studies may account for such differences. In addition to the difference in the sensory nature of the preparatory versus delay-period activity, our ping-related results also exhibited divergence from working memory studies (Wolff et al., 2017; 2020). While these studies used the visual impulse to differentiate active and latent representations of different items (e.g., attended vs. unattended memory item), our study demonstrated the active and latent representations of a single item in different formats (i.e., non-sensory vs. sensory-like). Moreover, unlike our study, the impulse did not evoke sensory-like neural patterns during memory retention (Wolff et al., 2017). These observations suggest that the cognitive and neural processes underlying preparatory attention and working memory maintenance could very well diverge. Future studies are necessary to delineate the relationship between these functions both at the behavioral and neural level.”

(4) If I understand correctly, the only ROI that showed a significant difference for the crosstask generalization is V1. Was it predicted that only V1 would have two functional states? It should also be made clear that the only difference where the two states differ is V1.

We thank the reviewer for this comment. We would like to clarify that our analyses revealed similar patterns of preparatory attentional representations in V1 and EVC. During the Ping session, the cross-task generalization analyses revealed decodable information in both V1 and EVC (ps < 0.001), significantly higher than that in the No-Ping session for V1 (independent t-test: t(38) = 3.145, p = 0.003; Cohen’s d = 0.995) and EVC (independent t-test: t(38) = 2.153, p = 0.038, Cohen’s d = 0.681) (Page 10; Line 194-196). While both areas maintained similar representations, additional measures (Mahalanobis distance, neural-behavior relationship and connectivity changes) showed more robust ping-evoked changes in V1 compared to EVC. This differential pattern likely reflects the primary role of V1 in orientation processing, with EVC showing a similar but weaker response profile. We have revised the text to clarity this point (Page 16; Line 327-329).

(5) My primary concern about the interpretation of the finding is that the result, differences in cross-task decoding within V1 between the ping and no-ping condition might simply be explained by the fact that the ping condition refocuses attention during the long delay thus "resharpening" the template. In the no-ping condition during the 5.5 to 7.5 seconds long delay, attention for orientation might start getting less "crisp." In the ping condition, however, the ping itself might simply serve to refocus attention. So, the result is not showing the difference between the latent and non-latent stages, rather it is the difference between a decaying template representation and a representation during the refocused attentional state. It is important to address this point. Would a simple tone during the delay do the same? If so, the interpretation of the results will be different.

We thank the reviewer for this comment. The reviewer proposed an alternative account suggesting that visual pings may function to refocus attention, rather than reactivate latent information during the preparatory period. If this account holds (i.e., attention became weaker in the no-ping condition and it was strengthened by the ping due to re-focusing), we would expect to observe a general enhancement of attentional decoding during the preparatory period. However, our data reveal no significant differences in overall attention decoding between two conditions during this period (ps > 0.519; BF_excl > 3.247), arguing against such a possibility.

The reviewer also raised an interesting question about whether an auditory tone during preparation could produce effects similar to those observed with visual pings. Although our study did not directly test this possibility, existing literature provides some relevant evidence. In particular, prior studies have shown that latent visual working memory contents are selectively reactivated by visual impulses, but not by auditory stimuli (Wolff et al., 2020). This finding supports the modality-specificity for visually encoded contents, suggesting that sensory impulses must match the representational domain to effectively access latent visual information, which also argues against the refocusing hypothesis above. However, we do think that this is an important question that merits direct investigation in future studies. We now added the related discussion on this point in the revised texts (Page 10, Line 202-203; Page 19, Line 392395).

(6) The neural pattern distances measured using Mahalanobis values are really great! Have the authors tried to use all of the data, rather than the high AMI and low AMI to possibly show a linear relationship between response times and AMI?

We thank the reviewer for this comment. We took the reviewer’s suggestion to explore the relationship between attentional modulation index (AMI) and RTs across participants for each session (see Figure 3). In the No-Ping session, we observed no significant correlation between AMI and RT (r = -0.366, p = 0.113). By contrast, the same analysis in the Ping condition revealed a significantly negative correlation (r = -0.518, p = 0.019). These results indicate that the attentional modulations evoked by visual impulse was associated with faster RTs, supporting the functional relevance of activating sensory-like representations during preparation. We have now included these inter-subject correlations in the main texts (Page 13, Line 258-264; Fig 3D and 3E) along with within-subject correlations in the Supplementary Information (Page 6, Line, 85-98; S3 Fig).

(7) After reading the whole manuscript I still don't understand what the authors think the ping is actually doing, mechanistically. I would have liked a more thorough discussion, rather than referencing previous papers (all by the co-author).

We thank the reviewer for this comment regarding the mechanistic basis of visual pings. We agree that this warrants deeper discussion. One possibility, as informed by theoretical studies of working memory, is that the sensory-like template could be maintained via an “activity-silent” mechanism through short-term changes in synaptic weights (Mongillo et al., 2008). In this framework, a visual impulse may function as nonspecific inputs that momentarily convert latent traces into detectable activity patterns (Rademaker & Serences, 2017). Related to our findings, it is unlikely that the orientation-specific templates observed during the Ping session emerged from purely non-sensory representations and were entirely induced by an exogenous ping, which was devoid of any orientation signal. Instead, the more parsimonious explanation is that visual impulse reactivated pre-existing latent sensory signals. To our knowledge, the detailed circuit-level mechanism of such reactivation is still unclear; existing evidence only suggests a relationship between ping-evoked inputs and the neural output (Wolff et al., 2017; Fan et al., 2021; Duncan et al., 2023). We now included the discussion on this point in the main texts (Page 19, Line 383-401).

Reviewer #2 (Public review):

(1) The origin of the latent sensory-like representation. By 'pinging' the neural activity with a high-contrast, task-irrelevant visual stimulus during the preparation period, the authors identified the representation of the attentional feature target that contains the same information as perceptual representations. The authors interpreted this finding as a 'sensory-like' template is inherently hosted in a latent form in the visual system, which is revealed by the pinging impulse. However, I am not sure whether such a sensory-like template is essentially created, rather than revealed, by the pinging impulses. First, unlike the classical employment of the pinging technique in working memory studies, the (latent) representation of the memoranda during the maintenance period is undisputed because participants could not have performed well in the subsequent memory test otherwise. However, this appears not to be the case in the present study. As shown in Figure 1C, there was no significant difference in behavioral performance between the ping and the no-ping sessions (see also lines 110-125, pg. 5-6). In other words, it seems to me that the subsequent attentional task performance does not necessarily rely on the generation of such sensory-like representations in the preparatory period and that the emergence of such sensory-like representations does not facilitate subsequent attentional performance either. In such a case, one might wonder whether such sensory-like templates are really created, hosted, and eventually utilized during the attentional process. Second, because the reference orientations (i.e. 45 degrees and 135 degrees) have remained unchanged throughout the experiment, it is highly possible that participants implicitly memorized these two orientations as they completed more and more trials. In such a case, one might wonder whether the 'sensory-like' templates are essentially latent working memory representations activated by the pinging as was reported in Wolff et al. (2017), rather than a functional signature of the attentional process.

We thank the reviewer for this comment. We agree that the question of whether the sensory-like template is created or merely revealed by visual pinging is crucial for the understanding our findings. First, we acknowledge that our task may not be optimized for detecting changes in accuracy, as the task difficulty was controlled using individually adjusted thresholds (i.e., angular difference). Nevertheless, we observed some evidence supporting the neural-behavioral relationships. In particular, the impulse-driven sensory-like template in V1 contributed to facilitated faster RTs during stimulus selection (Page 12, Fig. 3D and 3E in the main texts; also see our response to R1, Point 6).

Second, the reviewer raised an important concern about whether the attended feature might be stored in the memory system due to the trial-by-trial repetition of attention conditions (attend 45º or attend 135º). Although this is plausible, we don’t think it is likely. We note that neuroimaging evidence shows that attended working memory contents maintain sensory-like representations in visual cortex (Harrison & Tong, 2009; Serences et al., 2009; Rademaker et al., 2019), with generalizable neural activity patterns from perception to working memory delay-period, whereas unattended items in multi-item working memory tasks are stored in a latent state for prospective use (Wolff et al., 2017). Importantly, our task only required maintaining a single attentional template at a time. Thus, there was no need to store it via latent representations, if participants simply used a working memory mechanism for preparatory attention. Had they done so, we should expect to find evidence for a sensory template, i.e., generalizable neural pattern between perception and preparation in the No-Ping condition, which was not what we found. We have mentioned this point in the main texts (Page 18, Line 367-372).

(2) The coexistence of the two types of attentional templates. The authors interpreted their findings as the outcome of a dual-format mechanism in which 'a non-sensory template' and a latent 'sensory-like' template coexist (e.g. lines 103-106, pg. 5). While I find this interpretation interesting and conceptually elegant, I am not sure whether it is appropriate to term it 'coexistence'. First, it is theoretically possible that there is only one representation in either session (i.e. a non-sensory template in the no-ping session and a sensory-like template in the ping session) in any of the brain regions considered. Second, it seems that there is no direct evidence concerning the temporal relationship between these two types of templates, provided that they commonly emerge in both sessions. Besides, due to the sluggish nature of fMRI data, it is difficult to tell whether the two types of templates temporally overlap.

We thank the reviewer for the comment regarding our interpretation of the ‘coexistence’ of non-sensory and sensory-like attentional template. While we acknowledge the limitations of fMRI in resolving temporal relationships between these two types of templates, several aspects of our data support a dual-format interpretation.

First, our key findings remained consistent for the subset of participants (N=14) who completed both No-Ping and Ping sessions in counterbalanced order. It thus seems improbable that participants systematically switched cognitive strategies (e.g., using non-sensory templates in the No-Ping session versus sensory-like templates in the Ping session) in response to the task-irrelevant, uninformative visual impulse. Second, while we agree with the reviewer that the temporal dynamics between these two templates remain unclear, it is difficult to imagine that orientation-specific templates observed during the Ping session emerged de novo from a purely non-sensory templates and an exogenous ping. In other words, if there is no orientation information at all to begin with, how does it come into being from an orientation-less external ping? It seems to us that the more parsimonious explanation is that there was already some orientation signal in a latent format, and it was activated by the ping, in line with the models of “activity-silent” working memory. To address these concerns, we have added the related discussion of these alternative interpretations in the main texts (Page 19, Line 387-391)

(3) The representational distance. The authors used Mahalanobis distance to quantify the similarity of neural representation between different conditions. According to the authors' hypothesis, one would expect greater pattern similarity between 'attend leftward' and 'perceived leftward' in the ping session in comparison to the no-ping session. However, this appears not to be the case. As shown in Figures 3B and C, there was no major difference in Mahalanobis distance between the two sessions in either ROI and the authors did not report a significant main effect of the session in any of the ANOVAs. Besides, in all the ANOVAs, the authors reported only the statistic term corresponding to the interaction effect without showing the descriptive statistics related to the interaction effect. It is strongly advised that these descriptive statistics related to the interaction effect should be included to facilitate a more effective and intuitive understanding of their data.

We thank the reviewer for this comment. We expected greater pattern similarity between 'attend leftward' and 'perceived leftward' in the Ping session in comparison to the Noping session. This prediction was supported by a significant three-way interaction effect between session × attended orientation × perceived orientation (F(1,38) = 5.00, p = 0.031, η_p² = 0.116). In particular, there was a significant interaction between attended orientation × perceived orientation (F(1,19) = 9.335, p = 0.007, η_p² = 0.329) in the Ping session, but not in the No-Ping session (F(1,19) = 0.017, p = 0.898, η_p² = 0.001). These above-mentioned statistical results were reported in the original texts. In addition, this three-way mixed ANOVA (session × attended orientation × perceived orientation) on Mahalanobis distance in V1 revealed no significant main effects (session: F(1,38) = 0.009, p = 0.923, η_p² < 0.001; attended orientation: F(1,38) = 0.116, p = 0.735, η_p² = 0.003; perceived orientation: (F(1,38) = 1.106, p = 0.300, η_p² = 0.028). We agree with the reviewer that a complete reporting of analyses enhances understanding of the data. Therefore, we have now included the main effects in the main texts (Page 11, Line 233).

We thank the reviewer for the suggestion regarding the inclusion of descriptive statistics for interaction effects. However, since the data were already visualized in Fig. 3B and 3C in the main texts, to maintain conciseness and consistency with the reporting style of other analyses in the texts, we have opted to include these statistics in the Supplementary Information (Page 5, Table 1).

Reviewer #3 (Public review):

(1) The title is "Dual-format Attentional Template," yet the supporting evidence for the nonsensory format and its guiding function is quite weak. The author could consider conducting further generalization analysis from stimulus selection to preparation stages to explore whether additional information emerges.

We thank the reviewer for this comment. Our approach to investigate whether preparatory attention is encoded in sensory or non-sensory format - by training classifier using separate runs of perception task – closely followed methods from previous studies (Stokes et al., 2009; Peelen et al., 2011; Kok et al., 2017). Following the reviewer’s suggestion, we performed generalization analyses by training classifiers on activity during the stimulus selection period and testing them preparatory activity. However, we observed no significant generalization effects in either No-Ping and Ping sessions (ps > 0.780). This null result may stem from a key difference in the neural representations: classifiers trained on neural activity from stimulus selection period necessarily encode both target and distractor information, thus relying on somewhat different information than classifier trained exclusively on isolated target information in the perception task.

(2) In Figure 2, the author did not find any decodable sensory-like coding in IPS and PFC, even during the impulse-driven session, indicating that these regions do not represent sensory-like information. However, in the final section, the author claimed that the impulse-driven sensorylike template strengthens informational connectivity between sensory and frontoparietal areas. This raises a question: how can we reconcile the lack of decodable coding in these frontoparietal regions with the reported enhancement in network communication? It would be helpful if the author provided a clearer explanation or additional evidence to bridge this gap.

We thank the reviewer for this comment. We would like to clarity that although we did not observe sensory-like coding during preparation in frontoparietal areas, we did observe attentional signals in these regions, as evidenced by the above-chance within-task attention decoding performance (Fig. 2 in the main texts). This could reflect different neural codes in different areas, and suggests that inter-regional communication does not necessarily require identical representational formats. It seems plausible that the representation of a non-sensory attentional template in frontoparietal areas supports top-down attentional control, consistent with theories suggesting increasing abstraction as the cortical hierarchy ascends (Badre, 2008; Brincat et al., 2018), and their interaction with the sensory representation in the visual areas is enhanced by the visual impulse.

(3) Given that the impulse-driven sensory-like template facilitated behavior, the author proposed that it might also enhance network communication. Indeed, they observed changes in informational connectivity. However, it remains unclear whether these changes in network communication have a direct and robust relationship with behavioral improvements.

We thank the reviewer for the suggestion. To examine how network communication relates to behavior, we performed a correlation analysis between information connectivity (IC) and RTs across participants (see Figure S5). We observed a trend of correlations between V1-PFC connectivity and RTs in the Ping session (r = -0.394, p = 0.086), but not in the NoPing session (r = -0.046, <i.p\</i> = 0.846). No significant correlations were found between V1-IPS and RTs (\ps\ > 0.400) or between ICs and accuracy (ps > 0.399). These results suggests that ping-enhanced connectivity might contributed to facilitated responses. Although we may not have sufficient statistical power to warrant a strong conclusion, we think this result is still highly suggestive, so we now added the texts in the Supplementary Information (Page 8, Line 116121; S5 Fig) and mentioned this result in the main texts (Page 14, Line 292-293).

(4) I'm uncertain about the definition of the sensory-like template in this paper. Is it referring to the Ping impulse-driven condition or the decodable performance in the early visual cortex? If it is the former, even in working memory, whether pinging identifies an activity-silent mechanism is currently debated. If it's the latter, the authors should consider whether a causal relationship - such as "activating the sensory-like template strengthens the informational connectivity between sensory and frontoparietal areas" - is reasonable.

We apologize for the confusions. The sensory-like template by itself does not directly refer to representations under Ping session or the attentional decoding in early visual cortex. Instead, it pertains to the representational format of attentional signals during preparation. Specifically, its existence is inferred from cross-task generalization, where neural patterns from a perception task (perceive 45º or perceive 135º) generalize to an attention task (attend 45 º or attend 135º). We think this is a reasonable and accepted operational definition of the representational format. Our findings suggest that the sensory-like template likely existed in a latent state and was reactivated by visual pings, aligning more closely with the first account raised by the reviewer.

We agree with the reviewer that whether ping identifies an activity-silent mechanism is currently debated (Schneegans & Bays, 2017; Barbosa et al., 2021). It is possible that visual impulse amplified a subtle but active representation of the sensory template during attentional preparation and resulted in decodable performance in visual cortex. Distinguishing between these two accounts likely requires neurophysiological measurements, which are beyond the scope of the current study. We have explicitly addressed this limitation in our Discussion (Page 19, Line 395-399).

Nevertheless, the latent sensory-like template account remains plausible for three reasons. First, our interpretation aligns with theoretical framework proposing that the brain maintains more veridical, detailed target templates than those typically utilized for guiding attention (Wolfe, 2021; Yu et al., 2023). Second, this explanation is consistent with the proposed utility of latent working memory for prospective use, as maintaining a latent sensory-like template during preparation would be useful for subsequent stimulus selection. The latter point was further supported by the reviewer’s suggestion about whether “activating the sensory-like template strengthens the informational connectivity between sensory and frontoparietal areas is reasonable”. Our additional analyses (also refer to our response to Reviewer 3, Point 3) suggested that impulse-enhanced V1-PFC connectivity was associated with a trend of faster behavioral responses (r = -0.394, p = 0.086; see Supplementary Information, Page 8, Line 116-121; S5 Fig). Considering these findings in totality, we think it is reasonable to suggest that visual impulse may strengthen information flow among areas to enhance attentional control.

Recommendation for the Authors:

Reviewer #1 (Recommendation for the authors):

I hate to suggest another fMRI experiment, but in order to make strong claims about two states, I would want to see the methodological and interpretation confounds addressed. Ping condition - would a tone lead to the same result of sharpening the template? If so, then why? Can a ping be manipulated in its effectiveness? That would be an excellent manipulation condition.

We thank the reviewer for the comments. Please refer to our reply to Reviewer 1, Point 5 for detailed explanation.

Reviewer #2 (Recommendation for the authors):

It is strongly advised that these descriptive statistics related to the interaction effect should be included to facilitate a more effective understanding of their data.

We thank the reviewer for the comments. We now included the relevant descriptive statistics in the Supplementary Information, Table 1.

Reviewer #3 (Recommendation for the authors):

In addition to p-values, I see many instances of 'ps'. Does this indicate the plural form of p?

We used ‘ps’ to denote the minimal p-value across multiple statistical analyses, such as when applying identical tests to different region groups.

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eLife Assessment

This study aims to clarify the effects of cochlear neural degeneration on auditory processing in listeners with normal audiograms (sometimes referred to as 'hidden hearing loss'). The authors provide important new data demonstrating associations between cochlear neural degeneration, non-invasive assays of auditory processing, and speech perception. Based on a cross-species comparison, the findings pose compelling evidence that cochlear synaptopathy is associated with a significant part of hearing difficulties in complex environments.

Reviewer #1 (Public review):

This study is part of an ongoing effort to clarify the effects of cochlear neural degeneration (CND) on auditory processing in listeners with normal audiograms. This effort is important because ~10% of people who seek help for hearing difficulties have normal audiograms and current hearing healthcare has nothing to offer them.

The authors identify two shortcomings in previous work that they intend to fix. The first is a lack of cross-species studies that make direct comparisons between animal models in which CND can be confirmed and humans for which CND must be inferred indirectly. The second is the low sensitivity of purely perceptual measures to subtle changes in auditory processing. To fix these shortcomings, the authors measure envelope following responses (EFRs) in gerbils and humans using the same sounds, while also performing histological analysis of the gerbil cochleae, and testing speech perception while measuring pupil size in the humans.

The study begins with a comprehensive assessment of the hearing status of the human listeners. The only differences found between the young adult (YA) and middle aged (MA) groups are in thresholds at frequencies > 10 kHz and DPOAE amplitudes at frequencies > 5 kHz. The authors then present the EFR results, first for the humans and then for the gerbils, showing that amplitudes decrease more rapidly with increasing envelope frequency for MA than for YA in both species. The histological analysis of the gerbil cochleae shows that there were, on average, 20% fewer IHC-AN synapses at the 3 kHz place in MA relative to YA, and the number of synapses per IHC was correlated with the EFR amplitude at 1024 Hz.

The study then returns to the humans to report the results of the speech perception tests and pupillometry. The correct understanding of keywords decreased more rapidly with decreasing SNR in MA than in YA, with a noticeable difference at 0 dB, while pupillary slope (a proxy for listening effort) increased more rapidly with decreasing SNR for MA than for YA, with the largest differences at SNRs between 5 and 15 dB. Finally, the authors report that a linear combination of audiometric threshold, EFR amplitude at 1024 Hz, and a few measures of pupillary slope is predictive of speech perception at 0 dB SNR.

I only have two questions/concerns about the specific methodologies used:

(1) Synapse counts were made only at the 3 kHz place on the cochlea. But the EFR sounds were presented at 85 dB SPL, which means that a rather large section of the cochlea will actually be excited. Do we know how much of the EFR actually reflects AN fibers coming from the 3 kHz place? And are we sure that this is the same for gerbils and humans given the differences in cochlear geometry, head size, etc.?

[Note added after revision: the authors have added new data, references, and discussion that have answered my initial questions].

(2) Unless I misunderstood, the predictive power of the final model was not tested on held out data. The standard way to fit and test such model would be to split the data into two segments, one for training and hyperparameter optimization, and one for testing. But it seems that the only spilt was for training and hyperparameter optimization.

[Note added after revision: the authors now make it clear in their response that the modeling tells us how much of the current data can be explained but not necessary about generalization to other datasets.]

While I find the study to be generally well executed, I am left wondering what to make of it all. The purpose of the study with respect to fixing previous methodological shortcomings was clear, but exactly how fixings these shortcomings has allowed us to advance is not. I think we can be more confident than before that EFR amplitude is sensitive to CND, and we now know that measures of listening effort may also be sensitive to CND. But where is this leading us?

I think what this line of work is eventually aiming for is to develop a clinical tool that can be used to infer someone's CND profile. That seems like a worthwhile goal but getting there will require going beyond exploratory association studies. I think we're ready to start being explicit about what properties a CND inference tool would need to be practically useful. I have no idea whether the associations reported in this study are encouraging or not because I have no idea what level of inferential power is ultimately required.

[Note added after revision: the authors have added to the Discussion to put their work into a broader perspective.]

That brings me to my final comment: there is an inappropriate emphasis on statistical significance. The sample size was chosen arbitrarily. What if the sample had been half the size? Then few, if any, of the observed effects would have been significant. What if the sample had been twice the size? Then many more of the observed effects would have been significant (particularly for the pupillometry). I hope that future studies will follow a more principled approach in which relevant effect sizes are pre-specified (ideally as the strength of association that would be practically useful) and sample sizes are determined accordingly.

[Note added after revision: my intention with this comment was not to make a philosophical or nitty-gritty point about statistics. It was more of a follow on to the previous point. Because I don't know what sort of effect size is big enough to matter (for whatever purpose), I don't find the statistical significance (or lack thereof) of the effect size observed to be informative. But I don't think there is anything more that the authors can or should do in this regard.]

So, in summary, I think this study is a valuable but limited advance. The results increase my confidence that non-invasive measures can be used to infer underlying CND, but I am unsure how much closer we are to anything that is practically useful.

Reviewer #2 (Public review):

Summary:

This paper addresses the bottom-up and top-down causes of hearing difficulties in middle-aged adults with clinically-normal audiograms using a cross-species approach (humans vs. gerbils, each with two age groups) mixing behavioral tests and electrophysiology.. The study is not only a follow-up of Parthasarathy et al (eLife 2020), since there are several important differences. Parthasarathy et al. (2020) only considered a group of young normal-hearing individuals with normal audiograms yet with high complaints for hearing in noisy situations. Here, this issue is considered specifically regarding aging, using a between-subject design comparing young NH and older NH individuals recruited from the general population, without additional criterion (i.e. no specifically high problems of hearing in noise). In addition, this is a cross-species approach, with the same physiological EFR measurements with the same stimuli deployed on gerbils.

This article is of very high quality. It is extremely clear, and the results show clearly a decrease of neural phase-locking to high modulation frequencies in both middle-aged humans and gerbils, compared to younger groups/cohorts. In addition, pupillometry measurements conducted during the QuickSIN task suggest increased listening efforts in middle-aged participants, and a statistical model including both EFRs and pupillometry features suggest that both factors contribute to reduced speech-in-noise intelligibility evidenced in middle-aged individuals, beyond their slight differences in audiometric thresholds (although they were clinically normal in both groups).

These provide strong support to the view that normal aging in humans leads to auditory nerve synaptic loss (cochlear neural degeneration - CND- or, put differently, cochlear synaptopathy) as well as increased listening effort, before any clearly visible audiometric deficits as defined in current clinical standards. This result is very important for the community, since we are still missing direct evidence that cochlear synaptopathy might likely underly a significant part of hearing difficulties in complex environments for listeners with normal thresholds, such as middle-aged and senior listeners. This paper shows that these difficulties can be reasonably well accounted for by this sensory disorder (CND), but also that listening effort, i.e. a top-down factor, further contributes to this problem. The methods are sound, well described and I would like to emphasize that they are presented concisely yet in a very precise manner, so that they can be understood very easily - even for a reader that is not familiar with the employed techniques. I believe this study will be of interest to a broad readership. I have some comments and questions which I think would make the paper even stronger once addressed.

Main comments:

(1) Presentation of EFR analyses / Interpretation of EFR differences found in both gerbils and humans

a) Could you comment further on why you think you found a significant difference only at the highest mod. frequency of 1024 Hz in your study? Indeed, previous studies employing SAM or RAM tones very similar to the ones employed here were able to show age effects already at lower modulation freqs. of ~100H; e.g. there are clear age effects reported in human studies of Vasilikov et al. (2021) or Mepani et al. (2021), and also in animals ( see Garrett et al. bioRxiv : https://www.biorxiv.org/content/biorxiv/early/2024/04/30/2020.06.09.142950.full.pdf)

Furthermore, some previous EEG experiments in humans that SAM tones with modulation freqs. of ~100Hz showed that EFRs do not exhibit a single peak, i.e. there are peaks not only at fm but also for the first harmonics (e.g. 2fm or 3fm) see e.g. Garrett et al. bioXiv https://www.biorxiv.org/content/biorxiv/early/2024/04/30/2020.06.09.142950.full.pdf

Did you try to extract EFR strength by looking at the summed amplitude of multiple peaks (Vasilikov Hear Res. 2021), in particular for the lower modulation frequencies? (Indeed, there will be no harmonics for the higher mod. freqs).

b) How the present EFR results relate to FFR results, where effects of age are already at low carrier freqs? (e.g. Märcher-Rørsted et al., Hear. Res., 2022 for pure tones with freq < 500 Hz) Do you think it could be explained by the fact that this is not the same cochlear region, and that synapses die earlier in higher compared to lower CFs. This should be discussed. Beyond the main group effect of age, there were no negative correlations of EFRs with age in your data?

(2) Size of the effects / comparing age effects between two species: Although the size of the age effect on EFRs cannot be directly compared between humans and gerbils - the comparison remains qualitative - could you a least provide references regarding the rate of synaptic loss with aging in both humans and gerbils, so that we understand that the yNH/MA difference can be compared between the two age groups used for gerbils; it would have been critical in case of a non-significant age effect in one species.

Equalization / control of stimuli differences across the two species: For measuring EFRs, SAM stimuli were presented at 85 dB SPL for humans vs. 30 dB above detection threshold (inferred from ABRs) for gerbils - I do not think the results strongly depend on this choice, but it would be good to comment on why you did not choose also to present stimuli 30 dB above thresholds in humans.

Simulations of EFRs using functional models could have been used to understand (at least in humans) how the differences in EFRs obtained between the two groups are quantitatively compatible with the differences in % of remaining synaptic connections known from histopathological studies for their age range (see the approach in Märcher-Rørsted et al., Hear. Res., 2022)

(3) Synergetic effects of CND and listening effort Could you test whether there is an interaction between CNR and listening effort? (e.g. one could hypothesize that MA subjects with largest CND have also the higher listening effort)

Comments on revised version:

The authors did well to address all the points raised in my review. This paper will make an important contribution to our assessment of the sources of age-related auditory processing deficits beyond the cochlea that impair speech intelligibility.

eLife Assessment

This study provides valuable findings on the effects of mating experience on sweet taste perception. The data as presented provide convincing evidence that the dopaminergic signaling-mediated reward system underlies this mating state-dependent behavioral modulation. The work will interest neuroscientists and particularly biologists working on neuromodulation and the effects of internal states on sensory perception.

Reviewer #1 (Public review):

Wang et al. investigated how sexual failure influences sweet taste perception in male Drosophila. The study revealed that courtship failure leads to decreased sweet sensitivity and feeding behavior via dopaminergic signaling. Specifically, the authors identified a group of dopaminergic neurons projecting to the subesophageal zone that interact with sweet-sensing Gr5a+ neurons. These dopaminergic neurons positively regulate the sweet sensitivity of Gr5a+ neurons via DopR1 and Dop2R receptors. Sexual failure diminishes the activity of these dopaminergic neurons, leading to reduced sweet taste sensitivity and sugar feeding behavior in the male flies. These findings highlight the role of dopaminergic neurons in integrating reproductive experiences to modulate appetitive sensory responses.

Previous studies have explored the dopaminergic-to-Gr5a+ neuronal pathways in regulating sugar feeding under hunger conditions. Starvation has been shown to increase dopamine release from a subset of TH-GAL4 labeled neurons, known as TH-VUM, in the subesophageal zone. This enhanced dopamine release activates dopamine receptors in Gr5a+ neurons, heightening their sensitivity to sugar and promoting sucrose acceptance in flies. Since the function of the dopaminergic-to-Gr5a+ circuit motif has been well established, the primary contribution of Wang et al. is to show that mating failure in male flies can also engage this circuit to modulate sugar feeding behavior. This contribution is valuable because it highlights the role of dopaminergic neurons in integrating diverse internal state signals to inform behavioral decisions.

An intriguing discrepancy between Wang et al. and earlier studies lies in the involvement of dopamine receptors in Gr5a+ neurons. Prior research has shown that Dop2R and DopEcR, but not DopR1, mediate starvation-induced enhancement of sugar sensitivity in Gr5a+ neurons. In contrast, Wang et al. report that DopR1 and Dop2R, but not DopEcR, are involved in the mating failure-induced suppression of sugar sensitivity in these neurons. Further investigation is needed to clarify how dopamine selectively engages different receptor types depending on internal state.

The data in this revised version are largely convincing and support the authors' conclusions. However, I remain concerned about the results shown in Figure 6E. The authors show that knocking down DopR1 or Dop2R in Gr5a+ neurons restores sucrose-evoked activity in Failed flies to levels seen in Naive and Satisfied animals. This appears to contradict the proposed model, in which these receptors positively modulate Gr5a+ activity through dopaminergic input. If dopamine signaling is reduced in Failed flies, further receptor knockdown should have no effect or further reduce activity-not restore it. I encourage the authors to clarify this apparent inconsistency and, if possible, provide a mechanistic explanation.

Reviewer #2 (Public review):

Summary:

The authors exposed naïve male flies to different groups of females, either mated or virgin. Male flies can successfully copulate with virgin females; however, they are rejected by mated females. This rejection reduces sugar preference and sensitivity in males. Investigating the underlying neural circuits, the authors show that dopamine signaling onto GR5a sensory neurons is required for reduced sugar preference. GR5a sensory neurons respond less to sugar exposure when they lack dopamine receptors.

Strengths:

The findings add another strong phenotype to the existing dataset about brain-wide neuromodulatory effects of mating. The authors use several state-of-the-art methods, such as activity-dependent GRASP, to decipher the underlying neural circuitry. They further perform rigorous behavioral tests and provide convincing evidence for the local labellar circuit.

Weaknesses:

The authors focus on the circuit connection between dopamine and gustatory sensory neurons in the male SEZ. Therefore, it is still unknown how mating modulates dopamine signaling and what possible implications on other behaviors might result from a reduced sugar preference.

The authors updated missing literature in the manuscript and performed additional experiments regarding behavior, but also to further prove the functional connectivity between TH neurons and GR5a neurons.

I have no further recommendations.

Reviewer #3 (Public review):

Summary

This study by Wang et al. explores a compelling link between two fundamental innate behaviors in Drosophila melanogaster, mating and feeding, demonstrating that repeated sexual failure in male flies leads to a transient yet reversible decrease in sweet taste perception. The authors show that this modulation is mediated by dopamine signaling from a specific subset of dopaminergic neurons in the subesophageal zone (SEZ) that directly influence Gr5a⁺ sweet-sensing neurons.

Aims of the Study

The authors aimed to understand whether unsuccessful mating attempts could affect sensory processing of sweet stimuli and thus feeding behavior in male fruit flies. They further sought to dissect the neural circuitry and molecular pathways underlying this behavioral plasticity, with a particular focus on dopaminergic modulation.

Major Strengths and Weaknesses

Strengths:

• Novelty: The idea that reproductive experience modulates gustatory perception adds a new dimension to our understanding of cross-modal behavioral integration.

• Experimental approach: The study uses a broad array of genetic, pharmacological, imaging, and behavioral assays to demonstrate a causal relationship between sexual failure and reduced sweet perception, mediated by specific dopaminergic pathways.

• Methodological design: The authors link behavioral outcomes (reduced proboscis extension reflex) with neural activity (calcium imaging of Gr5a⁺ neurons) and molecular specificity (dopamine receptor subtype roles), providing a robust multi-level framework.

Weaknesses:

• Ecological relevance: While the laboratory conditions are well controlled, the adaptive value or natural context of this taste modulation following mating failure remains speculative.

Achievement of Aims and Support for Conclusions

The authors have convincingly achieved their central aim. The results support the conclusion that sexual failure reduces sweet taste sensitivity through dopamine signaling. The reduced activity in Gr5a⁺ neuron after courtship rejection, its rescue by dopamine or successful copulation, and the requirement of specific dopamine receptors support the proposed model.

Impact and Utility

This work advances the field's understanding of how motivational states shaped by social experiences can directly influence sensory perception and behavior. It underscores the role of the dopaminergic system not only in reward but in integrating internal states across distinct behavioral responses. The experimental approach, including courtship conditioning paradigms and in vivo imaging methods, provides a valuable foundation for related studies in sensory modulation and behavioral plasticity.

Additional Context

This study supports a growing body of literature suggesting that insects possess emotion-like internal states that influence their behavior across contexts. The findings resonate with prior work on how stressors like social isolation or courtship failure lead to compensatory changes in other reward-seeking behaviors (e.g., ethanol consumption). Moreover, the concept that neural systems underlying basic drives like hunger and mating are dynamically interconnected may be conserved across phyla, suggesting broader relevance to understanding internal state-dependent modulation of behavior.

The authors addressed all the comments of previous reviews. The changes increased the clarity of the manuscript, the interpretation of the results and reinforce the conclusion.

Author response:

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

Reviewer #1 (Public review):

Wang et al. investigated how sexual failure influences sweet taste perception in male Drosophila. The study revealed that courtship failure leads to decreased sweet sensitivity and feeding behavior via dopaminergic signaling. Specifically, the authors identified a group of dopaminergic neurons projecting to the suboesophageal zone that interacts with sweet-sensing Gr5a+ neurons. These dopaminergic neurons positively regulate the sweet sensitivity of Gr5a+ neurons via DopR1 and Dop2R receptors. Sexual failure diminishes the activity of these dopaminergic neurons, leading to reduced sweet-taste sensitivity and sugar-feeding behavior in male flies. These findings highlight the role of dopaminergic neurons in integrating reproductive experiences to modulate appetitive sensory responses.

Previous studies have explored the dopaminergic-to-Gr5a+ neuronal pathways in regulating sugar feeding under hunger conditions. Starvation has been shown to increase dopamine release from a subset of TH-GAL4 labeled neurons, known as TH-VUM, in the suboesophageal zone. This enhanced dopamine release activates dopamine receptors in Gr5a+ neurons, heightening their sensitivity to sugar and promoting sucrose acceptance in flies. Since the function of the dopaminergic-to-Gr5a+ circuit motif has been well established, the primary contribution of Wang et al. is to show that mating failure in male flies can also engage this circuit to modulate sugar-feeding behavior. This contribution is valuable because it highlights the role of dopaminergic neurons in integrating diverse internal state signals to inform behavioral decisions.

An intriguing discrepancy between Wang et al. and earlier studies lies in the involvement of dopamine receptors in Gr5a+ neurons. Prior research has shown that Dop2R and DopEcR, but not DopR1, mediate starvation-induced enhancement of sugar sensitivity in Gr5a+ neurons. In contrast, Wang et al. found that DopR1 and Dop2R, but not DopEcR, are involved in the sexual failure-induced decrease in sugar sensitivity in these neurons. I wish the authors had further explored or discussed this discrepancy, as it is unclear how dopamine release selectively engages different receptors to modulate neuronal sensitivity in a context-dependent manner.

Our immunostaining experiments showed that three dopamine receptors, Dop1R1, Dop2R, and DopEcR were expressed in Gr5a⁺ neurons in the proboscis, which was consistent with previous findings by using RT-PCR (Inagaki et al 2012). As the reviewer pointed out, we found that Dop1R1 and Dop2R were required for courtship failure-induced suppression of sugar sensitivity, whereas Marella et al 2012 and Inagaki et al 2012 found that Dop2R and DopEcR were required for starvation-induced enhancement of sugar sensitivity. These results may suggest that different internal states (courtship failure vs. starvation) modulate the peripheral sensory system via different signaling pathways (e.g. different subsets of dopaminergic neurons; different dopamine release mechanisms; and different dopamine receptors). We have discussed these possibilities in the revised manuscript.

The data presented by Wang et al. are solid and effectively support their conclusions. However, certain aspects of their experimental design, data analysis, and interpretation warrant further review, as outlined below.

(1) The authors did not explicitly indicate the feeding status of the flies, but it appears they were not starved. However, the naive and satisfied flies in this study displayed high feeding and PER baselines, similar to those observed in starved flies in other studies. This raises the concern that sexually failed flies may have consumed additional food during the 4.5-hour conditioning period, potentially lowering their baseline hunger levels and subsequently reducing PER responses. This alternative explanation is worth considering, as an earlier study demonstrated that sexually deprived males consumed more alcohol, and both alcohol and food are known rewards for flies. To address this concern, the authors could remove food during the conditioning phase to rule out its influence on the results.

This is an important consideration. To rule out potential confound from food intake during courtship conditioning, we have now also conducted courtship conditioning in vials absent of food. In the absence of any feeding opportunity over the 4.5-hour courtship conditioning period, sexually rejected males still exhibited a robust decrease in sweet taste sensitivity compared with Naïve and Satisfied controls (Figure 1-supplement 1C). These data confirm that the suppression of PER is driven by courtship failure per se, rather than by differences in feeding during the conditioning phase.

(2) Figure 1B reveals that approximately half of the males in the Failed group did not consume sucrose yet Figure 1-S1A suggests that the total volume consumed remained unchanged. Were the flies that did not consume sucrose omitted from the dataset presented in Figure 1-S1A? If so, does this imply that only half of the male flies experience sexual failure, or that sexual failure affects only half of males while the others remain unaffected? The authors should clarify this point.

Our initial description of the experimental setup might be a bit confusing. Here is a brief clarification of our experimental design and we have further clarified the details in the revised manuscript, which should resolve the reviewer’s concerns:

After the behavioral conditioning, male flies were divided for two assays. On the one hand, we quantified PER responses of individual flies. As shown in Figure 1C, Failed males exhibited decreased sweet sensitivity (as demonstrated by the right shift of the dose-response curve). On the other hand, we sought to quantify food consumption of individual flies by using the MAFE assay (Qi et al 2005).

In the initial submission, we used 400 mM sucrose for the MAFE assay. When presented with 400 mM sucrose, approximately 100% of the flies in the Naïve and Satisfied groups, and 50% of the flies in the Failed group, extended their proboscis and started feeding, as a natural consequence of decreased sugar sensitivity (Figure 1B). We were able to quantify the actual volume of food consumed of these flies showing PER responses towards 400 mM sucrose and observed no change (Figure 1-supplement 1A, left). To avoid potential confusion, we have now repeated the MAFE assay with 800 mM sucrose, which elicited feeding in ~100% of flies among all three groups, as shown in Figure 1C. Again, we observed no change in food intake (Figure 1-supplement 1A, right).

These experiments in combination suggest that sexual failure suppresses sweet sensitivity of the Failed males. Meanwhile, as long as they still responded to a certain food stimulus and initiated feeding, the volume of food consumption remained unchanged. These results led us to focus on the modulatory effect of sexual failure on the sensory system, the main topic of this present study.

(3) The evidence linking TH-GAL4 labeled dopaminergic neurons to reduced sugar sensitivity in Gr5a+ neurons in sexually failed males could be further strengthened. Ideally, the authors would have activated TH-GAL4 neurons and observed whether this restored GCaMP responses in Gr5a+ neurons in sexually failed males. Instead, the authors performed a less direct experiment, shown in Figures 3-S1C and D. The manuscript does not describe the condition of the flies used in this experiment, but it appears that they were not sexually conditioned. I have two concerns with this experiment. First, no statistical analysis was provided to support the enhancement of sucrose responses following activation of TH-GAL4 neurons. Second, without performing this experiment in sexually failed males, the authors lack direct evidence to confirm that the dampened response of Gr5a+ neurons to sucrose results from decreased activity in TH-GAL4 neurons.

We have now quantified the effect of TH⁺ neuron activation on Gr5a⁺ neuron calcium responses. in Naïve males, dTRPA1-mediated activation of TH⁺ cells significantly enhanced sucrose-induced calcium responses (Figure 3-supplement 1C); while in Failed males, the baseline activity of Gr5a⁺ neurons was lower (Figure 3C), the same activation also produced significant (even slightly larger) effect on the calcium responses of Gr5a⁺ neurons (Figure 3-supplement 1D).

Taken together, we would argue that these experiments using both Naïve and Failed males were adequate to show a functional link between TH⁺ neurons and Gr5a⁺ neurons. Combining with the results that these neurons form active synapses (Figure 3-supplement 1B) and that the activity of TH⁺ neurons was dampened in sexually failed males (Figure 3G-I), our data support the notion that sexual failure suppresses sweet sensitivity via TH-Gr5a circuitry.

(4) The statistical methods used in this study are poorly described, making it unclear which method was used for each experiment. I suggest that the authors include a clear description of the statistical methods used for each experiment in the figure legends. Furthermore, as I have pointed out, there is a lack of statistical comparisons in Figures 3-S1C and D, a similar problem exists for Figures 6E and F.

We have added detailed information of statistical analysis in each figure legend.

(5) The experiments in Figure 5 lack specificity. The target neurons in this study are Gr5a+ neurons, which are directly involved in sugar sensing. However, the authors used the less specific Dop1R1- and Dop2R-GAL4 lines for their manipulations. Using Gr5a-GAL4 to specifically target Gr5a+ neurons would provide greater precision and ensure that the observed effects are directly attributable to the modulation of Gr5a+ neurons, rather than being influenced by potential off-target effects from other neuronal populations expressing these dopamine receptors.

We agree with the reviewer that manipulating Dop1R1 and Dop2R genes (Figure 4) and the neurons expressing them (Figure 5) might have broader impacts. For specificity, we have also tested the role of Dop1R1 and Dop2R in Gr5a⁺ neurons by RNAi experiments (Figure 6). As shown by both behavioral and calcium imaging experiments, knocking down Dop1R1 and Dop2R in Gr5a⁺ neurons both eliminated the effect of sexual failure to dampen sweet sensitivity, further confirming the role of these two receptors in Gr5a⁺ neurons.

(6) I found the results presented in Fig. 6F puzzling. The knockdown of Dop2R in Gr5a+ neurons would be expected to decrease sucrose responses in naive and satisfied flies, given the role of Dop2R in enhancing sweet sensitivity. However, the figure shows an apparent increase in responses across all three groups, which contradicts this expectation. The authors may want to provide an explanation for this unexpected result.

We agree that there might be some potential discrepancies. We have now addressed the issues by re-conducting these calcium imaging experiments again with a head-to-head comparison with the controls (Gr5a-GCaMP, +/- Dop1R1 and Dop2R RNAi).

In these new experiments, Dop1R1 or Dop2R knockdown completely prevented the suppression of Gr5a⁺ neuron responsiveness by courtship failure (Figure 6E), whereas the activities of Gr5a⁺ neurons in Naïve/Satisfied groups were not altered. These results demonstrate that Dop1R1 and Dop2R are specifically required to mediate the decrease in sweet sensitivity following courtship failure.

(7) In several instances in the manuscript, the authors described the effects of silencing dopamine signaling pathways or knocking down dopamine receptors in Gr5a neurons with phrases such as 'no longer exhibited reduced sweet sensitivity' (e.g., L269 and L288), 'prevent the reduction of sweet sensitivity' (e.g., L292), or 'this suppression was reversed' (e.g. L299). I found these descriptions misleading, as they suggest that sweet sensitivity in naive and satisfied groups remains normal while the reduction in failed flies is specifically prevented or reversed. However, this is not the case. The data indicate that these manipulations result in an overall decrease in sweet sensitivity across all groups, such that a further reduction in failed flies is not observed. I recommend revising these descriptions to accurately reflect the observed phenotypes and avoid any confusion regarding the effects of these manipulations.

We have changed the wording in the revised manuscript. In brief, we think that these manipulations have two consequences: suppressing the overall sweet sensitivity, and eliminating the effect of sexual failure on sweet sensitivity.

Reviewer #2 (Public review):

Summary:

The authors exposed naïve male flies to different groups of females, either mated or virgin. Male flies can successfully copulate with virgin females; however, they are rejected by mated females. This rejection reduces sugar preference and sensitivity in males. Investigating the underlying neural circuits, the authors show that dopamine signaling onto GR5a sensory neurons is required for reduced sugar preference. GR5a sensory neurons respond less to sugar exposure when they lack dopamine receptors.

Strengths:

The findings add another strong phenotype to the existing dataset about brain-wide neuromodulatory effects of mating. The authors use several state-of-the-art methods, such as activity-dependent GRASP to decipher the underlying neural circuitry. They further perform rigorous behavioral tests and provide convincing evidence for the local labellar circuit.

Weaknesses:

The authors focus on the circuit connection between dopamine and gustatory sensory neurons in the male SEZ. Therefore, it is still unknown how mating modulates dopamine signaling and what possible implications on other behaviors might result from a reduced sugar preference.

We agree with the reviewer that in the current study, we did not examine the exact mechanism of how mating experience suppressed the activity of dopaminergic neurons in the SEZ. The current study mainly focused on the behavioral characterization (sexual failure suppresses sweet sensitivity) and the downstream mechanism (TH-Gr5a pathway). We think that examining the upstream modulatory mechanism may be more suitable for a separate future study.

We believe that a sustained reduction in sweet sensitivity (not limited to sucrose but extend to other sweet compounds Figure 1-supplement 1D-E) upon courtship failure suggests a generalized and sustained consequence on reward-related behaviors. Sexual failure may thus resemble a state of “primitive emotion” in fruit flies. We have further discussed this possibility in the revised manuscript.

Reviewer #3 (Public review):

Summary

In this work, the authors asked how mating experience impacts reward perception and processing. For this, they employ fruit flies as a model, with a combination of behavioral, immunostaining, and live calcium imaging approaches.

Their study allowed them to demonstrate that courtship failure decreases the fraction of flies motivated to eat sweet compounds, revealing a link between reproductive stress and reward-related behaviors. This effect is mediated by a small group of dopaminergic neurons projecting to the SEZ. After courtship failure, these dopaminergic neurons exhibit reduced activity, leading to decreased Gr5a+ neuron activity via Dop1R1 and Dop2R signaling, and leading to reduced sweet sensitivity. The authors therefore showed how mating failure influences broader behavioral outputs through suppression of the dopamine-mediated reward system and underscores the interactions between reproductive and reward pathways.

Concern

My main concern regarding this study lies in the way the authors chose to present their results. If I understood correctly, they provided evidence that mating failure induces a decrease in the fraction of flies exhibiting PER. However, they also showed that food consumption was not affected (Fig. 1, supplement), suggesting that individuals who did eat consumed more. This raises questions about the analysis and interpretation of the results. Should we consider the group as a whole, with a reduced sensitivity to sweetness, or should we focus on individuals, with each one eating more? I am also concerned about how this could influence the results obtained using live imaging approaches, as the flies being imaged might or might not have been motivated to eat during the feeding assays. I would like the authors to clarify their choice of analysis and discuss this critical point, as the interpretation of the results could potentially be the opposite of what is presented in the manuscript.

Please refer to our responses to the Public Review (Reviewer 1, Point 2) for details.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The label for the y-axis in Figure 1B should be "fraction", not "percentage".

We have revised the figure as suggested.

(2) I suggest that the authors indicate the ROIs they used to quantify the signal intensity in Figure 3E and G.

We have revised the figures as suggested.

(3) There is a typo in Figure 4A: it should be "Wilde type", not "Wide type".

We have revised the figure as suggested.

(4) The elav-GAL4/+ data in Figure 4-S1B, C, and D appears to be reused across these panels. However, the number of asterisks indicating significance in the MAT plots differs between them (three in panels B and C, and four in panel D). Is this a typo?

It is indeed a typo, and we have revised the figure accordingly.

Reviewer #2 (Recommendations for the authors):

Additional comments:

The authors should add this missing literature about dopamine and neuromodulation in courtship:

Boehm et al., 2022 (eLife) - this study shows that mating affects olfactory behavior in females.

Cazalé-Debat et al., 2024 (Nature) - Mating proximity blinds threat perception.

Gautham et al., 2024 (Nature) - A dopamine-gated learning circuit underpins reproductive state-dependent odor preference in Drosophila females.

We have added these references in the introduction section.

Has the mating behavior been quantified? How often did males copulate with mated and virgin females?

We tried to examine the copulation behavior based on our video recordings. In the “Failed” group (males paired with mated females), we observed virtually no successful copulation events at all, confirming that nearly 100% of those males experienced sexual failure. In contrast, males in the “Satisfied” group (paired with virgin females) mated on average 2-3 times during the 4.5-hour conditioning period. We have added some explanations in the manuscript.

Do the rejected males live shorter? Is the effect also visible when they are fed with normal fly food, or is it only working with sugar?

We did not directly measure the lifespan of these males. But we conducted a relevant assay (starvation resistance), in which “Failed” males died significantly faster than both Naïve and Satisfied controls, indicating a clear reduction in their ability to endure food deprivation (Figure 1-supplement 1B). Since sweet taste is a primary cue for food detection in Drosophila, and sugar makes up a large portion of their standard diet, the drop in sugar sensitivity we observed in Failed males could likewise impair their perception and consumption of regular fly food, hence their resistance to starvation.

Also, the authors mention that the reward pathway is affected, this is probably the case as sugar sensation is impaired. One interesting experiment would be (and maybe has been done?) to test rejected males in normal odor-fructose conditioning. The data would suggest that they would do worse.

We have already measured how courtship failure affected fructose sensitivity (Figure 1 supplement 1D), and we found that the reduction in fructose perception was even more profound than for sucrose. We have not yet tested whether Failed males showed deficits in odor-fructose associative conditioning. That was indeed a very interesting direction to explore. But olfactory reward learning relies on molecular and circuit mechanisms distinct from those governing taste. We therefore argue such experiments would be more suitable in a separate, follow up study.

The authors could have added another group where males are exposed to other males. It would be interesting if this is also a "stressful" context and if it would also reduce sugar preference - probably beyond the scope of this paper.

In our experiments, all flies, including those in the Naïve, Failed, and Satisfied groups, were housed in groups of 25 males per vial before the conditioning period (and the Naïve group remained in the same group housing until PER testing). This means every cohort experienced the same level of “social stress” from male-male interactions. While it would indeed be interesting to compare that to solitary housing or other male-only exposures, isolation itself imposes a different kind of stress, and disentangling these effects on sugar preference would require a separate, dedicated study beyond the scope of the present work.

Would the behavior effect also show up with experienced males? Maybe this has been tested before. Does mating rejection in formerly successful males have the same impact?

As suggested by the reviewer, we performed an additional experiment in which males that had previously mated successfully were subsequently subjected to courtship rejection. As shown in Figure 1 supplement 1F, prior successful mating did not prevent the decline in sweet sensitivity induced by subsequent mating failure, indicating that even experienced males exhibit the reduction in sugar sensitivity after rejection.

Is the same circuit present and functioning in females? Does manipulating dopamine receptors in GR5a neurons in females lead to the same phenotype? This would suggest that different internal states in males and females could lead to the same phenotype and circuit modulations.

This is indeed a very interesting suggestion. In male flies, Gr5a-specific knockdown of dopamine receptors did not alter baseline sweet sensitivity, but it selectively prevented the reduction in sugar perception that followed mating failure (Figure 6C-D), indicating that this dopaminergic pathway is engaged only in the context of courtship rejection. By extension, knocking down the same receptors in female GR5a neurons would likewise be expected to leave their basal sugar sensitivity unchanged. Moreover, because there is currently no established paradigm for inducing mating failure in female flies, we cannot yet test whether sexual rejection similarly modulates sweet taste in females, or whether it operates via the same circuit.

Reviewer #3 (Recommendations for the authors):

Suggestions to the authors:

Introduction, line 61. I suggest the authors add references in fruit flies concerning the rewarding nature of mating. For example, the paper from Zhang et al, 2016 "Dopaminergic Circuitry Underlying Mating Drive" demonstrates the role of the dopamine rewarding system in mating drive. There is a large body of literature showing the link between dopamine and mating.

We have added this literature in the introduction section.

Figure 1B and Figure Supplement 1: If I understood correctly, Figure Supplement 1A shows that the total food consumption across all tested flies remains unchanged. However, fewer flies that failed to mate consumed sucrose. I would be curious to see the results for sucrose consumption per individual fly that did eat. According to their results, individual flies that failed to mate should consume more sucrose. This would change the conclusion. The authors currently show that a group of flies that failed to mate consumed less sucrose overall, but since fewer males actually ate, those that failed to mate and did eat consumed more sucrose. The authors should distinguish between failed and satisfied flies in two groups: those that ate and those that did not.

Please see our responses to the Public Review for details (Reviewer 1, Point 2).

Figure 1C, right: For a better understanding of all the "MAT" figures, I suggest the authors start the Y axis with the unit 25 and increase it to 400. This would match better the text (line 114) saying that it was significantly elevated in the failed group. As it is, we have the impression of a decrease in the graph.

We have revised the figures accordingly.

Line 103: When suggesting a reduced likelihood of meal initiation of these males, do these males take longer to eat when they did it? In other words, is the latency to eat increased in failed males? That would be a good measure of motivational state.

We tried to analyze feeding latency in the MAFE assay by measuring the time from sucrose presentation to the first proboscis extension, but it was too short to be accurately accounted. Nevertheless, when conducting the experiments, we did not feel/observe any significant difference in the feeding latency between Failed males and Naïve or Satisfied controls.

Line 117. I don't understand which results the authors refer to when writing "an overall elevation in the threshold to initiate feeding upon appetitive cues". Please specify.

This phrase refers to the fact that for every sweet tastant we tested, including sucrose (Figure 1C), fructose and glucose (Figure 1 supplement 1D-E), the concentration-response curve in Failed males shifted to the right, and the Mean Acceptance Threshold (MAT) was significantly higher. In other words, for these different appetitive cues, mating failure raised the concentration of sugar required to trigger a proboscis extension, indicating a general elevation in the threshold to initiate feeding upon an appetitive cue.

Figure 1D. Please specify the time for the satisfied group.

For clarity, the Naïve and Satisfied groups in Figure 1D each represent pooled data from 0 to 72 hours post-treatment, as their sweet sensitivity remained stable throughout this period. Only the Failed group was shown with time-resolved data, since it was the only group exhibiting a dynamic change in sugar sensitivity over time. We have now specified this in the figure legend.

Figure 1F. The phenotype was not totally reversed in failed-re-copulated males. Could it be due to the timing between failure and re-copulation? I suggest the authors mention in the figure or in the text, the time interval between failure and re-copulation.

We’d like to clarify that the interval between the initial treatment (“Failed”) and the opportunity for re copulation was within 30 minutes. The incomplete reversal in the Failed-re-copulated group indeed raised interesting questions. One possible explanation is that mating failure reduces synaptic transmissions between the SEZ dopaminergic neurons and Gr5a⁺ sweet sensory neurons (Figure 3), and the regeneration of these transmissions takes a longer time. We have added this information to the figure legend and the Method section.

Line 227-228 and Figure 3E. The authors showed that the synaptic connections between dopaminergic neurons and Gr5a+ GRNs were significantly weakened. I am wondering about the delay between mating failure and the GFP observation. It would be informative to know this timing to interpret this decrease in synaptic connections. If the timing is relatively long, it is possible that we can observe a neuronal plasticity. However, if this timing is very short, I would not expect such synaptic plasticity.

The interval between the behavioral treatment and the GRASP-GFP experiment was approximately 20 hours. We chose this time window because it was sufficient for both GFP expression and accumulation. Therefore, the observed reduction in synaptic connections between dopaminergic neurons and Gr5a⁺ GRNs likely reflects a genuine, experience-induced structural and functional change rather than an immediate, transient effect. We have added this information to the revised manuscript for clarity in the Method section.

Line 240-243: The authors demonstrated that there is a reduction of CaLexA-mediated GFP signals in dopaminergic neurons in the SEZ after mating failure, but not a reduction in Gr5a+ GRNs. I suggest replacing "indicate" with "suggest' in line 240.

We have made the change accordingly. Meanwhile, we would like to clarify that while we observed a reduction of NFAT signal in SEZ dopaminergic neurons (Figure 3G), we did not directly test NFAT signal in Gr5a⁺ neurons. Notably, the results that the synaptic transmissions from SEZ dopaminergic neurons to Gr5a⁺ neurons were weakened (Figure 3E-F), and the reduction of NFAT signal in SEZ dopaminergic neurons (Figure 3G-I), were in line with a reduction in sweet sensitivity of Gr5a⁺ neurons upon courtship failure (Figure 3B-D).

Line 243: replace "consecutive" with "constitutive".

We have revised it accordingly.

Figure 5: I have trouble understanding the results obtained in Figure 5. Both constitutive activation and inhibition of Dop1R1 and Dop2R neurons lead to the same results, knowing that males who failed mating no longer exhibit decreased sweet sensitivity. I would have expected contrary results for both experimental conditions. I suggest the author to discuss their results.

Both activation and inhibition of Dop1R1 and Dop2R neurons eliminated the effect of courtship failure on sweet sensitivity (Figure 5). These results are in line with our hypothesis that courtship failure leads to changes in dopamine signaling and hence sweet sensitivity. If dopamine signaling via Dop1R1 and Dop2R was locked, either to a silenced or a constitutively activated state, the effect of courtship failure on sweet sensitivity was eliminated.

Nevertheless, as the reviewer pointed out, constitutive activation/inhibition should in principle lead to the opposite effect on Naïve flies. In fact, when Dop1R1⁺/Dop2R⁺ neurons were silenced in Naïve flies, PER to sucrose was significantly reduced (Figure 5C-D), confirming that these neurons normally facilitate sweet sensation. Meanwhile, while neuronal activation by NaChBac did show a trend towards enhanced PER compared to the GAL4/+ controls, it did not exhibit a difference compared to +>UAS-NaChBac controls that showed a high PER level, likely due to a potential ceiling effect. We have added the discussions to the manuscript.

Figure 7: I suggest the authors modify their figure a bit. It is not clear why in failed mating, the red arrow in "behavioral modulation" goes to the fly. The authors should find another way to show that mating failure decreased the percentage of flies that are motivated to eat sugar.

We have modified the figure as suggested.

Overall, I would suggest the authors be precautious with their conclusion. For example, line 337= "sexual failure suppressed feeding behavior". This is not what is shown by this study. Here, the study shows that mating failure decreases the fraction of flies to eat sucrose. Unless the authors demonstrate that this decrease is generalizable to other metabolites, I suggest the authors modify their conclusion.

While we primarily used sucrose as the stimulant in our experiments, we also tested responses to two other sugars: fructose and glucose (Figure 1 supplement 1D-E). In all three cases, mating failure led to a significant reduction in sweet perception, suggesting that the effect of courtship failure is not limited to a single metabolite but rather reflects a general decrease in sweet sensitivity. Meanwhile, reduced sweet sensitivity indeed led to a reduction of feeding initiation (Figure 1).

eLife Assessment

The authors examine the effect of cell-free chromatin particles (cfChPs) derived from human serum or from dying human cells on mouse cells in culture and propose that these cfChPs can serve as vehicles for cell-to-cell active transfer of foreign genetic elements. The work presented in this paper is intriguing and potentially important, but it is incomplete. At this stage, the claim that horizontal gene transfer can occur via cfChPs is not well supported because it is only based on evidence from one type of methodological approach (immunofluorescence and fluorescent in situ hybridization (FISH)) and is not validated by whole genome sequencing.

Reviewer #1 (Public review):

Summary:

Horizontal gene transfer is the transmission of genetic material between organisms through ways other than reproduction. Frequent in prokaryotes, this mode of genetic exchange is scarcer in eukaryotes, especially in multicellular eukaryotes. Furthermore, the mechanisms involved in eukaryotic HGT are unknown. This article by Banerjee et al. claims that HGT occurs massively between cells of multicellular organisms. According to this study, the cell free chromatin particles (cfChPs) that are massively released by dying cells are incorporated in the nucleus of neighboring cells. These cfChPs are frequently rearranged and amplified to form concatemers, they are made of open chromatin, expressed, and capable of producing proteins. Furthermore, the study also suggests that cfChPs transmit transposable elements (TEs) between cells on a regular basis, and that these TEs can transpose, multiply, and invade receiving cells. These conclusions are based on a series of experiments consisting in releasing cfChPs isolated from various human sera into the culture medium of mouse cells, and using FISH and immunofluorescence to monitor the state and fate of cfChPs after several passages of the mouse cell line.

Strengths:

The results presented in this study are interesting because they may reveal unsuspected properties of some cell types that may be able to internalize free-circulating chromatin, leading to its chromosomal incorporation, expression, and unleashing of TEs. The authors propose that this phenomenon may have profound impacts in terms of diseases and genome evolution. They even suggest that this could occur in germ cells, leading to within-organism HGT with long-term consequences.

Weaknesses:

The claims of massive HGT between cells through internalization of cfChPs are not well supported because they are only based on evidence from one type of methodological approach: immunofluorescence and fluorescent in situ hybridization (FISH) using protein antibodies and DNA probes. Yet, such strong claims require validation by at least one, but preferably multiple, additional orthogonal approaches. This includes, for example, whole genome sequencing (to validate concatemerization, integration in receiving cells, transposition in receiving cells), RNA-seq (to validate expression), ChiP-seq (to validate chromatin state).

Should HGT through internalization of circulating chromatin occur on a massive scale, as claimed in this study, and as illustrated by the many FISH foci observed on Fig 3 for example, one would expect that the level of somatic mosaicism may be so high that it would prevent assembling a contiguous genome for a given organism. Yet, telomere-to-telomere genomes have been produced for many eukaryote species, calling into question the conclusions of this study.

eLife Assessment

Fallah et al carefully dissect projections from substantia nigra pars reticulata (SNr) and the globus pallidus externa (GPe) - two key basal ganglia nuclei - to the pedunculopontine nucleus (PPN), a brainstem nucleus that has a central role in motor control. They consider inputs from these two areas onto three types of downstream PPN neurons - GABAergic, glutamatergic, and cholinergic neurons - and carefully map connectivity along the rostrocaudal axis of the PPN. Overall, this important study provides convincing data on PPN connectivity with two key input structures that will provide a basis for further understanding PPN function.

Reviewer #1 (Public review):

Summary:

Fallah and colleagues characterize the connectivity between two basal ganglia output nuclei, the SNr and GPe, and a the pedunculopontine nucleus, a brainstem nucleus that is part of the mesencephalic locomotor region. Through a series of systematic electrophysiological studies, they find that these regions target and inhibit different populations of neurons, with anatomical organization. Overall, SNr projects to PPN and inhibits all major cell types, while the GPe inhibits glutamatergic and GABAergic PPN neurons, and preferentially in the caudal part of the nucleus. Optogenetic manipulation of these inputs in the had opposing effects on behavior - SNr terminals in the PPN drove place aversion, while GPe terminals drove place preference.

Strengths:

This work is thorough and systematic characterization of a set of relatively understudied circuits. They build on the classic notions of basal ganglia connectivity and suggest a number of interesting future directions to dissect motor control and valence processing in brainstem systems.

Limitations:

All the cell type recording studies showing subtle differences in the degree of inhibition and anatomical organization of that inhibition suggest a complex effect of general optogenetic manipulation of SNr or GPe terminals in the PPN. It will be important to determine if SNr or GPe inputs onto a particular cell type in PPN are more or less critical for the how the locomotion and valence effects demonstrated here.

Reviewer #2 (Public review):

Strengths:

Fallah et al carefully dissect projections from SNr and GPe - two key basal ganglia nuclei - to the PPN, an important brainstem nucleus for motor control. They consider inputs from these two areas onto 3 types of downstream PPN neurons: GABAergic, glutamatergic, and cholinergic neurons. They also carefully map connectivity along the rostrocaudal axis of the PPN. They provide important and convincing data on PPN connectivity with two important input structures, which will provide a foundation for many future studies. They also consider the behavioral relevance of these different PPN inputs for controlling movement and reinforcement, showing convincing evidence that SNr and GPe inputs have opposing effects on behavior.

Weaknesses:

The optogenetics and behavioral studies are intriguing, although more work will be required to fit these data together into a specific model of circuit function and to distinguish the locomotor and reinforcement effects. Interestingly, stimulation of SNr axons in the rostral vs caudal PPN likely differs (as predicted by slice experiments), indicating an area for future investigation and dissection of pathways.

Reviewer #3 (Public review):

The study by Fallah et al. provides a thorough characterization of the effects of two basal ganglia output pathways, the SNr and the GPe, on cholinergic, glutamatergic, and GABAergic neurons of the PPN. Using a combination of optogenetics-assisted electrophysiology and behavioral assays in genetically defined mouse lines, the authors show that SNr projections broadly inhibit all PPN subtypes along the rostrocaudal axis, whereas GPe projections are mostly restricted to the caudal PPN and predominantly target glutamatergic neurons, with a lesser effect on GABAergic neurons. Activation of these inputs in vivo revealed opposing behavioral effects: SNr stimulation increased locomotion and caused avoidance in the real-time place preference (RTPP) task, while GPe stimulation reduced locomotion and increased time spent in the stimulation zone.

Strengths:

The evidence for functional connectivity between SNr and GPe inputs and specific PPN cell types is solid and highlights a prominent influence of SNr across the PPN. The identification of a GPe projection that selectively targets caudal glutamatergic PPN neurons is unexpected and highly relevant to understanding basal ganglia-brainstem interactions. The study stands out for its systematic cell-type-specific approach and the combination of electrophysiological and behavioral data. Importantly, the authors addressed key concerns from the initial review by performing new analyses and adding important controls:

Motor activity was re-analyzed at higher temporal resolution, revealing more nuanced effects of stimulation (Fig. S2).

The concern that motor effects might confound RTPP performance was mitigated by analyzing unstimulated test sessions, which showed that place preference or aversion persisted in the absence of stimulation (Fig. 7G).

The potential recruitment of SNc dopaminergic projections was directly tested using DAT-Cre mice, confirming that dopaminergic axon stimulation drives locomotion and reward but does not explain the aversive effect seen with broader SNr activation (Fig. S3).

Weaknesses:

While the revised analyses and added data strengthen the conclusions, the interpretation of the behavioral effects remains somewhat limited by the use of RTPP, which can be influenced by motor changes, even with unilateral stimulation. Nonetheless, the additional controls and thorough discussion now acknowledge and address these caveats appropriately.

Some minor clarifying edits would enhance the manuscript's precision and readability, including improvements to terminology, data presentation, figure referencing, and the organization of behavioral and statistical reporting.

Conclusion:

This is a strong and compelling study that provides a detailed and novel characterization of basal ganglia inputs to the PPN and their behavioral relevance. The authors were responsive to reviewer feedback, and the revised manuscript is significantly improved. The findings advance our understanding of how basal ganglia output pathways engage brainstem circuits to modulate locomotion and valence.

eLife Assessment

This useful modeling study shows how spatial representations similar to experiment emerge in a recurrent neural network trained on a navigation task by requiring path integration and decodability, but without relying on grid cells. The network modeling results are solid, although the link to experimental data may benefit from further development.

Reviewer #1 (Public review):

Summary:

This work studies representations in a network with one recurrent layer and one output layer that needs to path-integrate so that its position can be accurately decoded from its output. To formalise this problem, the authors define a cost function consisting of the decoding error and a regularisation term. They specify a decoding procedure that, at a given time, averages the output unit center locations, weighted by the activity of the unit at that time. The network is initialised without position information, and only receives a velocity signal (and a context signal to index the environment) at each timestep, so to achieve low decoding error it needs to infer its position and keep it updated with respect to its velocity by path integration.

The authors take the trained network and let it explore a series of environments with different geometries while collecting unit activities to probe learned representations. They find localised responses in the output units (resembling place fields) and border responses in the recurrent units. Across environments, the output units show global remapping and the recurrent units show rate remapping. Stretching the environment generally produces stretched responses in output and recurrent units. Ratemaps remain stable within environments and stabilise after noise injection. Low-dimensional projections of the recurrent population activity forms environment-specific clusters that reflect the environment's geometry, which suggests independent rather than generalised representations. Finally, the authors discover that the centers of the output unit ratemaps cluster together on a triangular lattice (like the receptive fields of a single grid cell), and find significant clustering of place cell centers in empirical data as well.

The model setup and simulations are clearly described, and are an interesting exploration of the consequences of a particular set of training requirements - here: path integration and decodability. But it is not obvious to what extent the modelling choices are a realistic reflection of how the brain solves navigation. Therefore, it is not clear whether the results generalize beyond the specifics of the setup here.

Strengths:

The authors introduce a very minimal set of model requirements, assumptions, and constraints. In that sense, the model can function as a useful 'baseline', that shows how spatial representations and remapping properties can emerge from the requirement of path integration and decodability alone. Moreover, the authors use the same formalism to relate their setup to existing spatial navigation models, which is informative.

The global remapping that the authors show is convincing and well-supported by their analyses. The geometric manipulations and the resulting stretching of place responses, without additional training, are interesting. They seem to suggest that the recurrent network may scale the velocity input by the environment dimensions so that the exact same path integrator-output mappings remain valid (but maybe there are other mechanisms too that achieve the same).

The simulations and analyses in the appendices serve as insightful controls for the main results.

The clustering of place cell peaks on a triangular lattice is intriguing, given there is no grid cell input. It could have something to do with the fact that a triangular lattice provides optimal coverage of 2d space? The included comparison with empirical data is valuable as a first exploration, showing a promising example, but doesn't robustly support the modelling results.

Reviewer #2 (Public review):

Summary:

The authors proposed a neural network model to explore the spatial representations of the hippocampal CA1 and entorhinal cortex (EC) and the remapping of these representations when multiple environments are learned. The model consists of a recurrent network and output units (a decoder) mimicking the EC and CA1, respectively. The major results of this study are: the EC network generates cells with their receptive fields tuned to a border of the arena; the decoder develops neuron clusters arranged in a hexagonal lattice. Thus, the model accounts for entrohinal border cells and CA1 place cells. It suggests that the remapping of place cells occurs between different environments through state transitions corresponding to unstable dynamical modes in the recurrent network.

Strengths:

The authors found a spatial arrangement of receptive fields similar to their model's prediction in experimental data recorded from CA1. Thus, the model proposes plausible mechanisms to generate hippocampal spatial representations without relying on grid cells. The model also suggests an interesting possibility that path integration is not the speciality of grid cells.

Weaknesses:

The role of grid cells in the proposed view, i.e., the boundary-to-place-to-grid model, remains elusive. The model can generate place cells without generating entorhinal grid cells. Moreover, the model can generate hexagonal grid patterns of place cells in a large arena. Whether and how the proposed model is integrated into the entire picture of the hippocampal-entorhinal meｍory processing remains elusive.

Reviewer #3 (Public review):

Summary:

The authors used recurrent neural network modelling of spatial navigation tasks to investigate border and place cell behaviour during remapping phenomena.

Strengths:

The neural network training seemed for the most part (see comments later) well-performed, and the analyses used to make the points were thorough.

The paper and ideas were well-explained.

Figure 4 contained some interesting and strong evidence for map-like generalisation as environmental geometry was warped.

Figure 7 was striking and potentially very interesting.

It was impressive that the RNN path-integration error stayed low for so long (Fig A1), given that normally networks that only work with dead-reckoning have errors that compound. I would have loved to know how the network was doing this, given that borders did not provide sensory input to the network. I could not think of many other plausible explanations... It would be even more impressive if it was preserved when the network was slightly noisy.

Update:

The analysis of how the RNN remapped, using a context signal to switch between largely independent maps, and the examination of the border like tuning in the recurrent units of the RNN, were both thorough and interesting. Further, in the updated response I appreciated the additional appendix E which helped substantiate the claim that the RNN neurons were border cells.

Author response:

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

Reviewer #1:

In the future, could you please include the exact changes made to the manuscript in the relevant section of the rebuttal, so it's clear which changes addressed the comment? That would make it easier to see what you refer to exactly - currently I have to guess which manuscript changes implement e.g. "We have tried to make these points more evident".

Yes, we apologize for the inconvenience.

On possible navigation solutions:

I'm not sure if I follow this argument. If the networks uses a shifted allocentric representation centred on its initial state, it couldn't consistently decode the position from different starting positions within the same environment (I don't think egocentric is the right term here - egocentric generally refers to representations relative to the animal's own direction like "to the left" rather than "to the west" but these would not work in the allocentric decoding scheme here). In other words: If I path integrate my location relative to my starting location s1 in environment 1 and learn how to decode that representation to an environment location, I cannot use the same representation when I start from s2 in environment 1, because everything will have shifted. I still believe using boundaries is the only solution to infer the absolute location for the agent here (because that's the only information that it gets), and that's the reason for finding boundary representations (and not grid cells). Imagine doing this task on a perfect torus where there are no boundaries: it would be impossible to ever find out at what 'absolute' location you are in the environment. I have therefore not updated this part of my review, but do let me know if I misunderstood.

Thank you for addressing this point, which is a somewhat unusual feature of our network: We believe the point you raise applies if the decoding were fixed. However, in our case, the decoding is dynamic and depends on the firing pattern, as place unit centers are decoded on a per-trajectory basis. Thus, a new place-like basis may be formed for each trajectory (and in each environment). Hence, the model is not constrained to reuse its representation across trajectories or environments, as place centers are inferred based on unit firing. However, we do observe that the network learns to use a fixed place field placement in each geometry, which likely reflects some optimal solution to the decoding problem. This might also help to explain the hexagonal arrangement of learned field centers. Finally, we agree that egocentric may not be entirely accurate, but we found it to be the best word to distinguish from the allocentric-type navigation adopted by the network.

Regarding noise injection:

Beyond that noise level, the network might return to high correlations, but that must be due to the boundary interactions - very much like what happens at the very beginning of entering an environment: the network has learned to use the boundary to figure out where it is from an uninformative initial hidden state. But I don't think this is currently reflected well in the main text. That still reads "Thus, even though the network was trained without noise, it appears robust even to large perturbations. This suggests that the learned solutions form an approximate attractor." I think your new (very useful!) velocity ablations show that only small noise is compensated for by attractor dynamics, and larger noise injections are error corrected through boundary interactions. I've added this to the new review.

Thank you for your kind feedback: We have changed the phrasing in the text to say “robust even to moderate perturbations. ” As we hold that, while numerically small, the amount of injected noise is rather large when compared to the magnitude of activities in the network (see Fig. A5d); the largest maximal rate is around 0.1, which is similar to the noise level at which output representations fail to re-converge. However, some moderation is appropriate, we agree.

On contexts being attractive:

In the new bit of text, I'm not sure why "each environment appears to correspond to distinct attractive states (as evidenced by the global-type remapping behavior)", i.e. why global-type remapping is evidence for attractive states. Again, to me global-type remapping is evidence that contexts occupy different parts of activity space, but not that they are attractive. I like the new analysis in Appendix F, as it demonstrates that the context signal determines which region of activity space is selected (as opposed to the boundary information!). If I'm not mistaken, we know three things: 1. Different contexts exist in different parts of representation space, 2. Representations are attractive for small amounts of noise, 3. The context signal determines which point in representation space is selected (thanks to the new analysis in Appendix F). That seems to be in line with what the paper claims (I think "contexts are attractive" has been removed?) so I've updated the review.

It seems to us that we are in agreement on this point; our aim is simply to point out that a particular context signal appears to correspond to a particular (discrete) attractor state (i.e., occupying a distinct part of representation space, as you state), it just seems we use slightly different language, but to avoid confusion, we changed this to say that “representations are attractive”.

Thanks again for engaging with us, this discussion has been very helpful in improving the paper.

Reviewer #2:

However, I still struggle to understand the entire picture of the boundary-to-place-to-grid model. After all, what is the role of grid cells in the proposed view? Are they just redundant representations of the space? I encourage the authors to clarify these points in the last two paragraphs on pages 17-18 of the discussion.

Thank you for your feedback. While we have discussed the possible role of a grid code to some extent, we agree that this point requires clarification. We have therefore added to the discussion on the role of grid cells, which now reads “While the lack of grid cells in this model is interesting, it does not disqualify grid cells from serving as a neural substrate for path integration. Rather, it suggests that path integration may also be performed by other, non-grid spatial cells, and/or that grid cells may serve additional computational purposes. If grid cells are involved during path integration, our findings indicate that additional tasks and constraints are necessary for learning such representations. This possibility has been explored in recent normative models, in which several constraints have been proposed for learning grid-like solutions. Examples include constraints concerning population vector magnitude, conformal isometry \cite{xu_conformal_2022, schaeffer_self-supervised_2023, schoyen_hexagons_2024}, capacity, spatial separation and path invariance \cite{schaeffer_self-supervised_2023}. Another possibility is that grid cells are geared more towards other cognitive tasks, such as providing a neural metric for space \cite{ginosar_are_2023, pettersen_self-supervised_2024}, or supporting memory and inference-making \cite{whittington_tolman-eichenbaum_2020}. That our model performs path integration without grid cells, and that a myriad of independent constraints are sufficient for grid-like units to emerge in other models, presents strong computational evidence that grid cells are not solely defined by path integration, and that path integration is not only reserved for grid cells.”

Thank you again for your time and input.

eLife Assessment

This important work by Diallo et al. substantially advances our understanding of the chemosensory system of a non-hymenopteran eusocial insect by identifying the first olfactory receptor for the trail pheromone in termites. The evidence supporting the conclusions that the receptor PsimOR14 is very narrowly tuned for the pheromone neocembrene is compelling. The work will be of broad interest to entomologists, chemical ecologists, neuroscientists, and molecular biologists.

Reviewer #1 (Public review):

Summary:

In their comprehensive analysis Diallo et al. deorphanise the first olfactory receptor of a non-hymenopteran eusocial insect - a termite and identified the well established trail pheromone neocembrene as the receptor's best ligand. By using a large set of odorants the authors convincingly show that, as expected for a pheromone receptor, PsimOR14 is very narrowly tuned. While the authors first make use of an ectopic expression system, the empty neuron of Drosophila melanogaster, to characterise the receptor's responses, they next perform single sensillum recordings with different sensilla types on the termite antenna. By that they are able to identify a sensillum which houses three neurons, of which the B neuron exhibits the narrow responses described for PsimOR14. Hence the authors do not only identify the first pheromone receptor in a termite but can even localise its expression on the antenna. The authors in addition perform a structural analysis to explain the binding properties of the receptor and its major and minor ligands (as this is beyond my expertise, I cannot judge this part of the manuscript). Finally, they compare expression patterns of ORs in different castes and find that PsimOR14 is more strongly expressed in worker than in soldier termites, which corresponds well with stronger antennal responses in the worker caste.

Strengths:

The manuscript is well written and a pleasure to read.

Weaknesses:

Whenever it comes to the deorphanization of a receptor and its potential role in behaviour (in the case of the manuscript it would be trail following of the termite) one thinks immediately of knocking out the receptor to check whether it is necessary for the behaviour. However, I definitely do not want to ask for this (especially as the establishment of CRISPR Cas-9 in eusocial insects usually turns out to be a nightmare). I also do not know either, whether knock downs via RNAi have been established in termites, but maybe the authors could consider some speculation on this in the discussion.

Comments on revisions:

I appreciate how the authors have replied to my comments and I have the feeling that also the other reviewers' comments have been dealt with carefully. I therefore support the acceptance of this very nice and interesting manuscript.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors performed the functional analysis of odorant receptors (ORs) of the termite Prorhinotermes simplex to identify the receptor of trail-following pheromone. The authors performed single-sensillum recording (SSR) using the transgenic Drosophila flies expressing a candidate of the pheromone receptor and revealed that PsimOR14 strongly responds to neocembrene, the major component of the pheromone. Also, the authors found that one sensillum type (S I) detects neocembrene and also performed SSR for S I in the wild termite workers. Furthermore, the authors revealed the gene, transcript, and protein structures of PsimOR14, predict the 3D model and ligand docking of PsimOR14, and demonstrated that PsimOR14 is higher expressed in workers than soldiers using RNA-seq for heads of workers and soldiers of P. simplex and that EAG response to neocembrene is higher in workers than soldiers. I considered that this study will contribute to further understanding of the molecular and evolutionary mechanisms of chemoreception system in termites.

Strength:

The manuscript is well written. As far as I know, this study is the first study that identified a pheromone receptor in termites. The authors not only present a methodology for analyzing the function of termite pheromone receptors but also provide important insights in terms of the evolution of ligand selectivity of termite pheromone receptors.

Weakness:

This revised manuscript appears to me to have no major weaknesses.

Reviewer #3 (Public review):

Summary:

Chemical communication is essential for the organization of eusocial insect societies. It is used in various important contexts, such as foraging and recruiting colony members to food sources. While such pheromones have been chemically identified and their function demonstrated in bioassays, little is known about their perception. Excellent candidates are the odorant receptors that have been shown to be involved in pheromone perception in other insects including ants and bees but not termites. The authors investigated the function of the odorant receptor PsimOR14, which was one of four target odorant receptors based on gene sequences and phylogenetic analyses. They used the Drosophila empty neuron system to demonstrate that the receptor was narrowly tuned to the trail pheromone neocembrene. Similar responses to the odor panel and neocembrene in antennal recordings suggested that one specific antennal sensillum expresses PsimOR14. Additional protein modeling approaches characterized the properties of the ligand binding pocket in the receptor. Finally, PsimOR14 transcripts were found to be significantly higher in worker antennae compared to soldier antennae, which corresponds to the worker's higher sensitivity to neocembrene.

Strengths:

The study presents an excellent characterization of a trail pheromone receptor in a termite species. The integration of receptor phylogeny, receptor functional characterization, antennal sensilla responses, receptor structure modeling, and transcriptomic analysis is especially powerful. All parts build on each other and are well supported with a good sample size. (I cannot comment on protein modeling and docking due to a lack of expertise in this area)

Weaknesses:

None.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their comprehensive analysis Diallo et al. deorphanise the first olfactory receptor of a nonhymenopteran eusocial insect - a termite and identified the well-established trail pheromone neocembrene as the receptor's best ligand. By using a large set of odorants the authors convincingly show that, as expected for a pheromone receptor, PsimOR14 is very narrowly tuned. While the authors first make use of an ectopic expression system, the empty neuron of Drosophila melanogaster, to characterise the receptor's responses, they next perform single sensillum recordings with different sensilla types on the termite antenna. By that, they are able to identify a sensillum that houses three neurons, of which the B neuron exhibits the narrow responses described for PsimOR14. Hence the authors do not only identify the first pheromone receptor in a termite but can even localize its expression on the antenna. The authors in addition perform a structural analysis to explain the binding properties of the receptor and its major and minor ligands (as this is beyond my expertise, I cannot judge this part of the manuscript). Finally, they compare expression patterns of ORs in different castes and find that PsimOR14 is more strongly expressed in workers than in soldier termites, which corresponds well with stronger antennal responses in the worker caste.

Strengths:

The manuscript is well-written and a pleasure to read. The figures are beautiful and clear. I actually had a hard time coming up with suggestions.

We thank the reviewer for the positive comments.

Weaknesses:

Whenever it comes to the deorphanization of a receptor and its potential role in behaviour (in the case of the manuscript it would be trail-following of the termite) one thinks immediately of knocking out the receptor to check whether it is necessary for the behaviour. However, I definitely do not want to ask for this (especially as the establishment of CRISPR Cas-9 in eusocial insects usually turns out to be a nightmare). I also do not know either, whether knockdowns via RNAi have been established in termites, but maybe the authors could consider some speculation on this in the discussion.

We agree that a functional proof of the PsimOR14 function using reverse genetics would be a valuable addition to the study to firmly establish its role in trail pheromone sensing. Nevertheless, such a functional proof is difficult to obtain. Due to the very slow ontogenetic development inherent to termites (several months from an egg to the worker stage) the CRISPR Cas-9 is not a useful technique for this taxon. By contrast, termites are quite responsive to RNAimediated silencing and RNAi has previously been used for the silencing of the ORCo co-receptor in termites resulting in impairment of the trail-following behavior (DOI: 10.1093/jee/toaa248). Likewise, our previous experiments showed a decreased ORCo transcript abundance, lower sensitivity to neocembrene and reduced neocembrene trail following upon dsPsimORCo administration to P. simplex workers, while we did not succeed in reducing the transcript abundance of PsimOR14 upon dsPsimOR14 injection. We do not report these negative results in the present manuscript so as not to dilute the main message. In parallel, we are currently developing an alternative way of dsRNA delivery using nanoparticle coating, which may improve the RNAi experiments with ORs in termites.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors performed the functional analysis of odorant receptors (ORs) of the termite Prorhinotermes simplex to identify the receptor of trail-following pheromone. The authors performed single-sensillum recording (SSR) using the transgenic Drosophila flies expressing a candidate of the pheromone receptor and revealed that PsimOR14 strongly responds to neocembrene, the major component of the pheromone. Also, the authors found that one sensillum type (S I) detects neocembrene and also performed SSR for S I in wild termite workers. Furthermore, the authors revealed the gene, transcript, and protein structures of PsimOR14, predicted the 3D model and ligand docking of PsimOR14, and demonstrated that PsimOR14 is higher expressed in workers than soldiers using RNA-seq for heads of workers and soldiers of P. simplex and that EAG response to neocembrene is higher in workers than soldiers. I consider that this study will contribute to further understanding of the molecular and evolutionary mechanisms of the chemoreception system in termites.

Strength:

The manuscript is well written. As far as I know, this study is the first study that identified a pheromone receptor in termites. The authors not only present a methodology for analyzing the function of termite pheromone receptors but also provide important insights in terms of the evolution of ligand selectivity of termite pheromone receptors.

We thank the reviewer for the overall positive evaluation of the manuscript.

Weakness:

As you can see in the "Recommendations to the Authors" section below, there are several things in this paper that are not fully explained about experimental methods. Except for this point, this paper appears to me to have no major weaknesses.

We address point by point the specific comments listed in the Recommendation to the authors chapter below.

Reviewer #3 (Public review):

Summary:

Chemical communication is essential for the organization of eusocial insect societies. It is used in various important contexts, such as foraging and recruiting colony members to food sources. While such pheromones have been chemically identified and their function demonstrated in bioassays, little is known about their perception. Excellent candidates are the odorant receptors that have been shown to be involved in pheromone perception in other insects including ants and bees but not termites. The authors investigated the function of the odorant receptor PsimOR14, which was one of four target odorant receptors based on gene sequences and phylogenetic analyses. They used the Drosophila empty neuron system to demonstrate that the receptor was narrowly tuned to the trail pheromone neocembrene. Similar responses to the odor panel and neocembrene in antennal recordings suggested that one specific antennal sensillum expresses PsimOR14. Additional protein modeling approaches characterized the properties of the ligand binding pocket in the receptor. Finally, PsimOR14 transcripts were found to be significantly higher in worker antennae compared to soldier antennae, which corresponds to the worker's higher sensitivity to neocembrene.

Strengths:

The study presents an excellent characterization of a trail pheromone receptor in a termite species. The integration of receptor phylogeny, receptor functional characterization, antennal sensilla responses, receptor structure modeling, and transcriptomic analysis is especially powerful. All parts build on each other and are well supported with a good sample size.

We thank the reviewer for these positive comments.

Weaknesses:

The manuscript would benefit from a more detailed explanation of the research advances this work provides. Stating that this is the first deorphanization of an odorant receptor in a clade is insufficient. The introduction primarily reviews termite chemical communication and deorphanization of olfactory receptors previously performed. Although this is essential background, it lacks a good integration into explaining what problem the current study solves.

We understand the comment about the lack of an intelligible cue to highlight the motivation and importance of the present study. In the current version of the manuscript the introduction has been reworked. As suggested by Reviewer 3 in the Recommendations section below, the introduction now integrates some parts of the original discussion, especially the part discussing the OR evolution and emergence of eusociality in hymenopteran social insects and in termites, while underscoring the need of data from termites to compare the commonalities and idiosyncrasies in neurophysiological (pre)adaptations potentially linked with the independent eusociality evolution in the two main social insect clades.

Selecting target ORs for deorphanization is an essential step in the approach. Unfortunately, the process of choosing these ORs has not been described. Were the authors just lucky that they found the correct OR out of the 50, or was there a specific selection process that increased the probability of success?

Indeed, we were extremely lucky. Our strategy was to first select a modest set of ORs to confirm the feasibility of the Empty Neuron Drosophila system and newly established SSR setup, while taking advantage of having a set of termite pheromones, including those previously identified in the P. simplex model, some of them de novo synthesized for this project. The selection criteria for the first set of four receptors were (i) to have full-length ORF and at least 6 unambiguously predicted transmembrane regions, and (ii) to be represented on different branches (subbranches) of the phylogenetic tree. Then it was a matter of a good luck to hit the PsimOR14 selectively responding to the genuine P. simplex trail-following pheromone main component. In the revised version, we state these selection criteria in the results section (Phylogenetic reconstruction and candidate OR selection).

The deorphanization attempts of additional P. simplex ORs are currently running.

The authors assigned antennal sensilla into five categories. Unfortunately, they did not support their categories well. It is not clear how they were able to differentiate SI and SII in their antennal recordings.

We agree that the classification of multiporous sensilla into five categories lacks robust discrimination cues. The identification of the neocembrene-responding sensillum was initially carried out by SSR measurements on individual olfactory sensilla of P. simplex workers one-by-one and the topology of each tested sensillum was recorded on optical microscope photographs taken during the SSR experiment. Subsequently, the SEM and HR-SEM were performed in which we localized the neocembrene sensillum and tried to find distinguishing characters. We admit that these are not robust. Therefore, in the revised version of the manuscript we decided to abandon the attempt of sensilla classification and only report the observations about the specific sensillum in which we consistently recorded the response to neocembrene (and geranylgeraniol). The modifications affect Fig. 4, its legend and the corresponding part of the results section (Identification of P. simplex olfactory sensillum responding to neocembrene).

The authors used a large odorant panel to determine receptor tuning. The panel included volatile polar compounds and non-volatile non-polar hydrocarbons. Usually, some heat is applied to such non-volatile odorants to increase volatility for receptor testing. It is unclear how it is possible that these non-volatile compounds can reach the tested sensilla without heat application.

The reviewer points at an important methodological error we made while designing the experiments. Indeed, the inclusion of long-chain hydrocarbons into Panel 1 without additional heat applied to the odor cartridges was inappropriate, even though the experiments were performed at 25–26 °C. We carefully considered the best solution to correct the mistake and finally decided to remove all tested ligands beyond C22 from Panel 1, i.e. altogether five compounds. These changes did not affect the remaining Panels 2-4 (containing compounds with sufficient volatility), nor did they affect the message of the manuscript on highly selective response of PsimOR14 to neocembrene (and geranylgeryniol). In consequence, Figures 2, 3 and 5 were updated, along with the supplementary tables containing the raw data on SSR measurements. In addition, the tuning curve for PsimOR14 was re-built and receptor lifetime sparseness value re-calculated (without any important change). We also exchanged squalene for limonene in the docking and molecular dynamics analysis and made new calculations.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) L 208: "than" instead of "that"

Corrected.

(2) L 527+527 strange squares (•) before dimensions

Apparently an error upon file conversion, corrected.

(3) L553 "reconstructing" instead of "reconstruct"

Corrected.

(4) Two references (Chahda et al. and Chang et al. appear too late in the alphabet.

Corrected. Thank you for spotting this mistake. Due to our mistake the author list was ordered according to the alphabet in Czech language, which ranks CH after H.

Reviewer #2 (Recommendations for the authors):

(1) L148: Why did the authors select only four ORs (PsimOR9, 14, 30, and 31) though there are 50 ORs in P. simplex? I would like you to explain why you chose them.

Our strategy was to first select a modest set of ORs to confirm the feasibility of the Empty Neuron Drosophila system and newly established SSR setup, while taking advantage of having a set of termite pheromones, including those previously identified in the P. simplex model, some of them de novo synthesized for this project. Then, it was a matter of a good luck to hit the PsimOR14 selectively responding to the genuine P. simplex trail-following pheromone main component, while the deorphanization attempts of a set of additional P. simplex ORs is currently running. In the revised version of the manuscript, we state the selection criteria for the four ORs studied in the Results section (Phylogenetic reconstruction and candidate OR selection).

(2) L149: Where is Figure 1A? Does this mean Figure 1?

Thank you for spotting this mistake. Fig. 1 is now properly labelled as Fig. 1A and 1B in the figure itself and in the legend. Also the text now either refers to either 1A or 1B.

(3) Figure 1: The authors also showed the transcription abundance of all 50 ORs of P. simplex in the right bottom of Figure 1, but there is no explanation about it in the main text.

The heatmap reporting the transcript abundances is now labelled as Fig. 1B and is referred to in the discussion section (in the original manuscript it was referred to on the same place as Fig. 1).

(4) L260-265: The authors confirmed higher expression of PsimOR14 in workers than soldiers by using RNA-seq data and stronger EAG responses of PsimOR14 to neocembrene in workers than soldiers, but I think that confirming the expression levels of PsimOR14 in workers and soldiers by RT-qPCR would strengthen the authors' argument (it is optional).

qPCR validation is a suitable complement to read count comparison of RNA Seq data, especially when the data comes from one-sample transcriptomes and/or low coverage sequencing. Yet, our RNA Seq analysis is based on sequencing of three independent biological replicates per phenotype (worker heads vs. soldier heads) with ~20 millions of reads per sample. Thus, the resulting differential gene expression analysis is a sufficient and powerful technique in terms of detection limit and dynamic range.

We admit that the replicate numbers and origin of the RNA seq data should be better specified since the Methods section only referred to the GenBank accession numbers in the original manuscript. Therefore, we added more information in the Methods section (Bioinformatics) and make clear in the Methods that this data comes from our previous research and related bioproject.

(5) L491: I think that "The synthetic processes of these fatty alcohols are ..." is better.

We replaced the sentence with “The de novo organic synthesis of these fatty alcohols is described …”

(6) L525 and 527: There are white squares between the number and the unit. Perhaps some characters have been garbled.

Apparently an error upon file conversion, corrected.

(7) L795: ORCo?

Corrected.

(8) L829-830 & Figure 4: Where is Figure 4D?

Thank you for spotting this mistake from the older version of Figure 4. The SSR traces referred to in the legend are in fact a part of Figure 5. Moreover, Figure 4 is now reworked based on the comments by Reviewer 3.

(9) L860-864: Why did the authors select the result of edgeR for the volcano plot in Figure 7 although the authors use both DESeq2 and edgeR? An explanation would be needed.

Both algorithms, DESeq2 and EdgeR, are routinely used for differential gene expression analysis. Since they differ in read count normalization method and statistical testing we decided to use both of them independently in order to reduce false positives. Because the resulting fold changes were practically identical in both algorithms (results for both analyses are listed in Supplementary table S15), we only reported in Fig. 7 the outputs for edgeR to avoid redundancies. We added in the Results section the information that both techniques listed PsimOR14 among the most upregulated in workers.

Reviewer #3 (Recommendations for the authors):

The discussion contains many descriptions that would fit better into the introduction, where they could be used to hint at the study's importance (e.g., 292-311, 381-412). The remaining parts often lack a detailed discussion of the results that integrates details from other insect studies. Although references were provided, no details were usually outlined. It would be helpful to see a stronger emphasis on what we learn from this study.

Along with rewriting the introduction, we also modified the discussion. As suggested, the lines 292-311 were rewritten and placed in the introduction. By contrast, we preferred to keep the two paragraphs 381-412 in the discussion, since both of them outline the potential future interesting targets of research on termite ORs.

As suggested, the discussion has been enriched and now includes comparative examples and relevant references about the broad/narrow selectivity of insect ORs, about the expected breadth of tuning of pheromone receptors vs. ORs detecting environmental cues, about the potential role of additional neurons housed in the neocembrene-detecting sensillum of P. simplex workers, etc. From both introduction and discussion the redundant details on the chemistry of termite communication have been removed.

This includes explanations of the advantages of the specific methodologies the authors used and how they helped solve the manuscript's problem. What does the phylogeny solve? Was it used to select the ORs tested? It would be helpful to discuss what the phylogeny shows in comparison to other well-studied OR phylogenies, like those from the social Hymenoptera.

We understand the comment. In fact, our motivation to include the phylogenetic tree of termite ORs was essentially to demonstrate (i) the orthologous nature of OR diversity with few expansions on low taxonomic levels, and (ii) to demonstrate graphically the relationship among the four selected sequences. We do not attempt here for a comprehensive phylogenetic analysis, because it would be redundant given that we recently published a large OR phylogeny which includes all sequences used in the present manuscript and analysed them in the proper context of related (cockroaches) and unrelated insect taxa (Johny et al., 2023). This paper also discusses the termite phylogenetic pattern with those observed in other Insecta. This paper is repeatedly cited on appropriate places of the present manuscript and its main observations are provided in the Introduction section. Therefore, we feel that thorough discussion on termite phylogeny would be redundant in the present paper.

The authors categorized the sensilla types. Potential problems in the categorization aside, it would be helpful to know if it is expected that you have sensilla specialized in perceiving one specific pheromone. What is known about sensilla in other insects?

We understand. In the discussion of the revised version, we develop more about the features typical/expected for a pheromone receptor and the sensillum housing this receptor together with two other olfactory sensory neurons, including examples from other insects.

As the manuscript currently stands, specialist readers with their respective background knowledge would find this study very interesting. In contrast, the general reader would probably fail to appreciate the importance of the results.

We hope that the re-organized and simplified introduction may now be more intelligible even for non-specialist readers.

(1) L35: Should "workers" be replaced with "worker antennae"?

Corrected.

(2) L62: Should "conservativeness" be replaced by "conservation"?

Replaced with “parsimony”.

(3) L129: How and why did the authors choose four candidate ORs? I could not find any information about this in the manuscript. I wondered why they did not pick the more highly expressed PsimOr20 and 26 (Figure 7).

As already replied above in the Weaknesses section, we selected for the first deorphanization attempts only a modest set of four ORs, while an additional set is currently being tested. We also explained above the inclusion criteria, i.e. (i) full-length ORF and at least 6 unambiguously predicted transmembrane regions, and (ii) presence on different branches (subbranches) of the OR phylogeny. For these reasons, we did not primarily consider the expression patterns of different ORs. As for Fig. 7, it shows differential expression between soldiers and workers, which was not the primary guideline either and the data was obtained only after having the ORs tested by SSR. Yet, even though we had data on P. simplex ORs expression (Fig. 1B), we did not presume that pheromone receptors should be among the most expressed ORs, given the richness of chemical cues detected by worker termites and unlike, e.g., male moths, where ORs for sex pheromones are intuitively highly expressed.

The strategy of OR selection is specified in the results section of the revised manuscript under “Phylogenetic reconstruction and candidate OR selection”.

(4) 198 to 200: SI, II, and III look very similar. Additional measurements rather than qualitative descriptions are required to consider them distinct sensilla. The bending of SIII could be an artifact of preparation. I do not see how the authors could distinguish between SI and SII under the optical microscope for recordings. A detailed explanation is required.

As we responded above in “Weaknesses” chapter, we admit that the sensilla classification is not intelligible. Therefore, we decided in the revised version to abandon the classification of sensilla types and only focus on the observations made on the neocembreneresponding sensillum. To recognize the specific sensillum, we used its topology on the last antennal segment. Because termite antennae are not densely populated with sensilla, it is relatively easy to distinguish individual sensilla based on their topology on the antenna, both in optical microscope and SEM photographs. The modifications affect Fig. 4, its legend and the corresponding part of the results section (Identification of P. simplex olfactory sensillum responding to neocembrene).

(5) 208: "Than" instead of "that"

Corrected.

(6) 280: I suggest replacing "demand" with "capabilities"

Corrected.

(7) 312: Why "nevertheless? It sounds as if the authors suggest that there is evidence that ORs are not important for communication. This should be reworded.

We removed “Nevertheless” from the beginning of the sentence.

(8) 321 to 323: This sentence sounds as if something is missing. I suggest rewriting it.

This sentence simply says that empty neuron Drosophila is a good tool for termite OR deorphanization and that termite ORs work well Drosophila ORCo. We reworded the sentence.

(9) 323: I suggest starting a new paragraph.

Corrected.

(10) 421: How many colonies were used for each of the analyses?

The data for this manuscript were collected from three different colonies collected in Cuba. We now describe in the Materials and Methods section which analyses were conducted with each of the colonies.

(11) 430: Did the termites originate from one or multiple colonies and did the authors sample from the Florida and Cuba population?

The data for this manuscript were collected from three different colonies collected in Cuba. We now describe in the Materials and Methods section which analyses were conducted with each of the colonies.

(12) 501: How was the termite antenna fixated? The authors refer to the Drosophila methods, but given the large antennal differences between these species, more specific information would be helpful.

Understood. We added the following information into the Methods section under “Electrophysiology”: “The grounding electrode was carefully inserted into the clypeus and the antenna was fixed on a microscope slide using a glass electrode. To avoid the antennal movement, the microscope slide was covered with double-sided tape and the three distal antennal segments were attached to the slide.”

(13)509: I want to confirm that the authors indicate that the outlet of the glass tube with the airstream and odorant is 4 cm away from the Drosophila or termite antenna. The distance seems to be very large.

Thank you for spotting this obvious mistake. The 4 cm distance applies for the distance between the opening for Pasteur pipette insertion into the delivery tube, the outlet itself is situated approx. 1 cm from the antenna. This information is now corrected.

(14) 510/527: It looks like all odor panels were equally applied onto the filter paper despite the difference in solvent (hexane and paraffin oil). How was the solvent difference addressed?

In our study we combine two types of odorant panels. First, we test on all four studied receptors a panel containing several compounds relevant for termite chemical communication including the C12 unsaturated alcohols, the diterpene neocembrene, the sesquiterpene (3R,6E)-nerolidol and other compounds. These compounds are stored in the laboratory as hexane solutions to prevent the oxidation/polymerization and it is not advisable to transfer them to another solvent. In the second step we used three additional panels of frequently occurring insect semiochemicals, which are stored as paraffin oil solutions, so as to address the breadth of PsimOR14 tuning. We are aware that the evaporation dynamics differ between the two solvents but we did not have any suitable option how to solve this problem. We believe that the use of the two solvents does not compromise the general message on the receptor specificity. For each panel, the corresponding solvent is used as a control. Similarly, the use of two different solvents for SSR can be encountered in other studies, e.g. 10.1016/j.celrep.2015.07.031.

(15) 518: delta spikes/sec works for all tables except for the wild type in Table S5. I could not figure out how the authors get to delta spikes/sec in that table.

Thank you for your sharp eye. Due to our mistake, the values of Δ spikes per second reported in Table S5 for W1118 were erroneously calculated using the formula for 0.5 sec stimulation instead of 1 sec. We corrected this mistake which does not impact the results interpretation in Table S5 and Fig. 2.

522: Did the workers and soldiers originate from different colonies or different populations?

We now clearly describe in the Material and Methods section the origin of termites for different experiments. EAG measurements were made using individuals (workers, soldiers) from one Cuban colony.

(16) Figure 6C/D: I suggest matching colors between the two figures. For example, instead of using an orange circle in C and a green coloration of the intracellular flap in D, I recommend using blue, which is not used for something else. In addition, the binding pocket could be separated better from anything else in a different color.

We agree that the color match for the intracellular flap was missing. This figure is now reworked and the colors should have a better match and the binding region is better delineated.

(17) Figure 7/Table S15: It is unclear where the transcriptome data originate and what they are based on. Are these antennal transcriptomes or head transcriptomes? Do these data come from previous data sets or data generated in this study? Figure 7 refers to heads, Table S15 to workers and soldiers, and the methods only refer to antennal extractions. This should be clarified in the text, the figure, and the table.

We admit that the replicate numbers and origin of the RNA seq data should be better specified and that the information that the RNASeq originated from samples of heads+antennae of workers and soldiers should be provided at appropriate places. Therefore, we added more information on replicates and origin of the data in the Methods section (Bioinformatics) and make clear that this data comes from our previous research and refer to the corresponding bioproject. Likewise, the Figure 7 legend and Table S15 heading have been updated.

eLife Assessment

This manuscript reports effects of a single dose of methamphetamine vs placebo on a probabilistic reversal learning task with different levels of noise, in a large group of young healthy volunteers. The paper is well written and the methods are rigorous. The findings are important and have theoretical or practical implications beyond a single a subfield. The strength of the evidence is convincing, with the methods, data, and analyses broadly supporting the claims in the paper, which are sufficiently qualified given the lack of a significant effect of the binary baseline performance variable, and the nonlinear effect of individual differences in baseline performance.

Reviewer #1 (Public review):

The authors examine how probabilistic reversal learning is affected by dopamine by studying the effects of methamphetamine (MA) administration. Based on prior evidence that the effects of pharmacological manipulation depend on baseline neurotransmitter levels, they hypothesized that MA would improve learning in people with low baseline performance. They found this effect, and specifically found that MA administration improved learning in noisy blocks, by reducing learning from misleading performance, in participants with lower baseline performance. The authors then fit participants' behavior to a computational learning model and found that an eta parameter, responsible for scaling learning rate based on previously surprising outcomes, differed in participants with low baseline performance on and off MA.

Questions:

(1) It would be helpful to confirm that the observed effect of MA on the eta parameter is responsible for better performance in low baseline performers. If performance on the task is simulated for parameters estimated for high and low baseline performers on and off MA, does the simulated behavior capture the main behavioral differences shown in Figure 3?

(2) In Figure 4C, it appears that the main parameter difference between low and high baseline performance is inverse temperature, not eta. If MA is effective in people with lower baseline DA, why is the effect of MA on eta and not IT?

Also, this parameter is noted as temperature but appears to be inverse temperature as higher values are related to better performance. The exact model for the choice function is not described in the methods.

Comments on revisions:

Thanks to the authors for their thorough responses and revisions. One typo to note: in the Methods, the "drug effects" paragraph is repeated.

Reviewer #2 (Public review):

Summary:

Kirschner and colleagues test whether methamphetamine (MA) alters learning rate dynamics in a validated reversal learning task. They find evidence that MA can enhance performance for low-performers, and that the enhancement reflects a reduction in the degree to which these low-performers dynamically up-regulate their learning rates when they encounter unexpected outcomes. The net effect is that poor performers show more volatile learning rates (e.g. jumping up when they receive misleading feedback), when the environment is actually stable, undermining their performance over trials.

Strengths:

The study has multiple strengths, including a large sample size, placebo control, double-blind randomized design, and rigorous computational modeling of a validated task. Additionally, the analytic methods are rigorous and offer new types of analyses for people interested in exploring learning as a function of dynamically changing volatility.

Weaknesses:

The limitations, which are acknowledged, include that the drug they use, methamphetamine, can influence multiple neuromodulatory systems including catecholamines and acetylcholine, all of which have been implicated in learning rate dynamics. They also do not have any independent measures of any of these systems, so it is impossible to know which is having an effect.

Another limitation which they should acknowledge is that the fact that participants were aware of having different experiences in the drug sessions means that their blinding was effectively single-blind (to the experimenters) and not double-blind. That said, the authors do provide some evidence that subjective effects of drugs (e.g. arousal, mood, etc.) did not drive differences in performance.

Comments on revisions:

The authors have done an outstanding job responding to, and allaying my prior concerns about their analyses.

eLife Assessment

Bonnifet et al. present data on the expression and interacting partners of the transposable element L1 in the mammalian brain. The work includes important findings addressing the potential role of L1 in aging and neurodegenerative disease. The reviewers conclude that several aspects of the study are well done. However, the experimental evidence presented supporting the L1 increase with aging is not fully conclusive and this finding remains incomplete in its current form.

Reviewer #1 (Public review):

Summary:

In this study, Bonnifet et al. profile the presence of L1 ORF1p in the mouse and human brain and report that ORF1p is expressed in the human and mouse brain specifically in neurons at steady state and that there is an age-dependent increase in expression. This is a timely report as two recent papers have extensively documented the presence of full-length L1 transcripts in the mouse and human brain (PMID: 38773348 & PMID: 37910626). Thus, the finding that L1 ORF1p is consistently expressed in the brain is important to document and will be of value to the field.

Strengths:

Several parts of this manuscript appear to be well done and include the necessary controls. In particular, the documentation of neuron-specific expression of ORF1p in the mouse brain is an interesting finding with nice documentation. This will be very useful information for the field.

Weaknesses:

Several parts of the manuscript appear to be more preliminary and need further experiments to validate their claims. In particular, the data suggesting expression of L1 ORF1p in the human brain and the data suggesting increased expression in the aged brain need further validation. Detailed comments:

(1) The expression of ORF1p in the human brain shown in Fig. 1j is puzzling. Why are there two strong bands in the WB? How can the authors be sure that this signal represents ORF1p expression and not non-specific labelling? While the authors discuss that others have found double bands when examining human ORF1p, there are also several labs that report only one band. This discrepancy in the field should at least be discussed and the uncertainties with their findings should be acknowledged.

(2) The data showing a reduction in ORF1p expression in the aged mouse brain is an interesting observation, but the effect magnitude of effect is very limited and somewhat difficult to interpret. This finding should be supported by orthogonal methods to strengthen this conclusion. For example, by WB and by RNA-seq (to verify that the increase in protein is due to an increase in transcription).

(3) The transcriptomic data using human postmortem tissue presented in Figure 4 and Figure 5 are not convincing. Quantification of transposon expression on short read sequencing has important limitations. Longer reads and complementary approaches are needed to study the expression of evolutionarily young L1s (see PMID: 38773348 & PMID: 37910626 for examples of the current state of the art). As presented, the human RNA data is inconclusive due to the short read length and small sample size. The value of including an inconclusive analysis in the manuscript is difficult to understand. With this data set, the authors cannot investigate age-related changes in L1 expression in human neurons.

(4) In line with these comments, the title should be changed to better reflect the findings in the manuscript. A title that does not mention "L1 increase with aging" would be better.

Reviewer #2 (Public review):

Summary:

Bonnifet et al. sought to characterize the expression pattern of L1 ORF1p expression across the entire mouse brain, in young and aged animals and to corroborate their characterization with Western blotting for L1 ORF1p and L1 RNA expression data from human samples. They also queried L1 ORF1p interacting partners in the mouse brain by IP-MS.

Strengths:

A major strength of the study is the use of two approaches: a deep-learning detection method to distinguish neuronal vs. non-neuronal cells and ORF1p+ cells vs. ORF1p- cells across large-scale images encompassing multiple brain regions mapped by comparison to the Allen Brain Atlas, and confocal imaging to give higher resolution on specific brain regions. These results are also corroborated by Western blotting on six mouse brain regions. Extension of their analysis to post-mortem human samples, to the extent possible, is another strength of the paper. The identification of novel ORF1p interactors in brain is also a strength in that it provides a novel dataset for future studies.

Weaknesses:

The main weakness of the study is that cell type specificity of ORF1p expression was not examined beyond neuron (NeuN+) vs non-neuron (NeuN-). Indeed, a recent study (Bodea et al. 2024, Nature Neuroscience) found that ORF1p expression is characteristic of parvalbumin-positive interneurons, and it would be very interesting to query whether other neuronal subtypes in different brain regions are distinguished by ORF1p expression. The data suggesting that ORF1p expression is increased in aged mouse brains is intriguing, although it seems to be based upon modestly (up to 27%, dependent on brain region) higher intensity of ORF1p staining rather than a higher proportion of ORF1+ neurons. Indeed, the proportion of NeuN+/Orf1p+ cells actually decreased in aged animals. It is difficult to interpret the significance and validity of the increase in intensity, as Hoechst staining of DNA, rather than immunostaining for a protein known to be stably expressed in young and aged neurons, was used as a control for staining intensity. The main weakness of the IP-MS portion of the study is that none of the interactors were individually validated or subjected to follow-up analyses. The list of interactors was compared to previously published datasets, but not to ORF1p interactors in any other mouse tissue.

The authors achieved the goals of broadly characterizing ORF1p expression across different regions of the mouse brain, and identifying putative ORF1p interactors in the mouse brain. However, findings from both parts of the study are somewhat superficial in depth.

This provides a useful dataset to the field, which likely will be used to justify and support numerous future studies into L1 activity in the aging mammalian brain and in neurodegenerative disease. Similarly, the list of ORF1p interacting proteins in the brain will likely be taken up and studied in greater depth.

Comments on revisions:

The co-staining of Orf1p with Parvalbumin (PV) presented in Supplemental Figure S5 is a welcome addition exploring the cell type-specificity of Orf1p staining, and broadly corroborates the work of Bodea et al. while revealing that Orf1p also is expressed in non-PV+ cells, consistent with L1 activity across a range of neuronal subtypes. The authors also have strengthened their findings regarding the increased intensity of ORF1p staining in aged compared to young animals, and the newly presented results are indeed more convincing. The prospect of increased neuronal L1 activity with age is exciting, and the results in this paper have provided the groundwork for ongoing discoveries in this area. While it is disappointing that no Orf1p interactors were followed up, this is understandable and the data are nonetheless valuable and will likely prove useful to future studies.

eLife Assessment

This fundamental study describes patterns of anatomical connectivity between the cortex and the thalamus using magnetic resonance imaging data in humans and non-human primates. The measures are related to numerous other modalities to develop a robust understanding of the organisation of the system. The authors provide convincing evidence that there is a difference between sensory and association cortices in terms of their connectivity with the thalamus, which may have downstream effects on brain function. This work will be of interest to neuroscientists interested in the organization and dynamics of cortico-thalamic circuits.

Reviewer #1 (Public review):

Summary:

The thalamus is a central subcortical structure consisting of that receives anatomical connections from various cortical areas, each displaying a unique pattern. Previous studies have suggested that certain cortical areas may establish more extensive connections within the thalamus, influencing distributed information flow. Despite these suggestions, a quantitative understanding of cortical areas' anatomical connectivity patterns within the thalamus is lacking. In this study, the researchers addressed this gap by employing diffusion magnetic resonance imaging (dMRI) on a large cohort of healthy adults from the Human Connectome Project. Using brain-wide probabilistic tractography, a framework was developed to measure the spatial extent of anatomical connections within the thalamus for each cortical area. Additionally, the researchers integrated resting-state functional MRI, cortical myelin, and human neural gene expression data to investigate potential variations in anatomical connections along the cortical hierarchy. The results unveiled two distinct cortico-thalamic tractography motifs: 1) a sensorimotor cortical motif featuring focused thalamic connections to the posterolateral thalamus, facilitating fast, feed-forward information flow; and 2) an associative cortical motif characterized by diffuse thalamic connections targeting the anteromedial thalamus, associated with slower, feed-back information flow. These motifs exhibited consistency across human subjects and were corroborated in macaques, underscoring cross-species generalizability. In summary, the study illuminates differences in the spatial extent of anatomical connections within the thalamus for sensorimotor and association cortical areas, potentially contributing to functionally distinct cortico-thalamic information flow.

Strengths:

Quantitative Approach: The study employs diffusion magnetic resonance imaging (dMRI) and probabilistic tractography on a substantial sample size of 828 healthy adults, providing a robust quantitative analysis of anatomical connectivity patterns within the thalamus.

Multi-Modal Integration: By incorporating resting-state functional MRI, cortical myelin, and human neural gene expression data, the study offers a comprehensive approach to understanding anatomical connections, enriching the interpretation of findings and enhancing the study's overall validity.

Cross-Species Generalizability: The identification of consistent cortico-thalamic tractography motifs in both human subjects and macaques demonstrates the robustness and cross-species generalizability of the findings, strengthening the significance and broader applicability of the study.

Supplementary Analyses: There are numerous, excellent examples of clear surrogates used to test the major claims of the paper. This is exemplary work.

Weaknesses:

Indirect Estimates of White Matter Connections: While dMRI is a valuable tool, it inherently provides indirect and inferred information about neural pathways. The accuracy and specificity of tractography can be influenced by various factors, including fiber crossing, partial volume effects, and algorithmic assumptions. A potential limitation in the accuracy of indirect estimates might affect the precision of spatial extent measurements, introducing uncertainty in the interpretation of cortico-thalamic connectivity patterns. Addressing the methodological limitations associated with indirect estimates and considering complementary approaches could strengthen the overall robustness of the findings.

Comments on revised version:

The authors have addressed my concerns.

Reviewer #2 (Public review):

Summary:

This paper by Howell and colleagues focuses on describing macro patterns of anatomical connections between cortical areas and the thalamus in the human brain. This research topic poses significant challenges due to the inability to apply the gold standard of mapping anatomical connections, viral tracing, to humans. Moreover, when applied to animal models, viral tracing often has limited scope and resolution. As a result, the field has thus far lacked a comprehensive and validated description of thalamocortical anatomical connectivity in humans.

The paper focuses on an intriguing question: whether anatomical connections from the cortex to the thalamus exhibit a diffuse pattern, targeting multiple thalamic sub-regions, or a more focal pattern, selectively targeting specific thalamic subregions. This novel and significant question holds substantial implications for our understanding of thalamocortical information processing. The authors have developed a sophisticated and innovative quantitative metric to address this question. The study revealed two main patterns: a focal pattern originating from sensorimotor cortical regions to the posterior thalamus and a more diffuse pattern from associative cortical regions to the anterior-medial thalamus. These findings are then framed within the context of thalamocortical motifs involved in feedforward versus feedback processing.

While this paper has several strengths, including its significance and methodological sophistication, its extension to non-human primates and other forms of data for testing hierarchy, there are important limitations. These limitations, discussed in more detail below, primarily concern tracking accuracy and the known limitations of using diffusion data to track thalamocortical connections in humans. These limitations may potentially introduce systematic biases into the results, weakening their support. Addressing these limitations through better validation is crucial, though some may remain unresolved due to the fundamental constraints of diffusion imaging.

Strengths:

This research holds significant basic, clinical, and translational importance as it contributes to our understanding of how thalamocortical anatomical connectivity is organized. Its relevance spans across cognitive, systems, and clinical neuroscientists in various subfields.

The central question addressed in this study, concerning whether cortico-thalamic projections are focal or diffuse, is both novel and previously unexplored to the best of my knowledge. It offers valuable insights into the potential capabilities of the thalamocortical system in terms of parallel or integrative processing.

The development of quantitative metrics to analyze anatomical connectivity is highly innovative and suitable for addressing the research questions at hand.

The findings are not only interesting but also robust, aligning with data from other sources that suggest a hierarchical organization in the brain.

Using PCA to integrate results across a range of thresholds is innovative.

The study's sophisticated integration of a diverse range of data and methods provides strong, converging support for its main findings, enhancing the overall credibility of the research.

Weaknesses:

Structural thalamocortical connectivity was estimated from diffusion imaging data obtained from the HCP dataset. Consequently, the robustness and accuracy of the results depend on the suitability of this data for such a purpose. Conducting tractography on the cortical-thalamic system is recognized as a challenging endeavour for several reasons. First, diffusion directions lose their clearly defined principal orientations once they reach the deep thalamic nuclei, rendering the tracking of structures on the medial side, such as the medial dorsal (MD) and pulvinar nuclei difficult. Somewhat concerning is those are regions that authors found to show diffuse connectivity patterns. Second, the thalamic radiata diverges into several directions, and routes to the lateral surface often lack the clarity necessary for successful tracking. It is unclear if all cortical regions have similar levels of accuracy, and some of the lateral associative regions might have less accurate tracking, making them appear to be more diffuse, biasing the results.

While the methodology employed by the authors appears to be state-of-the-art, there exists uncertainty regarding its appropriateness for validation, given the well-documented issues of false positives and false negatives in probabilistic diffusion tractography, as discussed by Thomas et al. 2014 PNAS. Although replicating the results in both humans and non-human primates strengthens the study, a more compelling validation approach would involve demonstrating the method's ability to accurately trace known tracts from established tracing studies or, even better, employing phantom track data. Many of the control analyses the authors presented, such as track density, do not speak to accuracy.

Because the authors included data from all thresholds into, it seems likely that false positives tracks were included into the results. The methodology described seems to unavoidably include anatomically implausible pathways in the spatial extent analyses.

If tracking the medial thalamus is indeed less accurate, characterized by higher false positives and false negatives, it could potentially lead to increased variability among individual subjects. In cases where results are averaged across subjects, as the authors have apparently done, this could inadvertently contribute to the emergence of the "diffuse" motif, as described in the context of the associative cortex. This presents a critical issue that requires a more thorough control analysis and validation process to ensure that the main results are not artifacts resulting from limitations in tractography.

The thresholding approach taken in the manuscript was aimed to control for inter-areal differences in anatomical connection strength that could confound the ED estimates. Here I am not quite clear why inter-areal differences in anatomical connection strength have to be controlled. A global threshold applied on all thalamic voxels might kill some connections that are weak but do exist. Those weak pathways are less possible to survive at high thresholds. In the meantime, the mean ED is weighted, with more conservative thresholds having higher weights. That being said, isn't it possible that more robust pathways might contribute more to the mean ED than weaker pathways?

Comments on revised version:

I appreciate the additional supplementary figures and responses from the authors. I think this is an important study, and the review I wrote should provide important context for readers to digest their responses.

Reviewer #3 (Public review):

Summary:

In the current work, Howell et al studied the connectivity between cortex and thalamus using DTI tractography per parcel to all voxels in the thalamus. Following they performed various dimensional reduction techniques to uncover how differences in connectivity to the thalamus vary across cortical parcels. Following they explore the spatial correlation of these variations with cortical myelin and functional organization, thalamic nuclei, gene expression derived core-matrix cell differentiation, and extend the model towards macaques. Overall, the authors find a differentiation between sensory and association areas in terms of the association with the thalamus, which reflects differences in cortical microstructure and function, and links to core-matrix differences and can be replicated in macaques.

Strengths:

A clear strength of the current work is the combination of different models and approaches to study the link between the cortex and the thalamus. This approach nicely bridges different approaches to describe the role of the thalamus in cortical organisation using a diffusion-based approach. Especially the extension of the model to the macaque is quite nice.

Appraisal:

The aim of the study: 'to investigate the spatial extent of anatomical connectivity patterns within the thalamus in both humans and non-human primates and determine if such patterns differ between sensorimotor and association cortical areas' has been met. Further work may continue to investigate other implications of this finding.

Discussion:

Overall, I think the study is an intriguing addition to a growing literature studying the anatomical connectivity between thalamus and cortex and its functional implications.

Comments on revised version:

Thank you for the responses.

Author response:

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

Reviewer 1:

Comment 1: Indirect Estimates of White Matter Connections: While dMRI is a valuable tool, it inherently provides indirect and inferred information about neural pathways. The accuracy and specificity of tractography can be influenced by various factors, including fiber crossing, partial volume effects, and algorithmic assumptions. A potential limitation in the accuracy of indirect estimates might affect the precision of spatial extent measurements, introducing uncertainty in the interpretation of cortico-thalamic connectivity patterns. Addressing the methodological limitations associated with indirect estimates and considering complementary approaches could strengthen the overall robustness of the findings.

We appreciate the reviewer’s comment and agree tractography is an indirect estimate and subject to limitations. Regarding this manuscript, the key question is not whether the anatomical tracts are without false positives or negatives, and in fact we argue that this question is outside the scope of this manuscript and has been addressed in several previous studies (e.g. Thomas et al. 2015, Schilling et al., 2020, Grisot et al. 2021, and many others). Instead, the key question for this manuscript is whether the focality of termination patterns within the thalamus is systematically biased in a way that the observation of a hierarchy effect is artifactual. The many supplementary analyses in this manuscript do help address this question and increase our confidence that the indirect nature of tractography does not systematically bias the EDpc1 measure such that association areas only appear to have more diffuse connectivity patterns relative to sensorimotor areas.

Comment 2: An over-arching theme of my review is that, each time I found myself wondering about a detail, a null, or a reference, I had only to read the next sentence or paragraph to find my concern handled in a clear and concise fashion. This is, in my opinion, the mark of work of the highest order. I congratulate the authors on their excellent work, which I believe will be impactful and well-received.

I have no notes that I feel can help improve what is already an impeccable piece of work.

We thank the reviewer for the kind comment.

Reviewer #2:

Comment 1: Structural thalamocortical connectivity was estimated from diffusion imaging data obtained from the HCP dataset. Consequently, the robustness and accuracy of the results depend on the suitability of this data for such a purpose. Conducting tractography on the cortical-thalamic system is recognized as a challenging endeavor for several reasons. First, diffusion directions lose their clearly defined principal orientations once they reach the deep thalamic nuclei, rendering the tracking of structures on the medial side, such as the medial dorsal (MD) and pulvinar nuclei difficult. Somewhat concerning is those are regions that authors found to show diffuse connectivity patterns. Second, the thalamic radiata diverge into several directions, and routes to the lateral surface often lack the clarity necessary for successful tracking. It is unclear if all cortical regions have similar levels of accuracy, and some of the lateral associative regions might have less accurate tracking, making them appear to be more diffuse, biasing the results.

As mentioned in the weakness section, it is crucial to address the need for better validation or the inclusion of control analyses to ensure that the results are not systematically biased due to known issues, such as the difficulty in tracking the medial thalamus and the potential for higher false positives when tracking the lateral frontal cortex.

We thank that reviewer for bringing up an important point. To determine if some areas of the thalamus were more difficult to track and, in turn, biased the EDpc1 measure we added an additional supplemental figure (S31). In this figure, shown below, we calculate the total SC of all ipsilateral cortical areas to each thalamic voxel. We show that, indeed, medial thalamic voxels have a lower total streamline count to ipsilateral cortex, and we see reduced total streamline counts to lateral thalamic areas and the very posterior end of the thalamus. We determined if some cortical areas preferentially projected to parts of the thalamus with lower ipsilateral total SC (i.e. by calculating the overlap between SC and total cortical SC for each thalamic voxel) and found only a weak relationship with our measure. Furthermore, we regressed each voxel’s mean ipsilateral cortical SC from streamline count matrix. We found that the EDpc1 measure didn’t significantly change after the regression.

Additionally, we note that this analysis assumes that all thalamic voxels should have equal strength of connectivity (i.e., total SC) to the ipsilateral cortex and that such a measure is a proxy for “accuracy.” While both of these assumptions may not be entirely valid, this figure does demonstrate that potential reductions in tracking from the medial thalamus does not significantly affect the EDpc1 measure.

Comment 2: While the methodology employed by the authors appears to be state-of-the-art, there exists uncertainty regarding its appropriateness for validation, given the well-documented issues of false positives and false negatives in probabilistic diffusion tractography, as discussed by Thomas et al. 2014 PNAS. Although replicating the results in both humans and non-human primates strengthens the study, a more compelling validation approach would involve demonstrating the method's ability to accurately trace known tracts from established tracing studies or, even better, employing phantom track data. Many of the control analyses the authors presented, such as track density, do not speak to accuracy.

In addition to or response to Reviewer 1 Comment 1, we would like to add the following:

We agree with the reviewer that tractography methods have known limitations. We would also like to point out that several studies have already performed the studies suggested by the reviewer. Many studies have compared tracts reconstructed from diffusion data using tractography methods to tracer-derived connections (eg. Thomas et al., 2014, as mentioned by the reviewer; Donahue et al., 2016, J Neurosci; Dauguet et al., 2007 NeuroImage; Gao et al., 2013 PloS One; van den Heuvel et al., 2015, Hum Brain Map; Azadbakht et al., 2015 Cereb Cortex; Ambrosen et al., 2020 NeuroIamge). Notably, studies comparing tractography and tracer-derived white matter tracts in the same animal (e.g. Grisot et al., 2021; Gao et al., 2013 PloS One) have demonstrated that tractography errors may be inflated in studies comparing tractography and tracer-derived connections in different animals.

Additionally, others have employed phantoms to assess the validity of tractography methods (e.g. Drobnjak et al., 2021). For the purposes of this manuscript, phantom data would not be an adequate control because phantom data would likely not capture the biological complexities of tracking subcortical white matter tracts and identifying projections within subcortical grey matter.

While a comparison of our tractography-derived ED measure to ED calculated on terminations from tracer studies within the thalamus from several somatomotor and associative regions in macaques would provide additional confidence for our results, such a control is certainly outside the scope of this study. Additionally, such a study would not provide a ground truth comparison for the human data. Even if this hypothetical experiment was performed, a negative finding would not refute our results, as any differences could be attributed to evolutionary differences. Unfortunately, there exists no ground truth to compare human white matter connectivity patterns to, which is why we stress-tested our results in as many ways as possible. These stress tests revealed that our main findings are very robust.

Specifically, as the key validity question of our study was whether there was a confound that systematically biased the ED measure as to make the hierarchy effect artifactual, the control analyses we performed to determine if track density, cortical geometry, bundle integrity, etc in fact do speak the robustness of the results. Regarding the track density analyses we argue that these control analyses do speaks to accuracy. The reviewer mentioned above that some cortical areas may be biased because their anatomical tracts may be more difficult to reconstruct using tractography. The mean streamline count is meant to reflect the density of a fiber bundle, but corticothalamic tracts that are more difficult to track will, by nature, have fewer streamline counts. So, the mean streamline not only reflects the density of a fiber bundle but also how easily that tract is to reconstruct. Therefore, if it was the case that cortical areas with more difficult to reconstruct white matter tracts to the thalamus are also more diffuse, then we should observe a strong positive correlation between the ED measure and the mean streamline count, which we tested directly and found only a weak correlation (Fig. S11). This is true for tracking to the entire thalamus, and the additional supplemental Figure S31 shows that reduced tracking to specific parts of the thalamus (e.g. the medial portion) also does not strongly relate to the ED measure. So, tracts that are more difficult to reconstruct may also be more diffuse, but this seems to add only a little noise and does not account for the strong relationship between the ED measure and T1w/T2w and RSFCpc1 measures the reflect the cortical hierarchy.

Comment 3: If tracking the medial thalamus is indeed less accurate, characterized by higher false positives and false negatives, it could potentially lead to increased variability among individual subjects. In cases where results are averaged across subjects, as the authors have apparently done, this could inadvertently contribute to the emergence of the "diffuse" motif, as described in the context of the associative cortex. This presents a critical issue that requires a more thorough control analysis and validation process to ensure that the main results are not artifacts resulting from limitations in tractography.

Additionally, conducting a control analysis to demonstrate that individual variability in tracking endpoints within the thalamus, when averaged across subjects, does not artificially generate a more diffuse connectivity pattern, is essential.

We thank the reviewer for bringing up this point, and the reviewer is correct that a simple group average of streamline counts across that thalamus could make some thalamic patterns appear more diffuse if those patterns vary slightly in location across people. The simplest way to address this concern is to show that diffuse patterns are present in individual subjects. Fig. 2 panels B, C, H, and I are all subject-level figures, which show that we can replicate the group level findings in Fig. 2 panels F, G. Specifically, Fig 2. Panels H and I show that the effect of association areas exhibiting more diffuse connectivity patterns within the thalamus relative to sensorimotor areas is generalizable across subjects.

To the reviewer’s point, the other way that averaged streamline counts could make focal connections seem diffuse is by averaging within cortical areas (e.g. to test the possibility that association areas may have highly variability focal patterns, and when averaged within the cortical area it makes these focal patterns appear more diffuse). To test this, we show that we can replicate the hierarchy effect at the vertex level, by calculating the extent of connectivity patterns for every cortical vertex and correlated vertex-level EDpc1 values to vertex-level T1w/T2w and RSFC_pc1 values (Fig S20).

Hopefully the data shown in Fig. 2 (replication at the individual level) and Fig. S20 (replication at the vertex level) ameliorate the reviewer’s concerns that averaging highly variable focal connectivity patterns within the thalamus (either across people or across vertices) does not artifactually produce diffuse thalamic connectivity patterns for associative cortical areas.

Comment 4: Because the authors included data from all thresholds, it seems likely that false positive tracks were included in the results. The methodology described seems to unavoidably include anatomically implausible pathways in the spatial extent analyses.

The thresholding approach taken in the manuscript aimed to control for inter-areal differences in anatomical connection strength that could confound the ED estimates. Here I am not quite clear why inter-areal differences in anatomical connection strength have to be controlled. A global threshold applied on all thalamic voxels might kill some connections that are weak but do exist. Those weak pathways are less likely to survive at high thresholds. In the meantime, the mean ED is weighted, with more conservative thresholds having higher weights. That being said, isn't it possible that more robust pathways might contribute more to the mean ED than weaker pathways?

This is a good point from the reviewer, and we appreciate them bringing up these points about our thresholding rationale. We would like to clarify two points: why it was appropriate for our question to threshold thalamic voxels for each cortical area separately and why we iteratively thresholded thalamic voxels.

Regarding thalamic connectivity differences between cortical areas: a global threshold would indeed exclude weak, but potentially true, connections. This was part of our rationale for thresholding thalamic voxels for each cortical area separately. Too conservative of a global threshold would exclude all thalamic voxels for some cortical areas and too liberal of a threshold would include many potentially false positive connections for other cortical areas. Our method of thresholding each cortical area’s thalamic voxels separately ensured that we were sampling thalamic voxels in an equitable manner across cortical areas. We updated the text to clarify this:

Methods section, pg. 11, section Framework to quantify the extent of thalamic connectivity patterns via Euclidean distance (ED)

“We used Euclidean distance (ED) to quantify the extent of each cortical area's thalamic connectivity patters. Probabilistic tractography data require thresholding before the ED calculation. To avoid the selection of an arbitrary threshold (Sotiropoulos et al., 2019, Zhang et al., 2022), we calculated ED for a range of thresholds (Figure 1a). Our thresholding framework uses a tractography-derived connectivity matrix as input. We iteratively excluded voxels with lower streamline counts for each cortical parcel such that the same number of voxels was included at each threshold. At each threshold, ED was calculated between the top x\% of thalamic voxels with the highest streamline counts. This produced a matrix of ED values (360 cortical parcels by 100 thresholds). This matrix was used as input into a PCA to derive a single loading for each cortical parcel. While alternative thresholding approaches have been proposed, this framework optimizes the examination of spatial patterns by proportionally thresholding the data, enabling equitable sampling of each cortical parcel's streamline counts within the thalamus.

This approach controlled for inter-areal differences in anatomical connection strength that could confound the ED estimates. In contrast, a global threshold, which is applied to all cortical areas, may exclude all thalamic streamline counts for some cortical areas that are more difficult to reconstruct, thus making it impossible to calculate ED for that cortical area, as there are no surviving thalamic voxels from which to calculate ED. This would be especially problematic for white matter tracts are more difficult to reconstruct (e.g. the auditory radiation), and cortical areas connected to the thalamus by those white matter tracts would have a disproportionate number of thalamic voxels excluded when using a global threshold.”

Regarding thalamic connectivity differences across the thalamus for a given cortical area, the thresholding method we use does include anatomically implausible connections in the ED calculation because we sample voxels iteratively, and as more and more thalamic voxels are included in the ED analysis the likelihood that they reflect spurious connections increases. This approach made the most sense to us, because there is no way to identify a threshold that only includes true positive connections. And since this method does not exist, we sampled all thresholds and leveraged the behavior of the ED metric across thresholds to quantify the spread of a connectivity pattern. As the reviewer points out, since the measure is effectively “weighted,” more “robust” or anatomically plausible pathways should contribute more to the EDpc1 rather than weaker pathways. This is exactly the balanced approach we aimed for: a measure that is driven by connections that have the highest likelihood of being a true positive but does not rely on an arbitrary threshold.

We did also replicate our main findings after thresholding and binarizing the data for separate thresholds, which show that our main effect was strongest only when thalamic voxels with the highest streamline counts (which are assumed to have a lower chance of being false positives) are included in the ED calculation (Fig. S5). This more traditional method of thresholding also supported our results, and increases our overall confidence that associative cortical areas have more diffuse connectivity patterns within the thalamus relative to somatomotor areas.

Comment 5: In the introduction, there is a bit of ambiguity that needs clarification. The overall goal of the study appears to be the examination of anatomical connectivity from the cortex to the thalamus, specifically whether a cortical region projects to a single thalamic subregion or multiple thalamic subregions. However, certain parts of the introduction also suggest an exploration of the concept of thalamic integration, which typically means a single thalamic region integrating input from multiple cortical regions (converging input). These two patterns, many cortical regions to one thalamic region versus one cortical region to many different thalamic regions, represent distinct and fundamentally different concepts that should be clarified in the manuscript.

We thank the reviewer for pointing out this ambiguity and have edited the introduction to clarify this point:

Our argument for a potential mechanism for integration is the following: because corticothalamic connectivity is topographically organized, if a cortical area has a more diffuse anatomical projection across the thalamus that means its connections overlap with more cortical areas. To the reviewer’s point, our argument is simply that one cortical area targeting multiple thalamic nuclei inherently suggests that such a cortical area has overlapping connectivity patterns with many other cortical areas in the same thalamic subregion. We have updated the introduction to clarify this further.

Intro, pg 1.

“Studies of cortical-thalamic connectivity date back to the early 19th century, yet we still lack a comprehensive understanding of how these connections are organized (see 13 and 14 for review). The traditional view of the thalamus is based on its histologically-defined nuclear structure (6). This view was originally supported by evidence that cortical areas project to individual thalamic nuclei, suggesting that the thalamus primarily relays information (15). However, several studies have demonstrated that cortical connectivity within the thalamus is topographically organized and follows a smooth gradient across the thalamus (16–21). Additionally, some cortical areas exhibit extensive connections within the thalamus, which target multiple thalamic nuclei (22? ). These extensive connections may enable information integration within the thalamus through overlapping termination patterns from different cortical areas, a key mechanism for higher-order associative thalamic computations (23– 25). However, our knowledge of how thalamic connectivity patterns vary across cortical areas, especially in humans, remains incomplete. Characterizing cortical variation in thalamic connectivity patterns may offer insights into the functional roles of distinct cortico-thalamic loops (6, 7).”

Discussion, pg 9. Section: The spatial properties of thalamic connectivity pat- terns provide insight into the role of the thalamus in shaping brain-wide information flow.

“In this study, we demonstrate that association cortical areas exhibit diffuse anatomical connections within the thalamus. This may enable these cortical areas to integrate information from distributed areas across the cortex, a critical mechanism supporting higher-order neural computations. Specifically, because thalamocortical connectivity is organized topographically, a cortical area that projects to a larger set of thalamic subregions has the potential to communicate with many other cortical areas. We observed that anterior cingulate cortical areas had some of the most diffuse thalamic connections. This observation aligns with findings from Phillips et al. that area 24 exhibited the most diffuse anatomical terminations across the mediodorsal nucleus of the thalamus relative to other prefrontal cortical area…”

Reviewer 3:

Comment 1: Potential weaknesses of the study are that it seems to largely integrate aspects of the thalamus that have been already described before. The differentiation between sensory and association systems across thalamic subregions is something that has been described before (see: Oldham and Ball, 2023; Zheng et al., 2023; Yang et al., 2020 Mueller, 2020; Behrens, 2003).

It is true that previous studies have shown that corticothalamic systems vary between sensory and associative cortical areas. Furthermore, there is much evidence that indicates that the sensory-association hierarchy is a major principle of brain organization in general. However, how and why these circuits are different is still not fully known, both across the whole brain and in corticothalamic circuits specifically.

Our study is the first to compare patterns of anatomical connectivity within the thalamus and determine if cortical areas vary in the extent of those patterns. So our main finding isn't that sensory and association cortical areas show differences in thalamic connectivity, it is that they specifically show differences in their pattern of connectivity within the thalamus. This provides a unique insight into how sensory and associative systems differ in their thalamic connectivity in primates.

Additionally, we show evidence that provides some insight into why these differences may exist. Although we cannot provide causal evidence, our data suggest that differences in patterns of anatomical connectivity within the thalamus were related to how different cortical areas process information via the thalamus, which aligns with speculations from Phillips et al 2021.

So our main finding isn't that sensory and association cortical areas show differences in thalamic connectivity, is it that they specifically show differences in their pattern of connectivity within the thalamus and these differences may help us understand how these cortical areas process information and, in turn, how they may support different types of computations, both of which are major goals in neuroscience. To better clarify this in the manuscript, we made the following changes:

Discussion, Paragraph 1, pg 8:

“This study contributes to the rich body of literature investigating the organization of cortico-thalamic systems in human and non-human primates. Prior research has shown that features of thalamocortical connectivity differ between sensory and association systems, and our work advances this understanding by demonstrating that these systems also differ in the pattern and spatial extent of their anatomical connections within the thalamus. Using dMRI-derived tractography across species, we show that these connectivity patterns vary systematically along the cortical hierarchy in both humans and macaques. These findings are critical for establishing the anatomical architecture of how information flows within distinct cortico-thalamic systems. Specifically, we identify reproducible tractography motifs that correspond to sensorimotor and association circuits, which were consistent across individuals and generalize across species. Collectively, this study offers convergent evidence that the spatial pattern of anatomical connections within the thalamus differs between sensory and association cortical areas, which may support distinct computations across cortico-thalamic systems.”

Comment 2: (1) Why not formally test the association between humans and macaques by bringing the brains to the same space?

We thank the reviewer for this query. We were primarily interested in using the macaque data as a validation of the human data, because it was acquired at a much higher resolution, there are no motion confounds, and it provides a bridge with the tract tracing literature in macaques. We are currently studying interspecies differences in patterns of thalamic connectivity, as well as extensions of our approach into structure-function coupling, and we believe these topics warrant their own paper.

Comment 3: (2) Possibly flesh out the differences between this study and other studies with related approaches a bit further.

We updated the discussion section to better clarify the differences in this study from previous research. See response to Reviewer 3 Comment 1 for text changes.

Comment 4: (3) The current title entails 'cortical hierarchy' but would 'differentiation between sensory and association regions' not be more correct? Or at least a reflection on how cortical hierarchy can be perceived?

We treat these phrases as synonymous terms. Our definition of cortical hierarchy is a smooth transition in features between sensory and motor areas to higher-order associative areas. The use of cortical hierarchy is meant to reflect that our measure continuously varies across the cortex. We updated the manuscript to make this clearer:

Abstract, pg 1.

“Additionally, we leveraged resting-state functional MRI, cortical myelin, and human neural gene expression data to test if the extent of anatomical connections within the thalamus varied along the cortical hierarchy, from sensory and motor to multimodal associative cortical areas.”

Comment 5: (4) For the core-matrix map, there is a marked left-right differences and also there are only two donors in the right hemisphere, possibly note this as a limitation?

We thank the reviewer for this observation. We updated Fig. S28 Panel D to show that the correspondence between EDpc1 and the Core-Matrix (CPc) cortical maps holds when the correlation was done for left and right cortex, separately.

Author response:

We would like to thank the reviewers. They have raised some points that we will address in a revised manuscript.

Reviewer #2 (Public review):

The work has significant implications for understanding immune evasion and nutrient uptake mechanisms in trypanosomes.

While the experimental rigor is commendable, revisions are needed to clarify methodological limitations and to broaden the discussion of functional consequences.

The authors argue that prior studies missed surface-localized TfR due to harsh washing/fixation (e.g., methanol). While this is plausible, additional evidence would strengthen the claim.

It remains unclear how centrifugation steps of various lengths (as in previous publications) can equally and quantitatively redistribute TfR into the flagellar pocket. If this were the case, it should be straightforward for the authors to test this experimentally.

If TfR is distributed over the cell surface, live-cell imaging with fluorescent transferrin should be performed as a control. Modern detection limits now reach the single-molecule level, and transient immobilization of live trypanosomes has been established, which would exclude hydrodynamic surface clearance as a confounding factor.

In most images, TfR is not evenly distributed on the surface but rather appears punctate. Could this reflect localization to membrane domains? Immuno-EM with high-pressure frozen parasites could resolve this question and is relatively straightforward.

The authors might consider discussing whether differences in parasite life cycle stages (procyclic versus bloodstream forms) or culture conditions (e.g., cell density) affect localization. The developmentally regulated retention of GPI-anchored procyclin in the flagellar pocket might be worth mentioning.

eLife Assessment

This valuable manuscript investigates the localisation of nutrient receptors in bloodstream stage trypanosomes, with implications for both nutrient uptake and immune evasion. Results after direct fixation of the cells in culture medium provide convincing evidence that the amounts of receptors on the surface of the cell, as opposed to the flagellar pocket, have previously been severely underestimated. Some results were essentially confirmatory, and there are questions regarding the quantitation of ligand binding by transferring receptors.

Reviewer #1 (Public review):

Summary:

An interesting manuscript from the Carrington lab is presented investigating the behavior of single vs double GPI-anchored nutrient receptors in bloodstream form (BSF) T. brucei. These include the transferrin receptor (TfR), the HpHb receptor (HpHbR), and the factor H receptor (FHR). The central question is why these critical proteins are not targeted by host-acquired immunity. It has generally been thought that they are sequestered in the flagellar pocket (FP), where they are subject to rapid endocytosis - any Ab:receptor complexes would be rapidly removed from the cell surface. This manuscript challenges that assumption by showing that these receptors can be found all over the outer cell body and flagella surfaces, if one looks in an appropriate manner (rapid direct fixation in culture media).

The main part of the manuscript focuses on TfR, typically a GPI1 heterodimer of very similar E6 (GPI anchored) and E7 (truncated, no GPI) subunits. These are expressed coordinately from 15 telomeric expression sites (BES), of which only one can be transcribed at a time. The authors identify a native E6:E7 pair in BES7 in which E7 is not truncated and therefore forms a GPI2 heterodimer. By in situ genetic manipulation, they generate two different sets of GPI1:GPI2 TfR combinations expressed from two different BESs (BES1 and BES7). Comparative analyses of these receptors form the bulk of the data.

The main findings are:

(1) Both GPI1 and GPI2 TfR can be found on the cell body/flagellar surface. (2) Both are functional for Tf binding and uptake. (3) GPI2 TfR is expressed at ~1.5x relative to GPI1 TfR. (4) Ultimate TfR expression level (protein) is dependent on the BES from which it is expressed.

Most of these results are quite reasonably explained in light of the hydrodynamic flow model of the Engstler lab and the GPI valence model of the Bangs lab. Additional experiments, again by rapid fixation, with HpHbR and FHR, show that these GPI1 receptors can also be seen on the cell surface, in contrast to published localizations.

It is quite interesting that the authors have identified a native GPI2 TfR. However, essentially all of the data with GPI2 TfR are confirmatory for the prior, more detailed studies of Tiengwe et al. (2017). That said, the suggestion that GPI2 was the ancestral state makes good evolutionary sense, and begs the question of why trypanosomes prefer GPI1 TfR in 14 of 15 ESs (i.e., what is the selection pressure?).

Strengths and weaknesses:

(1) BES7 TfR subunit genes (BES7_Tb427v10): There are actually three (in order 5'-3'): E7gpi, E6.1 and E6.2. E6.1 and E6.2 have a single nucleotide difference. This raises the issue of coordinate expression. If overall levels of E6 (2 genes) are not down-regulated to match E7 (1 gene), this will result in a 2x excess of E6 subunits. The most likely fate of these is the formation of non-functional GPI2 homodimers on the cell surface, as shown in Tiengwe et al. (2017), which will contribute to the elevated TfR expression seen in BES7.

(2) Surface binding studies: This is the most puzzling aspect of the entire manuscript. That surface GPI2 TfR should be functional for Tf binding and uptake is not surprising, as this has already been shown by Tiengwe et al. (2017), but the methodology for this assay raises important questions. First, labeled Tf is added at 500 nM to live cells in complete media containing 2.5 uM unlabeled Tf - a 5x excess. It is difficult to see how significant binding of labeled TfR could occur in as little as 15 seconds under these conditions. Second, Tiengwe et al. (2017) found that trypanosomes taken directly from culture could not bind labeled Tf in direct surface labeling experiments. To achieve binding, it was necessary to first culture cells in serum-free media for a sufficient time to allow new unligated TfR to be synthesized and transported to the surface. This result suggests that essentially all surface TfR is normally ligated and unavailable to the added probe. Third, the authors have themselves argued previously, based on binding affinities, that all surface-exposed TfR is likely ligated in a natural setting (DOI: 10.1002/bies.202400053). Could the observed binding actually be non-specific due to the high levels of fixative used?

(3) Variable TfR expression in different BESs: It appears that native TfR is expressed at higher levels from BES7 compared to BES1, and even more so when compared to BES3. This raises the possibility that the anti-TfR used in these experiments has differential reactivity with the three sets of TfRs. The authors discount this possibility due to the overall high sequence similarities of E6s and E7s from the various ESs. However, their own analyses show that the BES1, BES3, and BES7 TfRs are relatively distal to each other in the phylogenetic trees, and this Reviewer strongly suspects that the apparent difference in expression is due to differential reactivity with the anti-TfR used in this work. In the grand scheme, this is a minor issue that does not impact the other major conclusions concerning TfR localization and function, nor the behavior of HpHbR and FHR. However, the authors make very strong conclusions about the role of BESs in TfR expression levels, even claiming that it is the 'dominant determinant' (line 189).

(4) Surface immuno-localization of receptors: These experiments are compelling and useful to the field. To explain the difference with essentially all prior studies, the authors suggest that typical fixation procedures allow for clearance of receptor:ligand complexes by hydrodynamic flow due to extended manipulation prior to fixation (washing steps). Despite the fact that these protocols typically involve ice-cold physiological buffers that minimize membrane mobility, this is a reasonable possibility. Have the authors challenged their hypothesis by testing more typical protocols themselves? Other contributing factors that could play a role are the use of deconvolution, which tends to minimize weak signals, and also the fact that investigators tend to discount weak surface signals as background relative to stronger internal signals.

(5) Shedding: A central aspect of the GPI valence model (Schwartz et al., 2005, Tiengwe et al., 2017) is that GPI1 reporters that reach the cell body surface are shed into the media because a single dimyristoylglycerol-containing GPI anchor does not stably associate with biological membranes. As the authors point out, this is a major factor contributing to higher steady-state levels of cell-associated GPI2 TfR relative to GPI1 TfR. Those studies also found that the size/complexity of the attached protein correlated inversely with shedding, suggesting exit from the flagellar pocket as a restricting factor in cell body surface localization. The amount of newly synthesized TfR shed into the media was ~5%, indicating that very little actually exits the FP to the outer surface. In this regard, is it possible to know the overall ratio of cell surface:FP:endosomal localized receptors? Could these data not be 'harvested' from the 3D structural illumination imaging?

eLife Assessment

The manuscript reports fundamental findings supported by convincing data that supports the biological mechanism for optimal nodulation in soybean. The results are of relevance to understanding the signaling pathways (specifically those dependent on RIN4/RPM1-interacting protein 4) underpinning beneficial rhizobia symbiosis, while repressing the immune response.

Reviewer #1 (Public review):

The authors set out to illuminate how legumes promote symbiosis with beneficial nitrogen fixing bacteria while maintaining a general defensive posture towards the plethora of potentially pathogenic microbes in their environment. Intriguingly, a protein involved in plant defence signalling, RIN4, is implicated as a type of 'gatekeeper' for the symbiosis, connecting symbiosis signalling with defence signalling. Although questions remain about how exactly RIN4 enables the symbiosis, the work opens an important door to new discoveries in this area.

Strengths:

The study uses a multidisciplinary, state-of-the-art approach to implicate RIN4 in soybean nodulation and symbiosis development. The results support the authors' conclusions.

Weaknesses:

None after thoughtful revision.

Reviewer #3 (Public review):

Summary:

This manuscript by Toth et al reveals a conserved phosphorylation site within the RIN4 (RPM1-interacting protein 4) R protein that is exclusive to two of the four nodulating clades, Fabales and Rosales. The authors present persuasive genetic and biochemical evidence that phosphorylation at the serine residue 143 of GmRIN4b, located within a 15-aa conserved motif with a core five amino acids 'GRDSP' region, by SymRK, is essential for optimal nodulation in soybean. The experimental design and results are robust, the manuscript's discussion has been satisfactorily updated. Results described here are important to understand how the symbiosis signaling pathway prioritizes associations with beneficial rhizobia, while repressing immunity-related signals.

Strengths:

The manuscript asks an important question in plant-microbe interaction studies with interesting findings.

Overall, the experiments are detailed, thorough and very well-designed. The findings appear to be robust.

The authors provide results that are not overinterpreted and are instead measured and logical.

Weaknesses:

No major weaknesses.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The authors set out to illuminate how legumes promote symbiosis with beneficial nitrogen-fixing bacteria while maintaining a general defensive posture towards the plethora of potentially pathogenic bacteria in their environment. Intriguingly, a protein involved in plant defence signalling, RIN4, is implicated as a type of 'gatekeeper' for symbiosis, connecting symbiosis signalling with defence signalling. Although questions remain about how exactly RIN4 enables symbiosis, the work opens an important door to new discoveries in this area.

Strengths:

The study uses a multidisciplinary, state-of-the-art approach to implicate RIN4 in soybean nodulation and symbiosis development. The results support the authors' conclusions.

Weaknesses:

No serious weaknesses, although the manuscript could be improved slightly from technical and communication standpoints.

Reviewer #2 (Public Review):

Summary:

The study by Toth et al. investigates the role of RIN4, a key immune regulator, in the symbiotic nitrogen fixation process between soybean and rhizobium. The authors found that SymRK can interact with and phosphorylate GmRIN4. This phosphorylation occurs within a 15 amino acid motif that is highly conserved in Nfixation clades. Genetic studies indicate that GmRIN4a/b play a role in root nodule symbiosis. Based on their data, the authors suggest that RIN4 may function as a key regulator connecting symbiotic and immune signaling pathways.

Overall, the conclusions of this paper are well supported by the data, although there are a few areas that need clarification.

Strengths:

This study provides important insights by demonstrating that RIN4, a key immune regulator, is also required for symbiotic nitrogen fixation.

The findings suggest that GmRIN4a/b could mediate appropriate responses during infection, whether it is by friendly or hostile organisms.

Weaknesses:

The study did not explore the immune response in the rin4 mutant. Therefore, it remains unknown how GmRIN4a/b distinguishes between friend and foe.

Reviewer #3 (Public Review):

Summary:

This manuscript by Toth et al reveals a conserved phosphorylation site within the RIN4 (RPM1-interacting protein 4) R protein that is exclusive to two of the four nodulating clades, Fabales and Rosales. The authors present persuasive genetic and biochemical evidence that phosphorylation at the serine residue 143 of GmRIN4b, located within a 15-aa conserved motif with a core five amino acids 'GRDSP' region, by SymRK, is essential for optimal nodulation in soybean. While the experimental design and results are robust, the manuscript's discussion fails to clearly articulate the significance of these findings. Results described here are important to understand how the symbiosis signaling pathway prioritizes associations with beneficial rhizobia, while repressing immunity-related signals.

Strengths:

The manuscript asks an important question in plant-microbe interaction studies with interesting findings.

Overall, the experiments are detailed, thorough, and very well-designed. The findings appear to be robust.

The authors provide results that are not overinterpreted and are instead measured and logical.

Weaknesses:

No major weaknesses. However, a well-thought-out discussion integrating all the findings and interpreting them is lacking; in its current form, the discussion lacks 'boldness'. The primary question of the study - how plants differentiate between pathogens and symbionts - is not discussed in light of the findings. The concluding remark, "Taken together, our results indicate that successful development of the root nodule symbiosis requires cross-talk between NF-triggered symbiotic signaling and plant immune signaling mediated by RIN4," though accurate, fails to capture the novelty or significance of the findings, and left me wondering how this adds to what is already known. A clear conclusion, for eg, the phosphorylation of RIN4 isoforms by SYMRK at S143 modulates immune responses during symbiotic interactions with rhizobia, or similar, is needed.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I have no major criticism of the work, although it could be improved by addressing the following minor points:

(1) Page 8, Figure 2 legend. Consider changing "proper symbiosis formation" to "normal nodulation" or something that better reflects control of nodule development/number.

We thank you for the suggestion, the legend was changed to “...required for normal nodule formation” (see Page 10, revised manuscript)

(2) Page 9. Cut "newly" from the first sentence of paragraph 2, as S143 phosphorylation was identified previously.

Thank you for the suggestion, we removed “newly” from the sentence.

(3) Page 10, Figure 3. Panels B showing green-fluorescent nodules are unnecessary given the quantitative data presented in the accompanying panel A. This goes for similar supplemental figures later.

We appreciate the comment; regarding Figure 3 (complementing rin4b mutant, we updated the figures according to the other reviewer’s comment) and Suppl Figure 6 (OE phenotype of phospho-mimic/negative mutants), we removed the panels showing the micrographs. At the same time, we did not modify Figure 2 (where micrographs showing transgenic roots carrying the silencing constructs) for the sake of figure completeness. (See Page 10, revised manuscript)

(4) Consider swapping Figure 3 for Supplemental Figure S7, which I think shows more clearly the importance of RIN4 phosphorylation in nodulation.

We appreciate the comment and have swapped the figures according to the reviewer’s suggestion. Legend, figure description, and manuscript text have been updated accordingly. (See page 12 and 38, revised manuscript)

(5) Page 10. Replace "it will be referred to S143..." with "we refer to S143 instead of ....".

We replaced it according to the comment.

(6) Page 11, delete "While" from "While no interactions could be observed...".

We deleted it according to the suggestion.

(7) Page 33, Fig S5. How many biological replicates were performed to produce the data presented in panel C and what do the error bar and asterisk indicate? Check that this information is provided in all figures that show errors and statistical significance.

Thank you for the remark. The experiment was repeated three times, and this note was added to the figure description. All the other figure legends with error bar(s) were checked whether replicates are indicated accordingly.

(8) Page 37, Fig S11, panel B. Are averages of data from the 2 biological and 3 technical replicates shown? Add error bars and tests of significant difference.

Averages of a total of 6 replicates (from 2 biological replicates, each run in triplicates) are shown. We thank the reviewer for pointing out the missing error bars and statistical test, we have updated the figure accordingly.

(9) Fig S12. Why are panels A, C, E, and G presented? The other panels seem to show the same data more clearly- showing the linear relationship between peak area ratio and protein concentration.

We have taken the reviewer’s comment into consideration and revised the figure, removing the calibration curves and showing only four panels. The figure legend has been corrected accordingly. (Please see page 43, revised masnuscript). The original figure (unlike other revised figures) had to be deleted from the revised manuscript,as it caused technical issues when converting the document into pdf.

Reviewer #2 (Recommendations For The Authors):

Some small suggestions:

(1) It's good to include a protein schematic for RIN4 in Figure 1.

We appreciate the reviewer’s suggestion and we have drawn a protein schematic and added it to Figure 1. The figure legend was updated accordingly.

(2) There appears to be incorrect labeling in Figure 2c; please double-check and make the necessary corrections.

With respect, we do not understand the comment about incorrect labeling. Would the reviewer please help us out and give more explanation? In Figure 2C, RIN4a and RIN4b expression was checked in transgenic roots expressing either EV (empty vector) or different silencing constructs targeting RIN4a/b.

Reviewer #3 (Recommendations For The Authors):

I enjoyed the level of detail and precision in experimental design.

A discussion point could be - What does it mean that nodule number but not fixation is affected? Is RIN4 only involved in the entry stage of infection but not in nodules during N-fixation?

Current/Our data suggest that RIN4 does indeed appear to be involved in infection. This hypothesis is supported by the findings that RIN4a/b was found phosphorylated in root hairs but not in root (or it was not detected in the root). The interaction with the early signaling RLKs also suggests that RIN4 is likely involved in the early stage of symbiosis formation.

How would the authors explain their observation "However, the motif is retained in non-nodulating Fabales (such as C. canadensis, N. schottii; SI Appendix, Figure S2) and Rosales species as well." What does this imply about the role in symbiosis that the authors propose?

We appreciate the reviewer’s question. The motif seems to be retained, however, it might be not only the motif but also the protein structure that in case of nodulating plants might be different. We have not investigated the structure of RIN4, how it would look based on certain features/upon interaction with another protein and/or post-translational modification(s). Griesman et al, (2018) showed the absence of certain genes within Fabales in non-nodulating species, we can speculate that these absent genes can’t interact with RIN4 in those species, therefore the lack of downstream signaling could be possible (in spite of the retained motif in non-nodulating species). At this point, there is not enough data or knowledge to further speculate.

qPCR analysis of symbiotic pathway genes showed that both NIN-dependent and NIN-independent branches of the symbiosis signaling pathway were negatively affected in the rin4b mutant. Please derive a conclusion from this.

We appreciate the comment, it also prompted us to correct the following sentence; original: “Since NIN is responsible for induction of NF-YA and ERN1 transcription factors, their reduced expression in rin4b plants was not unexpected (Fig. 5). “As ERN1 expression is independent of NIN (Kawaharada et al, 2017). The following sentences were also deleted as it represented a repetition of a statement above these sentences: “Soybean NF-YA1 homolog responded significantly to rhizobial treatment in rin4b plants, whereas NF-YA3 induction did not show significant induction (Fig. 5).“

We added the following conclusion/hypothesis: “Based on the results of the expression data presented above, it seems that both NIN-dependent and NINindependent branches of the symbiotic signaling pathways are affected in the rin4b mutant background. This indicates that the role of RIN4 protein in the symbiotic pathway can be placed upstream of CYCLOPS, as the CYCLOPS transcription activating complex is responsible (directly or indirectly) for the activation of all TFs tested in our expression analysis (Singh et al, 2014/47, 48).” (Please see Page 16, revised manuscript)

The authors are highly encouraged to write a thoughtful discussion that would accompany the detailed experimental work performed in this manuscript.

We appreciate the comment, and we did some work on the discussion part of the document. (Please see Pages 17-19, revised manuscript)

Some minor suggestions for overall readability are below.

What about immune signaling genes? Given that authors hypothesize that "Absence of AtRIN4 leads to increased PTI responses and, therefore, it might be that GmRIN4b absence also causes enhanced PTI which might have contributed to significantly fewer nodules." Could check marker immune signaling gene expression FLS2 and others.

We appreciate the reviewer’s comment, and while we believe those are very interesting questions/suggestions, answering them is out of the scope of the current manuscript. Partially because it has been shown that several defenseresponsive genes that were described in leaf immune responses could not be confirmed to respond in a similar manner in root (Chuberre et al., 2018). It was also shown that plant immune responses are compartmentalized and specialized in roots (Chuberre et al., 2018). If we were looking at immune-responsive genes, the signal might be diluted because of its specialized and compartmentalized nature. Another reason why these questions cannot be answered as a part of the current manuscript is because finding a suitable immune responsive gene would require rigorous experiments (not only in root, but also in root hair (over a timecourse) which would be a ground work for a separate study (root hair isolation is not a trivial experiment, it requires at least 250-300 seedlings per treatment/per time-point).

Regarding FLS2, it is known in Arabidopsis that its expression is tissue-specific within the root, and it seems that FLS2 expression is restricted to the root vasculature (Wyrsch et al, 2015). In our manuscript, we showed that RIN4a/b is highly expressed in root hairs, as well as RIN4 phosphorylation was detectable in root hair but not in the root; therefore, we do not see the reason to investigate FLS2 expression.

"in our hands only ERN1a could be amplified. One possible explanation for this observation is that primers were designed based on Williams 82 reference genome, while our rin4b mutant was generated in the Bert cultivar background." Is the sequence between the two cultivars and the primers that bind to ERN1b in both cultivars so different? If not, this explanation is not very convincing.

At the time of performing the experiment the genomic sequence of the Bert cultivar (used for generating rin4b edited lines) was not publicly available. In accordance with the reviewer’s comment, we removed the explanation, as it does not seem to be relevant. (See page 16, revised manuscript)

The figures are clear and there is a logical flow. The images of fluorescing nodules in Figure 2,3 panels with nodules are not informative or unbiased .

We appreciate the comment, as for Figure 3 (complementing rin4b mutant), we updated the figures according to the other reviewer’s comment and Suppl. Figure 6 (OE phenotype of phospho-mimic/negative mutants) we removed the panels showing the micrographs. At the same time, we did not modify Figure 2 (where micrographs showing transgenic roots carrying the silencing constructs) for the sake of figure completeness. (See pages 10, 12 and 38, revised manuscript)

What does the exercise in isolation of rin4 mutants in lotus tell us? Is it worth including?

Isolation of the Ljrin4 mutant suggests that RIN4 carries such an importance that the mutant version of it is lethal for the plant (as in Arabidospis, where most of the evidence regarding the role of RIN4 has been described), and an additional piece of evidence that RIN4 is similarly crucial across most land plant species.

Sentence ambiguous. "Co-expression of RIN4a and b with SymRKßΔMLD and NFR1α _resulted in YFP fluorescence detected by Confocal Laser Scanning Microscopy (SI Appendix, Figure S8) suggesting that RIN4a and b proteins closely associate with both RLKs." Were all 4 expressed together?

Thank you for the remark. Not all 4 proteins were co-expressed together. We adjusted the sentence as follows: “Co-expression of RIN4a/ and b with SymRKßΔMLD as well as and NFR1α resulted in YFP fluorescence…” I hope it is phrased in a clearer way. (See page 13, revised manuscript)

Minor spelling errors throughout.. Costume-made (custom made?)

Thank you for noticing. According to the Cambridge online dictionary, it is written with a hyphen, therefore, we added a hyphen and corrected the manuscript accordingly.

CRISPR-cas9 or CRISPR/Cas9? Keep it consistent throughout. CRISPR-cas9 is the latest consensus.

We corrected it to “CRISPR-Cas9” throughout the manuscript.

References are missing for several 'obvious statements' but please include them to reach a broader audience. For example the first 5 sentences of the introduction. Also, statements such as 'Root hairs are the primary entry point for rhizobial infection in most legumes.'.

Thank you for the comment. To make it clearer, we also added reference #1, after the third sentence of the introduction, as well as we added an additional review as reference. This additional review was also cited as the source for the sentence “Root hairs are the primary…” (Please see page 2, revised manuscript)

Can you provide a percent value? Silencing of RIN4a and RIN4b resulted in significantly reduced nodule numbers on soybean transgenic roots in comparison to transgenic roots carrying the empty vector control. Also, this wording suggests it was a double K.D. but from the images, it appears they were individually silenced.

We appreciate the reviewer's comment. We observed a 50-70% reduction in the number of nodules. We adjusted the text according to the reviewer's remark. (See page 9, revised manuscript)

eLife Assessment

This paper shows that it is possible to optogenetically activate single retinal ganglion cells in vivo in monkeys. This is an important step towards towards causal tests of the role of specific ganglion cell types in visual perception. The paper presents convincing evidence for the promise of the approach but further work will be needed to full explore its limitations and specificity.

Reviewer #1 (Public review):

Summary

This manuscript reports preliminary evidence of successful optogenetic activation of single retinal ganglion cells (RGCs) through the eye of a living monkey using adaptive optics (AO).

Strengths

The eventual goals of this line of research have an enormous potential impact in that they will probe the perceptual impact of activating single RGCs. While I think more data should be included, the four examples shown look quite convincing.

Weaknesses

While this is undoubtedly a technical achievement and an important step along this group's stated goal to measure the perceptual consequences of single-RGC activations, the presentation lacks the rigor that I would expect from what is really a methods paper. In my view, it is perfectly reasonable to publish the details of a method before it has yielded any new biological insights, but in those publications, there is a higher burden to report the methodological details, full data sets, calibrations, and limitations of the method. There is considerable room for improvement in reporting those aspects. Specifically, more raw data should be shown for activations of neighboring RGCs to pinpoint the actual resolution of the technique, and more than two cells (one from each field of view) should be tested. Some information about the density of labeled RGCs in these animals would also be helpful to provide context for how many well-isolated target cells exist per animal.

Reviewer #2 (Public review):

Murphy et al. expressed ChrimsonR and GCaMP6s in retinal ganglion cells of a living macaque. They recorded calcium responses and stimulated individual cells, optically. Neurons targeted for stimulation were activated strongly whereas neighboring neurons were not.

The ability to record from neuronal populations while simultaneously stimulating a subset in controlled way is a high priority for systems neuroscience, and this has been particularly challenging in primates. This study marks an important milestone in the journey towards this goal.

Reviewer #3 (Public review):

This paper reports a considerable technical achievement: the optogenetic activation of single retinal ganglion cells in vivo in monkeys. As clearly specified in the paper, this is an important step towards causal tests of the role of specific ganglion cell types in visual perception. The paper is brief, and it will be important to follow this work with a more detailed methodological description to guide related work, to explore limitations, and to build confidence in the specificity of the approach.

Author response:

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

Reviewer #1 (Public Review):

Summary

This manuscript reports preliminary evidence of successful optogenetic activation of single retinal ganglion cells (RGCs) through the eye of a living monkey using adaptive optics (AO).

Strengths

The eventual goals of this line of research have enormous potential impact in that they will probe the perceptual impact of activating single RGCs. While I think more data should be included, the four examples shown look quite convincing. Weaknesses

While this is undoubtedly a technical achievement and an important step along this group's stated goal to measure the perceptual consequences of single-RGC activations, the presentation lacks the rigor that I would expect from what is really a methods paper. In my view, it is perfectly reasonable to publish the details of a method before it has yielded any new biological insights, but in those publications, there is a higher burden to report the methodological details, full data sets, calibrations, and limitations of the method. There is considerable room for improvement in reporting those aspects. Specifically, more raw data should be shown for activations of neighboring RGCs to pinpoint the actual resolution of the technique, and more than two cells (one from each field of view) should be tested.

We have expanded sections discussing both the methodology and limitations of this technique via a rewrite of the results and discussion section. The data used in the paper is available online via the link provided in the manuscript. We agree that a more detailed investigation of the strengths and limitations of the approach would have been a laudable goal. However, before returning to more detailed studies, we have shifted our effort to developing the monkey psychophysical performance we need to combine with the single cell stimulation approach described here. In addition, the optogenetic ChrimsonR used in this study is not the best choice for this experiment because of its poor sensitivity. We are currently exploring the use of ChRmine (as described in lines 93-97), which is roughly 2 orders of magnitude more sensitive. We have also been working on methods to improve probe stabilization to reduce tracking errors during eye movements. Once these improvements have been implemented, we will undertake the more detailed studies suggested here. Nonetheless, as a pragmatic matter, we submit that it is valuable to document proof-of-concept with this manuscript.

Some information about the density of labeled RGCs in these animals would also be helpful to provide context for how many well-isolated target cells exist per animal.

We agree. Getting reliable information about labeled cell density would be difficult without detailed histology of the retina, which we are reluctant to do because it would require sacrificing these precious and expensive monkeys from which we continue to get valuable information. We are actively exploring methods to reduce the cell density to make isolation easier including the use of the CAMKII promoter as well as the use of intracranial injections via AAV.retro that would allow calcium indicator expression in the peripheral retina where RGCs form a monolayer. It may be that the rarity of isolated RGCS will not be a fundamental limitation of the approach in the future.

Reviewer #2 (Public Review):

This proof-of-principle study lays important groundwork for future studies. Murphy et al. expressed ChrimsonR and GCaMP6s in retinal ganglion cells of a living macaque. They recorded calcium responses and stimulated individual cells, optically. Neurons targeted for stimulation were activated strongly whereas neighboring neurons were not.

The ability to record from neuronal populations while simultaneously stimulating a subset in a controlled way is a high priority for systems neuroscience, and this has been particularly challenging in primates. This study marks an important milestone in the journey towards this goal.

The ability to detect stimulation of single RGCs was presumably due to the smallness of the light spot and the sparsity of transduction. Can the authors comment on the importance of the latter factor for their results? Is it possible that the stimulation protocol activated neurons nearby the targeted neuron that did not express GCaMP? Is it possible that off-target neurons near the targeted neuron expressed GCaMP, and were activated, but too weakly to produce a detectable GCaMP signal? In general, simply knowing that off-target signals were undetectable is not enough; knowing something about the threshold for the detection of off-target signals under the conditions of this experiment is critical.

We agree with these points. We cannot rule out the possibility that some nearby cells were activated but we could not detect this because they did not express GCaMP. We also do not know whether cells responded but our recording methods were not sufficiently sensitive to detect them. A related limitation is that we do not know of course what the relationship is between the threshold for detection with calcium imaging and what the psychophysical detection threshold would have been an awake behaving monkey. Nonetheless, the data show that we can produce a much larger response in the target cell than in nearby cells whose response we can measure, and we suggest that that is a valuable contribution even if we can’t argue that the isolation is absolute. We’ve acknowledged these important limitations in the revised manuscript in lines 66-77.

Minor comments:

Did the lights used to stimulate and record from the retina excite RGCs via the normal lightsensing pathway? Were any such responses recorded? What was their magnitude?

The recording light does activate the normal light-sensing pathway to some extent, although it does not fall upon the RGC receptive fields directly. There was a 30 second adaptation period at the beginning of each trial to minimize the impact of this on the recording of optogeneticallymediated responses, as described in lines 222-224. The optogenetic probe does not appear to significantly excite the cone pathway, and we do not see the expected off-target excitations that would result from this.

The data presented attest to a lack of crosstalk between targeted and neighboring cells. It is therefore surprising that lines 69-72 are dedicated to methods for "reducing the crosstalk problem". More information should be provided regarding the magnitude of this problem under the current protocol/instrumentation and the techniques that were used to circumvent it to obtain the data presented.

The “crosstalk problem” referred to in this quote refers to crosstalk caused by targeting cells at higher eccentricities that are more densely packed, which are not represented in the data. The data presented is limited to the more isolated central RGCs.

Optical crosstalk could be spatial or spectral. Laying out this distinction plainly could help the reader understand the issues quickly. The Methods indicate that cells were chosen on the basis that they were > 20 µm from their nearest (well-labeled) neighbor to mitigate optical crosstalk, but the following sentence is about spectral overlap.

We have added a clearer explanation of what precisely we mean by crosstalk in lines 213-221.

Figure 2 legend: "...even the nearby cell somas do not show significantly elevated response (p >> 0.05, unpaired t-test) than other cells at more distant locations." This sentence does not indicate how some cells were classified as "nearby" whereas others were classified as being "at more distant locations". Perhaps a linear regression would be more appropriate than an unpaired t-test here.

The distinction here between “nearby” and “more distant” is 50 µm. We have clarified this in the figure caption. Performing a linear regression on cell response over distance shows a slight downward trend in two of the four cells shown here, but this trend does not reach the threshold of significance.

Line 56: "These recordings were... acquired earlier in the session where no stimulus was present." More information should be provided regarding the conditions under which this baseline was obtained. I assume that the ChrimsonR-activating light was off and the 488 nmGCaMP excitation light was on, but this was not stated explicitly. Were any other lights on (e.g. room lights or cone-imaging lights)? If there was no spatial component to the baseline measurement, "where" should be "when".

Your assumptions are correct. There was no spatial component to the baseline measurement, and these measurements are explained in more detail in lines 240-243.

Please add a scalebar to Figure 1a to facilitate comparison with Figure 2.

This has been done.

Lines 165-173: Was the 488 nm light static or 10 Hz-modulated? The text indicates that GCaMP was excited with a 488 nm light and data were acquired using a scanning light ophthalmoscope, but line 198 says that "the 488 nm imaging light provides a static stimulus".

The 488nm is effectively modulated at 25 Hz by the scanning action of the system. I believe the 10 Hz modulated you speak of is the closed-loop correction rate of the adaptive optics. The text has been updated in lines 217-219 to clarify this.

A potential application of this technology is for the study of visually guided behavior in awake macaques. This is an exciting prospect. With that in mind, a useful contribution of this report would be a frank discussion of the hurdles that remain for such application (in addition to eye movements, which are already discussed).

Lines 109-130 now offer an expanded discussion of this topic.

Reviewer #3 (Public Review):

This paper reports a considerable technical achievement: the optogenetic activation of single retinal ganglion cells in vivo in monkeys. As clearly specified in the paper, this is an important step towards causal tests of the role of specific ganglion cell types in visual perception. Yet this methodological advance is not described currently in sufficient detail to replicate or evaluate. The paper could be improved substantially by including additional methodological details. Some specific suggestions follow.

The start of the results needs a paragraph or more to outline how you got to Figure 1. Figure 1 itself lacks scale bars, and it is unclear, for example, that the ganglion cells targeted are in the foveal slope.

The results have been rewritten with additional explanation of methodology and the location of the RGCs has been clarified.

The text mentions the potential difficulties targeting ganglion cells at larger eccentricities where the soma density increases. If this is something that you have tried it would be nice to include some of that data (whether or not selective activation was possible). Related to this point, it would be helpful to include a summary of the ganglion cell density in monkey retina.

This is not something we tried, as we knew that the axial resolution allowed by the monkey’s eye would result in an axial PSF too large to only hit a single cell. The overall ganglion cell density is less relevant than the density of cells expressing ChrimsonR/GCaMP, which we only have limited info about without detailed histology.

Related to the point in the previous paragraph - do you have any experiments in which you systematically moved the stimulation spot away from the target ganglion cell to directly test the dependence of stimulation on distance? This would be a valuable addition to the paper.

We agree that this would have been a valuable addition to the paper, but we are reluctant to do them now. We are implementing an improved method to track the eye and a better optogenetic agent in an entirely new instrument, and we think that future experiments along these lines would be best done when those changes are completed.

The activity in Figure 1 recovers from activation very slowly - much more slowly than the light response of these cells, and much more slowly than the activity elicited in most optogenetic studies. Can you quantify this time course and comment on why it might be so slow?

We attribute the slow recovery to the calcium dynamics of the cell, and this slow recovery time is consistent with calcium responses seen in our lab elicited via the cone pathway. Similar time courses can be seen in Yin (2013) for RGCs excited via their cone inputs.

Traces from non-targeted cells should be shown in Figure 1 along with those of targeted cells.

We have added this as part of Figure 2.

eLife Assessment

The study reports an important finding on the role of the global metabolic regulator Crp/cAMP in the formation of antibiotic persister Escherichia coli. The evidence supporting the claims is solid including metabolomic analysis and characterization of many mutant strains.

Reviewer #1 (Public review):

The authors set out to understand the role played by a key global metabolic regulator called Crp/cAMP in the formation of persister Escherichia coli that survive antibiotic treatment without acquiring genetic mutations.

In order to achieve this aim, the authors employ an interdisciplinary approach integrating standard microbiology assays with cutting-edge genomic, metabolomic and proteomics screening.

The data presented by the authors convincingly demonstrate that the deletion of two key genes that are part of the Crp/cAMP complex (i.e. crp and cyaA) leads to a significant decrease in the number of E. coli.

The authors have carried out additional experiments to further validate this point by using the well characterised hipA7 E. coli mutant.

The data presented also demonstrate that deletion of the crp gene leads to an overall decrease in energy metabolism and an overall increase in anabolic metabolism at the population level. The deletion of cyaA has an opposite effect on cAMP concentration compared to crp deletion, the authors presented a possible hypotheses but did not test it.

The authors have now explicitly acknowledged in their discussion that the data presented in this study are obtained at the whole population level rather than at the level of the persister subpopulation and therefore should be considered with caution.

Finally, the authors convincingly show that the persisters they investigated are non-growing and have a higher redox activity and that the deletion of key genes involved in energy metabolism leads to a decrease in the number of persisters.

These data will be important for future investigations on the biochemical mechanisms that allow bacteria to adapt to stressors such as nutrient depletion or exposure to antibiotics. As such this work will likely have an impact in a variety of fields such as bacterial biochemistry, antimicrobial resistance research and environmental microbiology.

Strengths:

Interdisciplinary approach.

Excellent use of replication and ensuring reproducibility.

Excellent understanding and presentation of the biochemical mechanisms underpinning bacterial physiology via an integrated genomic, metabolomic and proteomic screening.

Weaknesses:

There is no tested mechanisms explaining why the deletion of cyaA has an opposite effect on cAMP concentration compared to crp deletion.

Metabolomics, proteomics and metabolic activity data are obtained at the whole population level rather than at the level of the persister sub-population.

eLife Assessment

This study introduces a valuable spring-bead model for epithelial cell layers, designed to improve previous cell-resolved approaches and to understand the connection between the biophysics of cell-cell contacts and the tissue mechanics. While the model is not entirely new and does not fully settle open questions such as the role of adhesion in tissue fluidity, it provides solid evidence and stands out as simple and efficient. A more comprehensive comparison with previous cell-revolved approaches and, in particular, with experimental data, would further strengthen the proposed model as a conceptual and practical tool.

Reviewer #1 (Public review):

Summary:

The manuscript by Ray et al. provides a theoretical framework to study tissue mechanics and the solid-to-fluid transition phenomenon observed in many tissues. The authors advanced previous models by directly incorporating cell-cell adhesion in force calculation with flexible cell geometries. They performed an in-depth analysis of the model and found that reducing cell-cell adhesion in near-confluent tissues can result in spontaneous cell rearrangements and transition to tissue fluidity. This is in contrast with previous predictions of Vertex models, which require higher adhesion for solid-to-fluid transition.

Strengths:

The authors provided a more general formulation of a 2D active foam model by directly incorporating cell-cell adhesion and performed a careful analysis of cell dynamics and cell shape in their simulations. They measured various quantities such as the mean-squared displacement of the cell center and shape index, which was introduced in previous studies to analyze jamming transition in tissues. By careful analysis of their simulations, they found a universal length scale in their simulations, explaining the observed heterogeneity. They provided a qualitative connection to previous experimental observations, where a reduction in cell adhesion caused tissue fluidity.

Weaknesses:

The phenomenon of tissue fluidity is an important and open question in biology. While theoretical models provide guidance to study such complex phenomena, the details in these models should go hand-in-hand with quantitative comparison with experiments. The study by Ray et al. indeed provided a more detailed description of deformable and adhesive cell collectives, but without a quantitative comparison with experiment, it is not clear if one needs all these details, or maybe more is needed. For example, do we need a more detailed mechanical model of the vertices, how the friction with substrate should be incorporated in such models, and is there a feedback between cell dynamics and its internal cytoskeleton organization?

While the manuscript by Ray et al. is an interesting theoretical study, without a quantitative comparison with experiments, it is not clear if it truly advances our understanding of tissue mechanics.

Reviewer #2 (Public review):

Summary:

Ray and coworkers introduce a discrete model of cellular layers aimed at investigating the role of inter-cellular adhesion in collective cell migration. The model combines aspects of particle-based models, in which cells are treated as simple point-particles with pair-interactions, and "morphological models", where interactions primarily depend on the cellular shape. In this case, cells are modeled as rings of beads connected by springs, thus allowing for exploration of the role of cell morphology while treating intercellular interactions as particle-like. Upon exploring the parameter space of this model, the authors recover physical behaviors reminiscent of reconstituted cell layers, including the onset of collective cell migration, when the forces leading to cell propulsion overweight inter-cellular adhesion, and various signatures of glassy dynamics.

Strengths:

The model presented in the article is simple, easy to implement, and scalable. The analysis appears solid and delivers a number of clear physical properties that could be tested in more depth in experiments and future numerical studies (e.g., distribution of displacements, etc.). The authors make an appreciable effort to make contact with other models and share their ideas for further investigations.

Weaknesses:

I found two main weaknesses in the original version of this manuscript, which I strongly encourage the authors to address.

(1) The manuscript explicitly aims at resolving an apparent contradiction of tessellation-based models, such as the Vertex and the Voronoi model. Both models used the so-called shape index p0 - i.e. the ratio between the preferential perimeter and the preferential area of the cells - to drive a solid/liquid phase transition in the presence of Brownian and/or rotational noise. Specifically, for sufficiently large p0 values, these in silico cell layers undergo a transition to a state of collective migration, where a rigid junction network becomes unstable to T1 events. Because p0 is often interpreted as "adhesion strength", this leads to the paradoxical conclusion that cell intercalation is favored by intercellular adhesion. The paradox, however, only lies in this interpretation, which assigns to the shape index p0 a biophysical role that is too specific. To illustrate this concept, let us consider the energy of an individual cell of area A and perimeter P: i.e. e = (a-1)^2+c*(p-p0)^2, where a=A/A_0, with A_0 the preferred area, p=P/sqrt(A_0) and p_0 = P_0/sqrt(A_0), with P_0 the preferred perimeter. Expanding the square in the second term gives e ~ p^2 - 2p_0 p. Thus, increasing p_0, favors longer cell junctions, from which it appears reasonable to interpret p0 as a dimensionless measure of intercellular adhesion. Such an increase in the length of the junctions is, however, only a byproduct of the effect of p0 on the overall shape of the cell, which becomes progressively less rounded as p0 is increased (e.g., for a circle, p0≈3.55, for an equilateral triangle, p0≈4.56). The roundness of an individual cell, on the other hand, cannot single-handedly be ascribed to intercellular adhesion, despite intercellular adhesion being undoubtedly one of the biophysical properties affecting this geometrical feature. Moreover, the shape index p0 ​enters the energy functional at the single-cell level, implying that even in isolation, without intercellular adhesion, an increase in p0 leads to a less rounded cell morphology. These peculiarities of the Vertex/Voronoi model do raise questions about its accuracy and validity, thus justify seeking for alternative cell-resolved models such as that introduced here by Ray et al., but, on the other hand, make the interpretation of p0 as an exclusive measure of adhesion evidently dubious.

(2) The spring-bead model by Ray and coworkers has at least two predecessors in the recent literature, none of which have been cited in the present manuscript. These are Boromand et al., Phys. Rev. Lett. 121, 248003 (2018) and Pasupalak et al. arXiv:2409.16128 (2024). The former paper investigates the packing of flexible polygons and is not specific to epithelial layers, while the latter is specifically designed to address various outstanding problems in tissue mechanics, including collective migration and wound healing. While none of these models is identical to that by Ray et al., it would be fair to present the latter as a member of the family rather than the first one of its kind and possibly comment about the differences and similarities with these previous models.

Reviewer #3 (Public review):

Summary:

This is a very focused and well-performed study that uses a somewhat less common approach in the field of tissue mechanics, a deformable particle model, to propose a solution to some important phenomenological inconsistencies between the standard vertex- and SPV-model approaches and experiments. The authors' focus in their study is on the role of adhesion in glassy dynamics and solid-fluid transition of epithelia.

Strengths:

It is a carefully performed study with an important technical edge compared to "mainstream" vertex and SPV models: the ability to describe cell-cell boundaries with two distinct membranes. This may have an important implication for the phenomenology, like the role of adhesion in solid-fluid transition.

Weaknesses:

Apart from some specific suggestions for improvement and clarification, I believe the authors could do a better job in comparing their results and their approach to other similar models, such as the one by Kim et al (Reference 7).

eLife Assessment

This important study utilizes the nematode C. elegans and mammalian cell culture to investigate the role of MML-1/Mondo in conserved regulation of metabolism and aging. The evidence supporting the conclusions is convincing and covers a range of areas including localization, upstream pathways, and conservation. The paper will be of interest to a broad range of biologists studying aging, metabolism, and transcriptional regulation.

Reviewer #1 (Public Review):

In this manuscript, Laboy and colleagues investigated upstream regulators of MML-1/Mondo, a key transcription factor that regulates aging and metabolism, using the nematode C. elegans and cultured mammalian cells. By performing a targeted RNAi screen for genes encoding enzymes in glucose metabolism, the authors found that two hexokinases, HXK-1 and HXK-2, regulate nuclear localization of MML-1 in C. elegans. The authors showed that knockdown of hxk-1 and hxk-2 suppressed longevity caused by germline-deficient glp-1 mutations. The authors demonstrated that genetic or pharmacological inhibition of hexokinases decreased nuclear localization of MML-1, via promoting mitochondrial β-oxidation of fatty acids. They found that genetic inhibition of hxk-2 changed the localization of MML-1 from the nucleus to mitochondria and lipid droplets by activating pentose phosphate pathway (PPP). The authors further showed that the inhibition of PPP increased the nuclear localization of mammalian MondoA in cultured human cells under starvation conditions, suggesting the underlying mechanism is evolutionarily conserved. This paper provides compelling evidence for the mechanisms by which novel upstream metabolic pathways regulate MML-1/Mondo, a key transcription factor for longevity and glucose homeostasis, through altering organelle communications, using two different experimental systems, C. elegans and mammalian cells. This paper will be of interest to a broad range of biologists who work on aging, metabolism, and transcriptional regulation.

Reviewer #2 (Public Review):

Raymond Laboy et.al explored how transcriptional Mondo/Max-like complex (MML-1/MXL-2) is regulated by glucose metabolic signals using germ-line removal longevity model. They believed that MML-1/MXL-2 integrated multiple longevity pathways through nutrient sensing and therefore screened the glucose metabolic enzymes that regulated MML-1 nuclear localization. Hexokinase 1 and 2 were identified as the most vigorous regulators, which function through mitochondrial beta-oxidation and the pentose phosphate pathway (PPP), respectively. MML-1 localized to mitochondria associated with lipid droplets (LD), and MML-1 nuclear localization was correlated with LD size and metabolism. Their findings are interesting and may help us to further explore the mechanisms in multiple longevity models. The data support their proposed working model.

Comments on Revised Version (from the Reviewing Editor):

The authors have addressed the remaining concerns from both reviewers, adding textual information for reviewer 1 and testing the roles of hxk-1 and lipid oxidation in regulating lipid droplets for reviewer 2. Specifically, they find that knockdown of acs-2 and hxk-1 acs-2 double knockdown each result in a mild but significant increase in LD size. This result supports that the two hexokinases regulate MML-1 via distinct mechanisms, and is reflected in the updated model.

Author response:

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

Recommendations for the authors:

Reviewer #1:

The authors addressed my previous concerns successfully. However, some critiques are addressed only in the response letter but not in the text (major comment 3, minor point 2). It will be great if they mention these in some parts of their manuscript.

Major 3: We now mention the effect of acs-2i on life span in the discussion, lines 475-480:

“Interestingly, acs-2 knockdown abolished glp-1 longevity (data not shown), consistent with previous work showing that NHR-49, a transcription factor that drives acs-2 expression, is required for glp-1 longevity (Ratnappan et al., 2014). Thus, inhibiting fatty acid β-oxidation promotes MML-1 nuclear localization under hxk-1i but abolishes lifespan extension, potentially due to epistatic effects on other transcription factors or processes.”

Minor 2: We now speculate on the differences concerning hxk-3 knockdown on MML-1 nuclear localization resulting from the low expression of hxk-3 in adults, lines 99-102:

“Among the three C. elegans hexokinase genes, hxk-1 and hxk-2 more strongly affected MML 1 nuclear localization in two independent MML-1::GFP reporter strains (Figure 1B, Supplementary Figure 1A), while hxk-3 had just a small effect on MML-1 nuclear localization, probably due to its low expression in adult worms (Hutter & Suh, 2016).”

Reviewer #2:

The authors have adequately addressed my previous concerns in their revised manuscript. However, I have one remaining minor concern regarding the link between lipid metabolism and MML-1 regulation. As proposed by the authors, HXKs modulate MML-1 localization between LD/mito and the nucleus. They have provided evidence supporting the roles of hxk-2 and the PPP in this regulatory process. Nonetheless, the involvement of hxk-1 and fatty acid oxidation (FAO) within this proposed framework remains unclear. Although FAO is generally believed to affect LD size, the potential effects of hxk-1 and FAO on LD should be investigated within the current study to further substantiate their model.

We thank the reviewer for this comment. We now examine how hxk-1 and acs-2 affect lipid droplet size. Interestingly, we found that knockdown of acs-2 and hxk-1 acs-2 double knockdown resulted in a mild but significant increase in LD size (Supplementary Figure 4I), supporting the notion that the two hexokinases regulate MML-1 via distinct mechanisms, reflected in the updated model (Figure 5E).

eLife Assessment

This Research Advance manuscript further elucidates the roles of SMC5/6 loader proteins and associated factors in the silencing of extrachromosomal circular DNA by the SMC5/6 complex. While the findings are largely in line with expectations, they are useful, representing a meaningful advance beyond the recent study (reference 33), contributing to a growing foundation for further comparative and mechanistic investigations. Solid evidence is presented for a role for SIMC1/SLF2 in the localization of the SMC5/6 complex to plasmid DNA, and the distinct requirements, as compared to the recruitment of SMC5/6 to chromosomal DNA lesions.

Reviewer #1 (Public review):

SMC5/6 is a highly conserved complex able to dynamically alter chromatin structure, playing in this way critical roles in genome stability and integrity that include homologous recombination and telomere maintenance. In the last years, a number of studies have revealed the importance of SMC5/6 in restricting viral expression, which is in part related to its ability to repress transcription from circular DNA. In this context, Oravcova and colleagues recently reported how SMC5/6 is recruited by two mutually exclusive complexes (orthologs of yeast Nse5/6) to SV40 LT-induced PML nuclear bodies (SIMC/SLF2) and DNA lesions (SLF1/2). In this current work, the authors extend this study, providing some new results. However, as a whole, the story lacks unity and does not delve into the molecular mechanisms responsible for the silencing process. One has the feeling that the story is somewhat incomplete, putting together not directly connected results.

(1) In the first part of the work, the authors confirm previous conclusions about the relevance of a conserved domain defined by the interaction of SIMC and SLF2 for their binding to SMC6, and extend the structural analysis to the modelling of the SIMC/SLF2/SMC complex by AlphaFold. Their data support a model where this conserved surface of SIMC/SLF2 interacts with SMC at the backside of SMC6's head domain, confirming the relevance of this interaction site with specific mutations. These results are interesting but confirmatory of a previous and more complete structural analysis in yeast (Li et al. NSMB 2024). In any case, they reveal the conservation of the interaction. My major concern is the lack of connection with the rest of the article. This structure does not help to understand the process of transcriptional silencing reported later beyond its relevance to recruit SMC5/6 to its targets, which was already demonstrated in the previous study.

(2) In the second part of the work, the authors focus on the functionality of the different complexes. The authors demonstrate that SMC5/6's role in transcription silencing is specific to its interaction with SIMC/SLF2, whereas SMC5/6's role in DNA repair depends on SLF1/2. These results are quite expected according to previous results. The authors already demonstrated that SLF1/2, but not SIMC/SLF2, are recruited to DNA lesions. Accordingly, they observe here that SMC5/6 recruitment to DNA lesions requires SLF1/2 but not SIMC/SLF2. Likewise, the authors already demonstrated that SIMC/SLF2, but not SLF1/2, targets SMC5/6 to PML NBs. Taking into account the evidence that connects SMC5/6's viral resistance at PML NBs with transcription repression, the observed requirement of SIMC/SLF2 but not SLF1/2 in plasmid silencing is somehow expected. This does not mean the expectation has not to be experimentally confirmed. However, the study falls short in advancing the mechanistic process, despite some interesting results as the dispensability of the PML NBs or the antagonistic role of the SV40 large T antigen. It had been interesting to explore how LT overcomes SMC5/6-mediated repression: Does LT prevent SIMC/SLF2 from interacting with SMC5/6? Or does it prevent SMC5/6 from binding the plasmid? Is the transcription-dependent plasmid topology altered in cells lacking SIMC/SLF2? And in cells expressing LT? In its current form, the study is confirmatory and preliminary. In agreement with this, the cartoons modelling results here and in the previous work look basically the same.

(3) There are some points about the presented data that need to be clarified.

Reviewer #2 (Public review):

Oracová et al. present data supporting a role for SIMC1/SLF2 in silencing plasmid DNA via the SMC5/6 complex. Their findings are of interest, and they provide further mechanistic detail of how the SMC5/6 complex is recruited to disparate DNA elements. In essence, the present report builds on the author's previous paper in eLife in 2022 (PMID: 36373674, "The Nse5/6-like SIMC1-SLF2 complex localizes SMC5/6 to viral replication centers") by showing the role of SIMC1/SLF2 in localisation of the SMC5/6 complex to plasmid DNA, and the distinct requirements as compared to recruitment to DNA damage foci. Although the findings of the manuscript are of interest, we are not yet convinced that the new data presented here represents a compelling new body of work and would better fit the format of a "research advance" article. In their previous paper, Oracová et al. show that the recruitment of SMC5/6 to SV40 replication centres is dependent on SIMC1, and specifically, that it is dependent on SIMC1 residues adjacent to neighbouring SLF2.

Other comments

(1) The mutations chosen in Figure 1 are quite extensive - 5 amino acids per mutant. In addition, they are in many cases 'opposite' changes, e.g., positive charge to negative charge. Is the effect lost if single mutations to an alanine are made?

(2) In Figure 2c, it isn't clear from the data shown that the 'SLF2-only' mutations in SMC6 result in a substantial reduction in SIMC1/SLF2 binding.

(3) In the GFP reporter assays (e.g. Figure 3), median fluorescence is reported - was there any observed difference in the percentage of cells that are GFP positive?

(4) The potential role of the large T antigen as an SMC5/6 evasion factor is intriguing. However, given the role of the large T antigen as a transcriptional activator, caution is required when interpreting enhanced GFP fluorescence. Antagonism of the SMC5/6 complex in this context might be further supported by ChIP experiments in the presence or absence of large T. Can large T functionally substitute for HBx or HIV-Vpr?

(5) In Figure 5c, the apparent molecular weight of large T and SMC6 appears to change following transfection of GFP-SMC5 - is there a reason for this?

Reviewer #3 (Public review):

Summary:

This study by the Boddy and Otomo laboratories further characterizes the roles of SMC5/6 loader proteins and related factors in SMC5/6-mediated repression of extrachromosomal circular DNA. The work shows that mutations engineered at an AlphaFold-predicted protein-protein interface formed between the loader SLF2/SIMC1 and SMC6 (similar to the interface in the yeast counterparts observed by cryo-EM) prevent co-IP of the respective proteins. The mutations in SLF2 also hinder plasmid DNA silencing when expressed in SLF2-/- cell lines, suggesting that this interface is needed for silencing. SIMC1 is dispensable for recruitment of SMC5/6 to sites of DNA damage, while SLF1 is required, thus separating the functions of the two loader complexes. Preventing SUMOylation (with a chemical inhibitor) increases transcription from plasmids but does not in SLF2-deleted cell lines, indicating the SMC5/6 silences plasmids in a SUMOylation dependent manner. Expression of LT is sufficient for increased expression, and again, not additive or synergistic with SIMC1 or SLF2 deletion, indicating that LT prevents silencing by directly inhibiting 5/6. In contrast, PML bodies appear dispensable for plasmid silencing.

Strengths:

The manuscript defines the requirements for plasmid silencing by SMC5/6 (an interaction of Smc6 with the loader complex SLF2/SIMC1, SUMOylation activity) and shows that SLF1 and PML bodies are dispensable for silencing. Furthermore, the authors show that LT can overcome silencing, likely by directly binding to (but not degrading) SMC5/6.

Weaknesses:

(1) Many of the findings were expected based on recent publications.

(2) While the data are consistent with SIMC1 playing the main function in plasmid silencing, it is possible that SLF1 contributes to silencing, especially in the absence of SIMC1. This would potentially explain the discrepancy with the data reported in ref. 50. SLF2 deletion has a stronger effect on expression than SIMC1 deletion in many but not all experiments reported in this manuscript. A double mutant/deletion experiments would be useful to explore this possibility.

(3) SLF2 is part of both types of loaders, while SLF1 and SIMC1 are specific to their respective loaders. Did the authors observe differences in phenotypes (growth, sensitivities to DNA damage) when comparing the mutant cell lines or their construction? This should be stated in the manuscript.

(4) It would be desirable to have control reporter constructs located on the chromosome for several experiments, including the SUMOylation inhibition (Figures 5A and 5-S2) and LT expression (Figure 5D) to exclude more general effects on gene expression.

(5) Figure 5A: There appears to be an increase in GFP in the SLF2-/- cells with SUMOi? Is this a significant increase?

(6) The expression level of SFL2 mut1 should be tested (Figure 3B).

Author response:

This study builds on, extends, and experimentally validates results/models from our previous study. Our and others’ data implicated SMC5/6, PML nuclear bodies (PML NBs), and SUMOylation in the transcriptional repression of extrachromosomal circular DNA (ecDNA). Moreover, multiple viruses were found to express early genes that combat SMC5/6-based repression through targeted proteasomal degradation (e.g. Hepatitis B virus HBx and HIV-1 Vpr). Thus, our analysis of the roles of the foregoing in plasmid repression yields a coherent set of results for the field to build on.

In our previous study we presented a model, but no supportive ecDNA silencing data, suggesting that distinct SMC5/6 subcomplexes, SIMC1-SLF2 and SLF1/2, separately control its transcriptional repression and DNA repair activities. In this study we experimentally validate that prediction using an ecDNA silencing assay and SMC5/6 localization analysis following DNA damage.

Our study further reveals the unexpected dispensability of PML NBs in the silencing of simple plasmid DNA, a departure from current dogma. This raises important questions for the field to address in terms of the silencing mechanisms for different ecDNAs across different cell types. Despite the dispensability of SUMO-rich PML NBs, SUMOylation is required for ecDNA repression. Lastly, the SV40 LT antigen early gene product counteracts ecDNA silencing. These results used genetic epistasis arguments to implicate SUMO and LT in SMC5/6-based transcriptional silencing. We provide provisional responses for some of the reviewer’s general comments below.

Public Reviews:

Reviewer #1 (Public review):

SMC5/6 is a highly conserved complex able to dynamically alter chromatin structure, playing in this way critical roles in genome stability and integrity that include homologous recombination and telomere maintenance. In the last years, a number of studies have revealed the importance of SMC5/6 in restricting viral expression, which is in part related to its ability to repress transcription from circular DNA. In this context, Oravcova and colleagues recently reported how SMC5/6 is recruited by two mutually exclusive complexes (orthologs of yeast Nse5/6) to SV40 LT-induced PML nuclear bodies (SIMC/SLF2) and DNA lesions (SLF1/2). In this current work, the authors extend this study, providing some new results. However, as a whole, the story lacks unity and does not delve into the molecular mechanisms responsible for the silencing process. One has the feeling that the story is somewhat incomplete, putting together not directly connected results.

Please see the introductory overview above.

(1) In the first part of the work, the authors confirm previous conclusions about the relevance of a conserved domain defined by the interaction of SIMC and SLF2 for their binding to SMC6, and extend the structural analysis to the modelling of the SIMC/SLF2/SMC complex by AlphaFold. Their data support a model where this conserved surface of SIMC/SLF2 interacts with SMC at the backside of SMC6's head domain, confirming the relevance of this interaction site with specific mutations. These results are interesting but confirmatory of a previous and more complete structural analysis in yeast (Li et al. NSMB 2024). In any case, they reveal the conservation of the interaction. My major concern is the lack of connection with the rest of the article. This structure does not help to understand the process of transcriptional silencing reported later beyond its relevance to recruit SMC5/6 to its targets, which was already demonstrated in the previous study.

Demonstrating the existence of a conserved interface between the Nse5/6-like complexes and SMC6 in both yeast and human is foundationally important and was not revealed in our previous study. It remains unclear how this interface regulates SMC5/6 function, but yeast studies suggest a potential role in inhibiting the SMC5/6 ATPase cycle. Nevertheless, the precise function of Nse5/6 and its human orthologs in SMC5/6 regulation remain undefined, largely due to technical limitations in available in vivo analyses. The SIMC1/SLF2/SMC6 complex structure likely extends to the SLF1/2/SMC6 complex, suggesting a unifying function of the Nse5/6-like complexes in SMC5/6 regulation, albeit in the distinct processes of ecDNA silencing and DNA repair. There have been no studies to date (including this one) showing that SIMC1-SLF2 is required for SMC5/6 recruitment to ecDNA. Our previous study showed that SIMC1 was needed for SMC5/6 to colocalize with SV40 LT antigen at PML NBs. Here we show that SIMC1 is required for ecDNA repression, in the absence of PML NBs, which was not anticipated.

(2) In the second part of the work, the authors focus on the functionality of the different complexes. The authors demonstrate that SMC5/6's role in transcription silencing is specific to its interaction with SIMC/SLF2, whereas SMC5/6's role in DNA repair depends on SLF1/2. These results are quite expected according to previous results. The authors already demonstrated that SLF1/2, but not SIMC/SLF2, are recruited to DNA lesions. Accordingly, they observe here that SMC5/6 recruitment to DNA lesions requires SLF1/2 but not SIMC/SLF2.

Our previous study only examined the localization of SLF1 and SIMC1 at DNA lesions. The localization of these subcomplexes alone should not be used to define their roles in SMC5/6 localization. Indeed, the field is split in terms of whether Nse5/6-like complexes are required for ecDNA binding/loading, or regulation of SMC5/6 once bound.

Likewise, the authors already demonstrated that SIMC/SLF2, but not SLF1/2, targets SMC5/6 to PML NBs. Taking into account the evidence that connects SMC5/6's viral resistance at PML NBs with transcription repression, the observed requirement of SIMC/SLF2 but not SLF1/2 in plasmid silencing is somehow expected. This does not mean the expectation has not to be experimentally confirmed. However, the study falls short in advancing the mechanistic process, despite some interesting results as the dispensability of the PML NBs or the antagonistic role of the SV40 large T antigen. It had been interesting to explore how LT overcomes SMC5/6-mediated repression: Does LT prevent SIMC/SLF2 from interacting with SMC5/6? Or does it prevent SMC5/6 from binding the plasmid? Is the transcription-dependent plasmid topology altered in cells lacking SIMC/SLF2? And in cells expressing LT? In its current form, the study is confirmatory and preliminary. In agreement with this, the cartoons modelling results here and in the previous work look basically the same.

We agree, determining the potential mechanism of action of LT in overcoming SMC5/6-based repression is an important next step. It will require the identification of any direct interactions with SMC5/6 subunits, and better methods for assessing SMC5/6 loading and activity on ecDNAs. Unlike HBx, Vpr, and BNRF1 it does not appear to induce degradation of SMC5/6, making it a more complex and interesting challenge. Also, the dispensability of PML NBs in plasmid silencing versus viral silencing raises multiple important questions about SMC5/6’s repression mechanism.

(3) There are some points about the presented data that need to be clarified.

Reviewer #2 (Public review):

Oracová et al. present data supporting a role for SIMC1/SLF2 in silencing plasmid DNA via the SMC5/6 complex. Their findings are of interest, and they provide further mechanistic detail of how the SMC5/6 complex is recruited to disparate DNA elements. In essence, the present report builds on the author's previous paper in eLife in 2022 (PMID: 36373674, "The Nse5/6-like SIMC1-SLF2 complex localizes SMC5/6 to viral replication centers") by showing the role of SIMC1/SLF2 in localisation of the SMC5/6 complex to plasmid DNA, and the distinct requirements as compared to recruitment to DNA damage foci. Although the findings of the manuscript are of interest, we are not yet convinced that the new data presented here represents a compelling new body of work and would better fit the format of a "research advance" article. In their previous paper, Oracová et al. show that the recruitment of SMC5/6 to SV40 replication centres is dependent on SIMC1, and specifically, that it is dependent on SIMC1 residues adjacent to neighbouring SLF2.

We agree, this manuscript fits the Research Advance model, which is the format that this manuscript was submitted in.

Reviewer #3 (Public review):

Summary:

This study by the Boddy and Otomo laboratories further characterizes the roles of SMC5/6 loader proteins and related factors in SMC5/6-mediated repression of extrachromosomal circular DNA. The work shows that mutations engineered at an AlphaFold-predicted protein-protein interface formed between the loader SLF2/SIMC1 and SMC6 (similar to the interface in the yeast counterparts observed by cryo-EM) prevent co-IP of the respective proteins. The mutations in SLF2 also hinder plasmid DNA silencing when expressed in SLF2-/- cell lines, suggesting that this interface is needed for silencing. SIMC1 is dispensable for recruitment of SMC5/6 to sites of DNA damage, while SLF1 is required, thus separating the functions of the two loader complexes. Preventing SUMOylation (with a chemical inhibitor) increases transcription from plasmids but does not in SLF2-deleted cell lines, indicating the SMC5/6 silences plasmids in a SUMOylation dependent manner. Expression of LT is sufficient for increased expression, and again, not additive or synergistic with SIMC1 or SLF2 deletion, indicating that LT prevents silencing by directly inhibiting 5/6. In contrast, PML bodies appear dispensable for plasmid silencing.

Strengths:

The manuscript defines the requirements for plasmid silencing by SMC5/6 (an interaction of Smc6 with the loader complex SLF2/SIMC1, SUMOylation activity) and shows that SLF1 and PML bodies are dispensable for silencing. Furthermore, the authors show that LT can overcome silencing, likely by directly binding to (but not degrading) SMC5/6.

Weaknesses:

(1) Many of the findings were expected based on recent publications.

Please see introductory paragraphs above.

Reviewer #3 (Public review):

This paper, with a slightly modified title from the initial version, presents the cognitive implications of claims made in two accompanying papers (Berger et al. 2023, 2024) about the creation of rock engravings, the intentional disposal of the dead, and fire use by Homo naledi. The importance of the paper, therefore, still relies on the validity of the claims for the presence of socio-culturally complex and cognitively demanding behaviors that are presented in the associated papers. Given the archaeological, hominin, and taphonomic analyses in the associated papers are not adequate to enable the exceptional claims for naledi-associated complex behaviors, the inferences made in this paper are currently incomplete.

The claimed behaviors are widely recognized as complex and even quintessential to Homo sapiens. The implications of their unequivocal association with such a small-brained Middle Pleistocene hominin are thus far reaching. Accordingly, the main thrust of the paper is to highlight that greater cognition and complex socio-cultural behaviors were not necessarily associated with a positively encephalized brain. This argument begs the obvious question of whether absolute brain size and/or encephalization quotient (i.e., the actual brain volume of a given species relative the expected brain size for a species of the same average body size) can measure cognitive capacity and the complexity of socio-cultural behaviors among late Middle Pleistocene hominins.

Claims for a positive correlation between absolute and/or relative brain size and cognitive ability are not common in discussions surrounding the evolution of Middle- and Late Pleistocene hominin behavior. Currently, the bulk of the evidence for early complex technological and social behaviors derives from multiple sites across South Africa and postdates the emergence of H. sapiens by more than 100,000 years. Such lag in the expression of complex technologies and behaviors within our species renders the brain size-implies-cognitive capacity argument moot. Instead, a rich body of research over the past several decades has focused on aspects related to socio-cultural, environmental, and even the wiring of the brain in order to understand factors underlying the expression of the capacity for greater behavioral variability. In this regard, even if the claimed evidence for complex behaviors among the small-brained naledi populations proves valid, the exploration of the specific/potential socio-cultural, neuro-structural, ecological and other factors will be more informative than the emphasis on absolute/relative brain size.

The paper presents as supporting evidence previous claims for the appearance of similar complex behaviors predating the emergence of our species, H. sapiens, although it does acknowledge their controversial nature. It then uses the current claims for the association of such behaviors with H. naledi as decisive. Given the inadequate analyses in the accompanying papers, and the lack of evidence for stone tools in the naledi sites, the present claims for the expression of culturally and symbolically mediated behaviors by this small-brained hominin must be adequately established. The importance of the paper thus rests on the validity of the claimed evidence-including contextual aspects-for rock engraving, mortuary practices, and the use of fire presented in the associated two papers.

eLife Assessment

This study provides an important understanding of the contribution of different striatal subregions, the anterior Dorsal Lateral Striatum (aDLS) and the posterior Ventrolateral Striatum (pVLS), to auditory discrimination learning. The authors have included robust behavior combined with multiple observational and perturbation techniques. The data provided are convincing of the relevance of task-related activity in these two subregions during learning.

Reviewer #1 (Public review):

In this study, Setogawa et al. employ an auditory discrimination task in freely moving rats, coupled with small animal imaging, electrophysiological recordings, and pharmacological inhibition/lesioning experiments to better understand the role of two striatal subregions: the anterior Dorsal Lateral Striatum (aDLS) and the posterior Ventrolateral Striatum (pVLS), during auditory discrimination learning. Attempting to better understand the contribution of different striatal subregions to sensory discrimination learning strikes me as a highly relevant and timely question, and the data presented in this study are certainly of major interest to the field. The authors have set up a robust behavioral task, systematically tackled the question about a striatal role in learning with multiple observational and manipulative techniques. Additionally, the structured approach the authors take by using neuroimaging to inform their pharmacological manipulation experiments and electrophysiological recordings is a strength.

Reviewer #2 (Public review):

The study by Setogawa et al. aims to understand the role that different striatal subregions belonging to parallel brain circuits have in associative learning and discrimination learning (S-O-R and S-R tasks). Strengths of the study are the use of multiple methodologies to measure and manipulate brain activity in rats, from microPET imaging to excitotoxic lesions and multielectrode recordings across anterior dorsolateral (aDLS), posterior ventral lateral (pVLS)and dorsomedial (DMS) striatum.

Author response:

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

Although we have no further revisions on the manuscript, we would like to respond to the remaining comments from the reviewers as follows.

Reviewer 1:

The authors have addressed some concerns raised in the initial review but some remain. In particular it is still unclear what conclusions can be drawn about taskrelated activity from scans that are performed 30 minutes after the behavioral task. I continue to think that a reorganization/analysis data according to event type would be useful and easier to interpret across the two brain areas, but the authors did not choose to do this. Finally, switching the cue-response association, I am convinced, would help to strengthen this study.

As for the task-related activity, the strategy for PET scan was explained in our response to the comment 2 from Reviewer 2. Briefly, rats receive intravenous administration of 18F-FDG solution before the start of the behavioral session. The 18FFDG uptake into the cells starts immediately and reaches the maximum level until 30 min, being kept at least for 1 h. A 30-min PET scan is executed 25 min after the session. Therefore, the brain activity reflects the metabolic state during task performance in rats.

Regarding data presentation of the electrophysiological experiments, we described the subpopulations of event-related neurons showing notable neuronal activity patterns in the order of aDLS and pVLS, according to the procedure of explanations for the behavioral study

For switching the cue-response association, we mentioned the difference in firing activity between HR and LL trials, suggesting that different combinations between the stimulus and response may affect the level of firing activity. As suggested by the reviewer, an examination of switching the cue-response association is useful to confirm our interpretation. We will address this issue in our future studies.

Reviewer 2:

The authors have made important revisions to the manuscript and it has improved in clarity. They also added several figures in the rebuttal letter to answer questions by the reviewers. I would ask that these figures are also made public as part of the authors' response or if not, included in the manuscript.

We will present the figures publicly available as part of our response.

eLife Assessment

This valuable paper used a longitudinal cohort of individuals initiating ART to suggest that CD8+ T cells may contribute to the clearance of intact HIV DNA during long-term antiretroviral therapy (ART) for HIV, which is relevant to our understanding of the mechanisms driving reservoir persistence in people living with HIV. The reviewers concluded that the evidence presented is incomplete to fully support these claims, as the cohort sampling is relatively infrequent, and the association direction could be bi-directional or due to other confounding variables.

Reviewer #1 (Public review):

Summary:

In this work, van Paassen et al. have studied how CD8 T cell functionality and levels predict HIV DNA decline. The article touches on interesting facets of HIV DNA decay, but ultimately comes across as somewhat hastily done and not convincing due to the major issues.

(1) The use of only 2 time points to make many claims about longitudinal dynamics is not convincing. For instance, the fact that raw data do not show decay in intact, but do for defective/total, suggests that the present data is underpowered. The authors speculate that rising intact levels could be due to patients who have reservoirs with many proviruses with survival advantages, but this is not the parsimonious explanation vs the data simply being noisy without sufficient longitudinal follow-up. n=12 is fine, or even reasonably good for HIV reservoir studies, but to mitigate these issues would likely require more time points measured per person.

1b) Relatedly, the timing of the first time point (6 months) could be causing a number of issues because this is in the ballpark for when the HIV DNA decay decelerates, as shown by many papers. This unfortunate study design means some of these participants may already have stabilized HIV DNA levels, so earlier measurements would help to observe early kinetics, but also later measurements would be critical to be confident about stability.

(2) Statistical analysis is frequently not sufficient for the claims being made, such that overinterpretation of the data is problematic in many places.

2a) First, though plausible that cd8s influence reservoir decay, much more rigorous statistical analysis would be needed to assert this directionality; this is an association, which could just as well be inverted (reservoir disappearance drives CD8 T cell disappearance).

2b) Words like "strong" for correlations must be justified by correlation coefficients, and these heat maps indicate many comparisons were made, such that p-values must be corrected appropriately.

(3) There is not enough introduction and references to put this work in the context of a large/mature field. The impacts of CD8s in HIV acute infection and HIV reservoirs are both deep fields with a lot of complexity.

Reviewer #2 (Public review):

Summary:

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow-up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies.

Strengths:

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper.

Weaknesses:

All participants were male (acknowledged by the authors), potentially reducing the generalizability of the findings to broader populations. A control group receiving ART during chronic infection would have been an interesting comparison.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, van Paassen et al. have studied how CD8 T cell functionality and levels predict HIV DNA decline. The article touches on interesting facets of HIV DNA decay, but ultimately comes across as somewhat hastily done and not convincing due to the major issues.

(1) The use of only 2 time points to make many claims about longitudinal dynamics is not convincing. For instance, the fact that raw data do not show decay in intact, but do for defective/total, suggests that the present data is underpowered. The authors speculate that rising intact levels could be due to patients who have reservoirs with many proviruses with survival advantages, but this is not the parsimonious explanation vs the data simply being noisy without sufficient longitudinal follow-up. n=12 is fine, or even reasonably good for HIV reservoir studies, but to mitigate these issues would likely require more time points measured per person.

(1b) Relatedly, the timing of the first time point (6 months) could be causing a number of issues because this is in the ballpark for when the HIV DNA decay decelerates, as shown by many papers. This unfortunate study design means some of these participants may already have stabilized HIV DNA levels, so earlier measurements would help to observe early kinetics, but also later measurements would be critical to be confident about stability.

We agree that in order to thoroughly investigate reservoir decay in acutely treated individuals, more participants and/or more time points measured per participant would increase the power of the study and potentially, in line with literature, show a significant decay in intact HIV DNA as well. By its design (1) the NOVA study allows for a detailed longitudinal follow-up of reservoir and immunity from start ART onwards. In the present analysis in the NOVA cohort, we decided to focus on the 24- and 156-week time points. We plan to include more individuals in our analysis in the future, so that we can better model the longitudinal dynamics of the HIV reservoir.

The main goal of the present study, however, was not to investigate the decay or longitudinal dynamics of the viral reservoir, but to understand the relationship of the HIV-specific CD8 T-cell responses early on ART with the reservoir changes across the subsequent 2.5-year period on suppressive therapy. We will revise the manuscript in order to clarify this. Moreover, we agree with the reviewer that the early time point (24 weeks) is a time at which many virological and immunological processes are ongoing and the reservoir may not have stabilized yet for every participant. We will highlight this in the revised manuscript.

(2) Statistical analysis is frequently not sufficient for the claims being made, such that overinterpretation of the data is problematic in many places.

(2a) First, though plausible that cd8s influence reservoir decay, much more rigorous statistical analysis would be needed to assert this directionality; this is an association, which could just as well be inverted (reservoir disappearance drives CD8 T cell disappearance).

The second point that was raised by reviewer 1 is the statistical analysis, which is referred to as “not sufficient for the claims being made”. Moreover, a more “rigorous statistical analysis would be needed”. At this stage, it is unclear from the reviewer's comments what specific type of additional statistical analysis is being requested. Correlation analyses, such as the one used in this study, are a well-established approach to investigate the relationship between the immune response and reservoir size. However, as we aim to perform the most rigorous analysis possible, for the revised submission we will adjust our analysis for putative confounders (e.g. age and antiretroviral regimen).

We would also like to note that the association between the CD8 T-cell response at 24 weeks and the subsequent decline (the difference between 24 and 156 weeks) in the reservoir cannot be bi-directional (that can only be the case when both variables are measured at the same time point).

(2b) Words like "strong" for correlations must be justified by correlation coefficients, and these heat maps indicate many comparisons were made, such that p-values must be corrected appropriately.

For the revised submission, we will provide correlation coefficients to justify the wording, and will adjust the p-values for multiple comparisons.

(3) There is not enough introduction and references to put this work in the context of a large/mature field. The impacts of CD8s in HIV acute infection and HIV reservoirs are both deep fields with a lot of complexity.

Lastly, reviewer 1 referred to the introduction and asked for more references and a more focused viewpoint because the field is large and complex. We aim to revise the introduction/discussion based on the suggestions from the reviewer.

Reviewer #2 (Public review):

Summary:

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow-up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies.

Strengths:

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper.

Weaknesses:

All participants were male (acknowledged by the authors), potentially reducing the generalizability of the findings to broader populations. A control group receiving ART during chronic infection would have been an interesting comparison.

We thank the reviewer for their appreciation of our study. The reviewer raises the point that it would be useful to compare our data to a control group. Unfortunately, these samples are not yet available, but our study protocol allows for a control group (chronic infection) to ensure we can include a control group in the future.

(1) Dijkstra M, Prins H, Prins JM, Reiss P, Boucher C, Verbon A, et al. Cohort profile: the Netherlands Cohort Study on Acute HIV infection (NOVA), a prospective cohort study of people with acute or early HIV infection who immediately initiate HIV treatment. BMJ Open. 2021;11(11):e048582.

eLife Assessment

This paper examines selection on induced epigenetic variation ("Lamarckian evolution") in response to herbivory in Arabidopsis thaliana. The authors find weak evidence for such adaptation, which contrasts with a recently published study that reported extensive heritable variation induced by the environment. The authors convincingly demonstrate that the findings of the previous study were confounded by mix-ups of genetically distinct material, so that standing genetic variation was mistaken for acquired (epigenetic) variation. Given the controversy surrounding the influence of heritable epigenetic variation on phenotypic variation and adaptation, this study is an important, clarifying contribution; it serves as a timely reminder that sequence-based verification of genetic material should be prioritized when either genetic identity or divergence is of importance to the conclusions.

Reviewer #1 (Public review):

Summary:

The authors extended a previous study of selective response to herbivory in Arabidopsis, in order to look specifically for selection on induced epigenetic variation ("Lamarckian evolution"). They found no evidence. In addition, the re-examined result from a previously published study arguing that environmentally induced epigenetic variation was common, and found that these findings were almost certainly artifactual.

Strengths:

The paper is very clearly written, there is no hype, and the methods used are state-of-the-art.

Weaknesses:

The result is negative, so the best you can do is put an upper bound on any effects.

Significance:

Claims about epigenetic inheritance and Lamarckian evolution continue to be made based on very shaky evidence. Convincing negative results are therefore important. In addition, the study presents results that, to this reviewer, suggest that the 2024 paper by Lin et al. [26] should probably be retracted.

Reviewer #2 (Public review):

In this paper, the authors examine the extent to which epigenetic variation acquired during a selection treatment (as opposed to standing epigenetic variation) can contribute to adaptation in Arabidopsis. They find weak evidence for such adaptation and few differences in DNA methylation between experimental groups, which contrasts with another recent study (reference 26) that reported extensive heritable variation in response to the environment. The authors convincingly demonstrate that the conclusions of the previous study were caused by experimental error, so that standing genetic variation was mistaken for acquired (epigenetic) variation. Given the controversy surrounding the possible role of epigenetic variation in mediating phenotypic variation and adaptation, this is an important, clarifying contribution.

I have a few specific comments about the analysis of DNA methylation:

(1) The authors group their methylation analysis by sequence context (CG, CHG, CHH). I feel this is insufficient, because CG methylation can appear in two distinct forms: gene body methylation (gbM), which is CG-only methylation within genes, and transposable element (TE) and TE-like methylation (teM), which typically involves all sequence contexts and generally affects TEs, but can also be found within genes. GbM and teM have distinct epigenetic dynamics, and it is hard to know how methylation patterns are changing during the experiment if gbM and teM are mixed. This can also have downstream consequences (see point below).

(2) For GO analysis, the authors use all annotated genes as a control. However, most of the methylation differences they observe are likely gbM, and gbM genes are not representative of all genes. The authors' results might therefore be explained purely as a consequence of analyzing gbM genes, and not an enrichment of methylation changes in any particular GO group.

Author response:

We thank you and the reviewers very much for the insightful comments on our manuscript. We plan to revise the manuscript as follows:

(A) As suggested by Reviewer 1, we will carefully read through the entire manuscript and try to improve its clarity. Regarding the comments and recommendations from Reviewer 2, we plan to address the first recommendation and the specific comments about the analysis of DNA methylation. We can currently not address the second recommendation because the person responsible for gathering the data works at a different university now. However, we keep this in mind for future projects.

(B) Regarding the two main comments of Reviewer 2, we plan the following:

(1) The authors group their methylation analysis by sequence context (CG, CHG, CHH). I feel this is insufficient, because CG methylation can appear in two distinct forms: gene body methylation (gbM), which is CG-only methylation within genes, and transposable element (TE) and TE-like methylation (teM), which typically involves all sequence contexts and generally affects TEs, but can also be found within genes. GbM and teM have distinct epigenetic dynamics, and it is hard to know how methylation patterns are changing during the experiment if gbM and teM are mixed. This can also have downstream consequences (see point below).

We thank Reviewer 2 for this suggestion. We usually separate the three contexts because they are set by different enzymes and not because of the entire process or function. It would indeed be informative to group DMCs into gbM and teM but as there are many regions with overlaps between genes and transposons, this also adds some complexity. Given that there were very few DMCs, we wanted to keep it short and simple. Therefore, we wrote that 87.3% of the DMCs were close to or within genes and that 98.1% were close to and within genes or transposons. Together with the clear overrepresentation of the CG context, this indicates that most of the DMCs were related to gbM. We will update the paragraph and specifically refer to gbM to make this clear.

(2) For GO analysis, the authors use all annotated genes as a control. However, most of the methylation differences they observe are likely gbM, and gbM genes are not representative of all genes. The authors' results might therefore be explained purely as a consequence of analyzing gbM genes, and not an enrichment of methylation changes in any particular GO group.

This indeed a point worth considering. We will update the GO analysis and define the background as genes with cytosines that we tested for differences in methylation and which also exhibited overall at least 10% methylation (i.e., one cytosine per gene was sufficient). This will reduce the background gene set from 34'615 to 18'315 genes. A first analysis shows that results will change with respect to the post-translational protein modifications but will remain similar for epigenetic regulation and terms related to transport and growth processes. We will update the paragraph accordingly.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Syed et al. investigate the circuit underpinnings for leg grooming in the fruit fly. They identify two populations of local interneurons in the right front leg neuromere of ventral nerve cord, i.e. 62 13A neurons and 64 13B neurons. Hierarchical clustering analysis identifies 10 morphological classes for both populations. Connectome analysis reveals their circuit interactions: these GABAergic interneurons provide synaptic inhibition either between the two subpopulations, i.e., 13B onto 13A, or among each other, i.e., 13As onto other 13As, and/or onto leg motoneurons, i.e., 13As and 13Bs onto leg motoneurons. Interestingly, 13A interneurons fall into two categories, with one providing inhibition onto a broad group of motoneurons, being called "generalists", while others project to a few motoneurons only, being called "specialists". Optogenetic activation and silencing of both subsets strongly affect leg grooming. As well as activating or silencing subpopulations, i.e., 3 to 6 elements of the 13A and 13B groups, has marked effects on leg grooming, including frequency and joint positions, and even interrupting leg grooming. The authors present a computational model with the four circuit motifs found, i.e., feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. This model can reproduce relevant aspects of the grooming behavior.

Strengths:

The authors succeeded in providing evidence for neural circuits interacting by means of synaptic inhibition to play an important role in the generation of a fast rhythmic insect motor behavior, i.e., grooming. Two populations of local interneurons in the fruit fly VNC comprise four inhibitory circuit motifs of neural action and interaction: feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. Connectome analysis identifies the similarities and differences between individual members of the two interneuron populations. Modulating the activity of small subsets of these interneuron populations markedly affects the generation of the motor behavior, thereby exemplifying their important role in generating grooming.

We thank the reviewer for their thoughtful and constructive evaluation of our work. We are encouraged by their recognition of the major contributions of our study, including the identification of multiple inhibitory circuit motifs and their contribution to organizing rhythmic leg grooming behavior. We also appreciate the reviewer’s comments highlighting our use of connectomics, targeted manipulations, and modeling to reveal how distinct subsets of inhibitory interneurons contribute to motor behavior.

Weaknesses:

Effects of modulating activity in the interneuron populations by means of optogenetics were conducted in the so-called closed-loop condition. This does not allow for differentiation between direct and secondary effects of the experimental modification in neural activity, as feedforward and feedback effects cannot be disentangled. To do so, open loop experiments, e.g., in deafferented conditions, would be important. Given that many members of the two populations of interneurons do not show one, but two or more circuit motifs, it remains to be disentangled which role the individual circuit motif plays in the generation of the motor behavior in intact animals.

We appreciate the reviewer’s point regarding the role of sensory feedback in our experimental design. We agree that reafferent (sensory) input from ongoing movements could contribute to the behavioral outcomes of our optogenetic manipulations. However, our aim was not to isolate central versus peripheral contributions, but rather to assess the role of 13A/B neurons within the intact, operational sensorimotor system during natural grooming behavior.

These inhibitory neurons form recurrent loops, synapse onto motor neurons, and receive proprioceptive input—placing them in a position to both shape central motor output and process sensory feedback. As such, manipulating their activity engages both central control and sensory consequences.

The finding that silencing 13A neurons in dusted flies disrupts rhythmic leg coordination highlights their role in organizing grooming movements. Prior studies (e.g., Ravbar et al., 2021) show that grooming rhythms persist when sensory input is reduced, indicating a central origin, while sensory feedback refines timing, coordination, and long-timescale stability. We concluded that rhythmicity arises centrally but is shaped and stabilized by mechanosensory or proprioceptive feedback. Our current results are consistent with this view and support a model in which inhibitory premotor neurons participate in a closed-loop control architecture that generates and tunes rhythmic output.

While we agree that fully removing sensory feedback and parsing distinct roles for neurons that participate in multiple circuit motifs would be desirable, we do not see a plausible experimental path to accomplish this - we would welcome suggestions!

We considered the method used by Mendes and Mann (eLife 2023) to assess sensory feedback to walking, 5-40-GAL4, DacRE-flp, UAS->stop>TNT + 13A/B-spGAL4 X UAS-csChrimson. This would require converting one targeting system to LexA and presents significant technical challenges. More importantly, we believe the core interpretation issue would remain: broadly silencing proprioceptors would produce pleiotropic effects and impair baseline coordination, making it difficult to distinguish whether observed changes reflect disrupted rhythm generation or secondary consequences of impaired sensory input.

We will clarify in the revised manuscript that our behavioral experiments were performed in freely moving flies under closed-loop conditions. We thank the reviewer for highlighting these important considerations and will revise the manuscript to better communicate the scope and interpretation of our findings.

Reviewer #2 (Public review):

Summary:

This manuscript by Syed et al. presents a detailed investigation of inhibitory interneurons, specifically from the 13A and 13B hemilineages, which contribute to the generation of rhythmic leg movements underlying grooming behavior in Drosophila. After performing a detailed connectomic analysis, which offers novel insights into the organization of premotor inhibitory circuits, the authors build on this anatomical framework by performing optogenetic perturbation experiments to functionally test predictions derived from the connectome. Finally, they integrate these findings into a computational model that links anatomical connectivity with behavior, offering a systems-level view of how inhibitory circuits may contribute to grooming pattern generation.

Strengths:

(1) Performing an extensive and detailed connectomic analysis, which offers novel insights into the organization of premotor inhibitory circuits.

(2) Making sense of the largely uncharacterized 13A/13B nerve cord circuitry by combining connectomics and optogenetics is very impressive and will lay the foundation for future experiments in this field.

(3) Testing the predictions from experiments using a simplified and elegant model.

We thank the reviewer for their thoughtful and encouraging evaluation of our work. We are especially grateful for their recognition of our detailed connectome analysis and its contribution to understanding the organization of premotor inhibitory circuits. We appreciate the reviewer’s comments highlighting the integration of connectomics with optogenetic perturbations to functionally interrogate the 13A and 13B circuits, as well as their recognition of our modeling approach as a valuable framework for linking circuit architecture to behavior.

Weaknesses:

(1) In Figure 4, while the authors report statistically significant shifts in both proximal inter-leg distance and movement frequency across conditions, the distributions largely overlap, and only in Panel K (13B silencing) is there a noticeable deviation from the expected 7-8 Hz grooming frequency. Could the authors clarify whether these changes truly reflect disruption of the grooming rhythm?

We are re-analyzing the whole dataset in the light of the reviews (specifically, we are now applying LMM to these statistics). For the panels in question (H-J), there is indeed a large overlap between the frequency distributions, but the box plots show median and quartiles, which partially overlap. (In the current analysis, as it stands, differences in means were small yet significant.) However, there is a noticeable (not yet quantified) difference in variability between the frequencies (the experimental group being the more variable one). If the activations/deactivations of 13A/B circuits disrupt the rhythm, we would indeed expect the frequencies to become more variable. So, in the revised version we will quantify the differences in both the means and the variabilities, and establish whether either shows significance after applying the LMM.

More importantly, all this data would make the most sense if it were performed in undusted flies (with controls) as is done in the next figure.

In our assay conditions, undusted flies groom infrequently. We used undusted flies for some optogenetic activation experiments, where the neuron activation triggers behavior initiation, but we chose to analyze the effect of silencing inhibitory neurons in dusted flies because dust reliably activates mechanosensory neurons and elicits robust grooming behavior, enabling us to assess how manipulation of 13A/B neurons alters grooming rhythmicity and leg coordination.

(2) In Figure 4-Figure Supplement 1, the inclusion of walking assays in dusted flies is problematic, as these flies are already strongly biased toward grooming behavior and rarely walk. To assess how 13A neuron activation influences walking, such experiments should be conducted in undusted flies under baseline locomotor conditions.

We agree that there are better ways to assay potential contributions of 13A/13B neurons to walking. We intended to focus on how normal activity in these inhibitory neurons affects coordination during grooming, and we included walking because we observed it in our optogenetic experiments and because it also involves rhythmic leg movements. The walking data is reported in a supplementary figure because we think this merits further study with assays designed to quantify walking specifically. We will make these goals clearer in the revised manuscript and we are happy to share our reagents with other research groups more equipped to analyze walking differences.

(3) For broader lines targeting six or more 13A neurons, the authors provide specific predictions about expected behavioral effects-e.g., that activation should bias the limb toward flexion and silencing should bias toward extension based on connectivity to motor neurons. Yet, when using the more restricted line labeling only two 13A neurons (Figure 4 - Figure Supplement 2), no such prediction is made. The authors report disrupted grooming but do not specify whether the disruption is expected to bias the movement toward flexion or extension, nor do they discuss the muscle target. This is a missed opportunity to apply the same level of mechanistic reasoning that was used for broader manipulations.

While we know which two neurons are labeled based on confocal expression, assigning their exact identity in the EM datasets has been challenging. One of these neurons appears absent from our 13A reconstructions of the right T1 neuropil in FANC, although we did locate it in MANC. However, its annotation in MANC has undergone multiple revisions, making confident assignment difficult at this time. Since we can’t be sure which motor neurons and muscles are most directly connected, we did not want to predict this line’s effect on leg movements.

(4) Regarding Figure 5: The 70ms on/off stimulation with a slow opsin seems problematic. CsChrimson off kinetics are slow and unlikely to cause actual activity changes in the desired neurons with the temporal precision the authors are suggesting they get. Regardless, it is amazing that the authors get the behavior! It would still be important for the authors to mention the optogenetics caveat, and potentially supplement the data with stimulation at different frequencies, or using faster opsins like ChrimsonR.

We were also surprised - and intrigued - by the behavioral consequences of activating these inhibitory neurons with CsChrimson. We tried several different activation paradigms: pulsed from 8Hz to 500Hz and with various on/off intervals. Because several of these different stimulation protocols resulted in grooming, and with different rhythmic frequencies, we think the phenotypes are a specific property of the neural circuits we have activated, rather than the kinetics of CsChrimson itself.

We will include the data from other frequencies in a new Supplementary Figure, we will discuss the caveats CsChrimson’s slow off-kinetics present to precise temporal control of neural activity, and we will try ChrimsonR in future experiments.

Overall, I think the strengths outweigh the weaknesses, and I consider this a timely and comprehensive addition to the field.

Thank you!

Reviewer #3 (Public review):

Summary:

The authors set out to determine how GABAergic inhibitory premotor circuits contribute to the rhythmic alternation of leg flexion and extension during Drosophila grooming. To do this, they first mapped the ~120 13A and 13B hemilineage inhibitory neurons in the prothoracic segment of the VNC and clustered them by morphology and synaptic partners. They then tested the contribution of these cells to flexion and extension using optogenetic activation and inhibition and kinematic analyses of limb joints. Finally, they produced a computational model representing an abstract version of the circuit to determine how the connectivity identified in EM might relate to functional output. The study, in its current form, makes an important but overclaimed contribution to the literature due to a mismatch between the claims in the paper and the data presented.

Strengths:

The authors have identified an interesting question and use a strong set of complementary tools to address it:

(1) They analysed serial‐section TEM data to obtain reconstructions of every 13A and 13B neuron in the prothoracic segment. They manually proofread over 60 13A neurons and 64 13B neurons, then used automated synapse detection to build detailed connectivity maps and cluster neurons into functional motifs.

(2) They used optogenetic tools with a range of genetic driver lines in freely behaving flies to test the contribution of subsets of 13A and 13B neurons.

(3) They used a connectome-constrained computational model to determine how the mapped connectivity relates to the rhythmic output of the behavior.

We appreciate the reviewer’s thorough and constructive feedback on our work. We are encouraged by their recognition of the complementary approaches used in our study.

Weaknesses:

The manuscript aims to reveal an instructive, rhythm-generating role for premotor inhibition in coordinating the multi-joint leg synergies underlying grooming. It makes a valuable contribution, but currently, the main claims in the paper are not well-supported by the presented evidence.

Major points

(1) Starting with the title of this manuscript, "Inhibitory circuits generate rhythms for leg movements during Drosophila grooming", the authors raise the expectation that they will show that the 13A and 13B hemilineages produce rhythmic output that underlies grooming. This manuscript does not show that. For instance, to test how they drive the rhythmic leg movements that underlie grooming requires the authors to test whether these neurons produce the rhythmic output underlying behavior in the absence of rhythmic input. Because the optogenetic pulses used for stimulation were rhythmic, the authors cannot make this point, and the modelling uses a "black box" excitatory network, the output of which might be rhythmic (this is not shown). Therefore, the evidence (behavioral entrainment; perturbation effects; computational model) is all indirect, meaning that the paper's claim that "inhibitory circuits generate rhythms" rests on inferred sufficiency. A direct recording (e.g., calcium imaging or patch-clamp) from 13A/13B during grooming - outside the scope of the study - would be needed to show intrinsic rhythmogenesis. The conclusions drawn from the data should therefore be tempered. Moreover, the "black box" needs to be opened. What output does it produce? How exactly is it connected to the 13A-13B circuit?

We will modify the title to better reflect our strongest conclusions: “Inhibitory circuits coordinate rhythmic leg movements during Drosophila grooming”

Our optogenetic activation was delivered in a patterned (70 ms on/off) fashion that entrains rhythmic movements but does not rule out the possibility that the rhythm is imposed externally. In the manuscript, we state that we used pulsed light to mimic a flexion-extension cycle and note that this approach tests whether inhibition is sufficient to drive rhythmic leg movements when temporally patterned. While this does not prove that 13A/13B neurons are intrinsic rhythm generators, it does demonstrate that activating subsets of inhibitory neurons is sufficient to elicit alternating leg movements resembling natural grooming and walking.

Our goal with the model was to demonstrate that it is possible to produce rhythmic outputs with this 13A/B circuit, based on the connectome. The “black box” is a small recurrent neural network (RNN) consisting of 40 neurons in its hidden layer. The inputs are the “dust” levels from the environment (the green pixels in Figure 6I), the “proprioceptive” inputs (“efference copy” from motor neurons), and the amount of dust accumulated on both legs. The outputs (all positive) connect to the 13A neurons, the 13B neurons, and to the motor neurons. We refer to it as the “black box” because we make no claims about the actual excitatory inputs to these circuits. Its function is to provide input, needed to run the network, that reflects the distribution of “dust” in the environment as well as the information about the position of the legs.

The output of the “black box” component of the model might be rhythmic. In fact, in most instances of the model implementation this is indeed the case. However, as mentioned in the current version of the manuscript: “But the 13A circuitry can still produce rhythmic behavior even without those external sensory inputs (or when set to a constant value), although the legs become less coordinated.” Indeed, when we refine the model (with the evolutionary training) without the “black box” (using a constant input of 0.1) the behavior is still rhythmic and sustained. Therefore, the rhythmic activity and behavior can emerge from the premotor circuitry itself without a rhythmic input.

The context in which the 13A and 13B hemilineages sit also needs to be explained. What do we know about the other inputs to the motorneurons studied? What excitatory circuits are there?

We agree that there are many more excitatory and inhibitory, direct and indirect, connections to motor neurons that will also affect leg movements for grooming and walking. Our goal was to demonstrate what is possible from a constrained circuit of inhibitory neurons that we mapped in detail, and we hope to add additional components to better replicate the biological circuit as behavioral and biomechanical data is obtained by us and others. We will add this clarification of the limits of the scope to the Discussion.

Furthermore, the introduction ignores many decades of work in other species on the role of inhibitory cell types in motor systems. There is some mention of this in the discussion, but even previous work in Drosophila larvae is not mentioned, nor crustacean STG, nor any other cell types previously studied. This manuscript makes a valuable contribution, but it is not the first to study inhibition in motor systems, and this should be made clear to the reader.

We thank the reviewer for this important reminder and we will expand our discussion of the relevant history and context in our revision. Previous work on the contribution of inhibitory neurons to invertebrate motor control certainly influenced our research and we should acknowledge this better.

(2) The experimental evidence is not always presented convincingly, at times lacking data, quantification, explanation, appropriate rationales, or sufficient interpretation.

We are committed to improving the clarity, rationale, and completeness of our experimental descriptions. We will revisit the statistical tests applied throughout the manuscript and expand the Methods.

(3) The statistics used are unlike any I remember having seen, essentially one big t-test followed by correction for multiple comparisons. I wonder whether this approach is optimal for these nested, high‐dimensional behavioral data. For instance, the authors do not report any formal test of normality. This might be an issue given the often skewed distributions of kinematic variables that are reported. Moreover, each fly contributes many video segments, and each segment results in multiple measurements. By treating every segment as an independent observation, the non‐independence of measurements within the same animal is ignored. I think a linear mixed‐effects model (LMM) or generalized linear mixed model (GLMM) might be more appropriate.

We thank the reviewer for raising this important point regarding the statistical treatment of our segmented behavioral data. Our initial analysis used independent t-tests with Bonferroni correction across behavioral classes and features, which allowed us to identify broad effects. However, we acknowledge that this approach does not account for the nested structure of the data. To address this, we will re-analyze key comparisons using linear mixed-effects models (LMMs) as suggested by the reviewer. This approach will allow us to more appropriately model within-fly variability and test the robustness of our conclusions. We will update the manuscript based on the outcomes of these analyses.

(4) The manuscript mentions that legs are used for walking as well as grooming. While this is welcome, the authors then do not discuss the implications of this in sufficient detail. For instance, how should we interpret that pulsed stimulation of a subset of 13A neurons produces grooming and walking behaviours? How does neural control of grooming interact with that of walking?

We do not know how the inhibitory neurons we investigated will affect walking or how circuits for control of grooming and walking might compete. We speculate that overlapping pre-motor circuits may participate in walking and grooming because both behaviors have extension flexion cycles at similar frequencies, but we do not have hard experimental data to support. This would be an interesting area for future research. Here, we focused on the consequences of activating specific 13A/B neurons during grooming because they were identified through a behavioral screen for grooming disruptions, and we had developed high-resolution assays and familiarity with the normal movements in this behavior. We will clarify this rationale in the revised discussion.

(5) The manuscript needs to be proofread and edited as there are inconsistencies in labelling in figures, phrasing errors, missing citations of figures in the text, or citations that are not in the correct order, and referencing errors (examples: 81 and 83 are identical; 94 is missing in text).

We will carefully proofread the manuscript to fix all figure labeling, citation order, and referencing errors.

eLife Assessment

Using a combination of connectomics, optogenetics, behavioral analysis, and modeling, this study provides important findings on the role of two populations of inhibitory neurons in the generation of leg grooming movements in Drosophila. The data as presented provide incomplete evidence that the identified neuronal populations contribute to the alternation of flexion and extension by inhibiting specific sets of motor neurons while disinhibiting their counterparts. While the manuscript provides comprehensive details about the 13A/B neuronal populations involved in grooming control, updates on statistics, and explicit mentioning of experimental/modeling caveats would strengthen the study. The work will interest neuroscientists, and particularly those working on motor control.

Reviewer #1 (Public review):

Summary:

Syed et al. investigate the circuit underpinnings for leg grooming in the fruit fly. They identify two populations of local interneurons in the right front leg neuromere of ventral nerve cord, i.e. 62 13A neurons and 64 13B neurons. Hierarchical clustering analysis identifies 10 morphological classes for both populations. Connectome analysis reveals their circuit interactions: these GABAergic interneurons provide synaptic inhibition either between the two subpopulations, i.e., 13B onto 13A, or among each other, i.e., 13As onto other 13As, and/or onto leg motoneurons, i.e., 13As and 13Bs onto leg motoneurons. Interestingly, 13A interneurons fall into two categories, with one providing inhibition onto a broad group of motoneurons, being called "generalists", while others project to a few motoneurons only, being called "specialists". Optogenetic activation and silencing of both subsets strongly affect leg grooming. As well aas ctivating or silencing subpopulations, i.e., 3 to 6 elements of the 13A and 13B groups, has marked effects on leg grooming, including frequency and joint positions, and even interrupting leg grooming. The authors present a computational model with the four circuit motifs found, i.e., feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. This model can reproduce relevant aspects of the grooming behavior.

Strengths:

The authors succeeded in providing evidence for neural circuits interacting by means of synaptic inhibition to play an important role in the generation of a fast rhythmic insect motor behavior, i.e., grooming. Two populations of local interneurons in the fruit fly VNC comprise four inhibitory circuit motifs of neural action and interaction: feed-forward inhibition, disinhibition, reciprocal inhibition, and redundant inhibition. Connectome analysis identifies the similarities and differences between individual members of the two interneuron populations. Modulating the activity of small subsets of these interneuron populations markedly affects the generation of the motor behavior, thereby exemplifying their important role in generating grooming.

Weaknesses:

Effects of modulating activity in the interneuron populations by means of optogenetics were conducted in the so-called closed-loop condition. This does not allow for differentiation between direct and secondary effects of the experimental modification in neural activity, as feedforward and feedback effects cannot be disentangled. To do so, open loop experiments, e.g., in deafferented conditions, would be important. Given that many members of the two populations of interneurons do not show one, but two or more circuit motifs, it remains to be disentangled which role the individual circuit motif plays in the generation of the motor behavior in intact animals.

Reviewer #2 (Public review):

Summary:

This manuscript by Syed et al. presents a detailed investigation of inhibitory interneurons, specifically from the 13A and 13B hemilineages, which contribute to the generation of rhythmic leg movements underlying grooming behavior in Drosophila. After performing a detailed connectomic analysis, which offers novel insights into the organization of premotor inhibitory circuits, the authors build on this anatomical framework by performing optogenetic perturbation experiments to functionally test predictions derived from the connectome. Finally, they integrate these findings into a computational model that links anatomical connectivity with behavior, offering a systems-level view of how inhibitory circuits may contribute to grooming pattern generation.

Strengths:

(1) Performing an extensive and detailed connectomic analysis, which offers novel insights into the organization of premotor inhibitory circuits.

(2) Making sense of the largely uncharacterized 13A/13B nerve cord circuitry by combining connectomics and optogenetics is very impressive and will lay the foundation for future experiments in this field.

(3) Testing the predictions from experiments using a simplified and elegant model.

Weaknesses:

(1) In Figure 4, while the authors report statistically significant shifts in both proximal inter-leg distance and movement frequency across conditions, the distributions largely overlap, and only in Panel K (13B silencing) is there a noticeable deviation from the expected 7-8 Hz grooming frequency. Could the authors clarify whether these changes truly reflect disruption of the grooming rhythm? More importantly, all this data would make the most sense if it were performed in undusted flies (with controls) as is done in the next figure.

(2) In Figure 4-Figure Supplement 1, the inclusion of walking assays in dusted flies is problematic, as these flies are already strongly biased toward grooming behavior and rarely walk. To assess how 13A neuron activation influences walking, such experiments should be conducted in undusted flies under baseline locomotor conditions.

(3) For broader lines targeting six or more 13A neurons, the authors provide specific predictions about expected behavioral effects-e.g., that activation should bias the limb toward flexion and silencing should bias toward extension based on connectivity to motor neurons. Yet, when using the more restricted line labeling only two 13A neurons (Figure 4 - Figure Supplement 2), no such prediction is made. The authors report disrupted grooming but do not specify whether the disruption is expected to bias the movement toward flexion or extension, nor do they discuss the muscle target. This is a missed opportunity to apply the same level of mechanistic reasoning that was used for broader manipulations.

(4) Regarding Figure 5: The 70ms on/off stimulation with a slow opsin seems problematic. CsChrimson off kinetics are slow and unlikely to cause actual activity changes in the desired neurons with the temporal precision the authors are suggesting they get. Regardless, it is amazing that the authors get the behavior! It would still be important for the authors to mention the optogenetics caveat, and potentially supplement the data with stimulation at different frequencies, or using faster opsins like ChrimsonR.

Overall, I think the strengths outweigh the weaknesses, and I consider this a timely and comprehensive addition to the field.

Reviewer #3 (Public review):

Summary:

The authors set out to determine how GABAergic inhibitory premotor circuits contribute to the rhythmic alternation of leg flexion and extension during Drosophila grooming. To do this, they first mapped the ~120 13A and 13B hemilineage inhibitory neurons in the prothoracic segment of the VNC and clustered them by morphology and synaptic partners. They then tested the contribution of these cells to flexion and extension using optogenetic activation and inhibition and kinematic analyses of limb joints. Finally, they produced a computational model representing an abstract version of the circuit to determine how the connectivity identified in EM might relate to functional output. The study, in its current form, makes an important but overclaimed contribution to the literature due to a mismatch between the claims in the paper and the data presented.

Strengths:

The authors have identified an interesting question and use a strong set of complementary tools to address it:

(1) They analysed serial‐section TEM data to obtain reconstructions of every 13A and 13B neuron in the prothoracic segment. They manually proofread over 60 13A neurons and 64 13B neurons, then used automated synapse detection to build detailed connectivity maps and cluster neurons into functional motifs.

(2) They used optogenetic tools with a range of genetic driver lines in freely behaving flies to test the contribution of subsets of 13A and 13B neurons.

(3) They used a connectome-constrained computational model to determine how the mapped connectivity relates to the rhythmic output of the behavior.

Weaknesses:

The manuscript aims to reveal an instructive, rhythm-generating role for premotor inhibition in coordinating the multi-joint leg synergies underlying grooming. It makes a valuable contribution, but currently, the main claims in the paper are not well-supported by the presented evidence.

Major points

(1) Starting with the title of this manuscript, "Inhibitory circuits generate rhythms for leg movements during Drosophila grooming", the authors raise the expectation that they will show that the 13A and 13B hemilineages produce rhythmic output that underlies grooming. This manuscript does not show that. For instance, to test how they drive the rhythmic leg movements that underlie grooming requires the authors to test whether these neurons produce the rhythmic output underlying behavior in the absence of rhythmic input. Because the optogenetic pulses used for stimulation were rhythmic, the authors cannot make this point, and the modelling uses a "black box" excitatory network, the output of which might be rhythmic (this is not shown). Therefore, the evidence (behavioral entrainment; perturbation effects; computational model) is all indirect, meaning that the paper's claim that "inhibitory circuits generate rhythms" rests on inferred sufficiency. A direct recording (e.g., calcium imaging or patch-clamp) from 13A/13B during grooming - outside the scope of the study - would be needed to show intrinsic rhythmogenesis. The conclusions drawn from the data should therefore be tempered. Moreover, the "black box" needs to be opened. What output does it produce? How exactly is it connected to the 13A-13B circuit? The context in which the 13A and 13B hemilineages sit also needs to be explained. What do we know about the other inputs to the motorneurons studied? What excitatory circuits are there? Furthermore, the introduction ignores many decades of work in other species on the role of inhibitory cell types in motor systems. There is some mention of this in the discussion, but even previous work in Drosophila larvae is not mentioned, nor crustacean STG, nor any other cell types previously studied. This manuscript makes a valuable contribution, but it is not the first to study inhibition in motor systems, and this should be made clear to the reader.

(2) The experimental evidence is not always presented convincingly, at times lacking data, quantification, explanation, appropriate rationales, or sufficient interpretation.

(3) The statistics used are unlike any I remember having seen, essentially one big t-test followed by correction for multiple comparisons. I wonder whether this approach is optimal for these nested, high‐dimensional behavioral data. For instance, the authors do not report any formal test of normality. This might be an issue given the often skewed distributions of kinematic variables that are reported. Moreover, each fly contributes many video segments, and each segment results in multiple measurements. By treating every segment as an independent observation, the non‐independence of measurements within the same animal is ignored. I think a linear mixed‐effects model (LMM) or generalized linear mixed model (GLMM) might be more appropriate.

(4) The manuscript mentions that legs are used for walking as well as grooming. While this is welcome, the authors then do not discuss the implications of this in sufficient detail. For instance, how should we interpret that pulsed stimulation of a subset of 13A neurons produces grooming and walking behaviours? How does neural control of grooming interact with that of walking?

(5) The manuscript needs to be proofread and edited as there are inconsistencies in labelling in figures, phrasing errors, missing citations of figures in the text, or citations that are not in the correct order, and referencing errors (examples: 81 and 83 are identical; 94 is missing in text).

eLife Assessment

This study presents a valuable finding on the perturbed pyruvate metabolism in models of repetitive traumatic brain injury. The evidence supporting the main claims of the authors is solid, but much of the accompanying analysis and interpretation relies on incomplete evidence. The work will be of interest to those working on the imaging of traumatic brain injury.

Joint Public Review:

Summary:

The authors present a metabolic imaging study of pyruvate metabolism in a mouse model of repetitive traumatic brain injury in the chronic recovery stage. They measure pyruvate metabolism with hyperpolarised 13C magnetic resonance spectroscopic imaging. This is acquired alongside semi-quantitative MR imaging metrics, a behavioural measure, and postmortem measures of relevant enzyme activity and expression of metabolic transporter proteins. They find that the MRSI-measured cortical lactate/pyruvate ratio (and signal from pyruvate and lactate independently) can differentiate the rTBI group from the sham group. They additionally find that postmortem, cortical pyruvate dehydrogenase activity is a statistically significant discriminator. All other metrics (MRI and enzyme/transporter measures) are not significantly different between groups. Finally, using a machine learning approach, the authors investigate the predictive power of combinations of all measures.

Strengths:

The primary strength of this work is the likely robustness of the primary finding - that hyperpolarised 13C lactate/pyruvate metabolite ratios are perturbed in this chronic rTBI model compared to the sham control.

Weaknesses:

Focal alterations in blood-brain-barrier permeability may affect the primary lactate/pyruvate measures. Whilst 13C urea measures perfusion, urea remains purely extracellular; whilst in the metabolism of the healthy brain, pyruvate must be transported through two levels of monocarboxylate transporters (MCTs) - in the endothelium surrounding the capillary bed and then into the parenchyma. By mechanically disrupting the brain, tight junctions in the BBB may be disrupted, therefore increasing the flux of pyruvate across the BBB and increasing pyruvate availability. In this case, lac/pyr would be a poor measure of metabolism as "delivery" has changed. While the authors assess perfusion using HP urea, it is unclear whether or how this metric would change in the presence of BBB disruption in relatively large and well-vascularised voxels.

The finding that "HP [1-13C]pyruvate levels were 1.05 fold higher" indicates that delivery of pyruvate might be increased. It is unclear if normalisation to the combined amplitude of lactate and pyruvate is fair in the case that the volume fraction in the voxel might have increased. Ideally, the authors would estimate polarisation separately as a normalisation.

No estimate of uncertainty is provided for the primary metabolic measures. Note that the lactate-pyruvate ratio is not normally distributed (see doi: 10.1002/mrm.26615), and this should be accounted for when carrying out statistical tests.

All metabolic maps are shown masked to the brain and interpolated to the structural MRI resolution (around 20 times). Nor is there any characterisation of the spectroscopic imaging's voxel volume, including the effect of the point spread function. It is, therefore, hard to have confidence in any spatial effects or potential partial volume effects from the tissue surrounding the brain.

The t2-weighted and SWI MRI measures used in this work are not quantitative. Normalisation in each case is carried out without regard to any spatially variable transmit and receive coil sensitivities (B1{plus minus}), which vary per subject. This adds intersubject variance, which could mask any effect between groups. No quality metrics (SNR or uncertainty estimates) are given for the MRI metrics.

Spectroscopic imaging was conducted 16 s after injection. Given the high heart rate of a mouse, measures of perfusion (using urea) could , therefore, be considered in a steady state, lowering sensitivity to any changes in perfusion or metabolite delivery. Furthermore, it is unclear how any changes in BBB permeability would manifest with the relatively low spatial resolution of MRSI. Would signal always be dominated by vascular compartments?

There is no apparent attempt to understand if an immune response occurs at this chronic time point. Macrophages are glycolytic and could affect the pyruvate measurement. Furthermore, is there any evidence for cellular changes in this model, namely density, cell type fraction, or microstructure? Are there any expected changes in glucose uptake?

There is no information or references provided for the accuracy or precision of the postmortem assays or their correlation with in vivo processes. What is the effect of cell density changes after injury on the assay kits?

The proposed interpretation of T1 as a measure of oxidative stress would seem to ignore the many confounding interpretations of T1.

Aims and impact:

In summary, the authors broadly achieve one aim, which is to find that HP 13C measured lac/pyruvate is a biomarker for the chronic effects of rTBI in a mouse model. As the authors themselves highlight in the discussion, the interpretation of this finding is tricky alongside their post-mortem assay results. The MR imaging in this work seems inconclusive, given the potential for inter-subject variance in the normalisation method.

The work, therefore, continues to highlight that HP 13C MRSI is a highly promising avenue of investigation to identify, characterise, and understand traumatic brain injury. It suggests that HP 13C MRSI is more promising in this sense than some standard MRI contrasts. The work currently fails to convincingly interpret the HP 13C MR results in conjunction with the other metrics.

eLife Assessment

This is a valuable and rigorous study that addresses the question of what determines the spatial organization of endocytic zones at synapses. The authors use compelling approaches, in both Drosophila and rodent model systems, to define the role of activity and active zone structure on the organization of the peri-active zone. While the findings are primarily negative, they are carefully executed and contribute to the field by refining existing models of presynaptic organization.

Reviewer #1 (Public review):

Summary:

In this manuscript, Emperador-Melero et al. seek to determine whether recruitment of endocytic machinery to the periactive zone is activity-dependent or tethered to delivery of active zone machinery. They use genetic knockouts and pharmacological block in two model synapses - cultured mouse hippocampal neurons and Drosophila neuromuscular junctions - to determine how well endocytic machinery localizes after chronic inhibition or acute depolarization by super-resolution imaging. They find that acute depolarization in both models has minimal to no effect on the localization of endocytic machinery at the periactive zone, suggesting that these proteins are constitutively maintained rather than upregulated in response to transient activity. Interestingly, chronic inhibition slightly increases endocytic machinery levels, implying a potential homeostatic upregulation in preparation for rebound depolarization. Using genetic knockouts, the authors show that localization of endocytic machinery to periactive zones occurs independently of proper active zone assembly, even in the absence of upstream organizers like Liprin-α.

Overall, they propose that the constitutive deployment of endocytic machinery reflects its critical role in facilitating rapid and reliable membrane internalization during synaptic functions beyond classical endocytosis, such as regulation of the exocytic fusion pore and dense-core vesicle fusion. Although many experiments reveal limited changes in the localization or abundance of endocytic machinery, the findings are thorough, and data substantially support a model in which endocytic components are organized through a pathway distinct from that of the active zone. This work advances our understanding of synaptic dynamics by supporting a model in which endocytic machinery is constitutively recruited and regulated by distinct upstream organizers compared to active zone proteins. It also highlights the utility of super-resolution imaging across diverse synapse types to uncover functionally conserved elements of synaptic biology.

Strengths:

The study's technical strengths, particularly the use of super-resolution microscopy and rigorous image analyses developed by the group, bolster their findings.

Weaknesses:

One notable limitation, however, is the absence of interrogation of endocytic proteins previously suggested to be recruited in an activity-dependent manner, in particular, endophilin.

Reviewer #2 (Public review):

Summary:

This study examines whether the localization of endocytic proteins to presynaptic periactive zones depends on synaptic activity or active zone scaffolds. Using a combination of genetic and pharmacological perturbations in Drosophila and mouse neurons, the authors show that proteins such as Dynamin, Amphiphysin, AP-180, and others are still recruited to periactive zones even when evoked release or active zone architecture is disrupted. While the results are mostly negative, the study is methodologically solid and contributes to a more nuanced understanding of synaptic vesicle recycling machinery.

Strengths:

(1) The experimental design is careful and systematic, covering both fly and mammalian systems.

(2) The use of advanced genetic models (e.g., Liprin-α quadruple knockout mice) is a notable strength.

(3) High-resolution imaging (STED, Airyscan) is well used to assess spatial localization.

(4) The findings clarify that certain core assumptions - such as strict activity dependence of endocytic recruitment - may not hold universally.

Weaknesses:

(1) The study would benefit from a clearer positive control to demonstrate activity-dependent recruitment (e.g., Endophilin).

(2) The reliance on Tetanus toxin in the Drosophila NMJ experiments in my eyes is a limitation, as it does not block all presynaptic fusion events; this should be discussed more directly.

(3) The potential role of Dynamin in organizing other periactive zone proteins is not addressed and could be an important next step.

(4) Some small changes in protein levels upon silencing are reported; their biological meaning (e.g., compensation vs. variability) is not fully clarified.

(5) While alternative organizing mechanisms (actin, lipids, adhesion molecules) are mentioned, a more forward-looking discussion of how to test these models would be helpful.

(6) The authors should consider including, or at least discussing, a well-established activity-dependent endocytic protein (e.g., Endophilin) as a positive control to help contextualize the negative findings.

Reviewer #3 (Public review):

Summary:

This study examines how synaptic endocytic zones are positioned using a combination of cultured neurons and the Drosophila neuromuscular junction. The authors test whether neuronal activity, active zone assembly, or liprin-α function is required to localize endocytic zone markers, including Dynamin, Amphiphysin, Nervous Wreck, PIPK1γ, and AP-180. None of the manipulations tested caused a coordinated disruption in the localization or abundance of these markers, leading to the conclusion that endocytic zones form independently of synaptic activity and active zone scaffolds.

Strengths:

The work is systematic and carefully executed, using multiple manipulations and two complementary model systems. The authors consistently examine multiple molecular markers, strengthening the interpretation that endocytic zone positioning is robust to changes in activity and structural assembly.

Weaknesses:

The main limitation is that the study does not test whether the methods used are sensitive enough to detect subtle functional disruption, and no condition tested produces clear disorganization of the endocytic zone. As a result, the conclusion that these zones assemble independently is supported by negative data, without a strong positive control for disassembly or mislocalization.

This paper addresses a longstanding question in synaptic biology and provides a well-supported boundary on the types of mechanisms that are likely to govern endocytic zone localization. The conclusions are well justified by the data, though additional evidence would be needed to define the assembly mechanism itself.

eLife Assessment

The authors conducted a valuable study that investigates a molecular pathway mediating the transformation of a cell aggregate into a sheet known as the nucleus laminaris, a crucial site for auditory processing. While the study offers a comprehensive view of the sequence of developmental events and suggests possible roles for FGF signaling, the transcription factor Mafb, and the cell surface adhesive molecule Cadherin-23 in this process, the current data were considered incomplete.

Reviewer #1 (Public review):

Summary:

In this study, the authors sought to define a molecular pathway that mediates the transformation of an aggregate of cells into a sheet known as the nucleus laminaris, a key site for auditory processing. The data offer a comprehensive view of the sequence of developmental events and suggest possible roles for FGF signaling, the transcription factor Mafb, and the cell surface adhesive molecule Cadherin-23 in this process.

Strengths:

The description of nL development is thorough and well-done, with extensive quantification of the overall structure of the nucleus and also of neuron number. Additionally, the study implicates several molecules in nL development, starting with a clear description of when and where FGF8, Mafb, and several cadherins are expressed, including antibody stains suggesting that one cadherin, cdh2, is localized to the neuronal dendrites. A series of perturbation experiments supports the idea that these three molecules play a role in nL formation. The computational model is an interesting addition that helps to conceptualize how cadherin-mediated adhesion might influence nL morphogenesis.

Weaknesses:

A number of weaknesses limit the impact of this work.

One problem is how the data is interpreted. The logic is often circular in that the same molecules are used both as markers of nL and also as players in its development. An independent measure of nL formation is needed. Along the same lines, while the experiments implicate each molecule, the data do not actually demonstrate that FGF directly modulates Mafb, which in turn modulates cadherin expression, especially as overexpression of cdh2 has no effect on FGF8 expression or lamina organization, and no manipulations of cdh22 are presented.

The other type of problem relates to how the experiments were performed and analyzed. Important details about the experiments, as well as key controls, are missing throughout. Sample sizes are rarely presented, and there is no evidence that either dominant negative construct actually acts as proposed. Some results are not well quantified, which further undermines the strength of the conclusions. For instance, the changes in mafb and cdh22 expression (Figure 7) are subtle and were not quantified for any of the conditions. Likewise, the claim that FGF8 has a dose-dependent effect on lamina size and neuron number needs to be supported by statistics.

There are also some questions about the quality of the data. Much of the histology is of poor quality and does not always show the same piece of brain in the same orientation from experiment to experiment, which makes it challenging to interpret the results. In particular, the quality of the in situ hybridization varies, with much more background in some cases than others, which makes it hard to know what signal is real.

Finally, there are some misstatements and problems with citations that weaken the scholarly nature of the paper. FGF signaling has been studied extensively in the hindbrain and even in auditory nucleus development (Abraira et al., 2007), but this literature is not discussed at all.

Due to these weaknesses, the authors have achieved their aims only in part. The data are suggestive, but the results do not yet fully support their conclusions.

Few labs study how populations of neurons assemble into spatially organized structures. This work has the potential to be very interesting to other developmental neuroscientists studying brain morphogenesis.

Reviewer #2 (Public review):

Summary:

The overall goal of this study by Smith et al. was to understand the mechanisms through which groups of cells form specific nuclei during development. These cell groupings may have importance for the development of nervous system connections. Smith et al. have taken advantage of the ordered structure of the nucleus laminaris of the chick, which plays an important role in sound source localization. They used a candidate gene approach to both mark cells in nL and to test for signaling pathways that regulate nucleogenesis. They found that MafB, FGF8, and cadherins were expressed in the auditory hindbrain at the critical ages. They used in ovo electroporation to test gene function effects on nL lamina formation. They found that both increasing and decreasing FGF signaling (through introduction of mouse FGF8 and expression of a dominant negative FGF receptor, respectively) reduced lamina formation in the nL. An optimal concentration of FGF needed for this process was obtained using cultured hindbrain slices. Misexpression of cadherins also perturbed the normal lamina formation. The authors showed that FGF regulates MafB expression, which in turn regulates cadherin expression, suggesting a pathway that shapes lamina development. They constructed computational models of adhesion on the development of nL cells and found that laminar formation is favored by nL cells modeled as bipolar adhesive units. Overall, the study has demonstrated the importance of these adhesion pathways for the formation of the nucleus laminaris, and the findings likely have significance for the development of other nuclei as well.

Strengths:

The experiments have used in situ hybridization, immunofluorescence, electroporation, and brainstem slice cultures to test their hypotheses, which were based on well-selected candidate molecules. The modeling adds to the rigor of the studies, particularly in light of the observation that cadherin expression is localized to nL dendrites.

Weaknesses:

(1) Some references should be considered more carefully for accuracy, and additional references may be needed (introduction and results).

(2) Information on animal numbers and statistical tests should be added.

eLife Assessment

This manuscript provides valuable information on the neurodynamics of emotional processing while participants were watching movie clips. The methods and results were solid in deciphering the temporal-spatial dynamics of emotional processing. This work will be of interest to affective neuroscientists.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors endeavor to capture the dynamics of emotion-related brain networks. They employ slice-based fMRI combined with ICA on fMRI time series recorded while participants viewed a short movie clip. This approach allowed them to track the time course of four non-noise independent components at an effective 2s temporal resolution at the BOLD level. Notably, the authors report a temporal sequence from input to meaning, followed by response, and finally default mode networks, with significant overlap between stages. The use of ICA offers a data-driven method to identify large-scale networks involved in dynamic emotion processing. Overall, this paradigm and analytical strategy mark an important step forward in shifting affective neuroscience toward investigating temporal dynamics rather than relying solely on static network assessments

Strengths:

(1) One of the main advantages highlighted is the improved temporal resolution offered by slice-based fMRI. However, the manuscript does not clearly explain how this method achieves a higher effective resolution, especially since the results still show a 2s temporal resolution, comparable to conventional methods. Clarification on this point would help readers understand the true benefit of the approach.

(2) While combining ICA with task fMRI is an innovative approach to study the spatiotemporal dynamics of emotion processing, task fMRI typically relies on modeling the hemodynamic response (e.g., using FIR or IR models) to mitigate noise and collinearity across adjacent trials. The current analysis uses unmodeled BOLD time series, which might risk suffering from these issues.

(3) The study's claims about emotion dynamics are derived from fMRI data, which are inherently affected by the hemodynamic delay. This delay means that the observed time courses may differ substantially from those obtained through electrophysiology or MEG studies. A discussion on how these fMRI-derived dynamics relate to - or complement - is critical for the field to understand the emotion dynamics.

(4) Although using ICA to differentiate emotion elements is a convenient approach to tell a story, it may also be misleading. For instance, the observed delayed onset and peak latency of the 'response network' might imply that emotional responses occur much later than other stages, which contradicts many established emotion theories. Given the involvement of large-scale brain regions in this network, the underlying reasons for this delay could be very complex.

Concerns and suggestions:

However, I have several concerns regarding the specific presentation of temporal dynamics in the current manuscript and offer the following suggestions.

(1) One selling point of this work regarding the advantages of testing temporal dynamics is the application of slice-based fMRI, which, in theory, should improve the temporal resolution of the fMRI time course. Improving fMRI temporal resolution is critical for a research project on this topic. The authors present a detailed schematic figure (Figure 2) to help readers understand it. However, I have difficulty understanding the benefits of this method in terms of temporal resolution.

a) In Figure 2A, if we examine a specific voxel in slice 2, the slice acquisitions occur at 0.7s, 2.7s, and 4.7s, which implies a temporal resolution of 2s rather than 0.7s. I am unclear on how the temporal resolution could be 0.7s for this specific voxel. I would prefer that the authors clarify this point further, as it would benefit readers who are not familiar with this technology.

b) Even with the claim of an increased temporal resolution (0.7s), the actual data (Figure 3) still appears to have a 2s resolution. I wonder what specific benefit slice-based fMRI brings in terms of testing temporal dynamics, aside from correcting the temporal distortions that conventional fMRI exhibits.

(2) In task-fMRI, the hemodynamic response is usually estimated using a specific model (e.g., FIR, IR model; see Lindquist et al., 2009). These models are effective at reducing noise and collinearity across adjacent trials. The current method appears to be conducted on unmodeled BOLD time series.

a) I am wondering how the authors avoid the issues that are typically addressed by these HRF modeling approaches. For example, if we examine the baseline period (say, -4 to 0s relative to stimulus onset), the activation of most networks does not remain around zero, which could be due to delayed influences from the previous trial. This suggests that the current time course may not be completely accurate.

b) A related question: if the authors take the spatial map of a certain network and apply a modeling approach to estimate a time series within that network, would the results be similar to the current ICA time series?

(3) Human emotion should be inherently fast to ensure survival, as shown in many electrophysiology and MEG studies. For example, the dynamics of a fearful face can occur within 100ms in subcortical regions (Méndez-Bértolo et al., 2016), and general valence and arousal effects can occur as early as 200ms (e.g., Grootswagers et al., 2020; Bo et al., 2022). In contrast, the time-to-peak or onset timing in the BOLD time series spans a much larger time range due to the hemodynamic delay. fMRI findings indeed add spatial precision to our understanding of the temporal dynamics of emotion, but could the authors comment on how the current temporal dynamics supplement those electrophysiology studies that operate on much finer temporal scales?

(4) The response network shows activation as late as 15 to 20s, which is surprising. Could the authors discuss further why it takes so long for participants to generate an emotional response in the brain?

(5) Related to 4. In many theories, the emotion processing stages-including perception, valuation, and response-are usually considered iterative processes (e.g., Gross, 2015), especially in real-world scenarios. The advantage of the current paradigm is that it incorporates more dynamic elements of emotional stimuli and is closer to reality. Therefore, one might expect some degree of dynamic fluctuation within the tested brain networks to reflect those potential iterative processes (input, meaning, response). However, we still do not observe much brain dynamics in the data. In Figure 5, after the initial onset, most network activations remain sustained for an extended period of time. Does this suggest that emotion processing is less dynamic in the brain than we thought, or could it be related to limitations in temporal resolution? It could also be that the dynamics of each individual trial differ, and averaging them eliminates these variations. I would like to hear the authors' comments on this topic.

(6) The activation of the default mode network (DMN), although relatively late, is very interesting. Generally, one would expect a deactivation of this network during ongoing external stimulation. Could this suggest that participants are mind-wandering during the later portion of the task?

Reviewer #2 (Public review):

Summary:

This manuscript examined the neural correlates of the temporal-spatial dynamics of emotional processing while participants were watching short movie clips (each 12.5 s long) from the movie "Forrest Gump". Participants not only watched each film clip, but also gave emotional responses, followed by a brief resting period. Employing fMRI to track the BOLD responses during these stages of emotional processing, the authors found four large-scale brain networks (labeled as IC0,1,2,4) were differentially involved in emotional processing. Overall, this work provides valuable information on the neurodynamics of emotional processing.

Strengths:

This work employs a naturalistic movie watching paradigm to elicit emotional experiences. The authors used a slice-based fMRI method to examine the temporal dynamics of BOLD responses. Compared to previous emotional research that uses static images, this work provides some new data and insights into how the brain supports emotional processing from a temporal dynamics view.

Weaknesses:

Some major conclusions are unwarranted and do not have relevant evidence. For example, the authors seemed to interpret some neuroimaging results to be related to emotion regulation. However, there were no explicit instructions about emotional regulation, and there was no evidence suggesting participants regulated their emotions. How to best interpret the corresponding results thus requires caution.

Relatedly, the authors argued that "In turn, our findings underscore the utility of examining temporal metrics to capture subtle nuances of emotional processing that may remain undetectable using standard static analyses." While this sentence makes sense and is reasonable, it remains unclear how the results here support this argument. In particular, there were only three emotional categories: sad, happy, and fear. These three emotional categories are highly different from each other. Thus, how exactly the temporal metrics captured the "subtle nuances of emotional processing" shall be further elaborated.

The writing also contained many claims about the study's clinical utility. However, the authors did not develop their reasoning nor elaborate on the clinical relevance. While examining emotional processing certainly could have clinical relevance, please unpack the argument and provide more information on how the results obtained here can be used in clinical settings.

Importantly, how are the temporal dynamics of BOLD responses and subjective feelings related? The authors showed that "the time-to-peak differences in IC2 ("response") align closely with response latency results, with sad trials showing faster response latencies and earlier peak times". Does this mean that people typically experience sad feelings faster than happy or fear? Yet this is inconsistent with ideas such that fear detection is often rapid, while sadness can be more sustained. Understandably, the study uses movie clips, which can be very different from previous work, mostly using static images (e.g., a fearful or a sad face). But the authors shall explicitly discuss what these temporal dynamics mean for subjective feelings.

eLife Assessment

This important study looks into the effect of exogenous CoA on the response of TLR4-activated macrophages. Specifically, CoA enhances the LPS response by examining metabolomics, 13C tracing, and assessments of transcription and acetylation. Together, these provide a compelling series of findings that show exogenous CoA is taken up by macrophages, and this facilitates histone acetylation and transcription associated with activation and antimicrobial activity.

Reviewer #1 (Public review):

Summary:

This paper describes how CoA can overcome suppression of OXPHOS in TLR3 signaling, acting as what the authors term a 'metabolic adjuvant'. Supplementing with CoA enhances TLR signaling, reverses tolerance, and promotes OXPHOS. It promotes histone acetylation, leading to epigenetic modulation of target genes. CoA is further shown to have adjuvant effects in vivo, in anti-tumor immunity, and also in host defense.

Strengths:

Something of a tour-de-force - impressive methodologies and the conclusions are well supported by the data.

Weaknesses:

I was unable to follow the basis for some experiments and have a question around the data on itaconate, since this metabolite should limit IL-1beta production. Also, this is a very wordy manuscript - editing should help the reader.

Reviewer #2 (Public review):

In this manuscript, Timblin et al provide a model where exogenous CoA is taken up by macrophages and utilized to support transcriptional events associated with activation. They provide a series of important findings, and for the most part, the data are clear and convincing. However, additional clarity on a few points would be helpful.

First of all, the contention that endogenous TLR ligands from the bone marrow cultures are driving the tonic signaling that makes exogenous CoA beneficial in unstimulated cells seems counter to the well-described anergic state of myeloid cells derived from TLR-null mice. This reviewer's understanding was that myeloid cells in MyD88 nulls or similar are developmentally anergic due to the lack of TLR stimulation in vivo. The data here (Figure 5G, etc) show these cells have much lower TLR responses, but the authors attribute it to loss of response to endogenous ligands during the cultures rather than in vivo. Testing some of the phenotypes ex vivo, etc, might make this argument more compelling and rule out that this is an effect in vivo.

Second, the data suggesting that CoA enhances anti-microbial activity via itaconate production needs additional context and/or clarification. Interactions between itaconate and CoA have been demonstrated. Itaconate exposure can deplete the CoA pool as it is converted into Itaconyl-CoA. The Irg-/- cells should not have reduced CoA due to the lack of the need to activate itaconate for metabolism. Has this been addressed by the authors? I believe that low levels of itaconate production have been shown in "resting" bone marrow cultures. The data show a full log of more bugs in the macs that lack Irg, confirming that endogenous itaconate is at work. In addition, itaconate, which is made very quickly and is likely there in considerable amounts in 4 hrs, is known to affect transcription via action on TET2. Perhaps this explains some of the connections to CoA?

Lastly, the idea that Acetyl-CoA phenocopies CoA suggests that CoA is the effector is interesting but could be supported more. Did the authors do the "unlabeling" experiment with Acetyl-CoA to confirm that it is readily converted to the CoA pool?

Do the ACLY inhibitors have the expected effects on the ChIP seq data?

eLife Assessment

Karimian et al. present a valuable new model to explain how gamma-band synchrony (30-80 Hz) can support human visual feature binding by selectively grouping image elements, countering recent criticisms that the stimulus dependence of gamma oscillations limits their functional role. Grounded in the theory of weakly coupled oscillators and informed by primate electrophysiology, the model captures behavioural patterns observed in human psychophysics, offering support for the potential role of synchrony-based mechanisms, but incomplete evidence for a specific role of gamma oscillations. This work could be strengthened by more direct evidence for the proposed mechanism, and expanding beyond figure-only model inputs with limited ecological validity.

Reviewer #1 (Public review):

Summary:

This paper by Karimian et al proposes an oscillator model tuned to implement binding by synchrony (BBS*) principles in a visual task. The authors set out to show how well these BBS principles explain human behavior in figure-ground segregation tasks. The model is inspired by electrophysiological findings in non-human primates, suggesting that gamma oscillations in early visual cortex implement feature-binding through a synchronization of feature-selective neurons. The psychophysics experiment involves the identification of a figure consisting of gabor annuli, presented on a background of gabor annuli. The participants' task is to identify the orientation of the figure. The task difficulty is varied based on the contrast and density of the gabor annuli that make up the figure. The same figures (without the background) are used as inputs to the oscillator model. The authors report that both the discrimination accuracy in the psychophysics experiment and the synchrony of the oscillators in the proposed model follow a similar "Arnold Tongue" relationship when depicted as a function of the texture-defining features of the figure. This finding is interpreted as evidence for BBS/gamma synchrony being the underlying mechanism of the figure-ground segregation.

• Note that I chose to use "BBS" over gamma synchrony (used by the authors) in this review, as I am not convinced that the authors show evidence for synchronization in the gamma-band.

Strengths:

The design of the proposed model is well-informed by electrophysiological findings, and the idea of using computational modeling to bridge between intracranial recordings in non-human primates and behavioral results in human participants is interesting. Previous work has criticized the BBS synchrony theory based on the observation that synchronization in the gamma-band is highly localized and the frequency of the oscillation depends on the visual features of the stimulus. I appreciate how the authors demonstrate that frequency-dependence and local synchronization can be features of BBS, and not contradictory to the theory. As such, I feel that this work has the potential to contribute meaningfully to the debate on whether BBS is a biophysically realistic model of feature-binding in visual cortex.

Weaknesses:

I have several concerns regarding the presented claims, assessment of meaning and size of the presented effects, particularly with regard to the absence of a priori defined effect sizes.

Firstly, the paper makes strong claims about the frequency-specificity (i.e., gamma synchrony) and anatomical correlates (early visual cortex) of the observed effects. These claims are informed by previous electrophysiological work in non-human primates but are not directly supported by the paper itself. For instance, the title contains the word "gamma synchrony", but the authors do not demonstrate any EEG/MEG or intracranial data in from their human subjects supporting such claims, nor do they demonstrate that the frequencies in the oscillator model are within the gamma band. I think that the paper should more clearly distinguish between statements that are directly supported by the paper (such as: "an oscillator model based on BBS principles accounts for variance in human behavior") and abstract inferences based on the literature (such as "these effects could be attributed to gamma oscillations in early visual cortex, as the model was designed based on those principles").

Secondly, unlike the human participants, the model strictly does not perform figure-ground segregation, as it only receives the figure as an input. Finally, it is unclear what effect sizes the authors would have expected a priori, making it difficult to assess whether their oscillator model represents the data well or poorly. I consider this a major concern, as the relationship between the synchrony of the oscillatory model and the performance of the human participants is confounded by the visual features of the figure. Specifically, the authors use the BBS literature to motivate the hypothesis that perception of the texture-defined figure is related to the density and contrast heterogeneity of the texture elements (gabor annuli) of the figure. This hypothesis has to be true regardless of synchrony, as the figure will be easier to spot if it consists of a higher number of high-contrast gabors than the background. As the frequency and phase of the oscillators and coupling strength between oscillators in the grid change as a function of these visual features, I wonder how much of the correlation between model synchrony and human performance is mediated by the features of the figure. To interpret to what extent the similarity between model and human behavior relies on the oscillatory nature of the model, the authors should find a way to estimate an empirical threshold that accounts for these confounding effects. Alternatively, it would be interesting to understand whether a model based on competing theories (e.g., Binding by Enhanced Firing, Roelfsema, 2023) would perform better or worse at explaining the data.

Reviewer #2 (Public review):

The authors aimed to investigate whether gamma synchrony serves a functional role in figure-ground perception. They specifically sought to test whether the stimulus-dependence of gamma synchrony, often considered a limitation, actually facilitates perceptual grouping. Using the theory of weakly coupled oscillators (TWCO), they developed a framework wherein synchronization depends on both frequency detuning (related to contrast heterogeneity) and coupling strength (related to proximity between visual elements). Through psychophysical experiments with texture discrimination tasks and computational modeling, they tested whether human performance follows patterns predicted by TWCO and whether perceptual learning enhances synchrony-based grouping.

Strengths:

(1) The theoretical framework connecting TWCO to visual perception is innovative and well-articulated, providing a potential mechanistic explanation for how gamma synchrony might contribute to both feature binding and separation.

(2) The methodology combines psychophysical measurements with computational modeling, with a solid quantitative agreement between model predictions and human performance.

(3) In particular, the demonstration that coupling strengths can be modified through experience is remarkable and suggests gamma synchrony could be an adaptable mechanism that improves with visual learning.

(4) The cross-validation approach, wherein model parameters derived from macaque neurophysiology successfully predict human performance, strengthens the biological plausibility of the framework.

Weaknesses:

(1) The highly controlled stimuli are far removed from natural scenes, raising questions about generalisability. But, of course, control (almost) excludes ecological validity. The study does not address the challenges of natural vision or leverage the rich statistical structure afforded by natural scenes.

(2) The experimental design appears primarily confirmatory rather than attempting to challenge the TWCO framework or test boundary conditions where it might fail.

(3) Alternative explanations for the observed behavioral effects are not thoroughly explored. While the model provides a good fit to the data, this does not conclusively prove that gamma synchrony is the actual mechanism underlying the observed effects.

(4) Direct neurophysiological evidence linking the observed behavioral effects to gamma synchrony in humans is absent, creating a gap between the model and the neural mechanism.

Achievement of Aims and Support for Conclusions:

The authors largely achieved their primary aim of demonstrating that human figure-ground perception follows patterns predicted by TWCO principles. Their psychophysical results reveal a behavioral "Arnold tongue" that matches the synchronization patterns predicted by their model, and their learning experiment shows that perceptual improvements correlate with predicted increases in synchrony.

The evidence supports their conclusion that gamma synchrony could serve as a viable neural grouping mechanism for figure-ground segregation. However, the conclusion that "stimulus-dependence of gamma synchrony is adaptable to the statistics of visual experiences" is only partially supported, as the study uses highly controlled artificial stimuli rather than naturalistic visual statistics, or shows a sensitivity to the structure of experience.

Likely Impact and Utility:

This work offers a fresh perspective on the functional role of gamma oscillations in visual perception. The integration of TWCO with perceptual learning provides a novel theoretical framework that could influence future research on neural synchrony.

The computational model, with parameters derived from neurophysiological data, offers a useful tool for predicting perceptual performance based on synchronization principles. This approach might be extended to study other perceptual phenomena and could inspire designs for artificial vision systems.

The learning component of the study may have a particular impact, as it suggests a mechanism by which perceptual expertise develops through modified coupling between neural assemblies. This could influence thinking about perceptual learning more broadly, but also raises questions about the underlying mechanism that the paper does not address.

Additional Context:

Historically, the functional significance of gamma oscillations has been debated, with early theories of temporal binding giving way to skepticism based on gamma's stimulus-dependence. This study reframes this debate by suggesting that stimulus-dependence is exactly what makes gamma useful for perceptual grouping.

The successful combination of computational neuroscience and psychophysics is a significant strength of this study.

The field would benefit from future work extending (if possible) these findings to more naturalistic stimuli and directly measuring neural activity during perceptual tasks. Additionally, studies comparing predictions from synchrony-based models against alternative mechanisms would help establish the specificity of the proposed framework.

Author response:

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

Reviewer #1 (Public Review):

Summary:

In this study, the authors provide a new computational platform called Vermouth to automate topology generation, a crucial step that any biomolecular simulation starts with. Given a wide arrange of chemical structures that need to be simulated, varying qualities of structural models as inputs obtained from various sources, and diverse force fields and molecular dynamics engines employed for simulations, automation of this fundamental step is challenging, especially for complex systems and in case that there is a need to conduct high-throughput simulations in the application of computer-aided drug design (CADD). To overcome this challenge, the authors develop a programing library composed of components that carry out various types of fundamental functionalities that are commonly encountered in topological generation. These components are intended to be general for any type of molecules and not to depend on any specific force field and MD engines. To demonstrate the applicability of this library, the authors employ those components to re-assemble a pipeline called Martinize2 used in topology generation for simulations with a widely used coarse-grained model (CG) MARTINI. This pipeline can fully recapitulate the functionality of its original version Martinize but exhibit greatly enhanced generality, as confirmed by the ability of the pipeline to faithfully generate topologies for two high-complexity benchmarking sets of proteins.

Strengths:

The main strength of this work is the use of concepts and algorithms associated with induced subgraph in graph theory to automate several key but non-trivial steps of topology generation such as the identification of monomer residue units (MRU), the repair of input structures with missing atoms, the mapping of topologies between different resolutions, and the generation of parameters needed for describing interactions between MRUs. In addition, the documentation website provided by the authors is very informative, allowing users to get quickly started with Vermouth.

Weaknesses:

Although the Vermouth library is designed as a general tool for topology generation for molecular simulations, only its applications with MARTINI have been demonstrated in the current study. Thus, the claimed generality of Vermouth remains to be exmained. The authors may consider to point out this in their manuscript.

In order to demonstrate generality of the here proposed concepts for generating topologies for molecular dynamics simulations, we have now implemented and tested a workflow that will produce topologies for the popular CHARMM36 all-atom force field. To facilitate generation of all-atom topologies with Martinize2 a .rtp reader was introduced, which allows users to provide .rtp files that are the native GROMACS topology files for proteins instead of .ff files. These .rtp files exist for all major atomic protein forcefields. In addition, for CHARMM36 we also included modification files, which describe non-standard pH amino acids, histidine tautomers, and end terminal modifications. Thus, the current implementation unlocks all features available at the CG Martini level also for CHARMM36. We note that users must add the modifications files for other all-atom force fields e.g. AMBER.

We have added a new item in the main manuscript (p28) briefly describing this proof-of-concept implementation. However, we like to point out that there are many specialized tools for the various force fields adopted by the respective communities. Thus, an exhaustive discussion on the capabilities of Martinize2 for all-atom force fields seemed out of place.

Reviewer #2 (Public Review):

This work introduces a Vermouth library framework to enhance software development within the Martini community. Specifically, it presents a Vermouth-powered program, Martinize2, for generating coarse-grained structures and topologies from atomistic structures. In addition to introducing the Vermouth library and the Martinize2 program, this paper illustrates how Martinize2 identifies atoms, maps them to the Martini model, generates topology files, and identifies protonation states or post-translational modifications. Compared with the prior version, the authors provide a new figure to show that Martinize2 can be applied to various molecules, such as proteins, cofactors, and lipids. To demonstrate the general application, Martinize2 was used for converting 73% of 87,084 protein structures from the template library, with failed cases primarily blamed on missing coordinates.

I was hoping to see some fundamental changes in the resubmitted version. To my disappointment, the manuscript remains largely unchanged (even the typo I pointed out previously was not fixed). I do not doubt that Martinize2 and Vermouth are useful to the Martini community, and this paper will have some impact. The manuscript is very technical and limited to the Martini community. The scientific insight for the general coarse-grained modeling community is unclear. The goal of the work is ambitious (such as high-throughput simulations and whole-cell modeling), but the results show just a validation of Martinize2. This version does not reverse my previous impression that it is incremental. As I pointed out in my previous review (and no response from the authors), all the issues associated with the Martini model are still there, e.g. the need for ENM. In this shape, I feel this manuscript is suitable for a specialized journal in computational biophysics or stays as part of the GitHub repository.

We apologize for not fixing the typo; it was fixed but unfortunately got reintroduced in the final resubmitted version. We politely disagree that the goal of the work itself is high-throughput simulations and whole-cell modeling, but the Martinize2 tool is certainly an important element in our ambitions to achieve this. Given the broad interest in these goals by the modeling community in general, we believe this work has a much wider impact beyond the (already large) group of Martini users. Addressing limitations of the Martini model itself, which are certainly there, is clearly not the scope of the current work.

Reviewer #3 (Public Review):

The manuscript Kroon et al. described two algorithms, which when combined achieve high throughput automation of "martinizing" protein structures with selected protonation states and post-translational modifications. After the revisions provided by the authors, I recommend minor revision.

The authors have addressed most of my concerns provided previously. Specifically, showcasing the capability of coarse-graining other types of molecules (Figure 7) is a useful addition, especially for the booming field of therapeutic macrocycles. My only additional concern is that to justify Martinize2 and Vermouth as a "high-throughput" method, the speed of these tools needs to be addressed in some form in the manuscript as a guideline to users.

We have added some benchmark timings in the manuscript SI and pointed to the data in the discussion part, which addresses the timing. Martinize2 is certainly slower than martinize version 1 as we already pointed out in the previous versions. However, even for larger proteins (> 2000 residues) we are able to generate topologies in about 60s. As Martinize2 runs on a single core, it can be massively parallelized. Keeping this in mind the topology file generation is likely to take up only a fraction in a high-throughput pipeline compared to the more costly simulations themselves.

Reviewer #3 (Public review):

Summary:

The manuscript Kroon et al. described two algorithms, which when combined achieve high throughput automation of "martinizing" protein structures with selected protonation states and post-translational modifications.

The authors have addressed all of my concerns as provided previously. Specifically, Figure S2 will be a very useful guideline for future improvement (e.g., parallelization) of the code.

Reviewer #2 (Public review):

This work introduces a Vermouth library framework to enhance software development within the Martini community. Specifically, it presents a Vermouth-powered program, Martinize2, for generating coarse-grained structures and topologies from atomistic structures. In addition to introducing the Vermouth library and the Martinize2 program, this paper illustrates how Martinize2 identifies atoms, maps them to the Martini model, generates topology files, and identifies protonation states or post-translational modifications. Compared with the prior version, the authors provide a new figure to show that Martinize2 can be applied to various molecules, such as proteins, cofactors, and lipids. To demonstrate the general application, Martinize2 was used for converting 73% of 87,084 protein structures from the template library, with failed cases primarily blamed on missing coordinates.

I appreciate the changes that the authors made to clarify the novelty. I have no doubt this paper will receive attention and citations.

Reviewer #1 (Public review):

Summary:

In this study, the authors provide a new computational platform called Vermouth to automate topology generation, a crucial step that any biomolecular simulation starts with. Given a wide arrange of chemical structures that need to be simulated, varying qualities of structural models as inputs obtained from various sources, and diverse force fields and molecular dynamics engines employed for simulations, automation of this fundamental step is challenging, especially for complex systems and in case that there is a need to conduct high-throughput simulations in the application of computer-aided drug design (CADD). To overcome this challenge, the authors develop a programing library composed of components that carry out various types of fundamental functionalities that are commonly encountered in topological generation. These components are intended to be general for any type of molecules and not to depend on any specific force field and MD engines. To demonstrate the applicability of this library, the authors employ those components to reassemble a pipeline called Martinize2 used in topology generation for simulations with a widely used coarse-grained model (CG) MARTINI. This pipeline can fully recapitulate the functionality of its original version Martinize but exhibit greatly enhanced generality, as confirmed by the ability of the pipeline to faithfully generate topologies for two high-complexity benchmarking sets of proteins.

Strengths:

The main strength of this work is the use of concepts and algorithms associated with induced subgraph in graph theory to automate several key but non-trivial steps of topology generation such as the identification of monomer residue units (MRU), the repair of input structures with missing atoms, the mapping of topologies between different resolutions, and the generation of parameters needed for describing interactions between MRUs. In addition, the documentation website provided by the authors is very informative, allowing users to get quickly started with Vermouth.

Weaknesses:

Although the Vermouth library can work for different force fields, exhibiting certain generality, its application has been demonstrated only with GROMACS. The extension of the library to other major MD engines could be future directions for improvement but may not be needed for this study.

eLife Assessment

The authors present an important multi-scale computational platform, which aims to automate the workflow for coarse-grained simulations of biomolecules in the framework of the popular MARTINI model. The capability of the platform has been convincingly demonstrated by the application to a large number of proteins as well as macrocycles and polymers. This work will be of interest to both computational biophysicists and chemists.

Author response:

Public Review

Joint Public Review:

This manuscript presents an algorithm for identifying network topologies that exhibit a desired qualitative behaviour, with a particular focus on oscillations. The approach is first demonstrated on 3-node networks, where results can be validated through exhaustive search, and then extended to 5-node networks, where the search space becomes intractable. Network topologies are represented as directed graphs, and their dynamical behaviour is classified using stochastic simulations based on the Gillespie algorithm. To efficiently explore the large design space, the authors employ reinforcement learning via Monte Carlo Tree Search (MCTS), framing circuit design as a sequential decision-making process.

This work meaningfully extends the range of systems that can be explored in silico to uncover non-linear dynamics and represents a valuable methodological advance for the fields of systems and synthetic biology.

Strengths

The evidence presented is strong and compelling. The authors validate their results for 3-node networks through exhaustive search, and the findings for 5-node networks are consistent with previously reported motifs, lending credibility to the approach. The use of reinforcement learning to navigate the vast space of possible topologies is both original and effective, and represents a novel contribution to the field. The algorithm demonstrates convincing efficiency, and the ability to identify robust oscillatory topologies is particularly valuable. Expanding the scale of systems that can be systematically explored in silico marks a significant advance for the study of complex gene regulatory networks.

Weaknesses

The principal weakness of the manuscript lies in the interpretation of biological robustness. The authors identify network topologies that sustain oscillatory behaviour despite perturbations to the system or parameters. However, in many cases, this persistence is due to the presence of partially redundant oscillatory motifs within the network. While this observation is interesting and of clear value for circuit design, framing it as evidence of evolutionary robustness may be misleading. The "mutant" systems frequently exhibit altered oscillatory properties, such as changes in frequency or amplitude. From a functional cellular perspective, mere oscillation is insufficient - preservation of specific oscillation characteristics is often essential. This is particularly true in systems like circadian clocks, where misalignment with environmental cycles can have deleterious effects. Robustness, from an evolutionary standpoint, should therefore be framed as the capacity to maintain the functional phenotype, not merely the qualitative behaviour.

A secondary limitation is that, despite the methodological advances, the scale of the systems explored remains modest. While moving from 3- to 5-node systems is non-trivial, five elements still represent a relatively small network. It is somewhat surprising that the algorithm does not scale further, particularly when considering the performance of MCTS in other domains - for instance, modern chess engines routinely explore far larger decision trees. A discussion on current performance bottlenecks and potential avenues for improving scalability would be valuable.

Finally, it is worth noting that the emergence of oscillations in a model often depends not only on the topology but also critically on parameter choices and the nature of the nonlinearities. The use of Hill functions and high Hill coefficients is a common strategy to induce oscillatory dynamics. Thus, the reported results should be interpreted within the context of the modelling assumptions and parameter regimes employed in the simulations.

We thank the reviewers for their careful consideration of our work and for the interesting feedback and scientific discussion. We are working on a revised text based on their recommendations, which will include some of the discussion below.

This work meaningfully extends the range of systems that can be explored in silico to uncover non-linear dynamics and represents a valuable methodological advance for the fields of systems and synthetic biology.

We thank the reviewers for their positive assessment of our work’s impact!

The use of reinforcement learning to navigate the vast space of possible topologies is both original and effective, and represents a novel contribution to the field. The algorithm demonstrates convincing efficiency, and the ability to identify robust oscillatory topologies is particularly valuable. Expanding the scale of systems that can be systematically explored in silico marks a significant advance for the study of complex gene regulatory networks.

We appreciate these kind comments about our work’s merits. We are excited to share our reinforcement learning (RL) based method with the fields of systems and synthetic biology, and we consider it a valuable tool for the systematic analysis and design of larger-scale regulatory networks!

The principal weakness of the manuscript lies in the interpretation of biological robustness. The authors identify network topologies that sustain oscillatory behaviour despite perturbations to the system or parameters… [However, these] "mutant" systems frequently exhibit altered oscillatory properties, such as changes in frequency or amplitude. From a functional cellular perspective, mere oscillation is insufficient - preservation of specific oscillation characteristics is often essential. This is particularly true in systems like circadian clocks, where misalignment with environmental cycles can have deleterious effects. Robustness, from an evolutionary standpoint, should therefore be framed as the capacity to maintain the functional phenotype, not merely the qualitative behaviour.

We thank the reviewers for their attention to this point. In the large-scale circuit search, summarized in Figures 4A and 4B, we ran a search for 5-component oscillators that can spontaneously oscillate even when subjected to the deletion of a random gene. Some of the best performing circuits under these conditions exhibited a design feature we call “motif multiplexing,” in which multiple smaller motifs are interleaved in a way that makes oscillation possible under many different mutational scenarios. Interestingly, despite not selecting for preservation of frequency, the 3Ai+3Rep circuit (a 5-gene circuit highlighted in Figure 5) anecdotally appears to have a natural frequency that is robust to partial gene knockdowns, although not to complete gene deletions. As shown in Figure 5C, this circuit has a natural frequency of 6 cycles/hr (with one particular parameterization), and it can sustain a knockdown of any of its 5 genes to 50% of the wild-type transcription rate without altering the natural frequency by more than 20%.

However, we agree that there are salient differences between this training scenario and natural evolution. The revised text will clarify that these differences limit what conclusions can be drawn about biological evolution by analogy. As the reviewers point out, we use the presence of spontaneous oscillations (with or without the deletion) as a measure of fitness, regardless of frequency, so as to screen for designs with promising behavior. Also, the deletion mutations introduced during training likely represent larger perturbations to the system than a typical mutation encountered during genome replication (for example, a point mutation in a response element leading to a moderate change in binding affinity). Finally, we do not introduce any entrainment. Real circadian oscillators are aligned to a 24-hour period (“entrained”) by environmental inputs such as light and temperature. For this reason, natural circadian clocks may have natural frequencies that are slightly shorter or longer than 24 hours, although a close proximity to the 24-hour period does seem to be an important selective factor [1].

...despite the methodological advances, the scale of the systems explored remains modest. While moving from 3- to 5-node systems is non-trivial, five elements still represent a relatively small network. It is somewhat surprising that the algorithm does not scale further, particularly when considering the performance of MCTS in other domains - for instance, modern chess engines routinely explore far larger decision trees. A discussion on current performance bottlenecks and potential avenues for improving scalability would be valuable.

We thank the reviewers for their attention to this point. The main limitation we encountered to exploring circuits with more than 5 nodes in this work was the poor computational scaling of the Gillespie stochastic simulation algorithm, rather than a limitation of MCTS itself. While the average runtime of a 3-node circuit simulation was roughly 7 seconds, this number increased to 18-20 seconds with 5-node circuits. For this reason, we limited the search to topologies with ≤15 interaction arrows (15 sec/simulation). In general, the simulation time was proportional to the square of the number of transcription factors (TFs). We will revise the text to include the reason for stopping at 5 nodes, which is significant for understanding CircuiTree’s scaling properties.

With regards to scaling, an important advantage of CircuiTree is its ability to generate useful candidate designs after exploring only a portion of the search space. Like exhaustive search, given enough time, MCTS will comprehensively explore the search space and find all possible solutions. However, for large search spaces, RL-based agents are generally given a finite number of simulations (or time) to learn as much as possible.

Across machine learning (ML) applications [2] and particularly with RL models [3], this training time tends to obey a power law with respect to the underlying complexity of the problem. Thus we can use the complexity of the 3-node and 5-node searches to infer the current scaling limits of CircuiTree. The first oscillator topology was discovered after 2,280 simulations for the 3-node search, and in the 5-node search, the first oscillator using 5 nodes appeared at ~8e5 simulations, resulting in a power law of Y ~ 84.4 X^0.333. Thus, useful candidate designs may be found for 6-node and 7-node searches after 4.5e7 and 5.26e9 simulations, respectively, even though these spaces contain 1.5e17 and 2.5e23 topologies, respectively. Thus, running a 7-node search with the current implementation of CircuiTree would require resources close to the current boundaries of computation, requiring roughly 1.8 million CPU-hours, or 2 weeks on 5,000 CPUs, assuming a 1-second simulation. These points will be incorporated into both the results and discussion sections in our revised text.

However, we are optimistic about CircuiTree’s potential to scale to much larger circuits with modifications to its algorithm. CircuiTree uses the original (so-called “vanilla”) implementation of MCTS, which has not been used in professional game-playing AIs in over a decade. Contemporary RL-based game-playing engines leverage deep neural networks to dramatically reduce the training time, using value networks to identify game-winning positions and policy networks to find game-winning moves. AlphaZero, developed by Google DeepMind to learn games by self-play and without domain knowledge, outperformed all other chess AIs after 44 million training games, much smaller than the 10^43 possible chess states [4]. Similarly, the game of go has 10¹⁷⁰ possible states, but AlphaZero outperformed other AIs after only 140 million games [4]. Large circuits live in similarly large search spaces; for example, 19-node and 20-node circuits represent spaces of 10¹⁷² and 10¹⁹⁰ possible topologies. The revised text will include this discussion and identify value and policy networks, as well as more scalable simulation paradigms such as ODEs and neural ODEs, as our future directions for improving CircuiTree’s scalability.

Finally, our revised discussion will note some important differences between game-playing and biological circuit design. Unlike deterministic games like chess, the final value of a circuit topology is determined stochastically, by running a simulation whose fitness depends on the parameter set and initial conditions. Thus, state-for-state, it is possible that training an agent for circuit design may inherently require more simulations to achieve the same level of certainty compared to classical games. Additionally, while we often possess a priori knowledge about a game such as its overall difficulty or certain known strategies, we lack this frame of reference when searching for circuit designs. Thus, it remains challenging to know if and when a large space of designs has been “satisfactorily” or “comprehensively” searched, since the answer depends on data that are unknown, namely the quantity, quality, and location of solutions residing in the search space.

Not accounting for redundancy due to structural symmetries

Finally, it is worth noting that the emergence of oscillations in a model often depends not only on the topology but also critically on parameter choices and the nature of the nonlinearities. The use of Hill functions and high Hill coefficients is a common strategy to induce oscillatory dynamics. Thus, the reported results should be interpreted within the context of the modelling assumptions and parameter regimes employed in the simulations.

In our dynamical modeling of transcription factor (TF) networks, we do not rely on continuum assumptions about promoter occupancy such as Hill functions. Rather, we model each reaction - transcription, translation, TF binding/unbinding, and degradation - explicitly, and individual molecules appear and disappear via stochastic birth and death events. Many natural TFs are homodimers that bind cooperatively to regulate transcription; similarly, we assume that pairs of TFs bind more stably to their response element than individual TFs. Thus, our model has similar cooperativity to a Hill function, and it can be shown that in the continuum limit, the effective Hill coefficient is always ≤2. Our revision will clarify this aspect of the modeling and include a derivation of this property. Currently, the parameter values used in the figures are shown in Table 2. In the revised text, these will be displayed in the body of the text as well for clarity.

Bibliography (1) Spoelstra, K., Wikelski, M., Daan, S., Loudon, A. S. I., & Hau, M. (2015). Natural selection against a circadian clock gene mutation in mice. PNAS, 113(3), 686–691. https://doi.org/https://doi.org/10.1073/pnas.1516442113<br /> (2) Neumann, O., & Gros, C. (2023). Scaling Laws for a Multi-Agent Reinforcement Learning Model. The Eleventh International Conference on Learning Representations. Retrieved from https://openreview.net/forum?id=ZrEbzL9eQ3W (3) Jones, A. L. (2021). Scaling Scaling Laws with Board Games. arXiv [Cs.LG]. Retrieved from http://arxiv.org/abs/2104.03113 (4) Silver, D., Hubert, T., Schrittwieser, J., Antonoglou, I., Lai, M., Guez, A., Lanctot, M., Sifre, L., Kumaran, D., Graepel, T., Lillicrap, T., Simonyan, K., & Hassabis, D. (2018). A general reinforcement learning algorithm that Masters Chess, Shogi, and go through self-play. Science, 362(6419), 1140–1144. https://doi.org/10.1126/science.aar6404

Author response:

Reviewer #1 (Public Review):

Summary: 

BMP signaling is, arguably, best known for its role in the dorsoventral patterning, but not in nematodes, where it regulates body size. In their paper, Vora et al. analyze ChIP-Seq and RNA-Seq data to identify direct transcriptional targets of SMA-3 (Smad) and SMA-9 (Schnurri) and understand the respective roles of SMA-3 and SMA-9 in the nematode model Caenorhabditis elegans. The authors use publicly available SMA-3 and SMA-9 ChIP-Seq data, own RNA-Seq data from SMA-3 and SMA-9 mutants, and bioinformatic analyses to identify the genes directly controlled by these two transcription factors (TFs) and find approximately 350 such targets for each. They show that all SMA-3-controlled targets are positively controlled by SMA-3 binding, while SMA-9-controlled targets can be either up or downregulated by SMA-9. 129 direct targets were shared by SMA-3 and SMA-9, and, curiously, the expression of 15 of them was activated by SMA-3 but repressed by SMA-9. Since genes responsible for cuticle collagen production were eminent among the SMA-3 targets, the authors focused on trying to understand the body size defect known to be elicited by the modulation of BMP signaling. Vora et al. provide compelling evidence that this defect is likely to be due to problems with the BMP signaling-dependent collagen secretion necessary for cuticle formation. 

We thank the reviewer for this supportive summary. We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, we have provided the first comprehensive analysis of these datasets.

Strengths: 

Vora et al. provide a valuable analysis of ChIP-Seq and RNA-Seq datasets, which will be very useful for the community. They also shed light on the mechanism of the BMP-dependent body size control by identifying SMA-3 target genes regulating cuticle collagen synthesis and by showing that downregulation of these genes affects body size in C. elegans. 

Weaknesses: 

(1) Although the analysis of the SMA-3 and SMA-9 ChIP-Seq and RNA-Seq data is extremely useful, the goal "to untangle the roles of Smad and Schnurri transcription factors in the developing C. elegans larva", has not been reached. While the role of SMA-3 as a transcriptional activator appears to be quite straightforward, the function of SMA-9 in the BMP signaling remains obscure. The authors write that in SMA-9 mutants, body size is affected, but they do not show any data on the mechanism of this effect. 

We thank the reviewer for directing our attention to the lack of clarity about SMA-9’s function. We will revise the text to highlight what this study and others demonstrate about SMA-9’s role in body size. We also plan to analyze additional target genes to deepen our model for how SMA-3 and SMA-9 interact functionally to produce a given transcriptional response.

(2) The authors clearly show that both TFs can bind independently of each other, however, by using distances between SMA-3 and SMA-9 ChIP peaks, they claim that when the peaks are close these two TFs act as complexes. In the absence of proof that SMA-3 and SMA-9 physically interact (e.g. that they co-immunoprecipitate - as they do in Drosophila), this is an unfounded claim, which should either be experimentally substantiated or toned down. 

A physical interaction between Smads and Schnurri has been amply demonstrated in other systems. The limitation in the previous work is that only a small number of target genes was analyzed. Our goal in this study was to determine how widespread this interaction is on a genomic scale.  Our analyses demonstrate for the first time that a Schnurri transcription factor has significant numbers of both Smad-dependent and Smad-independent target genes. We will revise the text to clarify this point.

(3) The second part of the paper (the collagen story) is very loosely connected to the first part. dpy-11 encodes an enzyme important for cuticle development, and it is a differentially expressed direct target of SMA-3. dpy-11 can be bound by SMA-9, but it is not affected by this binding according to RNA-Seq. Thus, technically, this part of the paper does not require any information about SMA-9. However, this can likely be improved by addressing the function of the 15 genes, with the opposing mode of regulation by SMA-3 and SMA-9. 

We appreciate this suggestion and will clarify how SMA-9 and its target genes contribute to collagen organization and body size regulation.

(4) The Discussion does not add much to the paper - it simply repeats the results in a more streamlined fashion. 

We thank the reviewer for this suggestion. We will add more context to the Discussion.

Reviewer #2 (Public Review): 

In the present study, Vora et al. elucidated the transcription factors downstream of the BMP pathway components Smad and Schnurri in C. elegans and their effects on body size. Using a combination of a broad range of techniques, they compiled a comprehensive list of genome-wide downstream targets of the Smads SMA-3 and SMA-9. They found that both proteins have an overlapping spectrum of transcriptional target sites they control, but also unique ones. Thereby, they also identified genes involved in one-carbon metabolism or the endoplasmic reticulum (ER) secretory pathway. In an elaborate effort, the authors set out to characterize the effects of numerous of these targets on the regulation of body size in vivo as the BMP pathway is involved in this process. Using the reporter ROL-6::wrmScarlet, they further revealed that not only collagen production, as previously shown, but also collagen secretion into the cuticle is controlled by SMA-3 and SMA-9. The data presented by Vora et al. provide in-depth insight into the means by which the BMP pathway regulates body size, thus offering a whole new set of downstream mechanisms that are potentially interesting to a broad field of researchers. 

The paper is mostly well-researched, and the conclusions are comprehensive and supported by the data presented. However, certain aspects need clarification and potentially extended data. 

(1) The BMP pathway is active during development and growth. Thus, it is logical that the data shown in the study by Vora et al. is based on L2 worms. However, it raises the question of if and how the pattern of transcriptional targets of SMA-3 and SMA-9 changes with age or in the male tail, where the BMP pathway also has been shown to play a role. Is there any data to shed light on this matter or are there any speculations or hypotheses? 

We agree that these are intriguing questions and we are interested in the roles of transcriptional targets at other developmental stages and in other physiological functions, but these analyses are beyond the scope of the current study.

(2) As it was shown that SMA-3 and SMA-9 potentially act in a complex to regulate the transcription of several genes, it would be interesting to know whether the two interact with each other or if the cooperation is more indirect. 

A physical interaction between Smads and Schnurri has been amply demonstrated in other systems. Our goal in this study was not to validate this physical interaction, but to analyze functional interactions on a genome-wide scale.

(3) It would help the understanding of the data even more if the authors could specifically state if there were collagens among the genes regulated by SMA-3 and SMA-9 and which. 

We thank the reviewer for this suggestion and will add the requested information in the text.

(4) The data on the role of SMA-3 and SMA-9 in the regulation of the secretion of collagens from the hypodermis is highly intriguing. The authors use ROL-6 as a reporter for the secretion of collagens. Is ROL-6 a target of SMA-9 or SMA-3? Even if this is not the case, the data would gain even more strength if a comparable quantification of the cuticular levels of ROL-6 were shown in Figure 6, and potentially a ratio of cuticular versus hypodermal levels. By that, the levels of secretion versus production can be better appreciated. 

rol-6 has been identified as a transcriptional target of this pathway. The level of ROL-6 protein, however, is not changed in sma-3 and sma-9 mutants, indicating that there is post-transcriptional compensation. We will include these data in the revised manuscript.

(5) It is known that the BMP pathway controls several processes besides body size. The discussion would benefit from a broader overview of how the identified genes could contribute to body size. The focus of the study is on collagen production and secretion, but it would be interesting to have some insights into whether and how other identified proteins could play a role or whether they are likely to not be involved here (such as the ones normally associated with lipid metabolism, etc.). 

We will add this information to the Discussion.

eLife Assessment

This study provides a fundamental analysis of the EmrE efflux pump, highlighting the role of the C-terminal domain in influencing uncoupled proton leak. The integration of biophysical techniques with molecular dynamics simulations offers solid support for the key findings and adds substantial evidence toward a definitive understanding of EmrE transport mechanism.

Reviewer #1 (Public review):

Summary:

Work by Brosseau et. al. combines NMR, biochemical assays, and MD simulations to characterize the influence of the C-terminal tail of EmrE, a model multi-drug efflux pump, on proton leak. The authors compare the WT pump to a C-terminal tail deletion, delta_107, finding that the mutant has increased proton leak in proteoliposome assays, shifted pH dependence with a new titratable residue, faster alternating access at high pH values, and reduced growth, consistent with proton leak of the PMF.

Strengths:

The work combines thorough experimental analysis of structural, dynamic, and electrochemical properties of the mutant relative to WT proteins. The computational work is well aligned in vision and analysis. Although all questions are not answered, the authors lay out a logical exploration of the possible explanations.

Weaknesses:

A few analyses that were missing in the first submission were included/corrected in the revision.

Reviewer #2 (Public review):

Summary:

This manuscript explores the role of the C-terminal tail of EmrE in controlling uncoupled proton flux. Leakage occurs in the wild-type transporter under certain conditions but is amplified in the C-terminal truncation mutant D107. The authors use an impressive combination of growth assays, transport assays, NMR on WT and mutants with and without key substrates, classical MD, and reactive MD to address this problem. Overall, I think that the claims are well supported by the data, but I am most concerned about the reproducibility of the MD data, initial structures used for simulations, and the stochasticity of the water wire formation. These can all be addressed in a revision with more simulations as I point out below. I want to point out that the discussion was very nicely written, and I enjoyed reading the summary of the data and the connection to other studies very much.

Strengths:

The Henzler-Wildman lab is at the forefront of using quantitative experiments to probe the peculiarities in transporter biophysics, and the MD work from the Voth lab complements the experiments quite well. The sheer number of different types of experimental and computational approaches performed here is impressive.

Weaknesses:

The primary weaknesses are related to the reproducibility of the MD results with regard to the formation of water wires in the WT and truncation mutant. This could be resolved with simulations starting from structures built using very different loops and C-terminal tails.

The water wire gates identified in the MD should be tested experimentally with site-directed mutagenesis to determine if those residues do impact leak.

Comments on revisions:

Having reviewed the latest version of the manuscript, I continue to believe that this is a solid paper with important results. I find the new data regarding the computational pKa estimate of E14 compelling.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Work by Brosseau et. al. combines NMR, biochemical assays, and MD simulations to characterize the influence of the C-terminal tail of EmrE, a model multi-drug efflux pump, on proton leak. The authors compare the WT pump to a C-terminal tail deletion, delta_107, finding that the mutant has increased proton leak in proteoliposome assays, shifted pH dependence with a new titratable residue, faster-alternating access at high pH values, and reduced growth, consistent with proton leak of the PMF.

Strengths:

The work combines thorough experimental analysis of structural, dynamic, and electrochemical properties of the mutant relative to WT proteins. The computational work is well aligned in vision and analysis. Although all questions are not answered, the authors lay out a logical exploration of the possible explanations.

Weaknesses:

There are a few analyses that are missing and important data left out. For example, the relative rate of drug efflux of the mutant should be reported to justify the focus on proton leak. Additionally, the correlation between structural interactions should be directly analyzed and the mutant PMF also analyzed to justify the claims based on hydration alone. Some aspects of the increased dynamics at high pH due to a potential salt bridge are not clear.

Reviewer #2 (Public review):

Summary:

This manuscript explores the role of the C-terminal tail of EmrE in controlling uncoupled proton flux. Leakage occurs in the wild-type transporter under certain conditions but is amplified in the C-terminal truncation mutant D107. The authors use an impressive combination of growth assays, transport assays, NMR on WT and mutants with and without key substrates, classical MD, and reactive MD to address this problem. Overall, I think that the claims are well supported by the data, but I am most concerned about the reproducibility of the MD data, initial structures used for simulations, and the stochasticity of the water wire formation. These can all be addressed in a revision with more simulations as I point out below. I want to point out that the discussion was very nicely written, and I enjoyed reading the summary of the data and the connection to other studies very much.

Strengths:

The Henzler-Wildman lab is at the forefront of using quantitative experiments to probe the peculiarities in transporter biophysics, and the MD work from the Voth lab complements the experiments quite well. The sheer number of different types of experimental and computational approaches performed here is impressive.

Weaknesses:

The primary weaknesses are related to the reproducibility of the MD results with regard to the formation of water wires in the WT and truncation mutant. This could be resolved with simulations starting from structures built using very different loops and C-terminal tails.

The water wire gates identified in the MD should be tested experimentally with site-directed mutagenesis to determine if those residues do impact leak.

We appreciate the reviewers thoughtful consideration of our manuscript, and their recognition of the variety of experimental and computational approaches we have brought to bear in probing the very challenging question of uncoupled proton leak through EmrE.

We did record SSME measurements with MeTPP+, a small molecule substrate at two different protein:lipid ratios. These experiments report the rate of net flux when both proton-coupled substrate antiport and substrate-gated proton leak are possible. We will add this data to the revision, including data acquired with different lipid:protein ratio that confirms we are detecting transport rather than binding. In brief, this data shows that the net flux is highly dependent on both proton concentration (pH) and drug-substrate concentration, as predicted by our mechanistic model. This demonstrates that both types of transport contribute to net flux when small molecule substrates are present.

In the absence of drug-substrate, proton leak is the only possible transport pathway. The pyranine assay directly assesses proton leak under these conditions and unambiguously shows faster proton entry into proteoliposomes through the ∆107-EmrE mutant than through WT EmrE, with the rate of proton entry into ∆107-EmrE proteoliposomes matching the rate of proton entry achieved by the protonophore CCCP. We have revised the text to more clearly emphasize how this directly measures proton leak independently of any other type of transport activity. The SSME experiments with a proton gradient only (no small molecule substrate present) provide additional data on shorter timescales that is consistent with the pyranine data. The consistency of the data across multiple LPRs and comparison of transport to proton leak in the SSME assays further strengthens the importance of the C-terminal tail in determining the rate of flux.

None of the current structural models have good resolution (crystallography, EM) or sufficient restraints (NMR) to define the loop and tail conformations sufficiently for comparison with this work. We are in the process of refining an experimental structure of EmrE with better resolution of the loop and tail regions implicated in proton-entry and leak. Direct assessment of structural interactions via mutagenesis is complicated because of the antiparallel homodimer structure of EmrE. Any point mutation necessarily affects both subunits of the dimer, and mutations designed to probe the hydrophobic gate on the more open face of the transporter also have the potential to disrupt closure on the opposite face, particularly in the absence of sufficient resolution in the available structures. Thus, mutagenesis to test specific predicted structural features is deferred until our structure is complete so that we can appropriately interpret the results.

In our simulation setup, the MD results can be considered representative and meaningful for two reasons. First, the C-terminal tail, not present in the prior structure and thus modeled by us, is only 4 residues long. We will show in the revision and detailed response that the system will lose memory of its previous conformation very quickly, such that velocity initialization alone is enough for a diverse starting point. Second, our simulation is more like simulated annealing, starting from a high free energy state to show that, given such random initialization, the tail conformation we get in the end is consistent with what we reported. It is also difficult to sample back-and-forth tail motion within a realistic MD timescale. Therefore, it can be unconclusive to causally infer the allosteric motions with unbiased MD of the wildtype alone. The best viable way is to look at the equilibrium statistics of the most stable states between WT- and ∆107-EmrE and compare the differences.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The work is well done and well presented. In my opinion, the authors must address the following questions.

(1) It is unclear to a non-SSME-expert, why the net charge translocated in delta_107 is larger than in WT. For such small pH gradients (0.5-1pH unit), it seems that only a few protons would leave the liposome before the internal pH is adjusted to be the same as the external. This number can be estimated given the size of the liposomes. What is it? Once the pH gradient is dissipated, no more net proton transport should be observed. So, why would more protons flow out of the mutant relative to WT?

We appreciate the complexity of both the system and assay and have made revisions to both the main text and SI to address these points more clearly. While we can estimate liposomes size, we cannot easily quantify the number of liposomes on the sensor surface so cannot calculate the amount of charge movement as suggested by the reviewer. We have revised Fig. 3.2 and added additional data at low and high pH with different lipid to protein ratios to distinguish pre-steady state (proton release from the protein) and steady state processes (transport). An extended Fig. 3.2 caption and revised discussion in the main text clarify these points.

We have also revised SI figure 3.2 to include an example of transport driven by an infinite drug gradient. Drug-proton antiport results in net charge build-up in the liposome since two protons will be driven out for every +1 drug transported in. This also creates a pH gradient is created (higher proton concentration outside). The negative inside potential inhibits further antiport of drug. However, both the negative-inside potential and proton gradient will drives protons back into the liposome if there is a leak pathway available. This is clearly visible with a reversal of current negative (antiport) to positive (proton backflow), and the magnitude of this back flow is larger for ∆107-EmrE which lacks the regulatory elements provided by the C-terminal tail. We have amended the main text and SI to include this discussion.

(2) Given the estimated rate of transport, size of liposomes, and pH gradient, how quickly would the SSME liposomes reach pH balance?

Since SSME measurements are due to capacitive coupling and will represent the net charge movement, including pre-steady state contributions, the current values will be incredibly sensitive to individual rates of alternating access, proton and drug on- and off-rates. Time to pH balance would, therefore, differ based on the construct, LPR, absolute pH or drug concentrations as well as the magnitude of the given gradients. For this reason, we necessarily use integrated currents (transported charge over time) when comparing mutants as it reflects kinetic differences inherent to the mutant without over-processing the data, for example, by normalizing to peak currents which would over emphasize certain properties that will differ across mutants. This process allows for qualitative comparisons by subjecting mutants to the same pH and substrate gradients when the same density of transporter construct is present, and care is given to not overstate the importance of the actual quantities of charges that are moving as they will be highly context dependent. This is clearly seen in Fig 3.2 where the current is not zero and the net transported charge is still changing at the end of 1 second. We have amended SI figure 3.2 and the main text to include this discussion.

(3) Given that H110 and E14 would deprotonate when the external pH is elevated above 7 and that these protons would be released to external bulk, the external bulk pH would decrease twice as much for WT compared to delta107. This would decrease the pH gradient for WT relative to the mutant. Can these effects be quantified and accounted for? Would this ostensibly decrease the amount of charge that transfers into the liposomes for WT? How would this impact the current interpretation that the two systems are driven by the same gradient?

The reviewer is correct that there will be differences in deprotonation of WT and ∆107 and the amount of proton release will also change with pH. We have amended Figure 3.2 to clarify this difference and its significance. For the proton gradient only conditions in Figure 3, each set of liposomes were equilibrated to the starting pH by repeated washings and incubation before measurement occurred. For example, for the pH 6.5 inside, pH 7 outside condition, both the inside and outside pH were equilibrated at 6.5, and both E14 residues will be predominantly protonated in WT and ∆107, and H110 will be predominantly protonated in WT-EmrE. Upon application of the external pH 7 solution, protons will be released from the E14 of either construct, with additional proton being released from H110 for WT-EmrE causing a large pre-steady state negative contribution to the signal (Fig. 3.2A). Under this pH condition, we the peak current correlates with the LPR, as this release of protons will depend on density of the transporter. However, we also see that the longer-time decay of the signal correlates with the construct (WT or ∆107) and is relatively independent of LPR, consistent with a transport process rather than a rapid pre-steady state release of protons. Therefore, when we look at the actual transported charge over time, despite the higher contribution of proton release to the WT-EmrE signal, the significant increase in uncoupled proton transport for the C-terminal deletion mutant dominates the signal.

As a contrast, we apply this same analysis to the pH 8 inside, pH 8.5 outside condition where both sets of transports will be deprotonated from the start (Fig. 3.2B). Now the peak currents, decay rates, and transported charge over time are all consistent for a given construct (WT or ∆107). The two LPRs for an individual construct match within error, as the differences in overall charge movement and transported charge over time are independent of pre-steady-state proton release from the transporter at high pH.

(4) A related question, how does the protonation of H110 influence the potential rate of proton transport between the two systems? Does the proton on H110 transfer to E14?

The protonation of H110 will only influence the rate of transport of WT-EmrE as its protonation is required for formation of the hydrogen bonding network that coordinates gating. However, protonation of both E14s will influence the rate of proton transport of both systems as protonation state affects the rate of alternating access which is necessary for proton turnover. This is another reason we use the transported charge over time metric to compare mutants as it allows for a common metric for mutants with altered rates which are present in the same density and under the same gradient conditions. We do not have any evidence to support transfer of proton from H110 to E14, but there is also no evidence to exclude this possibility. We do not discuss this in the manuscript because it would be entirely speculative.

(5) Is the pKa in the simulations (Figure 6B) consistent with the experiment?

We calculated the pKa from this WT PMF and got a pKa of 7.1, which is in close proximity of the experimental value of 6.8

(6) Why isn't the PMF for delta_107 compared to WT to corroborate the prediction that hydration sufficiently alters both the rate and pKa of E14?

We appreciate the reviewer’s suggestion and agree that a direct comparison would be valuable. However, several factors limit the interpretability of such an analysis in this context:

(a) Our data indicate that the primary difference in free energy barriers between WT and Δ107 lies in the hydration step rather than proton transport itself. To fully resolve this, a 2D PMF calculation via 2D umbrella sampling would be required which can be very expensive. Solely looking at the proton transport side of this PMF will not give much difference.

(b) Given this, the aim for us to calculate this PMF is to support our conjecture that the bottleneck for such transport is the hydrophobic gate.

(7) The authors suggest that A61 rotation 'controls the water wire formation' by measuring the distribution of water connectivity (water-water distances via logS) and average distances between A61 and I68/I67. Delta_107 has a larger inter-residue distance (Figure 6A) more probable small log S closer waters connecting E14 and two residues near the top of the protein (Figure 5A). However, it strikes me that looking at average distances and the distribution of log S is not the best way to do this. Why not quantify the correlation between log S and A61 orientation and/or A61-I68/I71 distances as well as their correlation to the proposed tail interactions (D84-R106 interactions) to directly verify the correlation (and suggest causation) of these interactions on the hydration in this region. Additionally, plotting the RMSD or probability of waters below I68 and I171 as a function of A61-I68 distances and/or numbers over time would support the log S analysis.

The reviewer requested that we provide direct correlation analyses between A61 orientation, residue distances (A61-I68/I71), and water connectivity (logS) to better support the claim about water wire formation, rather than relying solely on average distances and distributions.

We appreciate the reviewer’s suggestion to strengthen our analysis with direct correlations. However, due to the slow kinetics of hydration/dehydration events, unbiased simulation timescales do not permit sufficient sampling of multiple transitions to perform statistically robust dynamic correlation analyses. Instead, our approach focuses on equilibrium statistics, which reveal the dominant conformational states of WT- and Δ107-EmrE and provide meaningful insights into shifts in hydration patterns.

(8) It looks like the D84-R106 salt bridge controls this A61-I68 opening. Could this also be quantifiably correlated?

As discussed in response to the previous question, the unbiased simulation timescales do not permit sufficient sampling of multiple transitions to perform statistically robust dynamic correlation analyses.

(9) The NMR results show that alternating access increases in frequency from ~4/s for WT at low and high pH to ~17/s for delta_107 only at high pH. They then go on to analyze potential titration changes in the delta_107 mutant, finding two residues with approximate pKa values of 5.6 and 7.1. The former is assigned to E14, consistent with WT. But the latter is suggested to be either D84, which salt bridges to R106, or the C-terminal carboxylate. If it is D84, why would deprotonation, which would be essential to form the salt bridge, increase the rate of alternating access relative to WT?

We note that the faster alternating access rate was observed for TPP+-bound ∆107-EmrE, not the transporter in the absence of substrate. In the absence of substrate the relatively broad lines preclude quantitative determination of the alternating access rate by NMR making it difficult to judge the validity of the reviewers reasoning. Identification of which residue (D84 or H110) corresponds to the shifted pKa is ultimately of little consequence as this mutant does not reflect the native conditions of the transporter. It is far more important to acknowledge that both R106 and D84 are sensitive to this deprotonation as it indicates these residues are close in space and provides experimental support for the existence of the salt bridge identified in the MD simulations, as discussed in the manuscript.

(10) In a more general sense, can the authors speculate why an efflux pump would evolve this type of secondary gate that can be thrown off by tight binding in the allosteric site such as that demonstrated by Harmane? What potential advantage is there to having a tail-regulated gate?

This was likely a necessity to allow for better coupling as these transporters evolved to be more promiscuous. The C-terminal tail is absent in tightly coupled family members such as Gdx who are specific for a single substrate and have a better-defined transport stoichiometry. We have included this discussion in the main text and are currently investigating this phenomenon further. Those experiments are beyond the scope of the current manuscript.

(11) It is hard to visualize the PT reaction coordinate. Is the e_PT unit vector defined for each window separately based on the initial steered MD pathway? If so, how reliant is the PT pathway on this initial approximate path? Also, how does this position for each window change if/when E14 rotates? This could be checked by plotting the x,y,z distributions for each window and quantifying the overlap between windows in cartesian space. These clouds of distributions could also be plotted in the protein following alignment so the reader can visualize the reaction coordinate. Does the CEC localization ever stray to different, disconnected regions of cartesian phase space that are hidden by the reaction coordinate definition?

The unit vector e_PT is the same across all windows based on unbiased MD. Therefore, the reaction coordinate (a scalar) is the vector from the starting point to the CEC, projected on this unit vector. E14 rotation does not significantly change the window definition a lot unless the CEC is very close to E14, where we found this to be a better CV. For detailed discussions about this CV, especially a comparison between a curvilinear CV, please see J. Am. Chem. Soc. 2018, 140, 48, 16535–16543 “Simulations of the Proton Transport” and its SI Figure S1.In the Supplementary Information, we added figure 6.1 to show the average X, Y, Z coordinates of each umbrella window.

(12) Lastly, perhaps I missed it, but it's unclear if the rate of substrate efflux is also increased in the delta_107 mutant. If this is also increased, then the overall rate of exchange is faster, including proton leak. This would be important to distinguish since the focus now is entirely on proton leaks. I.e., is it only leak or is it overall efflux and leak?

We have amended SI figure 3.2 to include a gradient condition where an infinite drug gradient is created across the liposome. The infinite gradient allows for rapid transport of drug into the liposomes until charge build-up opposes further transport. This peak is at the same time for both LPRs of WT- and ∆107-EmrE suggesting the rate of substrate transport is similar. Differences in the peak heights across LPRs can be attributed to competition between drug and proton for the primary binding site such that more proton will be released for the higher density constructs as described above. This process does also create a proton gradient as drug moving in is coupled to two protons moving out so as charge build-up inhibits further drug movement, the building proton gradient will also begin to drive proton back in which is another example of uncoupled leak. Here, again we see that this back-flow of protons or leak is of greater magnitude for ∆107-EmrE proteoliposomes that for those with WT-EmrE. We have included this discussion in the SI and main text.

Minor

(1) Introduction - the authors describe EmrE as a model system for studying the molecular mechanism of proton-coupled transport. This is a rather broad categorization that could include a wide range of phenomena distal from drug transport across membranes or through efflux pumps. I suggest further specifying to not overgeneralize.

We revised to note the context of multidrug efflux.

Reviewer #2 (Recommendations for the authors):

Simulations. The initial water wire analysis is based on 4 different 1 ms simulations presented in Figure 5. The 3 WT replicates show similar results for the tail-blocking water wire formation, but the details of the system build and loop/C-terminal tail placement are not clear. It does appear that a single C-terminal tail model was created for all WT replicates. Was there also modeling for any parts of the truncation mutant? Regardless, since these initial placements and uncertainties in the structures may impact the results and subsequent water wire formation, I would like a discussion of how these starting structures impacted the formation or not of wires. I think that another WT replicate should be run starting from a completely new build that places the tail in a different (but hopefully reasonable location). This could be built with any number of tools to generate reasonable starting structures. It's critical to ensure that multiple independent simulations across different initial builds show the same water wire behavior so that we know the results are robust and insensitive to the starting structure and stochastic variation.

We thank Reviewer 2 for their suggestion regarding the discussion of the initial structure. In our simulations, the C-terminal tail was initially modeled in an extended conformation (solvent-exposed) to mimic its disordered state prior to folding. This approach resembles an annealing process, where the system evolves from a higher free-energy state toward equilibrium. Notably, across all three replicas, we observed consistent folding of the tail onto the protein surface, supporting the robustness of this conformational preference.

For the Δ107 truncation mutant, minimal modeling was required, as most experimental structures resolve residues up to S105 or R106. To rigorously assess the influence of the starting configuration, we analyzed the tail’s dynamics using backbone dihedral angle auto- and cross-correlation functions (new Supplementary Figures 10.1 and 10.2). These analyses reveal rapid decay of correlations—consistent with the tail’s short length (5 residues) and high flexibility—indicating that the system "forgets" its initial configuration well within the simulation timescale. Thus, we conclude that our sampling is sufficient to capture equilibrium behavior, independent of the starting structure.

What does the size of the barrier in the PMF (Figure 6B) imply about the rate of proton transfer/leak and can the pKa shift of the acidic residue be estimated with this energy value compared to bulk?

We noticed this point aligns with a related concern raised by Reviewer 1. For a detailed discussion please refer to Point 5 in our response to Reviewer 1.

Experimental validation. The hypotheses generated by this work would be better buttressed if there were some mutation work at the hydrophobic gate (61, 68, 71) to support it. I realize that this may be hard, but it would significantly improve the quality.

Due to the small size of the transporter, any mutagenesis of EmrE should necessarily be accompanied by functional characterization to fully assess the effects of the mutation on rate-limiting steps. We have revised the manuscript to add a discussion of the challenges with analyzing simple point mutants and citing what is known from prior scanning mutagenesis studies of EmrE.

eLife Assessment

This fundamental study investigates the role of polyunsaturated fatty acids (PUFAs) in physiology and membrane biology, using a unique model to perform a thorough genetic screen that demonstrates that PUFA synthesis defects cannot be compensated for by mutations in other pathways. These findings are supported by compelling evidence from a high quality genetic screen, functional validation of their hits, and lipid analyses. This study will appeal to researchers in membrane biology, lipid metabolism, and C. elegans genetics.

Reviewer #1 (Public review):

Summary:

This study addresses the roles of polyunsaturated fatty acids (PUFAs) in animal physiology and membrane function. A C. elegans strain carrying the fat-2(wa17) mutation possesses a very limited ability to synthesize PUFAs and there is no dietary input because the E. coli diet consumed by lab grown C. elegans does not contain any PUFAs. The fat-2 mutant strain was characterized to confirm that the worms grow slowly, have rigid membranes, and have a constitutive mitochondrial stress response. The authors showed that chemical treatments or mutations known to increase membrane fluidity did not rescue growth defects. A thorough genetic screen was performed to identify genetic changes to compensate for the lack of PUFAs. The newly isolated suppressor mutations that compensated for FAT-2 growth defects included intergenic suppressors in the fat-2 gene, as well as constitutive mutations in the hypoxia sensing pathway components EGL-9 and HIF-1, and loss of function mutations in ftn-2, a gene encoding the iron storage protein ferritin. Taken together, these mutations lead to the model that increased intracellular iron, an essential cofactor for fatty acid desaturases, allows the minimally functional FAT-2(wa17) enzyme to be more active, resulting in increased desaturation and increased PUFA synthesis.

Strengths:

(1) This study provides new information further characterizing fat-2 mutants. The authors measured increased rigidity of membranes compared to wild type worms, however this rigidity is not able to be rescued with other fluidity treatments such as detergent or mutants. Rescue was only achieved with polyunsaturated fatty acid supplementation.

(2) A very thorough genetic suppressor screen was performed. In addition to some internal fat-2 compensatory mutations, the only changes in pathways identified that are capable of compensating for deficient PUFA synthesis was the hypoxia pathway and the iron storage protein ferritin. Suppressor mutations included an egl-9 mutation that constitutively activates HIF-1, and Gain of function mutations in hif-1 that are dominant. This increased activity of HIF conferred by specific egl-9 and hif-1 mutations lead to decreased expression of ftn-2. Indeed, loss of ftn-2 leads to higher intracellular iron. The increased iron apparently makes the FAT-2 fatty acid desaturase enzyme more active, allowing for the production of more PUFAs.

(3) The mutations isolated in the suppressor screen show that the only mutations able to compensate for lack of PUFAs were ones that increased PUFA synthesis by the defective FAT-2 desaturase, thus demonstrating the essential need for PUFAs that cannot be overcome by changes in other pathways. This is a very novel study, taking advantage of genetic analysis of C. elegans, and it confirms the observations in humans that certain essential PUFAs are required for growth and development.

(4) Overall, the paper is well written, and the experiments were carried out carefully and thoroughly. The conclusions are well supported by the results.

Weaknesses:

Overall, there are not many weaknesses. The main one I noticed is that the lipidomic analysis shown in Figs 3C, 7C, S1 and S3. While these data are an essential part of the analysis and provide strong evidence for the conclusions of the study, it is unfortunate that the methods used did not enable the distinction between two 18:1 isomers. These two isomers of 18:1 are important in C. elegans biology, because one is a substrate for FAT-2 (18:1n-9, oleic acid) and the other is not (18:1n-7, cis vaccenic acid). Although rarer in mammals, cis-vaccenic acid is the most abundant fatty acid in C. elegans and is likely the most important structural MUFA. The measurement of these two isomers is not essential for the conclusions of the study.

Reviewer #2 (Public review):

Summary:

The authors use a genetic screen in C. elegans to investigate the physiological roles of polyunsaturated fatty acids (PUFAs). They screen for mutations that rescue fat-2 mutants, which have strong reductions in PUFAs. As a result, either mutations in fat-2 itself or mutations in genes involved in the HIF-1 pathway were found to rescue fat-2 mutants. Mutants in the HIF-1 pathway rescue fat-2 mutants by boosting their catalytic activity (via upregulated Fe2+). Thus, the authors show that in the context of fat-2 mutation, the sole genetic means to rescue PUFA insufficiency is to restore PUFA levels.

Strengths:

As C. elegans can produce PUFAs de novo as essential lipids, the genetic model is well-suited to study the fundamental roles of PUFAs. The genetic screen finds mutations in convergent pathways, suggesting that it has reached near-saturation. The authors extensively validate the results of the screening and provide sufficient mechanistic insights to show how PUFA levels are restored in HIF-1 pathway mutants. As many of the mutations found to rescue fat-2 mutants are of gain-of-function, it is unlikely that similar discoveries could have been made with other approaches like genome-wide CRISPR screenings, making the current study distinctive. Consequently, the study provides important messages. First, it shows that PUFAs are essential for life. The inability to genetically rescue PUFA deficiency, except for mutations that restore PUFA levels, suggests that they have pleiotropic essential functions. In addition, the results suggest that the most essential functions of PUFAs are not in fluidity regulation, which is consistent with recent reviews proposing that the importance of unsaturation goes beyond fluidity (doi: 10.1016/j.tibs.2023.08.004 and doi: 10.1101/cshperspect.a041409). Thus, the study provides fundamental insights about how membrane lipid composition can be linked to biological functions.

Weaknesses:

The authors put in a lot of effort to answer the questions that arose through peer review, and now all the claims seem to be supported by experimental data. Thus, I do not see obvious weaknesses. Of course, it remains unclear what PUFAs do beyond fluidity regulation, but this is something that cannot be answered from a single study.

Author response:

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

Reviewer #1:

The addition of the discussion about the two isomers of 18:1 didn't quite work in the place that the authors added. What the authors wrote on line 126 is true about 18:1 isomers in wild type worms. However, they are reporting their lipidomics results of the fat-2(wa17) mutant worms. In this case, a substantial amount of the 18:1 is the oleic acid (18:1n-9) isomer. The authors can check Table 2 in their reference [10] and see that wild type and other fat mutants indeed contain approximately 10 fold more cis vaccenic than oleic acid, the fat-2(wa17) mutants do accumulate oleic acid, because the wild type activity of FAT-2 is to convert oleic acid to linoleic acid, where it can be converted to downstream PUFAs. I suggest editing their sentence on line 126 to say that the high 18:1 they observed agrees with [10], and then comment about reference 10 showing the majority of 18:1 being the cis-vaccenic isomer in most strains, but the oleic acid isomer is more abundantly in the fat-2(wa17) mutant strain.

We thank the reviewer for spotting that and sparing us a bit of embarrassment. We have now modified the text and hope we got it right this time:

"Even though the lipid analysis methods used here are not able to distinguish between different 18:1 species, a previous study showed that the majority of the 18:1 fatty acids in the fat-2(wa17) mutant is actually 18:1n9 (OA) [10] and not 18:1n7 (vaccenic acid) as in most other strains [10,23]; this is because OA is the substrate of FAT-2 and thus accumulates in the mutant."

Reviewer #2:

I still do not agree with the answer to my previous comment 6 regarding Figure S2E. The authors claim that hif-1(et69) suppresses fat-2(wa17) in a ftn-2 null background (in Figure S2 legend for example). To claim so, they would need to compare the triple mutant with fat2(wa17);ftn-2(ok404) and show some rescue. However, we see in Figure 5H that ftn2(ok404) alone rescues fat-2(wa17). Thus, by comparing both figures, I see no additional effect of hif-1(et69) in an ftn-2(ok404) background. I actually think that this makes more sense, since the authors claim that hif-1(et69) is a gain-of-function mutation that acts through suppression of ftn-2 expression. Thus, I would expect that without ftn-2 from the beginning, hif-1(et69) does not have an additional effect, and this seems to be what we see from the data. Thus, I would suggest that the authors reformulate their claims regarding the effect of hif1(et69) in the ftn-2(ok404) background, which seems to be absent (consistently with what one would expect).

We completely agree with the reviewer and indeed this is the meaning that we tried to convey all along. The text has now been modified as follows:

"Lastly, ftn-2(et68) is still a potent fat-2(wa17) suppressor when hif-1 is knocked out (S2D Fig), suggesting that no other HIF-1-dependent functions are required as long as ftn-2 is downregulated; this conclusion is supported by the observation that the potency of the ftn2(ok404) null allele to act as a fat-2(wa17) suppressor is not increased by including the hif-1(et69) allele (compare Fig 5H and S2E Fig)."

eLife Assessment

The authors design and implement an elegant strategy to delete genomic sequences encoding the dopamine receptor dop1R2 from specific subsets of mushroom body neurons (ab, a'b' and gamma) and show that while none of these manipulations affect short term appetitive or aversive memory, loss of dop1R2 from ab or a'b' block the ability of flies to display measurable forms of longer forms of memory. These findings are important in confirming and extending prior observations, and well supported by convincing evidence that build on precise techniques for genetic perturbation.

Reviewer #1 (Public review):

Summary:

In this manuscript the authors present a novel CRISPR/Cas9-based genetic tool for the dopamine receptor dop1R2. Based on the known function of the receptor in learning and memory, they tested the efficacy of the genetic tool by knocking out the receptor specifically in mushroom body neurons. The data suggest that dop1R2 is necessary for longer lasting memories through its action on ⍺/ß and ⍺'/ß' neurons but is dispensable for short-term memory and thus in ɣ neurons. The experiments impressively demonstrate the value of such a genetic tool and illustrate the specific function of the receptor in subpopulations of KCs for longer-term memories.

Reviewer #2 (Public review):

Summary:

This manuscript examines the role of the dopamine receptor, Dop1R2, in memory formation. This receptor has complex roles in supporting different stages of memory, and the neural mechanisms for these functions is poorly understood. The authors are able to localize Dop1R2 function to the vertical lobes of the mushroom body, revealing a role in later (presumably middle-term) aversive and appetitive memory. In general the experimental design is rigorous, and statistics are appropriately applied. The manuscript provides a thorough assessment of how Dop1R2 functions within the mushroom bodies to regulate protein-synthesis dependent and independent memory, and provides a valuable new tool for the community.

Strengths:

(1) The FRT lines generated provide a novel tool for temporal and spatially precise manipulation of Dop1R2 function. This tool will be valuable to study the role of Dop1R2 in memory and other behaviors potentially regulated by this gene.

(2) Given the highly conserved role of Dop1R2 in memory and other processes, these findings have high potential to translate to vertebrate species.

Reviewer #3 (Public review):

Summary:

Kaldun et al. investigated the role of Dopamine Receptor Dop1R2 in different types and stages of olfactory associative memory in Drosophila melanogaster. Dop1R2 is a type 1 Dopamine receptor that can act both through Gs-cAMP and Gq-ERCa2+ pathways. The authors first developed a sophisticated tool where tissue-specific knock-out mutants can be generated using Crispr/Cas9 technology in combination with the Gal4/UAS gene-expression toolkit. They direct the K.O. mutation to intrinsic neurons of the main associative memory centre fly brain: the mushroom body (MB). There are three main types of MB-neurons, or Kenyon cells, according to their axonal projections: a/b; a'/b' and g neurons.

Kaldun et al. found that, while not required for short-term memory, dop1R2 is necessary in a/b and a'/b' but not in gamma neurons to display normal appetitive and aversive middle-term (2h) and long-term (24h) memory. These results showcase a compartmentalized role of Dop1R2 in specific neuronal subtypes of the main memory centre of the fly brain for the expression of middle and long-term memories.

The conclusions of this paper are very well supported by the data, and the authors systematically addressed the requirement of a very interesting type of dopamine receptor in both appetitive and aversive memories. These findings are important for the fields of learning and memory and dopaminergic neuromodulation, among others.

Importantly, the authors of this paper produced a tool to generate tissue-specific knock out mutants of dop1R2. Although reports on the requirement of this gene in different memory phases exist, the genetic tools used here represent the most sophisticated approach to induce a loss of function phenotypes in neurons of interest.

Overall, the authors generated a very useful tool to study dopamine neuromodulation in any given circuit when used in combination with the powerful genetic toolkit available in Drosophila. The reports on this paper confirmed a previously described role of Dop1R2 in the expression of aversive and appetitive LTM providing spatio-temporal resolution and additionally, they mapped these effects to two types of memory neurons in the fly brain, shedding light into the intricate modulation of dopamine in memory circuits.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors present a novel CRISPR/Cas9-based genetic tool for the dopamine receptor dop1R2. Based on the known function of the receptor in learning and memory, they tested the efficacy of the genetic tool by knocking out the receptor specifically in mushroom body neurons. The data suggest that dop1R2 is necessary for longer-lasting memories through its action on ⍺/ß and ⍺'/ß' neurons but is dispensable for short-term memory and thus in ɣ neurons. The experiments impressively demonstrate the value of such a genetic tool and illustrate the specific function of the receptor in subpopulations of KCs for longer-term memories. The data presented in this manuscript are significant.

Reviewer #2 (Public Review):

Summary:

This manuscript examines the role of the dopamine receptor, Dop1R2, in memory formation. This receptor has complex roles in supporting different stages of memory, and the neural mechanisms for these functions are poorly understood. The authors are able to localize Dop1R2 function to the vertical lobes of the mushroom body, revealing a role in later (presumably middle-term) aversive and appetitive memory. In general, the experimental design is rigorous, and statistics are appropriately applied. While the manuscript provides a useful tool, it would be strengthened further by additional mechanistic studies that build on the rich literature examining the roles of dopamine signaling in memory formation. The claim that Dop1R2 is involved in memory formation is strongly supported by the data presented, and this manuscript adds to a growing literature revealing that dopamine is a critical regulator of olfactory memory. However, the manuscript does not necessarily extend much beyond our understanding of Dop1R2 in memory formation, and future work will be needed to fully characterize this reagent and define the role of Dop1R2 in memory.

Strengths:

(1) The FRT lines generated provide a novel tool for temporal and spatially precise manipulation of Dop1R2 function. This tool will be valuable to study the role of Dop1R2 in memory and other behaviors potentially regulated by this gene.

(2) Given the highly conserved role of Dop1R2 in memory and other processes, these findings have a high potential to translate to vertebrate species.

Weaknesses:

(1) The authors state Dop1R2 associates with two different G-proteins. It would be useful to know which one is mediating the loss of aversive and appetitive memory in Dop1R2 knockout flies.

We thank you for the insightful comment. We agree that it would be very useful to know which G-proteins are transmitting Dop1R2 signaling. To that extent, we examined single-cell transcriptomics data to check the level of co-expression of Dop1R2 with G-proteins that are of interest to us. (Figure 1 S1)

Lines 312-325

“Some RNA binding proteins and Immediate early genes help maintain identities of Mushroom body cells and are regulators of local transcription and translation (de Queiroz et al., 2025; Raun et al., 2025). So, the availability of different G-proteins may change in different lobes and during different phases of memory. The G-protein via which GPCRs signal, may depend on the pool of available G-proteins in the cell/sub-cellular region (Hermans, 2003)., Therefore, Dop1R2 may signal via different G-proteins in different compartments of the Mushroom body and also different compartments of the neuron. We looked at Gαo and Gαq as they are known to have roles in learning and forgetting (Ferris et al., 2006; Himmelreich et al., 2017). We found that Dop1R2 co-expresses more frequently with Gαo than with Gαq (Figure 1 S1). While there is evidence for Dop1R2 to act via Gαq (Himmelreich et al., 2017). It is difficult to determine whether this interaction is exclusive, or if Dop1R2 can also be coupled to other G-proteins. It will be interesting to determine the breadth of G-proteins that are involved in Dop1R2 signaling.”

(2) It would be interesting to examine 24hr aversive memory, in addition to 24hr appetitive memory.

This is indeed an important point and we agree that it will complete the assessment of temporally distinct memory traces. We therefore performed the Aversive LTM experiments and include them in the results.

Lines 208-228

“24h memory is impaired by loss of Dop1R2

Next, we wanted to see if later memory forms are also affected. One cycle of reward training is sufficient to create LTM (Krashes & Waddell, 2008), while for aversive memory, 5-6 cycles of electroshock-trainings are required to obtain robust long-term memory scores (Tully et al., 1994). So, we looked at both, 24h aversive and appetitive memory. For aversive LTM, the flies were tested on the Y-Maze apparatus as described in (Mohandasan et al., (2022).

Flipping out Dop1R2 in the whole MB causes a reduced 24h memory performance (Figure 4A, E). No phenotype was observed when Ddop1R2 was flipped out in the γ-lobe (Figure 4B, F). However, similar to 2h memory, loss of Ddop1R2 in the α/β-lobes (Figure 4C, G) or the α’/β’-lobes (Figure 4D, H) causes a reduction in memory performance. Thus, Dop1R2 seems to be involved in aversive and appetitive LTM in the α/β-lobes and the α’/β’-lobes.

Previous studies have shown mutation in the Dop1R2 receptor leads to improvement in LTM when a single shock training paradigm is used (Berry et al., 2012). As we found that it disrupts LTM, we wanted to verify if the absence of Dop1R2 outside the MB is what leads to an improvement in memory. To that extent, we tested panneuronal flip-out of Dop1R2 flies for 6hr and 24hr memory upon single shock using the elav-Gal4 driver. We found that it did not improve memory at both time points (Figure 4 S1). Confirming that flipping out Dop1R2 panneuronally does not improve LTM (Figure 4 S1C) and highlighting its irrelevance in memory outside the MB.”

(3) The manuscript would be strengthened by added functional analysis. What are the DANs that signal through Dop1R. How do these knockouts impact MBONs?

We thank you for this question. We indeed agree that it is a highly relevand and open question, how distinct DANs signal via distinct Dopamine receptors. Our work here uniquely focusses on Dop1R2 within the MB. We aim to investigate other DopRs and the connection between DANs in the future using similar approaches.

(4) Also in Figure 2, the lobe-specific knockouts might be moved to supplemental since there is no effect. Instead, consider moving the control sensory tests into the main figure.

We thank you for this suggestion and understand that in Figure 2 no significant difference is seen. However, we have emphasized in the text that the results from the supplementary figures are just to confirm that the modifications made at the Dop1R2 locus did not alter its normal function.

Lines 156-162

“We wanted to see if flipping out Dop1R2 in the MB affects memory acquisition and STM by using classical olfactory conditioning. In short, a group of flies is presented with an odor coupled to an electric shock (aversive) or sugar (appetitive) followed by a second odor without stimulus. For assessing their memory, flies can freely choose between the odors either directly after training (STM) or at a later timepoint.

To ensure that the introduced genetic changes to the Dop1R2 locus do not interfere with behavior we first checked the sensory responses of that line”

(5) Can the single-cell atlas data be used to narrow down the cell types in the vertical lobes that express Dop1R2? Is it all or just a subset?

This is indeed an interesting question, and we thank you for mentioning it. To address this as best as we could, we analyzed the single cell transcriptomic data from (Davie et al., 2018) and presented it in Figure 1 S1.

Reviewer #3 (Public Review):

Summary:

Kaldun et al. investigated the role of Dopamine Receptor Dop1R2 in different types and stages of olfactory associative memory in Drosophila melanogaster. Dop1R2 is a type 1 Dopamine receptor that can act both through Gs-cAMP and Gq-ERCa2+ pathways. The authors first developed a very useful tool, where tissue-specific knock-out mutants can be generated, using Crispr/Cas9 technology in combination with the powerful Gal4/UAS gene-expression toolkit, very common in fruit flies.

They direct the K.O. mutation to intrinsic neurons of the main associative memory centre fly brain-the mushroom body (MB). There are three main types of MB-neurons, or Kenyon cells, according to their axonal projections: a/b; a'/b', and g neurons.

Kaldun et al. found that flies lacking dop1R2 all over the MB displayed impaired appetitive middle-term (2h) and long-term (24h) memory, whereas appetitive short-term memory remained intact. Knocking-out dop1R2 in the three MB neuron subtypes also impaired middle-term, but not short-term, aversive memory.

These memory defects were recapitulated when the loss of the dop1R2 gene was restricted to either a/b or a'/b', but not when the loss of the gene was restricted to g neurons, showcasing a compartmentalized role of Dop1R2 in specific neuronal subtypes of the main memory centre of the fly brain for the expression of middle and long-term memories.

Strengths:

(1) The conclusions of this paper are very well supported by the data, and the authors systematically addressed the requirement of a very interesting type of dopamine receptor in both appetitive and aversive memories. These findings are important for the fields of learning and memory and dopaminergic neuromodulation among others. The evidence in the literature so far was generated in different labs, each using different tools (mutants, RNAi knockdowns driven in different developmental stages...), different time points (short, middle, and long-term memory), different types of memories (Anesthesia resistant, which is a type of protein synthesis independent consolidated memory; anesthesia sensitive, which is a type of protein synthesis-dependent consolidated memory; aversive memory; appetitive memory...) and different behavioral paradigms. A study like this one allows for direct comparison of the results, and generalized observations.

(2) Additionally, Kaldun and collaborators addressed the requirement of different types of Kenyon cells, that have been classically involved in different memory stages: g KCs for memory acquisition and a/b or a'/b' for later memory phases. This systematical approach has not been performed before.

(3) Importantly, the authors of this paper produced a tool to generate tissue-specific knock-out mutants of dop1R2. Although this is not the first time that the requirement of this gene in different memory phases has been studied, the tools used here represent the most sophisticated genetic approach to induce a loss of function phenotypes exclusively in MB neurons.

Weaknesses:

(1) Although the paper does have important strengths, the main weakness of this work is that the advancement in the field could be considered incremental: the main findings of the manuscript had been reported before by several groups, using tissue-specific conditional knockdowns through interference RNAi. The requirement of Dop1R2 in MB for middle-term and long-term memories has been shown both for appetitive (Musso et al 2015, Sun et al 2020) and aversive associations (Plaçais et al 2017).

Thank you for this comment. We believe that the main takeaway from the paper is the elegant tool we developed, to study the role of Dop1R2 in fruit flies by effectively flipping it out spatio-temporally. Additionally, we studied its role in all types of olfactory associative memory to establish it as a robust tool that can be used for further research in place of RNAi knockouts which are shown to be less efficient in insects as mentioned in the texts in line 394-398.

“The genetic tool we generated here to study the role of the Dop1R2 dopamine receptor in cells of interest, is not only a good substitute for RNAi knockouts, which are known to be less efficient in insects (Joga et al., 2016), but also provides versatile possibilities as it can be used in combination with the powerful genetic tools of Drosophila.”

(2) The approach used here to genetically modify memory neurons is not temporally restricted. Considering the role of dopamine in the correct development of the nervous system, one must consider the possible effects that this manipulation can have in the establishment of memory circuits. However, previous studies addressing this question restricted the manipulation of Dop1R2 expression to adulthood, leading to the same findings than the ones reported in this paper for both aversive and appetitive memories, which solidifies the findings of this paper.

We thank you for this comment and we agree that it would be important to show a temporally restricted effect of Dop1R2 knockout. To assess this and rule out potential developmental defects we decided to restrict the knockout to the post-eclosion stage and to include these results.

Lines 230-250

“Developmental defects are ruled out in a temporally restricted Dop1R2 conditional knockout.

To exclude developmental defects in the MB caused by flip-out of Dop1R2, we stained fly brains with a FasII antibody. Compared to genetic controls, flies lacking Dop1R2 in the mushroom body had unaltered lobes (Figure 4 S2C).

Regardless, we wanted to control for developmental defects leading to memory loss in flip-out flies. So, we generated a Gal80ts-containing line, enabling the temporal control of Dop1R2 knockout in the entire mushroom body (MB). Given that the half-life of the receptor remains unknown, we assessed both aversive short-term memory (STM) and long-term memory (LTM) to determine whether post-eclosion ablation of Dop1R2 in the MB produced differences compared to our previously tested line, in which Dop1R2 was constitutively knocked out from fertilization. To achieve this, flies were maintained at 18°C until eclosion and subsequently shifted to 30°C for five to seven days. On the fifth day, training was conducted, followed by memory testing. Our results indicate that aversive STM was not significantly impaired in Dop1R2-deficient MBs compared to control flies (Figure 4 S3), consistent with our previous findings (Figure 2). However, aversive LTM was significantly impaired relative to control lines (Figure 4 S3), which also aligned with prior observations. These findings strongly indicate that memory loss caused by Dop1R2 flip-out is not due to developmental defects.”

(3) The authors state that they aim to resolve disparities of findings in the field regarding the specific role of Dop1R2 in memory, offering a potent tool to generate mutants and addressing systematically their effects on different types of memory. Their results support the role of this receptor in the expression of long-term memories, however in the experiments performed here do not address temporal resolution of the genetic manipulations that could bring light into the mechanisms of action of Dop1R2 in memory. Several hypotheses have been proposed, from stabilization of memory, effects on forgetting, or integration of sequences of events (sensory experiences and dopamine release).

We thank you for this comment. We agree that it would be interesting to dissect the memory stages by knocking out the receptor selectively in some of them (encoding, consolidation, retrieval). However, our tool irreversibly flips out Dop1R2 preventing us from investigating the receptor’s role in retrieval. Our results show that the receptor is dispensable for STM formation (Figure 2, Figure 4 Supplement 3), suggesting that it is not involved in encoding new information. On the other hand, it is instead involved in consolidation and/or retrieval of long-term and middle-term memories (Figure 3, Figure 4, Figure 5B).

Overall, the authors generated a very useful tool to study dopamine neuromodulation in any given circuit when used in combination with the powerful genetic toolkit available in Drosophila. The reports in this paper confirmed a previously described role of Dop1R2 in the expression of aversive and appetitive LTM and mapped these effects to two specific types of memory neurons in the fly brain, previously implicated in the expression and consolidation of long-term associative memories.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) On the first view, the results shown here are different from studies published earlier, while in the same line with others (e.g. Sun et al, for appetitive 24h memories). For example, Berry et al showed that the loss of dop1R2 impairs immediate memory, while memory scores are enhanced 3h, 6h, and 24h after training. Further, they showed data that shock avoidance, at least for higher shock intensities, is reduced in mutant (damb) flies. All in all, this favors how important it is to improve the genetic tools for tissue-specific manipulation. Despite the authors nicely discussing their data with respect to the previous studies, I wondered whether it would be suitable to use the new tool and knock out dop1R2 panneuronally to see whether the obtained data match the results published by Berry et al.. Further, as stated in line 105ff: "As these studies used different learning assays - aversive and appetitive respectively as well as different methods, it is unclear if Dop1R2 has different functions for the different reinforcement stimulus" I wondered why the authors tested aversive and appetitive learning for STM and 2h memory, but only appetitive memory for 24h.

Thank you for this comment. To that extent, as mentioned above in response to reviewer #2, we included in the results the aversive LTM experiment (Figure 4). Moreover, we performed experiments along the line of Berry et al. using our tool as shown in Figure 4 S1. Our results support that Dop1R2 is required for LTM, rather than to promote forgetting.

(2) Line 165ff: I can´t find any of the supplementary data mentioned here. Please add the corresponding figures.

Thank you for pointing this out. In that line we don’t refer to any supplementary data, but to the Figure 1F, showing the absence of the HA-tag in our MB knock-out line. We have clarified this in the text (lines 151-153)

(3) I can't imagine that the scale bar in Figure 1D-F is correct. I would also like to suggest to show a more detailed analysis of the expression pattern. For example, both anterior and posterior views would be appropriate, perhaps including the VNC. This would allow the expression pattern obtained with this novel tool to be better compared with previously published results. Also, in relation to my comment above (1), it may help to understand the functional differences with previous studies, especially as the authors themselves state that the receptor is "mainly" expressed in the mushroom body (line 99). It would be interesting to see where else it is expressed (if so). This would also be interesting for the panneuronal knockdown experiment suggested under (1). If the receptor is indeed expressed outside the mushroom body, this may explain the differences to Berry et al.

Thank you for noting this, there was indeed a mistake in the scale bar which we now fixed. Since with our HA-tag immunostaining we could not detect any noticeable signal outside of the MB, we decided to analyze previously existing single cell transcriptomics data that showed expression of the receptor in 7.99% of cells in the VNC and in 13.8% of cells outside the MB (lines 98-100) confirming its sparse expression in the nervous system. The lack of detection of these cells is likely due to the sparse and low expression of the protein. The HA-tag allows to detect the endogenous level of the locus (it is possible that a Gal4/UAS amplification of the signal might allow to detect these cells).

Regarding the panneuronal knockout, we decided to try to replicate the experiment shown in Berry et al. in Figure 4 S1 and found that Dop1R2 is required for LTM.

(4) Related to learning data shown in Figures 2-4, the authors should show statistical differences between all groups obtained in the ANOVA + PostHoc tests. Currently, only an asterisk is placed above the experimental group, which does not adequately reflect the statistical differences between the groups. In addition, I would like to suggest adding statistical tests to the chance level as it may be interesting to know whether, for example, scores of knockout flies in 3C and 3D are different from the chance level.

Many thanks for this correction, we agree with the fact that the way significance scores were shown was not informative enough. We fixed the point by now showing significance between all the control groups and the experimental ones. We also inserted the chance level results in the figure legends.

(5) Unfortunately, the manuscript has some typing errors, so I would like to ask the authors to check the manuscript again carefully.

Some Examples:

Line 31: the the

Line 56: G-Protein

Line 64: c-AMP

Line 68: Dopamine

Line 70: G-Protein (It alternates between G-protein and G-Protein)

Line 76: References are formatted incorrectly

Line 126: Ha-Tag (It alternates between Ha and HA)

Line 248: missing space before the bracket...is often found

Thank you for noticing these errors, we have now corrected the spelling throughout the manuscript.

(6) In the figures the axes are labelled Preference Index (Pref"I"). In the methods, however, the calculation formula is defined as "PREF".

We thank you for drawing attention to this. To avoid confusion, we changed the definition in the methods section so that it could be clear and coherent (“Memory tests” paragraph in the methods section).

“PREF = ((N_arm1 - N_arm2) 100) / N_total the two preference indices were calculated from the two reciprocal experiments. The average of these two PREFs gives a learning index (LI). LI = (PREF₁ + PREF₂) / 2.

In case of all Long-term Aversive memory experiments, Y-Maze protocol was adapted to test flies 24 hours post training. Testing using the Y-Maze was done following the protocol as described in (Mohandasan et al., 2022) where flies were loaded at the bottom of 20-minutes odorized 3D-printed Y-Mazes from where they would climb up to a choice point and choose between the two odors. The learning index was then calculated after counting the flies in each odorized vial as follows: LI = ((N_CS- - N_CS+) 100) / N_total. Where NCS- and NCS+ are the number of flies that were found trapped in the untrained and trained odor tube respectively.

Reviewer #2 (Recommendations For The Authors):

(1) In Figures 2 and 3, the legends running two different subfigures is confusing. Would be helpful to find a different way to present.

Thank you for your suggestion. We modified how we present legends, placing them vertically so that it is clearer.

(2) Use additional drivers to verify middle and long-term memory phenotypes.

We agree that it would be interesting to see the role of Dop1R2 in other neurons. To that extent, we looked at long term aversive memory in flies where the receptor was panneuronaly flipped out, and did not find evidence that suggested involvement of Dop1R2 in memory processes outside the MB. (Figure 4 S1)

(3) Additional discussion of genetic background for fly lines would be helpful.

Thank you for your advice. We have mentioned the genetic background of flies in the key resources table of the methods sections. Additionally, we also included further explanation on how the lines were created and their genetic background (see “Fly Husbandry” paragraph in the methods section).

“UAS-flp;;Dop1R2 cko flies and Gal4;Dop1R2^cko flies were crossed back with ;;Dop^cko flies to obtain appropriate genetic controls which were heterozygous for UAS and Gal4 but not Dop1R2^cko.”

Reviewer #3 (Recommendations For The Authors):

Line 109 states that to resolve the problem a tool is developed to knock down Dop1R2 in s spatial and temporal specific manner- while I agree that this is within the potential of the tool, there is no temporal control of the flipase action in this study; at least I cannot find references to the use of target/gene switch to control stages of development or different memory phases. However the version available for download is missing supplementary information, so I did not have access to supplementary figures and tables.

Thank you for the comment, as mentioned before it would be great to be able to dissect the memory phases. We show in lines 232 – 250 and Figure 4 S3 that the temporally restricted flip-out to the post-eclosion life stage gave us coherent results with the previous findings, ruling out potential developmental defects.

In relation to my comment on the possible developmental effects of the loss of the gene, Figure 1F could showcase an underdeveloped g lobe when looking at the lobe profiles. I understand this is not within the scope of the figure, but maybe a different z projection can be provided to confirm there are no obvious anatomical alterations due to the loss of the receptor.

We understand the doubt about the correct development of the MB and we thank you for your insightful comment. To that extent we decided to perform a FasII immunostaining that could show us the MB in the different lines (Figure 4 S2) and it appears that there are no notable differences in the lobes development in our knockout line.

It seems that the obvious missing piece of the puzzle would be to address the effects of knocking out Dop1R2 in aversive LTM. The idea of systematically addressing different types of memory at different time points and in different KCs is the most attractive aspect of this study beyond the technical sophistication, and it feels that the aim of the study is not delivered without that component.

We agree and we thank you for the clarification. As mentioned above in response to Reviewer #2, we decided to test aversive LTM as described in lines –208-228, Figure 4, Figure 4 S1.

Some statements of the discussion seem too vague, and I think could benefit from editing:

Line 284 "however other receptors could use Gq and mediate forgetting"- does this refer to other dopamine receptors? Other neuromodulators? Examples?

Thank you for pointing this out. We Agree and therefore decided to omit this line.

Line 289 "using a space training protocol and a Dop1R2 line" - this refers to RNAi lines, but it should be stated clearly.

That is correct, we thank you for bringing attention to this and clarified it in the manuscript.

–Lines 329-330

“Interestingly, using a spaced training protocol and a Dop1R2 RNAi knockout line another study showed impaired LTM (Placais et al., 2017).”

The paragraph starting in line 305 could be re-written to improve clarity and flow. Some statements seem disconnected and require specific citations. For example "In aversive memory formation, loss of Dop1R2 could lead to enhanced or impaired memory, depending on the activated signaling pathways and the internal state of the animal...". This is not accurate. Berry et al 2012 report enhanced LTM performance in dop1R2 mutants whereas Plaçais et al 2017 report LTM defects in Dop1R2 knock-downs, but these different findings do not seem to rely on different internal states or signaling pathways. Maybe further elaboration can help the reader understand this speculation.

We agree and we thank you for this advice. We decided to add additional details and citations to validate our speculation

Lines 350-353

“In aversive memory formation, loss of Dop1R2 could lead to enhanced or impaired memory, depending on the activated signaling pathways. The signaling pathway that is activated further depends on the available pool of secondary messengers in the cell (Hermans, 2003) which may be regulated by the internal state of the animal.”

"...for reward memory formation, loss of Dop1R2 seems to impair memory", this seems redundant at this point, as it has been discussed in detail, however, citations should be provided in any case (Musso 2015, Sun 2020)

Thank you for noting this. We recognize the redundancy and decided to exclude the line.

Finally, it would be useful to additionally refer to the anatomical terminology when introducing neuron names; for example MBON MVP2 (MBON-g1pedc>a/b), etc.

Thank you for this suggestion. We understand the importance of anatomical terminologies for the neurons. Therefore, we included them when we introduce neurons in the paper.

We thank you for your observations. We recognize their value, so we have made appropriate changes in the discussion to sound less vague and more comprehensive.

Reviewer #1 (Public review):

Summary:

The study by Deng et al reports single cell expression analysis of developing mouse hearts and examines the requirements for cardiac fibroblasts in heart maturation. The work includes extensive gene expression profiling and bioinformatic analysis. The prenatal fibroblast ablation studies show new information on the requirement of these cells on heart maturation before birth.

The strengths of the manuscript are the new single cell datasets and comprehensive approach to ablating cardiac fibroblasts in pre and postnatal development in mice. Extensive data are presented on mouse embryo fibroblast diversity and morphology in response to fibroblast ablation. Histological data support localization of major cardiac cell types and effects of fibroblast ablation on cardiac gene expression at different times of development.

A weakness of the study is that the major conclusions regarding collagen signaling and heart maturation are based on gene expression patterns and are not functionally validated.

Comments on Revised Version (from BRE):

Most of my comments have been adequately addressed. Additional comments on new data in the revised manuscript are below.

(1) In the new figure S11, it is not really possible to draw major conclusions on mitral valve morphology and maturation since the planes of sections to not seem comparable. Observations regarding attachment to the papillary muscle might be dependent on the particular section being evaluated. However, it is useful to see that the valves are not severely affected in the ablated animals.

(2) In the last supplemental figure S19, it is not possible to determine if results are or are not statistically significant for n=2 as shown for FS and EF for the ablated animals and controls. The text says that there is a trend of improved heart function, but evaluation of additional animals is needed to support this conclusion.

eLife Assessment

This study provides a comprehensive analysis of gene expression and bioinformatics data, offering important insights into the roles of fibroblasts in cardiac development. The large and well-analyzed single-cell RNA sequencing (scRNA-seq) dataset is compelling and a significant contribution to the field, and will be of broad interest to the scientific community.

Reviewer #2 (Public review):

This study aims to elucidate the role of fibroblasts in regulating myocardium and vascular development through signaling to cardiomyocytes and endothelial cells. This focus is significant, given that fibroblasts, cardiomyocytes, and vascular endothelial cells are the three primary cell types in the heart. The authors employed a Pdgfra-CreER-controlled diphtheria toxin A (DTA) system to ablate fibroblasts at various embryonic and postnatal stages, characterizing the resulting cardiac defects, particularly in myocardium and vasculature development. Single-cell RNA sequencing (scRNA-seq) analysis of the ablated hearts identified collagen as a crucial signaling molecule from fibroblasts that influences the development of cardiomyocytes and vascular endothelial cells.

This is an interesting manuscript; however, there are several major issues, including an over-reliance on the scRNA-seq data, which shows inconsistencies between replicates.

Some of the major issues are described below.

(1) The CD31 immunostaining data (Figure 3B-G) indicate a reduction in endothelial cell numbers following fibroblast deletion using PdgfraCreER+/-; RosaDTA+/- mice. However, the scRNA-seq data show no percentage change in the endothelial cell population (Figure 4D). Furthermore, while the percentage of Vas_ECs decreased in ablated samples at E16.5, the results at E18.5 were inconsistent, showing an increase in one replicate and a decrease in another, raising concerns about the reliability of the RNA-seq findings.

(2) Similarly, while the percentage of Ven_CMs increased at E18.5, it exhibited differing trends at E16.5 (Fig. 4E), further highlighting the inconsistency of the scRNA-seq analysis with the other data.

(3) Furthermore, the authors noted that the ablated samples had slightly higher percentages of cardiomyocytes in the G1 phase compared to controls (Fig. 4H, S11D), which aligns with the enrichment of pathways related to heart development, sarcomere organization, heart tube morphogenesis, and cell proliferation. However, it is unclear how this correlates with heart development, given that the hearts of ablated mice are significantly smaller than those of controls (Figure 3E). Additionally, the heart sections from ablated samples used for CD31/DAPI staining in Figure 3F appear much larger than those of the controls, raising further inconsistencies in the manuscript.

(4) The manuscript relies heavily on the scRNA-seq dataset, which shows inconsistencies between the two replicates. Furthermore, the morphological and histological analyses do not align with the scRNA-seq findings.

(5) There is a lack of mechanistic insight into how collagen, as a key signaling molecule from fibroblasts, affects the development of cardiomyocytes and vascular endothelial cells.

(6) In Figure 1B, Col1a1 expression is observed in the epicardial cells (Figure 1A, E11.5), but this is not represented in the accompanying cartoon.

(7) Do the PdgfraCreER+/-; RosaDTA+/- mice survive after birth when induced at E15.5, and do they exhibit any cardiac defects?

Comments on Revised Version (from BRE):

The manuscript has greatly improved following the revision, and I have no additional comments to offer.

Reviewer #3 (Public review):

Summary:

The authors investigated fibroblasts' communication with key cell types in developing and neonatal hearts, with focus on critical roles of fibroblast-cardiomyocyte and fibroblast-endothelial cells network in cardiac morphogenesis. They tried to map the spatial distribution of these cell types and reported the major pathways and signaling molecules driving the communication. They also used Cre-DTA system to ablate Pdgfra labeled cells and observed myocardial and endothelial cell defects at development. They screened the pathways and genes using sequencing data of ablated heart. Lastly they reported a compensatory collagen expression in long term ablated neonate heart. Overall, this study provides us with important insight on fibroblasts' roles in cardiac development and will be a powerful resource for collagens and ECM focused research.

Strengths:

The authors utilized good analyzing tools to investigate on multiple database of single cell sequencing and Multi-seq. They identified significant pathways, cellular and molecular interactions of fibroblasts. Additionally, they compared some of their analytic findings with human database, and identified several groups of ECM genes with varying roles in mice.

Weaknesses:

This study is majorly based on sequencing data analysis. At the bench, they used very strident technique to study fibroblast functions by ablating one of the major cell population of heart. Also, experimental validation of their analyzed downstream pathways will be required eventually.

Comments on Revised Version (from BRE):

The authors did a good job addressing the questions asked at first review. However, I have some minor concerns.

(1) The paper notes that collagen signaling is observed in FB-VasEC in humans, but not in FB-VenCM, unlike mice. Did the authors analyze predictive ligand receptor interaction as they did with control and ablated mice heart? This could add valuable new insights that how FB regulate ventricular CM in human heart.

(2) The authors provided data on Defect in CD31 expression in several models. Did they observe any other phenotypes associated with defective endothelial or vascular system? Such as, blood accumulation in pericardium, larger/smaller capillaries? Did they also examine percentage of Cdh5+ cells?

(3) Please mention the sample age of Figure 2A-C.

(4) Please follow the same style to describe X axis in graphs in Figure 3D (and all similar graphs in the manuscript) as followed in 3G.

(5) It is important to provide echocardiographic M mode images with a comparable number of cardiac cycles in control and ablated (Fig. 6H).

(6) In the long-term neonatal ablation experiments, collagen expressions return to normal. The manuscript attributes this to possible "compensatory expression," Do they have any thoughts how this is regulated? Are other cell types stepping in, or are surviving FBs proliferating?

(7) While collagen is shown to be a dominant signaling molecule, its centrality is inferred primarily from scRNA-seq and ligand-receptor predictions. Did authors try any functional rescue experiment (e.g., exogenous collagen supplementation or receptor blockade) to directly validate this pathway's role in vivo?

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Deng et al reports single cell expression analysis of developing mouse hearts and examines the requirements for cardiac fibroblasts in heart maturation. The work includes extensive gene expression profiling and bioinformatic analysis. The prenatal fibroblast ablation studies show new information on the requirement of these cells on heart maturation before birth.

The strengths of the manuscript are the new single cell datasets and comprehensive approach to ablating cardiac fibroblasts in pre and postnatal development in mice. Extensive data are presented on mouse embryo fibroblast diversity and morphology in response to fibroblast ablation. Histological data support localization of major cardiac cell types and effects of fibroblast ablation on cardiac gene expression at different times of development.

A weakness of the study is that the major conclusions regarding collagen signaling and heart maturation are based on gene expression patterns and are not functionally validated.

Reviewer #2 (Public review):

This study aims to elucidate the role of fibroblasts in regulating myocardium and vascular development through signaling to cardiomyocytes and endothelial cells. This focus is significant, given that fibroblasts, cardiomyocytes, and vascular endothelial cells are the three primary cell types in the heart. The authors employed a Pdgfra-CreER-controlled diphtheria toxin A (DTA) system to ablate fibroblasts at various embryonic and postnatal stages, characterizing the resulting cardiac defects, particularly in myocardium and vasculature development. Single-cell RNA sequencing (scRNA-seq) analysis of the ablated hearts identified collagen as a crucial signaling molecule from fibroblasts that influences the development of cardiomyocytes and vascular endothelial cells.

This is an interesting manuscript; however, there are several major issues, including an over-reliance on the scRNA-seq data, which shows inconsistencies between replicates.

We thank the reviewer for carefully reading our revised manuscript. All of the questions listed below were raised in the previous round and have been addressed in the current revision. As noted in the “Recommendations for the Authors” section, the reviewer has no additional comments at this time.

Some of the major issues are described below.

(1) The CD31 immunostaining data (Figure 3B-G) indicate a reduction in endothelial cell numbers following fibroblast deletion using PdgfraCreER+/-; RosaDTA+/- mice. However, the scRNA-seq data show no percentage change in the endothelial cell population (Figure 4D). Furthermore, while the percentage of Vas_ECs decreased in ablated samples at E16.5, the results at E18.5 were inconsistent, showing an increase in one replicate and a decrease in another, raising concerns about the reliability of the RNA-seq findings.

(2) Similarly, while the percentage of Ven_CMs increased at E18.5, it exhibited differing trends at E16.5 (Fig. 4E), further highlighting the inconsistency of the scRNA-seq analysis with the other data.

(3) Furthermore, the authors noted that the ablated samples had slightly higher percentages of cardiomyocytes in the G1 phase compared to controls (Fig. 4H, S11D), which aligns with the enrichment of pathways related to heart development, sarcomere organization, heart tube morphogenesis, and cell proliferation. However, it is unclear how this correlates with heart development, given that the hearts of ablated mice are significantly smaller than those of controls (Figure 3E). Additionally, the heart sections from ablated samples used for CD31/DAPI staining in Figure 3F appear much larger than those of the controls, raising further inconsistencies in the manuscript.

(4) The manuscript relies heavily on the scRNA-seq dataset, which shows inconsistencies between the two replicates. Furthermore, the morphological and histological analyses do not align with the scRNA-seq findings.

(5) There is a lack of mechanistic insight into how collagen, as a key signaling molecule from fibroblasts, affects the development of cardiomyocytes and vascular endothelial cells.

(6) In Figure 1B, Col1a1 expression is observed in the epicardial cells (Figure 1A, E11.5), but this is not represented in the accompanying cartoon.

(7) Do the PdgfraCreER+/-; RosaDTA+/- mice survive after birth when induced at E15.5, and do they exhibit any cardiac defects?

Reviewer #3 (Public review):

Summary:

The authors investigated fibroblasts' communication with key cell types in developing and neonatal hearts, with focus on critical roles of fibroblast-cardiomyocyte and fibroblast-endothelial cells network in cardiac morphogenesis. They tried to map the spatial distribution of these cell types and reported the major pathways and signaling molecules driving the communication. They also used Cre-DTA system to ablate Pdgfra labeled cells and observed myocardial and endothelial cell defects at development. They screened the pathways and genes using sequencing data of ablated heart. Lastly they reported a compensatory collagen expression in long term ablated neonate heart. Overall, this study provides us with important insight on fibroblasts' roles in cardiac development and will be a powerful resource for collagens and ECM focused research.

Strengths:

The authors utilized good analyzing tools to investigate on multiple database of single cell sequencing and Multi-seq. They identified significant pathways, cellular and molecular interactions of fibroblasts. Additionally, they compared some of their analytic findings with human database, and identified several groups of ECM genes with varying roles in mice.

Weaknesses:

This study is majorly based on sequencing data analysis. At the bench, they used very strident technique to study fibroblast functions by ablating one of the major cell population of heart. Also, experimental validation of their analyzed downstream pathways will be required eventually.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Most of my comments have been adequately addressed. Additional comments on new data in the revised manuscript are below.

(1) In the new figure S11, it is not really possible to draw major conclusions on mitral valve morphology and maturation since the planes of sections to not seem comparable. Observations regarding attachment to the papillary muscle might be dependent on the particular section being evaluated. However, it is useful to see that the valves are not severely affected in the ablated animals.

We appreciate the reviewer’s comment and agree with the reviewer’s observation. Accordingly, we have updated the manuscript by removing the original conclusion-related statement and instead highlighting that the valves were not severely affected in the ablated animals (page 6).

(2) In the last supplemental figure S19, it is not possible to determine if results are or are not statistically significant for n=2 as shown for FS and EF for the ablated animals and controls. The text says that there is a trend of improved heart function, but evaluation of additional animals is needed to support this conclusion.

We thank the reviewer for the comment and agree that a sample size of n = 2 is too small to draw meaningful conclusions. As previously suggested by the reviewer, we have removed this result from the manuscript (page 10).

Reviewer #2 (Recommendations for the authors):

The manuscript has greatly improved following the revision, and I have no additional comments to offer.

Thanks!

Reviewer #3 (Recommendations for the authors):

Authors did a good job addressing questions asked at first review. However, I have some minor concerns.

(1) The paper notes that collagen signaling is observed in FB-VasEC in humans, but not in FB-VenCM, unlike mice. Did authors analyze predictive ligand receptor interaction as they did with control and ablated mice heart? This could add valuable new insights that how FB regulate ventricular CM in human heart.

Thank you. We have analyzed the predicted ligand-receptor interactions between Fb and Ven_CM, as well as between Fb and Vas_EC, using human scRNA-seq data. The results are provided as a supplemental figure (Fig. S8C).

(2) The authors provided data on Defect in CD31 expression in several models. Did they observed any other phenotypes associated with defective endothelial or vascular system? Such as, blood accumulation in pericardium, larger/smaller capillaries? Did they also examined percentage of Cdh5+ cells?

We thank the reviewer for the questions. We did not observe clear evidence of blood accumulation in the pericardium of the ablated hearts, as shown in figure 3B, 3E, 6B, and 6F. Additionally, we did not perform Cdh5 staining in either the control or ablated hearts.

(3) Please mention the sample age of Figure 2A-C.

These are single-cell mRNA sequencing data from CD1 mice across 18 developmental stages, ranging from E9.5 to P9. We have added this information to the manuscript (page 4).

(4) Please follow the same style to describe X axis in graphs in Figure 3D (and all similar graphs in manuscript) as followed in 3G.

Thank you. We assume the reviewer was referring to the descriptions in the relevant figure legends. We have updated the legend for Figure 3D to ensure consistency with the description provided for Figure 3G (page 15).

(5) It is important to provide echocardiographic M mode images with a comparable number of cardiac cycles in control and ablated (Fig. 6H).

We thank the reviewer for the comment. As explained in our previous response, the echocardiographic data for both control and mutant mice were collected in conscious animals. The differences in their cardiac cycles reflect variations in heart rate, which represent a disease phenotype and cannot be altered. Therefore, we are unable to provide M-mode images with a similar number of cardiac cycles for control and ablated mice.

(6) In the long-term neonatal ablation experiments, collagen expressions return to normal. The manuscript attributes this to possible "compensatory expression," Do they have any thoughts how this is regulated? Are other cell types stepping in, or are surviving FBs proliferating?

We thank the reviewer for the question. As suggested, the compensatory collagen expression could be driven by surviving fibroblasts or other cell types. Since we currently lack evidence to exclude either possibility, we believe both could be contributing factors.

(7) While collagen is shown to be a dominant signaling molecule, its centrality is inferred primarily from scRNAseq and ligand-receptor predictions. Did authors try any functional rescue experiment (e.g., exogenous collagen supplementation or receptor blockade) to directly validate this pathway's role in vivo?

We thank the reviewer for the comment. As noted in our previous revision in response to similar questions from the other two reviewers, we agree that these rescue experiments are of interest but are beyond the scope of the current study. We plan to pursue these investigations in future work and share our findings when available.

eLife Assessment

This important study presents an alternative platform for nanobody discovery using phage-displayed synthetic libraries. The evidence supporting the platform, which is used to isolate and validate nanobodies targeting Drosophila secreted proteins, is compelling. By making the library openly accessible, this provides an excellent resource to the wider scientific community. The paper presents a detailed protocol for nanobody screening; as this protocol is refined and optimized over time, this will increase the success rate for discovering nanobodies with improved properties using this alternative platform.

Reviewer #2 (Public review):

Summary:

In this study, authors propose an alternative platform for nanobody discovery using a phage-displayed synthetic library. Authors relied on DNA templates originally created by McMahon et al. (2018) to build the yeast-displayed synthetic library. To validate their platform, authors screened for nanobodies against 8 Drosophila secreted proteins. Nanobody screening has been performed with phage-displayed nanobody libraries followed by an enzyme-linked immunosorbent assay (ELISA) to validate positive hits. Nanobodies with higher affinity have been then tested for immunostaining and immunoblotting applications using Drosophila adult guts and hemolymph, respectively.

Strengths:

The authors presented a detailed protocol with various and complementary approaches to select nanobodies and test their application for immunostaining and immunoblotting experiments. Data are convincing and the manuscript is well-written, clear and easy to read.

Weaknesses:

When using membrane-tethered forms of the antigens to test the affinity of nanobodies identified by ELISA, many nanobodies fail to recognize the antigens. While authors suggested a low affinity of these nanobodies for their antigens, this hypothesis has not been tested in the manuscript.

Improving the protocol at each step for nanobody selection would greatly increase a successful rate for nanobodies discovery with high affinity.

Author response:

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

Reviewer #1 (Public review):

Summary:

Using highly specific antibody reagents for biological research is of prime importance. In the past few years, novel approaches have been proposed to gain easier access to such reagents. This manuscript describes an important step forward toward the rapid and widespread isolation of antibody reagents. Via the refinement and improvement of previous approaches, the Perrimon lab describes a novel phage-displayed synthetic library for nanobody isolation. They used the library to isolate nanobodies targeting Drosophila secreted proteins. They used these nanobodies in immunostainings and immunoblottings, as well as in tissue immunostainings and live cell assays (by tethering the antigens on the cell surface).

Since the library is made freely available, it will contribute to gaining access to better research reagents for non-profit use, an important step towards the democratisation of science.

Strengths:

(1) New design for a phage-displayed library of high content.

(2) Isolation of valuble novel tools.

(3) Detailed description of the methods such that they can be used by many other labs.

We are grateful for these supportive comments.

Weaknesses:

My comments largely concentrate on the representation of the data in the different Figures.

We have made adjustments according to the reviewer’s recommendations.

Reviewer #2 (Public review):

Summary:

In this study, the authors propose an alternative platform for nanobody discovery using a phage-displayed synthetic library. The authors relied on DNA templates originally created by McMahon et al. (2018) to build the yeast-displayed synthetic library. To validate their platform, the authors screened for nanobodies against 8 Drosophila secreted proteins. Nanobody screening has been performed with phage-displayed nanobody libraries followed by an enzyme-linked immunosorbent assay (ELISA) to validate positive hits. Nanobodies with higher affinity have been tested for immunostaining and immunoblotting applications using Drosophila adult guts and hemolymph, respectively.

Strengths:

The authors presented a detailed protocol with various and complementary approaches to select nanobodies and test their application for immunostaining and immunoblotting experiments. Data are convincing and the manuscript is well-written, clear, and easy to read.

We thank the reviewer for these supportive comments.

Weaknesses:

On the eight Drosophila secreted proteins selected to screen for nanobodies, the authors failed to identify nanobodies for three of them. While the authors mentioned potential improvements of the protocol in the discussion, none of them have been tested in this manuscript.

We prepared all eight antigens by single-step IgG purification (see Materials and Methods) without additional biophysical quality control (e.g., size-exclusion chromatography). Consequently, we cannot definitively determine whether the three “no-binder” cases resulted from the aggregation or misfolding of the antigens, versus gaps in our naive library’s sequence space. While approaches such as additional purification steps or affinity maturation of weak binders would likely rescue these difficult targets, comprehensive pipeline optimization is beyond the scope of establishing and validating the phage-displayed nanobody platform. We have clarified this limitation and suggested these strategies in third paragraph of the Discussion.

The same comment applies to the experiments using membrane-tethered forms of the antigens to test the affinity of nanobodies identified by ELISA. Many nanobodies fail to recognize the antigens. While authors suggested a low affinity of these nanobodies for their antigens, this hypothesis has not been tested in the manuscript.

We observed that several nanobodies with strong ELISA signals showed reduced binding to membrane-displayed antigens. This discrepancy may result from low affinity of the nanobodies or differences in post-translational modifications (e.g., glycosylation) and antigen context between secreted IgG-fusion proteins (used for panning/ELISA) and GPI- or mCD8-anchored proteins. In an ongoing work, we have performed affinity maturation of the nanobodies and successfully increased the affinity toward the target antigen. These results will be reported separately.

Improving the protocol at each step for nanobody selection would greatly increase the success rate for the discovery of nanobodies with high affinity.

We fully agree that systematic optimization—from antigen preparation (e.g., additional purification steps) through screening conditions (e.g., buffer composition, additional affinity-maturation steps)—could substantially increase the success rate and nanobody affinity. These represent important directions for future work.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 3. The merge of two GFP channels does not make much sense. Can the authors not use artificial colours? And show the panels at higher resolution, such that a viewer can really see and judge what they are seeing? The same comments apply to all Supplementary Figures.

We appreciate the reviewer’s comment. In the revised Figure 3, we have replaced the cyan/green overlay with red/green overlay and used enlarged pictures so that GFP-positive cells and corresponding nanobody staining are clearly visible. We applied the same layout to all relevant Supplementary Figures.

(2) Figure 4. Also, in this Figure, it is not really possible to see what the authors say one should see. The resolution should be higher, and arrows or arrowheads should point to important structures.

We appreciate the reviewer’s comment. In the revised Figure 4A, we have added arrows to point to the immunostaining signal in cells with smaller nuclei and added inset panels to show a closer view of representative NbMip-4G staining.

Reviewer #2 (Recommendations for the authors):

(1) Images are sometimes quite small and difficult to interpret. For example, Figures S2C-D.

We thank the reviewer for this suggestion. In the revised figures, we have replaced the cyan/green overlay with red/green overlay and used enlarged pictures that clearly show GFP-positive cells alongside their corresponding nanobody staining.

(2) Supplemental figures are not always cited in the text.

Thank you for the comment. To eliminate this misunderstanding, we have updated the Nesfatin1 nanobody screen data as Supplementary Figure 1 and Mip nanobody screen data as Supplementary Figure 2. We have made the corresponding changes in the Results section.

eLife Assessment

This study reveals a neural signature of a common behavioural phenomenon: serial dependence, whereby estimates of a visual feature (here motion direction) are attracted towards the recent history of encoded and reported stimuli. The study provides solid evidence that this phenomenon arises primarily during working memory maintenance. The pervasiveness of serial dependencies across modalities and species makes these findings important for researchers interested in perceptual decision-making across subfields.

Reviewer #1 (Public review):

This study uses MEG to test for a neural signature of the trial history effect known as 'serial dependence.' This is a behavioral phenomenon whereby stimuli are judged to be more similar than they really are, in feature space, to stimuli that were relevant in the recent past (i.e., the preceding trials). This attractive bias is prevalent across stimulus classes and modalities, but a neural source has been elusive. This topic has generated great interest in recent years, and I believe this study makes a unique contribution to the field.

Specifically, while previous neuroimaging studies have found apparent reactivations of previous information, or repulsive biases that may indirectly relate to serial dependence, here Fischer at al. find an attractive bias in neural activity patterns that aligns with the direction of the behavioral effect. Moreover, the data show that the bias emerges later in a trial, after perceptual encoding, which speaks to an ongoing debate about whether such biases are perceptual or decisional.

The revised preprint thoroughly addresses many of the initial concerns, but the results are still open to interpretation. For instance, the model training/testing regime allows that some training data timepoints may be inherently noisier than others (e.g., delay period more so than encoding), and potentially more (or differently) susceptible to bias. The S1 and S2 epochs show no attractive bias, but they may also be based on more high fidelity training sets (i.e., encoding), and therefore less susceptible to the bias that is evident in the retrocue epoch. So, the results could reflect that serial dependence is indeed a post-perceptual process, or it may instead be that the WM representations, as detected with these MEG analyses, become noisier and more subject to reveal the attractive bias over time.

The results are intriguing, but the study was not powered to examine whether there is any feature-specificity to the neural bias (e.g., whether it matches the behavioral pattern that biases are amplified within a particular range of feature distances between stimuli). Nor do analyses get at temporally precise information about when attractive and repulsive biases appear, which would help to better reconcile the work with previous findings. As in, the reconstructions average across coarse trial epochs. The S1 and S2 reconstructions show no attractive bias, and appear to show subtle repulsion, but if the timing were examined more precisely, we might see repulsion magnified at earlier timepoints that shift toward attraction at later time points, thereby counteracting the effect. That is to say that the averaging approach, across feature values and timepoints, still leaves these important theoretical questions unresolved.

Nonetheless, the work marks an important step in identifying the neurophysiological bases of serial dependence. Ideally, all of the data, including the eye-tracking, would be made available so that others might try to address some of these follow-up questions.

Reviewer #2 (Public review):

Summary:

The study aims to probe the neural correlates of visual serial dependence - the phenomenon that estimates of a visual feature (here motion direction) are attracted towards the recent history of encoded and reported stimuli. The authors utilize an established retro-cue working memory task together with magnetoencephalography, which allows to probe neural representations of motion direction during encoding and retrieval (retro-cue) periods of each trial. The main finding is that neural representations of motion direction are not systematically biased during the encoding of motion stimuli, but are attracted towards the motion direction of the previous trial's target during the retrieval (retro-cue period), just prior to the behavioral response. By demonstrating a neural signature of attractive biases in working memory representations, which align with attractive behavioral biases, this study highlights the importance of post-encoding memory processes in visual serial dependence.

Strengths:

The main strength of the study is its elegant use of a retro-cue working memory task together with high temporal resolution MEG, enabling to probe neural representations related to stimulus encoding and working memory. The behavioral task elicits robust behavioral serial dependence and replicates previous behavioral findings by the same research group. The careful neural decoding analysis benefits from a large number of trials per participant, considering the slow-paced nature of the working memory paradigm. This is crucial in a paradigm with considerable trial-by-trial behavioral variability (serial dependence biases are typically small, relative to the overall variability in response errors). While the current study is broadly consistent with previous studies showing that attractive biases in neural responses are absent during stimulus encoding (prev. studies reported repulsive biases), to my knowledge, it is the first study showing attractive biases in current stimulus representations during working memory. The study also connects to previous literature showing reactivations of previous stimulus representations, although the link between reactivations and biases remains somewhat vague in the current manuscript. Together, the study reveals an interesting avenue for future studies investigating the neural basis of visual serial dependence.

Weaknesses:

The main weakness of the current manuscript is that the authors could have done more analyses to address the concern that their neural decoding results are driven by signals related to eye movements. The authors show that participants' gaze position systematically depended on the current stimuli's motion directions, which, together with previous studies on eye movement-related confounds in neural decoding, justifies such a concern. The authors seek to rule out this confound by showing that the consistency of stimulus-dependent gaze position does not correlate with (a) the neural reconstruction fidelity and (b) the attractive shift in reconstructed motion direction. However, the authors' approach of quantifying stimulus-dependent eye movements only considers gaze angle and not gaze amplitude, and thus potentially misses important features of eye movements that could manifest in the MEG data. Moreover, it is unclear whether the gaze consistency metric should correlate with attractive history biases in neural decoding, if there were a confound. These two concerns could be potentially addressed by (1) directly decoding stimulus motion direction from x-y gaze coordinates and relating this decoding performance to neural reconstruction fidelity, and (2) investigating whether gaze coordinates themselves are history-dependent and are attracted to the average gaze position associated with the previous trials' target stimulus. If the authors could show that (2) is not the case, I would be much more convinced that their main finding is not driven by eye movement confounds.

The sample size (n = 10) is definitely at the lower end of sample sizes in this field. The authors collected two sessions per participant, which partly alleviates the concern. However, given that serial dependencies can be very variable across participants, I believe that future studies should aim for larger sample sizes.

It would have been great to see an analysis in source space. As the authors mention in their introduction, different brain areas, such as PPC, mPFC and dlPFC have been implicated in serial biases. This begs the question which brain areas contribute to the serial dependencies observed in the current study? For instance, it would be interesting to see whether attractive shifts in current representations and pre-stimulus reactivations of previous stimuli are evident in the same or different brain areas.

Reviewer #2 (Public review):

Summary:

The study aims to probe the neural correlates of visual serial dependence - the phenomenon that estimates of a visual feature (here motion direction) are attracted towards the recent history of encoded and reported stimuli. The authors utilize an established retro-cue working memory task together with magnetoencephalography, which allows to probe neural representations of motion direction during encoding and retrieval (retro-cue) periods of each trial. The main finding is that neural representations of motion direction are not systematically biased during the encoding of motion stimuli, but are attracted towards the motion direction of the previous trial's target during the retrieval (retro-cue period), just prior to the behavioral response. By demonstrating a neural signature of attractive biases in working memory representations, which align with attractive behavioral biases, this study highlights the importance of post-encoding memory processes in visual serial dependence.

Strengths:

The main strength of the study is its elegant use of a retro-cue working memory task together with high temporal resolution MEG, enabling to probe neural representations related to stimulus encoding and working memory. The behavioral task elicits robust behavioral serial dependence and replicates previous behavioral findings by the same research group. The careful neural decoding analysis benefits from a large number of trials per participant, considering the slow-paced nature of the working memory paradigm. This is crucial in a paradigm with considerable trial-by-trial behavioral variability (serial dependence biases are typically small, relative to the overall variability in response errors). While the current study is broadly consistent with previous studies showing that attractive biases in neural responses are absent during stimulus encoding (prev. studies reported repulsive biases), to my knowledge, it is the first study showing attractive biases in current stimulus representations during working memory. The study also connects to previous literature showing reactivations of previous stimulus representations, although the link between reactivations and biases remains somewhat vague in the current manuscript. Together, the study reveals an interesting avenue for future studies investigating the neural basis of visual serial dependence.

Weaknesses:

The main weakness of the current manuscript is that the authors could have done more analyses to address the concern that their neural decoding results are driven by signals related to eye movements. The authors show that participants' gaze position systematically depended on the current stimuli's motion directions, which, together with previous studies on eye movement-related confounds in neural decoding, justifies such a concern. The authors seek to rule out this confound by showing that the consistency of stimulus-dependent gaze position does not correlate with (a) the neural reconstruction fidelity and (b) the attractive shift in reconstructed motion direction. However, the authors' approach of quantifying stimulus-dependent eye movements only considers gaze angle and not gaze amplitude, and thus potentially misses important features of eye movements that could manifest in the MEG data. Moreover, it is unclear whether the gaze consistency metric should correlate with attractive history biases in neural decoding, if there were a confound. These two concerns could be potentially addressed by (1) directly decoding stimulus motion direction from x-y gaze coordinates and relating this decoding performance to neural reconstruction fidelity, and (2) investigating whether gaze coordinates themselves are history-dependent and are attracted to the average gaze position associated with the previous trials' target stimulus. If the authors could show that (2) is not the case, I would be much more convinced that their main finding is not driven by eye movement confounds.

The sample size (n = 10) is definitely at the lower end of sample sizes in this field. The authors collected two sessions per participant, which partly alleviates the concern. However, given that serial dependencies can be very variable across participants, I believe that future studies should aim for larger sample sizes.

It would have been great to see an analysis in source space. As the authors mention in their introduction, different brain areas, such as PPC, mPFC and dlPFC have been implicated in serial biases. This begs the question which brain areas contribute to the serial dependencies observed in the current study? For instance, it would be interesting to see whether attractive shifts in current representations and pre-stimulus reactivations of previous stimuli are evident in the same or different brain areas.

eLife Assessment

In this valuable study, Nold et al. examined exercise-induced pain modulation in a pharmacological within-subject fMRI study using the opioid-antagonist naloxone and different levels of aerobic exercise intensity and pain. This investigation provides solid evidence to show that the intensity of exercise does not seem to impact the hypoalgesic effect. Moreover, exploratory analysis identified that fitness level and sex may potentially play a role in exercise-induced hypoalgesia, and that further confirmatory studies are required in order to verify these findings.

Reviewer #1 (Public review):

Summary:

Participants in this study completed three visits. In the first, participants received experimental thermal stimulations which were calibrated to elicit three specific pain responses (30, 50, 70) on a 0-100 visual analogue scale (VAS). Experimental pressure stimulations were also calibrated at an intensity to the same three pain intensity responses. In the subsequent two visits, participants completed another pre-calibration check (Visit 2 of 3 only). Then, prior to the exercise NALOXONE or a SALINE placebo-control was administered intravenously. Participants then completed 1 of 4 blocks of HIGH (100%) or LOW (55%) intensity cycling which was tailored according to a functional threshold power (FTP) test completed in Visit 1. After each block of cycling lasting 10 minutes, participants entered an MRI scanner and were stimulated with the same thermal and pressure stimulations that corresponded to 30, 50, and 70 pain intensity ratings from the calibration stage. Therefore, this study ultimately sought to investigate whether aerobic exercise does indeed incur a hypoalgesia effect. More specifically, researchers tested the validity of the proposed endogenous pain modulation mechanism. Further investigation into whether the intensity of exercise had an effect on pain and the neurological activation of pain-related brain centres were also explored. Results show that in the experimental visits (Visit 2 and 3), when participants exercised at two distinct intensities as intended. Power output, heart rate, and perceived effort ratings were higher during the HIGH versus LOW intensity cycling. In particular. HIGH intensity exercise was perceived as "hard" / ~15 on the Borg (1974, 1998) scale, whereas LOW intensity exercise was perceived as "very light" / ~9 on the same scale.

The fMRI data from Figure 1 indicates that the anterior insula, dorsal posterior insula and middle cingulate cortex show pronounced activation as stimulation intensity and subsequent pain responses increased, thus linking these brain regions with pain intensity and corroborating what many studies have shown before.

Results also showed that participants rated a higher pain intensity in the NALOXONE condition at all three stimulation intensities compared to the SALINE condition. Therefore, the expected effect of NALOXONE in this study seemed to occur whereby opioid receptors were "blocked" and thus resulted in higher pain ratings compared to a SALINE condition where opioid receptors were "not blocked". When accounting for participant sex, NALOXONE had negligible effects at lower experimental nociceptive stimulations for females compared to males who showed a hyperalgesia effect to NALOXONE at all stimulation intensities (peak effect at 50 VAS). Females did show a hyperalgesia effect at stimulation intensities corresponding to 50 and 70 VAS pain ratings. The fMRI data showed that the periaqueductal gray (PAG) showed increased activation in the NALOXONE versus SALINE condition at higher thermal stimulation intensities. The PAG is well-linked to endogenous pain modulation.

When assessing the effects of NALOXONE and SALINE after exercise, results showed no significant differences in subsequent pain intensity ratings.

When assessing the effect of aerobic exercise intensity on subsequent pain intensity ratings, authors suggested that aerobic exercise in the form of a continuous cycling exercise tailored to an individual's FTP is not effective at eliciting an exercise-induced hypoalgesia response -irrespective of exercise intensity. This is because results showed that pain responses did not differ significantly between HIGH and LOW intensity exercise with (NALOXONE) and without (SALINE) an opioid antagonist. Therefore, authors have also questioned the mechanisms (endogenous opioids) behind this effect.

Strengths:

Altogether, the paper is great piece of work that has provided some truly useful insight into the neurological and perceptual mechanisms associated with pain and exercise-induced modulation of pain. The authors have gone to great lengths to delve into their research question(s) and their methodological approach is relatively sound. The study has incorporated effective pseudo-randomisation and conducted a rigorous set of statistical analysis to account for as many confounds as possible. I will particularly credit the authors on their analysis which explores the impact of sex and female participants' stage of menses on the study outcomes. It would be particularly interesting for future work to pursue some of these lines of research which investigate the differences in the endogenous opioid mechanism between sexes and the added interaction of stage of menses or training status - all of which the authors point out in their discussion.

There are certainly many other areas that this article contributes to the literature due to the depth of methods the research team have used. For example, the authors provide much insight into: the impact of exercise intensity on the exercise-induced hypoalgesia effect; the impact of sex on the endogenous opioid modulation mechanism; and the impact of exercise intensity on the neurological indices associated with endogenous pain modulation and pain processing. All of which, the researchers should be credited for due to the time and effort they have spent completing this study. Indeed, their in-depth analysis of many of these areas provides ample support for the claims they make in relation to these specific questions. As such, I consider their evidence concerning the fMRI data to be very convincing (and interesting).

Weaknesses:

Although the authors have their own view of their results, I, however, do still maintain a slightly different take on what the post-exercise pain ratings seem to show and its implications for judging whether an exercise-induced hypoalgesia effect is present or not and whether this is related to the opioid system.

For example, my basic assumptions relate to data which appears to show that there is an exercise-induced hypoalgesia effect as average pain ratings are ~30% lower than pre-calibrated/resting pain ratings within the SALINE condition at the same temperature of stimulation. Then, it appears there is evidence for the endogenous opioid mechanism as the NALOXONE condition demonstrates a minimal hypoalgesia effect after exercise. I.e., NALOXONE indeed blocked the opioid receptors, and such inhibition prevented the endogenous opioid system from taking effect.

However, through a comprehensive revision of their work, the authors have addressed many areas that myself and my fellow reviewer have questioned and provided a comprehensive set of responses and edits about this. So while I may have some opposing views on the mechanisms at play, I believe that each reader can decide and interpret the data for themselves which has been presented well by the authors.

Reviewer #2 (Public review):

Summary:

This interesting study compared two different intensities of aerobic exercise (low-intensity, high-intensity) and their efficacy in inducing a hypoalgesic reaction (i.e. exercise-induced hypoalgesia; EIH). fMRI was used to identify signal changes in the brain, with infusion of naloxone used to identify hypoalgesia mechanisms. No differences were found in post exercise pain perception between the high-intensity and low-intensity conditions, with naloxone infusion causing increased pain perception across both conditions which was mirrored by activation in the medial frontal cortex (identified by fRMI).

Strengths:

• The use of fMRI and naloxone provides a strong approach by which to identify possible mechanisms of EIH.

• The infusion of naloxone to maintain a stable concentration helps to ensure a consistent effect and that the time-course of the protocol won't affect consistency of changes in pain perception

• The manipulation checks (differences in intensity of exercise, appropriate pain induction) are approached in a systematic way.

• The interactions for fitness level and sex provide some interesting findings which should be explored further.

Weaknesses:

• Given the absence of a baseline/control condition (for exercise), the efficacy of high/low intensity exercise on EIH cannot be assessed. Providing this would have extended and strengthened the findings/conclusions.

• Whilst the exercise test (functional threshold power) used to set the intensity of the low/high exercise bouts set participants to exercise at different intensities, this method does not ensure that they exercised above/below particular thresholds (i.e. within either heavy or severe domains). This could have created very different relative challenges between participants.

Author response:

Reviewer #1 (Public review):

Summary:

The manuscript "Rho-ROCK liberates sequestered claudin for rapid de novo tight junction formation" by Cho and colleagues investigates de novo tight junction formation during the differentiation of immortalized human HaCaT keratinocytes to granular-like cells, as well as during epithelial remodeling that occurs upon the apoptotic of individual cells in confluent monolayers of the representative epithelial cell line EpH4. The authors demonstrate the involvement of Rho-ROCK with well-conducted experiments and convincing images. Moreover, they unravel the underlying molecular mechanism, with Rho-ROCK activity activating the transmembrane serine protease Matriptase, which in turn leads to the cleavage of EpCAM and TROP2, respectively, releasing Claudins from EpCAM/TROP2/Claudin complexes at the cell membrane to become available for polymerization and de novo tight junction formation. These functional studies in the two different cell culture systems are complemented by localization studies of the according proteins in the stratified mouse epidermis in vivo.

In total, these are new and very intriguing and interesting findings that add important new insights into the molecular mechanisms of tight junction formation, identifying Matriptase as the "missing link" in the cascade of formerly described regulators. The involvement of TROP2/EpCAM/Claudin has been reported recently (Szabo et al., Biol. Open 2022; Bugge lab), and Matriptase had been formerly described to be required for in tight junction formation as well, again from the Bugge lab. Yet, the functional correlation/epistasis between them, and their relation to Rho signaling, had not been known thus far.

However, experiments addressing the role of Matriptase require a little more work.

Strengths:

Convincing functional studies in two different cell culture systems, complemented by supporting protein localization studies in vivo. The manuscript is clearly written and most data are convincingly demonstrated, with beautiful images and movies.

Weaknesses:

The central finding that Rho signaling leads to increased Matriptase activity needs to be more rigorously demonstrated (e.g. western blot specifically detecting the activated version or distinguishing between the full-length/inactive and processed/active version).

We plan to provide more direct evidence that matriptase activation is regulated by the Rho-ROCK pathway, utilizing antibodies that specifically recognize the activated form of matriptase.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigate how epithelia maintain intercellular barrier function despite and during cellular rearrangements upon e.g. apoptotic extrusion in simple epithelia or regenerative turnover in stratified epithelia like this epidermis. A fundamental question in epithelial biology. Previous literature has shown that Rho-mediated local regulation of actomyosin is essential not only for cellular rearrangement itself but also for directly controlling tight junction barrier function. The molecular mechanics however remained unclear. Here the authors use extensive fluorescent imaging of fixed and live cells together with genetic and drug-mediated interference to show that Rho activation is required and sufficient to form novo tight junctional strands at intercellular contacts in epidermal keratinocytes (HaCat) and mammary epithelial cells. After having confirmed previous literature they then show that Rho activation activates the transmembrane protease Matriptase which cleaves EpCAM and TROP2, two claudin-binding transmembrane proteins, to release claudins and enable claudin strand formation and therefore tight junction barrier function.

Strengths:

The presented mechanism is shown to be relevant for epithelial barriers being conserved in simple and stratifying epithelial cells and mainly differs due to tissue-specific expression of EpCAM and TROP2. The authors present careful state-of-the-art imaging and logical experiments that convincingly support the statements and conclusion. The manuscript is well-written and easy to follow.

Weaknesses:

Whereas the in vitro evidence of the presented mechanism is strongly supported by the data, the in vivo confirmation is mostly based on the predicted distribution of TROP2. Whereas the causality of Rho-mediated Matriptase activation has been nicely demonstrated it remains unclear how Rho activates Matriptase.

As noted, while we have demonstrated that Rho activation is both necessary and sufficient to induce matriptase activation, the precise mechanism by which Rho mediates this activation remains unclear. As discussed in the manuscript, several potential molecular mechanisms could underlie the contribution of Rho to matriptase activation. As part of our future work, we intend to systematically investigate each of these mechanisms.

eLife Assessment

The study is a timely and important contribution to our knowledge of the circuit mechanisms of fear analgesia. The novel cue-induced analgesia paradigm allowed a compelling identification of a brainstem circuit element, i.e., somatostatin-expressing neurons within the ventrolateral periaqueductal grey that project to the rostroventral medulla, in mediating fear analgesia. The vlPAG is a known region of pain modulation, and this study adds key insight to the circuit involved in fear-associated analgesia. This work will be of interest to systems and behavioral neuroscientists, especially those interested in emotional behavior, pain, and/or brainstem function.

Reviewer #1 (Public review):

Summary:

In the manuscript by Winke et al, the authors present evidence that fear-induced analgesia is mediated by somatostatin projection cells from the vlPAG to the RVM. This study uses a mouse model of fear-induced analgesia, and incorporates optogenetic circuit manipulation with behaviour and electrophysiology to gain a meaningful insight into a novel circuit involved in fear-induced analgesia.

Strengths:

(1) This is a well-constructed study with appropriate controls and analyses.

(2) Alternative interpretations of the data are systematically considered and eliminated via rational experiments. The authors are commended for a nice piece of experimental work.

(3) The vlPAG is a known region of pain modulation, and this study adds valuable insight to the circuit involved in fear-associated analgesia.

Weaknesses:

(1) Only male mice are included in this study.

(2) Animals are excluded from analyses based on clearly defined criteria, but it is not clear how many mice were excluded from each group.

(3) The authors implement a pain sensitivity assay that involves a hot plate with progressively increasing temperature. The time to nociceptive responses is reported. Without reporting the actual temperature at which the mice respond, it makes it difficult to compare nociceptive responses to previously published work (which typically use a defined and static hotplate temperature).

(4) The authors present evidence that inhibition of SST vlPAG cells enhances spinal nociceptive electrophysiological responses, but the corresponding pain sensitivity is not altered (Figure 2, CS- condition). The reason for the discrepancy between electrophysiological and behavioural responses is not clear.

Reviewer #2 (Public review):

Summary:

Wenke et al. investigated the role of vlPAG somatostatin-expressing neurons in the mediation of analgesia during defensive states. A newly developed paradigm of cued fear-conditioned analgesia, which consists of a combination of an auditory fear retrieval session and a pain test, was used to evaluate this cell population's contribution to fear-mediated analgesia. Optogenetic manipulation of vlPAG SST+ neurons modulated the responses to a nociceptive cue (Hot Plate) presented concomitantly with an aversively conditioned tone. At the same time, alterations in the freezing levels could be observed during optogenetic activation of vlPAG SST+ neurons. In order to disentangle the impact of these cells on analgesia from their impact on the expression of defensive behaviors, the authors performed electrophysiological recordings from the dorsal horn in the spinal cord of anesthetized mice. A vlPAG-RVM-DH pathway was identified to trigger nociceptive C-fibers upon optic activation of the RVM. Finally, pathway-specific activation of SST+ vlPAG-RVM neurons could abolish CS-induced analgesia.

Strengths:

The study addresses a relevant topic, that is, brainstem circuits for pain-modulatory mechanisms as part of defensive states evoked by threat. This is important because the circuit mechanisms underlying pain are still not fully understood, and defining molecular markers of cellular circuit substrates may support the identification of potential pharmaceutical targets in treating pain. The authors confirm a previous study in that a somatostatin-positive cellular population presents a crucial vlPAG circuit element mediating anti-nociceptive effects. Key novelty aspects of the present study are the demonstration that these neurons seem to play a role specifically in threat-induced analgesia. This was possible by the elegant design and application of a novel fear analgesia paradigm, combined with cell- and pathway-specific optogenetics.

Weaknesses:

Despite the convincing and rigorous experimental approach, the study leaves some interpretational room when it comes to the proposed circuit mechanism. This could either be addressed by additional experiments or by more discussion of alternative circuit layouts.

Major Comments:

(1) The paper by Zhang et al. (https://pubmed.ncbi.nlm.nih.gov/36641028/), which identified a role for vlPAG SOM+ neurons in mediating anti-nociception in neuropathic pain, needs to be referenced and its results discussed, if not reconciled. While functionally, both studies find an analgetic role of vlPAG SOM+ neurons projecting to the RVM, Zhang et al., using slice physiology, characterize those neurons as glutamatergic. In Figure 4E of Zhang et al. they find general (fear-independent) analgetic effects with PAG-RVM specificity by performing chemogenetic experiments.

It can be argued that in addition to the two functionally distinct inhibitory SOM subtypes hypothesized by Winke et al., there is another, excitatory subpopulation. Also, the different experimental conditions (chronic vs. acute pain, non-threat vs. fearful cues/contexts may recruit different vlPAG SOM+ populations. All of this is conceivable, yet I wonder whether the contrasting findings could more parsimoniously be reconciled. The author's own results presented here in Supplementary Figure 3 suggests that SOM+ vlPAG cells are co-localizing with glutamate and thus could also be excitatory. In addition to this rather complementary piece of evidence, a more extensive characterization of vlPAG neurons using IHC and slice physiology would be needed to justify the unambiguous identification of their inhibitory nature.

In the absence of a direct identification of these cells exclusively releasing GABA, an alternative explanation should be considered. What about looking at vlPAG SOM+ neurons as a putatively mixed bag of local, inhibitory interneurons and long-range, RVM-projecting excitatory cells? This model would then open up interesting questions as to the actual function of somatostatin as a modulator of vlPAG circuit activity and associated function, and from my perspective, would nicely fit into the view of PAG circuits as integrators of complex survival responses.

(2) "Our data indicate that the optogenetic inhibition of SST+ vlPAG cells promotes analgesia irrespective of the animal's defensive state. In contrast, the optogenetic activation of long-range SST+ vlPAG cells that project to the rostral ventromedial medulla (RVM) abolishes the analgesia mediated by fear behavior." (lines 32-35). Consider toning down these conclusions, as contrasting activation with inhibition of two different (though overlapping) populations cannot be fully conclusive. Alternatively, a pathway-specific (vlPAG-RVM) inhibitory experiment could help to fully understand the circuit mechanism and verify the necessity of these neurons.

(3) Despite an overall very thorough reporting style, some information is missing from the manuscript:

a) In Figures 2d and f, what are the freezing levels during optogenetic manipulation? From Figure 3d, one can expect that freezing is inhibited during the hot plate test, which could bias the NC response towards shorter latencies. b) In Figure 5, the histological experiment showing the vlPAG-to-RVM pathway is presented by a qualitative image only. Here, some quantification would strengthen the finding. c) In Figures 6 c and d "Consistently, activation of the SST+ vlPAG-RVM pathway during CFCA had no impact on CS-presentation, whereas the same manipulation performed during CS+ blocked the increase in NC response latency compared to GFP controls." (line 194-196). Is it possible that the NC response cannot be any lower than the one during CS-, thus constituting a floor effect? d) Connected to major point 1- this experiment is important for defining the circuit mode and therefore should be as convincing as possible. However, for the colocalization experiment in Supplementary Figure 3, the methodological description is missing and thus makes it hard to comprehend how this data set was generated (how many data points, etc.). The visual depiction of the results is non-standard and not easily graspable. Consider e.g., a Venn diagram.

Reviewer #3 (Public review):

Summary:

Conditioned analgesia refers to the ability of a learned fear cue to suppress pain-related behavior and neural activity. Understudied, the authors developed a novel conditioned analgesia procedure in which a cue that had been paired or unpaired with shock was played while a hot plate increased temperature. Compared to several control conditions, the authors found increased latency to a nociceptive response (paw licking). The authors identified somatostatin neurons in the periaqueductal gray as a likely mediator of the behavior. They then showed that: (1) stimulating vlPAG-SST neurons blocked nociceptive response latency increases to the CS+, (2) stimulating vlPAG-SST neurons suppressed fear retrieval freezing, (3) stimulating vs. inhibiting vlPAG-SST neurons drove opposing modulation of c-fibers and Aδ-fibers, (4) direct-projecting vlPAG SST neurons modulate freezing while RVM-projecting vlPAG SST neurons modulate conditioned analgesia.

Strengths:

These experiments have many strengths. The behavioral assay is chief among them. The assay is robust and controls for confounding factors to reveal a repeatable effect of a shock-paired cue to delay nociceptive responding. The optogenetic experiments provide the correct level of temporal precision, given the authors' time-specific interest in cued responding. Combining neuronal manipulations with spinal recordings is particularly innovative, especially in the context of more behavioral neuroscience-based assays. All-in-all, I found this to be an exceptionally strong set of experiments.

Weaknesses:

No obvious weaknesses were identified by this Reviewer.

eLife Assessment

This valuable study addresses the structural basis of voltage-activation of BK channels using atomistic simulations of several microseconds, to assess conformational changes that underlie both voltage-sensing and gating of the pore. The findings, including movement of specific charged residues, combined with the degree to which these movements are coupled to pore movements, provide a solid basis for understanding voltage-gating mechanisms in this class of channels. This paper will likely be of interest to ion channel biologists and biophysicists focused on voltage-dependent channel gating mechanisms.

Reviewer #1 (Public review):

Summary:

This study provides new insight into the non-canonicial voltage-gating mechanism of BK channels through prolonged (10 us) MD simulations of the Slo1 transmembrane domain conformation and K+ conduction in response to high imposed voltages (300, 750 mV). The results support previous conclusions based on functional and structural data and MD simulations that the voltage-sensor domain (VSD) of Slo1 undergoes limited conformational changes compared to Kv channels, and predicts gating charge movement comparable in magnitude to experimental results. The gating charge calculations further indicate that R213 and R210 in S4 are the main contributors owing to their large side chain movements and the presence of a locally focused electric field, consistent with recent experimental and MD simulation results by Carrasquel-Ursulaez et al.,2022. Most interestingly, changes in pore conformation and K+ conduction driven by VSD activation are resolved, providing information regarding changes in VSD/pore interaction through S4/S5/S6 segments proposed to underly electromechanical coupling.

Strengths:

Include that the prolonged timescale and high voltage of the simulation allow apparent equilibration in the voltage-sensor domain (VSD) conformational changes and at least partial opening of the pore. The study extends the results of previous MD simulations of VSD activation by providing quantitative estimates of gating charge movement, showing how the electric field distribution across the VSD is altered in resting and activated states, and testing the hypothesis that R213 and R210 are the primary gating charges by steered MD simulations. The ability to estimate gating charge contributions of individual residues in the WT channel is useful as a comparison to experimental studies based on mutagenesis which have yielded conflicting results that could reflect perturbations in structure. Use of dynamic community analysis to identify coupling pathways and information flow for VSD-pore (electromechanical) coupling as well as analysis of state-dependent S4/S5/S6 interactions that could mediate coupling provide useful predictions extending beyond what has been experimentally tested.

Weaknesses:

Weaknesses include that a truncated channel (lacking the C-terminal gating ring) was used for simulations, which is known to have reduced single channel conductance and electromechanical coupling compared to the full-length channel. In addition, as VSD activation in BK channels is much faster than opening, the timescale of simulations was likely insufficient to achieve a fully open state as supported by differences in the degree of pore expansion in replicate simulations, which are also smaller than observed in Ca-bound open structures of the full-length channel. Taken together, these limitations suggest that inferences regarding coupling pathways and interactions in the fully open voltage-activated channel may be only partially supported and therefore incomplete. That said, adequate discussion regarding these limitations are provided together with dynamic community analysis based on the Ca-bound open structure. The latter supports the main conclusions based on simulations, while providing an indication of potential interaction differences between simulated and fully open conformations. Another limitation is that while the simulations convincingly demonstrate voltage-dependent channel opening as evidenced by pore expansion and conduction of K+ and water through the pore, single channel conductance is underestimated by at least an order of magnitude, as in previous studies of other K+ channels. These quantitative discrepancies suggest that MD simulations may not yet be sufficiently advanced to provide insight into mechanisms underlying the extraordinarily large conductance of BK channels.

Comments on revisions:

My previous questions and concerns have been adequately addressed.

My only new comment is that the numbering of residues in Fig. S8 does not match the standard convention for hSlo and needs to be doublechecked. For the residues I checked, the numbers appear to be shifted 3 compared hSlo (e.g. Y315, P317, E318, G324 should be Y318, P320, E321, G327).

Reviewer #2 (Public review):

Summary:

The manuscript by Jia and Chen addresses the structural basis of voltage-activation of BK channels using computational approaches. Although a number of experimental studies using gating current and patch-clamp recording have analyzed voltage-activation in terms of observed charge movements and the apparent energetic coupling between voltage-sensor movement and channel opening, the structural changes that underlie this phenomenon have been unclear. The present studies use a reduced molecular system comprising the transmembrane portion of the BK channel (i.e. the cytosolic domain was deleted), embedded in a POPC membrane, with either 0 or 750 mV applied across the membrane. This system enabled acquisition of long simulations of 10 microseconds, to permit tracking of conformational changes of the channel. The authors principal findings were that the side chains of R210 and R213 rapidly moved toward the extracellular side of the membrane (by 8 - 10 Å), with greater displacements than any of the other charged transmembrane residues. These movements appeared tightly coupled to movement of the pore-lining helix, pore hydration, and ion permeation. The authors estimate that R210 and R213 contribute 0.25 and 0.19 elementary charges per residue to the gating current, which is roughly consistent with estimates based on electrophysiological measurements that used the full-length channel.

Strengths:

The methodologies used in this work are sound, and these studies certainly contribute to our understanding of voltage-gating of BK channels. An intriguing observation is the strongly coupled movement of the S4, S5, and S6 helices that appear to underlie voltage-dependent opening. Based on Fig 2a-d, the substantial movements of the R210 and R213 side chains occur nearly simultaneously to the S6 movement (between 4 - 5 usec of simulation time). This seems to provide support for a "helix-packing" mechanism of voltage gating in the so-called "non-domain-swapped" voltage-gated K channels.

Weaknesses:

The main limitation is that these studies used a truncated version of the BK channel, and there are likely to be differences in VSD-pore coupling in the context of the full-length channels that will not be resolved in the present work. Nonetheless, the authors provide a strong rationale for their use of the truncated channel, and the results presented will provide a good starting point for future computational studies of this channel.

Author response:

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

Recommendations for the authors:

Reviewing Editor Comments:

The resubmitted version of the manuscript adequately addressed several initial comments made by reviewing editors, including a more detailed analysis of the results (such as those of bilayer thickness). This version was seen by 2 reviewers. Both reviewers recognize this work as being an important contribution to the field of BK and voltage-dependent ion channels in general. The long trajectories and the rigorous/novel analyses have revealed important insights into the mechanisms of voltage-sensing and electromechanical coupling in the context of a truncated variant of the BK channel. Many of these observations are consistent with structural and functional measurements of the channel, available thus far. The authors also identify a novel partially expanded state of the channel pore that is accessed after gating-charge displacement, which informs the sequence of structural events accompanying voltage-dependent opening of BK.

However, there are key concerns regarding the use of the truncated channel in the simulations. While many gating features of BK are preserved in the truncated variant, studies have suggested that opening of the channel pore to voltage-sensing domain rearrangement is impaired upon gating-ring deletion. So the inferences made here might only represent a partial view of the mechanism of electromechanical coupling.

It is also not entirely clear whether the partially expanded pore represents a functionally open, sub-conductance, or another closed state. Although the authors provide evidence that the inner pore is hydrated in this partially open state, in the absence of additional structural/functional restraints, a confident assignment of a functional state to this structure state is difficult. Functional measurements of the truncated channel seem to suggest that not only is their single channel conductance lower than full-length channels, but they also appear to have a voltage-independent step that causes the gates to open. It is unclear whether it is this voltage-independent step that remains to be captured in these MD trajectories. A clean cut resolution of this conundrum might not be feasible at this time, but it could help present the various possibilities to the readers.

We appreciate the positive comments and agree that there will likely be important differences between the mechanistic details of voltage activation between the Core-MT and full-length constructs of BK channels. We also agree that the dilated pore observed in the simulation may not be the fully open state of Core-MT.

Nonetheless, the notion that the simulation may not have captured the full pore opening transition or the contribution of the CTD should not render the current work “incomplete”, because a complete understanding of BK activation would be an unrealistic goal beyond the scope of this work. We respectfully emphasize that the main insights of the current simulations are the mechanisms of voltage sensing (e.g., the nature of VSD movements, contributions of various charged residues, how small charge movements allow voltage sensing, etc.) as well as the role of the S4-S5-S6 interface in VSD-pore coupling. As noted by the Editor and reviewers, these insights represent important steps towards establishing a more complete understanding of BK activation.

Below are the specific comments of the two experts who have assessed the work and made specific suggestions to improve the manuscript.

Reviewer #1 (Recommendations for the authors):

(1) Although the successful simulation of V-dependent K+ conduction through the BK channel pore and analysis of associated state dependent VSD/pore interactions and coupling analysis is significant, there are two related questions that are relevant to the conclusions and of interest to the BK channel community which I think should be addressed or discussed.

One key feature of BK channels is their extraordinarily large conductance compared to other K+ selective channels. Do the simulations of K+ conductance provide any insight into this difference? Is the predicted conductance of BK larger than that of other K+ channels studied by similar methods? Is there any difference in the conductance mechanism (e.g., the hard and soft knock-on effects mentioned for BK)?

The molecular basis of the large conductance of BK channels is indeed an interesting and fundamental question. Unfortunately, this is beyond the scope of this work and the current simulation does not appear to provide any insight into the basis of large conductance. It is interesting to note, though, the conductance is apparently related to the level of pore dilation and the pore hydration level, as increasing hydration level from ~30 to ~40 waters in the pore increases the simulated conductance from ~1.5 to 6 pS (page 8). This is consistent with previous atomistic simulations (Gu and de Groot, Nature Communications 2023; ref. 33) showing that the pore hydration level is strongly correlated with observed conductance. As noted in the manuscript, the conductance mechanism through the filter appears highly similar to previous simulations of other K+ channels (Page 8). Given the limit conductance events observed in the current simulations, we will refrain from discussing possible basis of the large conductance in BK channels except commenting on the role of pore hydration (page 8; also see below in response to #5).

The pore in the MD simulations does not open as wide as the Ca-bound open structure, which (as the authors note) may mean that full opening requires longer than 10 us. I think that is highly likely given that the two 750 mV simulations yielded different degrees of opening and that in BK channels opening is generally much slower than charge movement. Therefore, a question is - do any of the conclusions illustrated in Figures 6, S5, S6 differ if the Ca-bound structure is used as the open state? For example, I expect the interactions between S5 and S6 might at least change to some extent as S6 moves to its final position. In this case, would conclusions about which residues interact, and get stronger or weaker, be the same as in Figures S6 b,c? Providing a comparison may help indicate to what extent the conclusions are dependent on achieving a fully open conformation.

We appreciate the reviewer’s suggestion and have further analyzed the information flow and coupling pathways using the simulation trajectory initiated from the Ca2+-bound cryo-EM structure (sim 7, Table S1). The new results are shown in two new SI Figures S7 and S8, and new discussion has been added to pages 14-15. Comparing Figures 5 and S7, we find that dynamic community, coupling pathways, and information flow are highly similar between simulation of the open and closed states, even though there are significant differences in S5 contacts in the simulated open state vs Ca2+-bound open state (Figure S8). Interestingly, there are significant differences in S4-S5 packing in the simulated and Ca2+-bound open states (Figure S8 top panel), which likely reflect important difference in VSD/pore interactions during voltage vs Ca2+ activation.

(2) P4 Significance -"first, successful direct simulation of voltage-activation"

This statement may need rewording. As noted above Carrasquel-Ursulaez et al.,2022 (reference 39) simulated voltage sensor activation under comparable conditions to the current manuscript (3.9 us simulation at +400 mV), and made some similar conclusions regarding R210, R213 movement, and electric field focusing within the VSD. However, they did not report what happens to the pore or simulate K+ movement. So do the authors here mean something like "first, successful direct simulation of voltage-dependent channel opening"?

We agree with the reviewer and have revised the statement to “ … the first successful direct simulation of voltage-dependent activation of the big potassium (BK) channel, ..”

(3) P5 "We compare the membrane thickness at 300 and 750 mV and the results reveal no significant difference in the membrane thickness (Figure S2)" The figure also shows membrane thickness at 0 mV and indicates it is 1.4 Angstroms less than that at 300 or 750 mV. Whether or not this difference is significant should be stated, as the question being addressed is whether the structure is perturbed owing to the use of non-physiological voltages (which would include both 300 and 750 mV).

We have revised the Figure S2 caption to clarify that one-way ANOVA suggest the difference is not significant.

(4) P7 "It should be noted that the full-length BK channel in the Ca2+ bound state has an even larger intracellular opening (Figure 2f, green trace), suggesting that additional dilation of the pore may occur at longer timescales."

As noted above, I agree it is likely that additional pore dilation may occur at longer timescales. However, for completeness, I suppose an alternative hypothesis should be noted, e.g. "...suggesting that additional dilation of the pore may occur at longer timescales, or in response to Ca-binding to the full length channel."

This is a great suggestion. Revised as suggested.

(5) Since the authors raise the possibility that they are simulating a subconductance state, some more discussion on this point would be helpful, especially in relation to the hydrophobic gate concept. Although the Magleby group concluded that the cytoplasmic mouth of the (fully open) pore has little impact on single channel conductance, that doesn't rule out that it becomes limiting in a partially open conformation. The simulation in Figure 3A shows an initial hydration of the pore with ~15 waters with little conductance events, suggesting that hydration per se may not suffice to define a fully open state. Indeed, the authors indicate that the simulated open state (w/ ~30-40 waters) has 1/4th the simulated conductance of the open structure (w/ ~60 waters). So is it the degree of hydration that limits conductance? Or is there a threshold of hydration that permits conductance and then other factors that limit conductance until the pore widens further? Addressing these issues might also be relevant to understanding the extraordinarily large conductance of fully open BK compared to other K channels.

We agree with the reviewer’s proposal that pore hydration seems to be a major factor that can affect conductance. This is also well in-line with the previous computational study by Gu and de Groot (2023). We have now added a brief discussion on page 8, stating “Besides the limitation of the current fixed charge force fields in quantitively predicting channel conductance, we note that the molecular basis for the large conductance of BK channels is actually poorly understood (78). It is noteworthy that the pore hydration level appears to be an important factor in determining the apparent conductance in the simulation, which has also been proposed in a previous atomistic simulation study of the Aplysia BK channel (33).”

Minor points

(1) P5 "the fully relaxed pore profile (red trace in Figure S1d, top row) shows substantial differences compared to that of the Ca2+-free Cryo-EM structure of the full-length channel." For clarity, I suggest indicating which is the Ca-free profile - "... Ca2+-free Cryo-EM structure of the full-length channel (black trace)."

We greatly appreciate the thoughtful suggestion. Revised as suggested.

(2) P8 "Consistent with previous simulations (78-80), the conductance follows a multi-ion mechanism, where there are at least two K+ ions inside the filter" For clarity, I suggest indicating these are not previous simulations of BK channels (e.g., "previous simulations of other K+ channels ...").

Revised as suggested. Thank you.

(3) Figure 2, S1 - grey traces representing individual subunits are very difficult to see (especially if printed). I wonder if they should be made slightly darker. Similar traces in Figure 3 are easier to see.

The traces in Figure S1 are actually the same thickness in Figure 3 and they appear lighter due to the size of the figure. Figure 2 panels a-c have been updated to improve the resolution.

(4) Figure 2 - suggest labeling S6 as "S6 313-324" (similar to S4 notation) to indicate it is not the entire segment.

Figure 2 panel d) has been updated as suggested.

(5) Figure 2 legend - "Voltage activation of Core-MT BK channels. a-d)..."

It would be easier to find details corresponding to individual panels if they were referenced individually. For example:

"a-d) results from a 10-μs simulation under 750 mV (sim2b in Table S1). Each data point represents the average of four subunits for a given snapshot (thin grey lines), and the colored thick lines plot the running average. a) z-displacement of key side chain charged groups from initial positions. The locations of charged groups were taken as those of guanidinium CZ atoms (for Arg) and sidechain carboxyl carbons (for Asp/Glu) b) z-displacement of centers-of-mass of VSD helices from initial positions, c) backbone RMSD of the pore-lining S6 (F307-L325) to the open state, and d) tilt angles of all TM helices. Only residues 313-324 of S6 were included inthe tilt angle calculation, and the values in the open and closed Cryo-EM structures are marked using purple dashed lines. "

We appreciate the thoughtful suggestion and have revised the caption as suggested.

(6) Figure S1 - column labels a,b,c, and d should be referenced in the legend.

The references to column labels have been added to Figure S1 caption.

(7) References need to be double-checked for duplicates and formatting.

a) I noticed several duplicate references, but did not do a complete search: Budelli et al 2013 (#68, 100), Horrigan Aldrich 2002 (#22,97), Sun Horrigan 2022 (#40, 86), Jensen et al 2012 (#56,81).

b) Reference #38 is incorrectly cited with the first name spelled out and the last name abbreviated.

We appreciate the careful proofreading of the reviewer. The duplicated references were introduced by mistake due to the use of multiple reference libraries. We have gone through the manuscript and removed a total of 5 duplicated references.

Reviewer #2 (Recommendations for the authors):

This manuscript has been through a previous level of review. The authors have provided their responses to the previous reviewers, which appear to be satisfactory, and I have no additional comments, beyond the caveats concerning interpretations based on the truncated channel, which are noted above.

We greatly appreciate the constructive comments and insightful advice. Please see above response to the Reviewing Editor’s comments for response and changes regarding the caveats concerning interpretations of the current simulations.

eLife Assessment

Sanchez-Vasquez et al establish an innovative approach to induce aneuploidy in preimplantation embryos. This important study extends the author's previous publications evaluating the consequences of aneuploidy in the mammalian embryo. In this work, the authors investigate the developmental potential of aneuploid embryos and characterize changes in gene expression profiles under normoxic and hypoxic culture conditions. Using a solid methodology they identify sensitivity to Hif1alpha loss in aneuploid embryos, and in further convincing experiments they assess how levels of DNA damage and DNA repair are altered under hypoxic and normoxic conditions.

Reviewer #1 (Public review):

Summary:

This paper developed a model of chromosome mosaicism by using a new aneuploidy-inducing drug (AZ3146), and compared this to their previous work where they used reversine, to demonstrate the fate of aneuploid cells during murine preimplantation embryo development. They found that AZ3146 acts similarly to reversine in inducing aneuploidy in embryos, but interestingly showed that the developmental potential of embryos is higher in AZ3146-treated vs. reversine-treated embryos. This difference was associated with changes in HIF1A, p53 gene regulation, DNA damage, and fate of euploid and aneuploid cells when embryos were cultured in a hypoxic environment.

Strengths:

In the current study, the authors investigate the fate of aneuploid cells in the preimplantation murine embryo using a specific aneuploidy-inducing compound to generate embryos that were chimeras of euploid and aneuploid cells. The strength of the work is that they investigate the developmental potential and changes in gene expression profiles under normoxic and hypoxic culture conditions. Further, they also assessed how levels of DNA damage and DNA repair are altered in these culture conditions. They also assessed the allocation of aneuploid cells to the divergent cell lineages of the blastocyst stage embryo.

Weaknesses:

The authors have still not addressed the inconsistent/missing description for sample size, the appropriate number of * for each figure panel, and the statistical tests used.

The authors assign 5% oxygen as hypoxia. This is not the case as the in vivo environment is close to this value. 5% is normoxia. Clinical IVF/embryo culture occurs at 5% O2. Please adjust your narrative around this.

Reviewer #2 (Public review):

Summary:

This study by Sanchez-Vasquez is a very innovative approach to induce aneuploidy and then study the contribution of treated cells to different lineages, including post implantation. It connects well to the authors previous work to induce mosaic aneuploidies. The authors identify sensitivity to HIF1a loss in treated embryos with likely aneuploidy. This work is part of an important line of work with evaluates the consequences of aneuploidy in mammalian embryo.

Weaknesses:

Given that this is a study on the induction of aneuploidy, it would be meaningful to assess aneuploidy immediately after induction, and then again before implantation. This is also applicable to the competition experiments on page 7/8. What is shown is the competitiveness of treated cells. Because the publication centers around aneuploidy, inclusion of such data in the main figure at all relevant points would strengthen it. There is some evaluation of karyotypes only in the supplemental - why? Would be good not to rely on a single assay that the authors appear to not give much importance.

eLife Assessment

This paper identifies a crucial step in the regulation of tight junction formation by identifying Rho-ROCK activity-dependent activation of the serine protease Matriptase, making Claudins available for tight junction formation. The reviewers were satisfied with the revisions and found the work important and the approach convincing.

Reviewer #1 (Public review):

Summary:

The manuscript by Cho and colleagues investigates de novo tight junction formation during the differentiation of immortalized human HaCaT keratinocytes to granular-like cells, as well as during epithelial remodeling that occurs upon the apoptotic of individual cells in confluent monolayers of the representative epithelial cell line EpH4. The authors demonstrate the involvement of Rho-ROCK with well-conducted experiments and convincing images. Moreover, they unravel the underlying molecular mechanism, with Rho-ROCK activity activating the transmembrane serine protease Matriptase, which in turn leads to the cleavage of EpCAM and TROP2, respectively, releasing Claudins from EpCAM/TROP2/Claudin complexes at the cell membrane to become available for polymerization and de novo tight junction formation. These functional studies in two different cell culture systems are complemented by localization studies of the according proteins in the stratified mouse epidermis in vivo.

In total, these are new and very intriguing and interesting findings that add important new insights into the molecular mechanisms of tight junction formation, identifying Matriptase as the "missing link" in the cascade of formerly described regulators. The involvement of TROP2/EpCAM/Claudin has been reported recently (Szabo et al., Biol. Open 2022; Bugge lab), and Matriptase had been formerly described to be required for tight junction formation as well, again from the Bugge lab. Yet, the functional correlation / epistasis between them, and their relation to Rho signaling, had not been known thus far.

Strengths:

Convincing functional studies in two different cell culture systems, complemented by supporting protein localization studies in vivo. The manuscript is clearly written and most data are convincingly demonstrated, with beautiful images and movies.

Weaknesses:

The previously described weaknesses have been fully wiped out during the revisions.

Reviewer #2 (Public review):

Summary:

In this manuscript the authors investigate how epithelia maintain intercellular barrier function despite and during cellular rearrangements upon e.g. apoptotic extrusion in simple epithelia or regenerative turnover in stratified epithelia like this epidermis. A fundamental question in epithelial biology. Previous literature has shown that Rho mediated local regulation of actomyosin is essential not only for cellular rearrangement itself but also directly controls tight junction barrier function. The molecular mechanics however remained unclear. Here the authors use extensive fluorescence imaging of fixed and live cells together with genetic and drug mediated interference to show that Rho activation is required and sufficient to form de novo tight junctional strands at intercellular contacts in epidermal keratinocytes (HaCat) and mammary epithelial cells. After having confirmed previous literature they then show that Rho activation activates the transmembrane protease matriptase which cleaves EpCAM and TROP2, two claudin binding transmembrane proteins, to release claudins and enable claudin strand formation and therefore tight junction barrier function.

Strengths:

The presented mechanism is shown to be relevant for epithelial barriers being conserved in simple and stratifying epithelial cells and mainly differs due to tissue specific expression of EpCAM and TROP2. The authors present carefull state of the art imaging and logical experiments that convincingly support the statements and conclusion. The manuscript is well written and easy to follow.

Weaknesses:

Whereas the in vitro evidence of the presented mechanism is strongly supported by the data, the in vivo confirmation is mostly based on the predicted distribution of TROP2. Whereas the causality of Rho mediated matriptase activation has been nicely demonstrated it remains unclear how Rho activates matriptase.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript "Rho-ROCK liberates sequestered claudin for rapid de novo tight junction formation" by Cho and colleagues investigates de novo tight junction formation during the differentiation of immortalized human HaCaT keratinocytes to granular-like cells, as well as during epithelial remodeling that occurs upon the apoptotic of individual cells in confluent monolayers of the representative epithelial cell line EpH4. The authors demonstrate the involvement of Rho-ROCK with well-conducted experiments and convincing images. Moreover, they unravel the underlying molecular mechanism, with Rho-ROCK activity activating the transmembrane serine protease Matriptase, which in turn leads to the cleavage of EpCAM and TROP2, respectively, releasing Claudins from EpCAM/TROP2/Claudin complexes at the cell membrane to become available for polymerization and de novo tight junction formation. These functional studies in the two different cell culture systems are complemented by localization studies of the according proteins in the stratified mouse epidermis in vivo.

In total, these are new and very intriguing and interesting findings that add important new insights into the molecular mechanisms of tight junction formation, identifying Matriptase as the "missing link" in the cascade of formerly described regulators. The involvement of TROP2/EpCAM/Claudin has been reported recently (Szabo et al., Biol. Open 2022; Bugge lab), and Matriptase had been formerly described to be required for in tight junction formation as well, again from the Bugge lab. Yet, the functional correlation/epistasis between them, and their relation to Rho signaling, had not been known thus far.

However, experiments addressing the role of Matriptase require a little more work.

Strengths:

Convincing functional studies in two different cell culture systems, complemented by supporting protein localization studies in vivo. The manuscript is clearly written and most data are convincingly demonstrated, with beautiful images and movies.

Weaknesses:

The central finding that Rho signaling leads to increased Matriptase activity needs to be more rigorously demonstrated (e.g. western blot specifically detecting the activated version or distinguishing between the full-length/inactive and processed/active version).

First, we thank the reviewer for their fair evaluation of our manuscript and for providing constructive feedback. Regarding the detection of matriptase activation—which Reviewer 1 identified as a weakness—we fully agree that direct validation is crucial. Therefore, in this revision we have carried out additional experiments using the M69 antibody, which specifically recognizes the activated form of matriptase. Details of these new experiments are provided in our point-by-point responses below.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigate how epithelia maintain intercellular barrier function despite and during cellular rearrangements upon e.g. apoptotic extrusion in simple epithelia or regenerative turnover in stratified epithelia like this epidermis. A fundamental question in epithelial biology. Previous literature has shown that Rho-mediated local regulation of actomyosin is essential not only for cellular rearrangement itself but also for directly controlling tight junction barrier function. The molecular mechanics however remained unclear. Here the authors use extensive fluorescent imaging of fixed and live cells together with genetic and drug-mediated interference to show that Rho activation is required and sufficient to form novo tight junctional strands at intercellular contacts in epidermal keratinocytes (HaCat) and mammary epithelial cells. After having confirmed previous literature they then show that Rho activation activates the transmembrane protease Matriptase which cleaves EpCAM and TROP2, two claudin-binding transmembrane proteins, to release claudins and enable claudin strand formation and therefore tight junction barrier function.

Strengths:

The presented mechanism is shown to be relevant for epithelial barriers being conserved in simple and stratifying epithelial cells and mainly differs due to tissue-specific expression of EpCAM and TROP2. The authors present careful state-of-the-art imaging and logical experiments that convincingly support the statements and conclusion. The manuscript is well-written and easy to follow.

Weaknesses:

Whereas the in vitro evidence of the presented mechanism is strongly supported by the data, the in vivo confirmation is mostly based on the predicted distribution of TROP2. Whereas the causality of Rho-mediated Matriptase activation has been nicely demonstrated it remains unclear how Rho activates Matriptase.

Thank you for your valuable feedback on our manuscript. As Reviewer 2 points out, the precise mechanism by which the Rho/ROCK pathway activates matriptase remains unclear. We have discussed the possible molecular mechanisms in the Discussion section. Elucidating the detailed mechanism of matriptase activation will be the focus of our future work.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comment 1-1 - Matriptase activation by Rho: The authors show activation of Matriptase in western blots by the simple reduction of (full-length?) protein level in Figures 5 and 7. Most publications however show activated Matriptase either by antibodies detecting specifically the active form (including the publication referenced in this manuscript), or the appearance of the activated form next to the inactive form (based on different molecular weights). Therefore, it is not completely clear whether the treatment with Rho activators (Figure 5) results in an overall decrease of Matriptase, or really in an increase in the activated form. Therefore, the authors should show the actual increase of the active form. As a control, the impact of camostat treatment and overexpression of Hai1 on the active form of Matriptase could be included. It also should be indicated in the figure legend how long cells had been treated with the drugs before being subjected to lysis. Moreover, the western blots need to be quantified.

We performed a more rigorous analysis using the M69 antibody, which specifically recognizes the activated form of matriptase and has been widely used in previous studies（e.g. Benaud et al., 2001; Hung et al., 2004; Wang et al., 2009）. We likewise confirmed a significant increase in M69 signals by both western blotting and immunostaining from samples in which matriptase was activated by acid medium treatment (Figure 5A). Crucially, we also observed matriptase activation with the M69 antibody both in Rho/ROCK activator-treated cells (Figure 5A) and in differentiated granular-layer-like cells (Figures 7A and 7D). These findings strongly support the conclusion that matriptase is activated downstream of the Rho/ROCK pathway.

Comment 1-2 - Based on their results, the authors conclude that Matriptase cleaves TROP2 in the SG2 layer of the epidermis, which is a little contradictory to former studies, which have shown Matriptase to be most prominently expressed and active in the basal layer and only little in the spinous layer (e.g Chen et al., Matriptase regulates proliferation and early, but not terminal, differentiation of human keratinocytes. J Invest Dermatol.2013). In this light, one could also argue that inhibiting Matriptase "simply" reduces epidermal differentiation. Can other differentiation markers be tested to rule that the effects on tight junctions are secondary consequences of interferences with earlier / more global steps of keratinocyte differentiation?

As the reviewer noted, previous studies have demonstrated that matriptase is essential for keratinocyte differentiation, and that it cleaves substrates beyond EpCAM and TROP2—any of which could potentially influence the differentiation process. To test this possibility, we chose to monitor maturation of adherens junction (AJ) as an indicator of keratinocyte differentiation into granular-layer cells. Prior work has shown that during differentiation into granular-layer cells, AJs develop and experience increased intercellular mechanical tension, and that this rise in mechanical tension at AJs is critical for subsequent TJ formation (Rübsam et al., 2017). To assess AJ tension, we stained with the α-18 monoclonal antibody, which specifically recognizes the tension-dependent conformational change of α-catenin, a core AJ component. In control cells, differentiation into granular-layer like cells led to a marked increase in α-18 signal at cell–cell adhesion sites. Importantly, when HaCaT cells were treated with Camostat to inhibit matriptase and then induced to differentiate, we observed an equivalent increase in α-18 signal at AJs (Figure 7F). However, we did not detect claudin enrichment at cell-cell contacts under these conditions (Figures 7F and 7H). These results suggest that matriptase inhibition does not impair AJ maturation during granular-layer differentiation, but does profoundly disrupt TJ formation. While we cannot rule out the possibility that matriptase acts more broadly from these results, we judged that a comprehensive substrate survey lies outside the scope of the present manuscript.

Comment 1-3 - In addition, as in Figure 5, full-length levels of Matriptase in Figure 7A need to be complemented by the active version to demonstrate more convincingly that TROP2 processing coincides with (and is most likely caused by) increased Matriptase activation. In the quantification in 7B, levels actually go up again after 2 and 4 hours. How is that explained, and what would this mean with respect to tight junction formation seen at 24 h of differentiation? The TROP2 cleavage shown in Figure 7A should be quantified.

This comment is related to Comment 1-1. Using the M69 antibody, which specifically recognizes the activated matriptase, we directly demonstrated that matriptase activation occurs during the differentiation of granular layer-like cells (Figures 7A and 7D). Furthermore, we performed quantitative analysis of TROP2 cleavage and found that, compared with undifferentiated cells, differentiation into granular-layer like cells was accompanied by an increase in the cleaved TROP2 fragments (Figures 7A and 7B).

Minor points:

Comment 1-4 - Figure 1B and C: Including orthogonal views would be a nice add-on to appreciate the findings.

In the revised version, we have added the corresponding orthogonal views to Figure 1B and Figure 1C.

Comment 1-5 - Figure 2D: last row: indication of orthogonal view.

We stated that the bottom panels are orthogonal views in the figure legend of Figure 2D.

Comment 1-6 - Figure 3A: quantification is missing. GST-Rhotekin assay is missing in methods.

In the revised manuscript, we have added quantitative analysis for Figure 3A. We have also supplemented the Materials and Methods section with detailed information on the GST–Rhotekin assay used to quantify levels of active RhoA.

Comment 1-7 - Figure 4H: quantification of the Western blot is missing.

In the revised manuscript, we have added quantitative analysis for Figure 4H as Figure 4I.

Comment 1-8 - Figure 5 and 6: Quantifications of Western blots are missing.

In the revised manuscript, we have added quantitative analyses for Figure 5D as Figure 5F and for Figure 6A as Figure 6B.

Comment 1-9 - Figure 7C: quantification of the Western blot is missing.

Figure 7C does not present western blotting data. For the other western blotting results, we have added quantitative analyses as suggested by Reviewer 1.

Comment 1-10 - Figure 8I: Including Hai1 overexpression would be good for a complete picture.

Following Reviewer 1’s suggestion, we have added staining data for Hai1-overexpressing cells to Figure 8J.

Comment 1-11 - Line 377: The authors say they found Matriptase always present in lateral membranes. I did not find evidence for this in the manuscript.

Previous studies have demonstrated that in polarized epithelial cells, matriptase is localized to the basolateral membrane below TJs (Buzza et al., 2010; Wang et al., 2009). We also found that matriptase consistently localizes to the basolateral membrane but more crucially that it becomes activated there during differentiation into granular layer cells. We added these new data as Figures 7C-7E in the revised manuscript. These findings suggest that matriptase activation occurs without a change in its subcellular localization.

Comment 1-12 - Line 381: should most likely say: and ADAM17 but it is not known whether...

We corrected the sentence in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

The authors have added a significant number of quantifications verifying their observations, which was a major comment in a previous version of the manuscript and thus I have only a few minor comments which should be addressed.

Comment 2-1 - It is not required to have scale bars in every image of a panel if the same scale is used.

Unnecessary scale bars were removed. Specifically, scale bars were removed from Figure 1B, 1C, 1F, 8F, 8G, and 8H.

Comment 2-2 - Throughout all figures: Please state for non-quantified images whether this is a representative example and for how many technical or biological repeats this is representative. Also for "N" number, state what the N stands for and if this is what the dots in the graph represent. Are these the number of junctions or technical, experimental or biological repeats?

In the revised manuscript, we have added the number of independent experiments and corresponding “N” values to the Quantification and Statistical Analysis subsection of the Materials and Methods.

Comment 2-3 - Some Zooms have a scale bar (6d), and some do not (e.g. 5b).

The scale bar was removed from the magnified image in Figure 6D.

eLife Assessment

This valuable study by Wu et al presents data on bacterial cell organization, demonstrating that the two structures that account for bacterial motility - the chemotaxis complex and the flagella - colocalize to the same pole in Pseudomonas aeruginosa cells. The work provides convincing results for the regulation underlying this spatial organization and its functioning.

Reviewer #1 (Public review):

Summary:

The study by Wu et al presents interesting data on bacterial cell organization, a field that is progressing now, mainly due to the advances in microscopy. Based mainly on fluorescence microscopy images, the authors aim to demonstrate that the two structures that account for bacterial motility, the chemotaxis complex and the flagella, colocalize to the same pole in Pseudomonas aeruginosa cells and to expose the regulation underlying their spatial organization and functioning.

Comments on revisions:

The authors have addressed all major and minor points that I raised in a satisfying way during the revision process. The work can now be regarded as complete, the assumptions were clarified, the results are convincing, the conclusions are justified, and the novelty has been made clear.

This manuscript will be of interest to cell biologists, mainly those studying bacteria, but not only

Reviewer #2 (Public review):

Summary:

Here, the authors studied the molecular mechanisms by which the chemoreceptor cluster and flagella motor of Pseudomonas aeruginosa (PA) are spatially organized in the cell. They argue that FlhF is involved in localizing the receptors-motor to the cell pole, and even without FlhF, the two are colocalized. Finally, the authors argue that the functional reason for this colocalization is to insulate chemotactic signaling from other signaling pathways, such as cyclic-di-GMP signaling.

Strength:

The experiments and data are high quality. It is clear that the motor and receptors co-localize, and that elevated CheY levels lead to elevated c-di-GMP.

Weakness:

The explanation for the functional importance of receptor-motor colocalization is plausible but is still not conclusively demonstrated. Colocalization might reduce CheY levels throughout the cell in order to reduce cross-talk with c-di-GMP. This would mean that if physiologically-relevant levels of CheYp near the pole were present throughout the cell, c-di-GMP levels would be elevated to a point that is problematic for the cell. Clearly demonstrating this seems challenging.

Reviewer #3 (Public review):

Summary:

The authors investigated the assembly and polar localization of the chemosensory cluster in P. aeruginosa. They discovered that a certain protein (FlhF) is required for the polar localization of the chemosensory cluster while a fully-assembled motor is necessary for the assembly of the cluster. They found that flagella and chemosensory clusters always co-localize in the cell; either at the cell pole in wild type cells or randomly-located in the cell in FlhF mutant cells. They hypothesize that this co-localization is required to keep the level of another protein (CheY-P), which controls motor switching, at low levels as the presence of high-levels of this protein (if the flagella and chemosensory clusters were not co-localized) is associated with high-levels of c-di-GMP and cell aggregations.

Strengths:

The manuscript is clearly written and straightforward. The authors applied multiple techniques to study the bacterial motility system including fluorescence light microscopy and gene editing. In general, the work enhances our understanding of the subtlety of interaction between the chemosensory cluster and the flagellar motor to regulate cell motility.

Weaknesses:

The major weakness for me in this paper is that the authors never discussed how the flagellar genes expression is controlled in P. aeruginosa. For example, in E. coli there is a transcriptional hierarchy for the flagellar genes (early, middle, and late genes, see Chilcott and Hughes, 2000). Similarly, Campylobacter and Helicobacter have a different regulatory cascade for their flagellar genes (See Lertsethtakarn, Ottemann, and Hendrixson, 2011). How does the expression of flagellar genes in P. aeruginosa compare to other species? how many classes are there for these genes? is there a hierarchy in their expression and how does this affect the results of the FliF and FliG mutants? In other words, if FliF and FliG are in class I (as in E. coli) then their absence might affect the expression of other later flagellar genes in subsequent classes (i.e., chemosensory genes). Also, in both FliF and FliG mutants no assembly intermediates of the flagellar motor are present in the cell as FliG is required for the assembly of FliF (see Hiroyuki Terashima et al. 2020, Kaplan et al. 2019, Kaplan et al. 2022). It could be argued that when the motor is not assembled then this will affect the expression of the other genes (e.g., those of the chemosensory cluster) which might play a role in the decreased level of chemosensory clusters the authors find in these mutants.

Comments on revisions:

I believe the authors have performed additional experiments that improved their manuscript and they have answered many of my comments and those of the other reviewers. I am supportive of publishing this manuscript, but I still find the following points that are not clear to me (probably I am misunderstanding some points; the authors can clarify).

(1) In response to reviewer 1, the authors say that they "analyzed and categorized the distribution of the chemotaxis complex in both wild-type and flhF mutant strains into three patterns: precise-polar, near-polar, and mid-cell localization." I can see what they mean by polar and mid-cell, but near-polar sounds a bit elusive? Can they provide examples of this stage and mention how accurately they can identify it? Also, do the pie charts they show in Figure S4 really show "significant alterations"? There is a difference between 98% and 85% as they mention in their response to reviewer 1, but I am not sure that this is significant? Probably they can explain/change the language in the text? Also, the number of cells they counted for FlhF mutant is more than the double of other strains (WT and FlhF FliF mutant)?

(2) One thing that also confused me is the following: One point that the authors stress is that FlhF localizes both the flagellum and the chemoreceptors to the pole. However, if I look at Figure 2B, the flagellum and the chemoreceptors still co-localize together (although not at the pole). If FlhF was responsible for co-localizing both of them to the pole, then wouldn't one expect them to be randomly localized in this mutant and by that I mean that they do not co-localize but that each of them (the flagellum and the chemoreceptors) are located in a different random location of the cell (not co-localized). The fact that they are still co-localized together in this mutant could also be interpreted by, for example, that FlhF localizes the flagellum to the pole and another mechanism localizes the chemoreceptors to the flagellum, hence, they still co-localize in this mutant because the chemoreceptors follow the flagellum by another mechanism to wherever it goes?

(3) In the response to reviewers, the authors mention "suggesting that the assembly of the receptor complex is likely influenced mainly by the C-ring and MS-ring structures rather than by the P ring" . However, in the article, they still write "The complete assembly of the motor serves as a partial prerequisite for the assembly of the chemotaxis complex, and its assembly site is also regulated by the polar anchor protein FlhF" despite their FlgI results which is not in accordance with this statement? Also, As I mentioned in my previous report, in FliG and FliF mutant the motor does not assemble (see Hiroyuki Terashima et al. 2020., and Kaplan et al., 2022).

(4) The authors have said in their response to my point "and currently, there is no evidence that FliA activity is influenced by proteins like FliG". I just want to clarify what I meant in my previous report: In E. coli, FliA binds to FlgM, and when the hook is assembled FlgM is secreted outside the cell allowing FliA to trigger the transcription of class III genes, which include the chemosensory genes (see Figure 5 in Beeby et al, 2020 in FEMS Microbiology, and Chilcott and Hughes, 2000). This implies that if the hook is not built, then late genes (including the chemoreceptors) should not be present. However, in Kaplan et al., 2019, the authors imaged a FliF mutant in Shewanella oneidensis (Figure S3) and still saw that chemoreceptors are present (I believe the authors must highlight this). This suggests that species such as Shewanella and Pseudomonas have a different assembly process than that E. coli, and although the authors say that in the text, I believe they still can refine this part more in the spirit of what I wrote here.

I do not like to ask for additional experiments in the second round of review, so for me if the authors modify the text to tackle these points and allow for probable alternative explanations/ highlight gaps/ modify language used for some claims, then that is fine with me.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The study by Wu et al presents interesting data on bacterial cell organization, a field that is progressing now, mainly due to the advances in microscopy. Based mainly on fluorescence microscopy images, the authors aim to demonstrate that the two structures that account for bacterial motility, the chemotaxis complex and the flagella, colocalize to the same pole in Pseudomonas aeruginosa cells and to expose the regulation underlying their spatial organization and functioning.

Strengths:

The subject is of importance.

Weaknesses:

The conclusions are too strong for the presented data. The lack of statistical analysis makes this paper incomplete. The novelty of the findings is not clear.

We have strengthened the data analysis by including appropriate statistical tests to support our conclusions more convincingly. Additionally, we have refined the description of the research background to better emphasize the novelty and significance of our findings. Please see the detailed responses below for further information.

Major issues:

(1) The novelty is in question since in the Abstract the authors highlight their main finding, which is that both the chemotaxis complex and the flagella localize to the same pole, as surprising. However, in the Introduction they state that "pathway-related receptors that mediate chemotaxis, as well as the flagellum are localized at the same cell pole17,18". I am not a pseudomonas researcher and from my short glance at these references, I could not tell whether they report colocalization of the two structures to the same pole. However, I trust the authors that they know the literature on the localization of the chemotaxis complex and flagella in their organism. See also major issue number 5 on the novelty regarding the involvement of c-di-GMP.

We thank the reviewer for this valuable comment and appreciate the opportunity to clarify our statements.

Kazunobu et al. (ref. 18) used scanning electron microscopy to preliminarily characterize the flagellation pattern of Pseudomonas aeruginosa during cell division, showing that existing flagella are located at the old pole. Zehra et al. (ref. 17), through fluorescence microscopy, observed that CheA and CheY proteins in dividing cells are typically also present at the old pole. Based on these observations, we inferred in the Introduction that the chemotaxis complex and flagellum may localize to the same cell pole.

However, this inference is indirect and lacks direct live-cell evidence of colocalization, leaving its validity to be confirmed. This uncertainty was indeed the starting point and motivation for our study.

In our work, we simultaneously visualized flagellar filaments and core chemoreceptor proteins at the single-cell level in P. aeruginosa. We characterized the assembly and spatial coordination of the chemotaxis network and flagellar motor throughout the cell cycle, providing direct evidence of their colocalization and coordinated assembly. This represents a significant advance beyond prior indirect observations and supports the novelty of our study.

Accordingly, we have revised the relevant statements in lines 71-75 of the manuscript to better reflect the current state of the literature and emphasize the novelty of our direct observations.

(2) Statistics for the microscopy images, on which most conclusions in this manuscript are based, are completely missing. Given that most micrographs present one or very few cells, together with the fact that almost all conclusions depend on whether certain macromolecules are at one or two poles and whether different complexes are in the same pole, proper statistics, based on hundreds of cells in several fields, are absolutely required. Without this information, the results are anecdotal and do not support the conclusions. Due to the importance of statistics for this manuscript, strict statistical tests should be used and reported. Moreover, representative large fields with many cells should be added as supportive information.

We thank the reviewer for this important comment, which significantly improves the rigor and persuasiveness of our manuscript.

For the colocalization analyses presented in Fig. 1D and Fig. 2B, we quantified 145 and 101 cells with fluorescently labeled flagella, respectively, and observed consistent colocalization of the chemoreceptor complexes and flagella in all examined cells (now added in the figure legends). Regarding the distribution patterns of chemoreceptors shown in Fig. 3A, we have now included comprehensive statistical analyses for both wild-type and mutant strains. For each strain, more than 300 cells were analyzed across at least three independent microscopic fields, providing robust statistical power (detailed data are presented in Fig. 3C).

To further strengthen the evidence, statistical tests were applied to confirm the significance and reproducibility of our findings (Fig. 3C). In addition, representative large-field fluorescence images containing numerous cells have been added to the supplementary materials (Fig. S1 and Fig. S3).

The problem is more pronounced when the authors make strong statements, as in lines 157-158: "The results revealed that the chemoreceptor arrays no longer grow robustly at the cell pole (Figure 2A)". Looking at the seven cells shown in Figure 2A, five of them show polar localization of the chemoreceptors. The question is then: what is the percentage of cells that show precise polar, near-polar, or mid cell localization (the three patterns shown here) in the mutant and in the wild type? Since I know that these three patterns can also be observed in WT cells, what counts is the difference, and whether it is statistically significant.

We thank the reviewer for raising this important point. Following the reviewer's suggestion, we have now analyzed and categorized the distribution of the chemotaxis complex in both wild-type and flhF mutant strains into three patterns: precise-polar, near-polar, and mid-cell localization. For each strain, more than 200 cells across three independent fields of view were quantified.

Our statistical analysis shows that in the wild-type strain, approximately 98% of cells exhibit precise polar localization of the chemotaxis complex. In contrast, the ΔflhF mutant displays a clear shift in distribution, with about 5% of cells showing mid-cell localization and 9.5% showing near-polar localization. These differences demonstrate a significant alteration in the spatial pattern upon flhF deletion.

We have revised the relevant text in lines 166-170 accordingly and included the detailed statistical data in the newly added Fig. S4.

Even for the graphs shown in Figures 3C and 3D, where the proportion of cells with obvious chemoreceptor arrays and absolute fluorescence brightness of the chemosensory array are shown, respectively, the questions that arise are: for how many individual cells these values hold and what is the significance of the difference between each two strains?

The number of cells analyzed for each strain is indicated in the original manuscript: 372 wild-type cells (line 123), 221 ΔflhF cells (line 172), 234 ΔfliG cells (line 197), 323 ΔfliF cells (line 200), 672 ΔflhFΔfliF cells (line 202), and 242 ΔmotAΔmotCD cells (line 207). For each strain, data were collected from three independent fields of view. We have now also provided the number of cells in Fig. 3 legend.

We have now performed statistical comparisons using t-tests between strains. Notably, the measured values in Fig. 3C exhibit a clear, monotonic decrease with successive gene knockouts, supporting the robustness of the observed trend.

Regarding the absolute fluorescence intensity shown in the original Fig. 3D, the mutants did not display consistent directional changes compared to the wild type. Reliable comparison of absolute fluorescence intensity requires consistent fluorescent protein maturation levels across strains. Given the likely variability in maturation levels between strains, we concluded that this data may not accurately reflect true differences in protein concentrations. Therefore, we have removed the fluorescence intensity graph from the revised manuscript to avoid potential misinterpretation.

(3) The authors conclude that "Motor structural integrity is a prerequisite for chemoreceptor self-assembly" based on the reduction in cells with chemoreceptor clusters in mutants deleted for flagellar genes, despite the proper polar localization of the chemotaxis protein CheY. They show that the level of CheY in the WT and the mutant strains is similar, based on Western blot, which in my opinion is over-exposed. "To ascertain whether it is motor integrity rather than functionality that influences the efficiency of chemosensory array assembly", they constructed a mutant deleted for the flagella stator and found that the motor is stalled while CheY behaves like in WT cells. The authors further "quantified the proportion of cells with receptor clusters and the absolute fluorescence intensity of individual clusters (Figures 3C-D)". While Figure 3DC suggests that, indeed, the flagella mutants show fewer cells with a chemotaxis complex, Figure 3D suggests that the differences in fluorescence intensity are not statistically significant. Since it is obvious that the regulation of both structures' production and localization is codependent, I think that it takes more than a Western blot to make such a decision.

We thank the reviewer for the suggestions. To further clarify that the assembly of flagellar motors and chemoreceptor clusters occurs in an orderly manner rather than being merely codependent, we performed additional experiments. Specifically, we constructed a ΔcheA mutant strain, in which chemoreceptor clusters fail to assemble. Using in vivo fluorescent labeling of flagellar filaments, we observed that the proportion of cells with flagellar filaments in the ΔcheA strain was comparable to that of the wild type (Fig. S5).

In contrast, mutants lacking complete motor structures, such as ΔfliF and ΔfliG, showed a significant reduction in the proportion of cells with obvious receptor clusters (Fig. 3C). Based on these results, we conclude that the structural integrity of the flagellar motor is, to a certain extent, a prerequisite for the self-assembly of chemoreceptor clusters.

Accordingly, we have revised the relevant statement in lines 213-217 of the manuscript to reflect this clarification.

(4) I wonder why the authors chose to label CheY, which is the only component of the chemotaxis complex that shuttles back and forth to the base of the flagella. In any case, I think that they should strengthen their results by repeating some key experiments with labeled CheW or CheA.

We thank the reviewer for this valuable suggestion. In our study, we initially focused on the positional relationship between chemoreceptor clusters and flagella, then investigated factors influencing cluster distribution and assembly efficiency. The physiological significance of motor and cluster co-localization was ultimately proposed with CheY as the starting point.

Previous work by Harwood's group demonstrated that both CheY-YFP and CheA-GFP localize to the old poles of dividing Pseudomonas aeruginosa cells. Since our physiological hypothesis centers on CheY, we chose to label CheY-EYFP in our experiments.

To further strengthen our conclusions, we constructed a plasmid expressing CheA-CFP and introduced it into the cheY-eyfp strain via electroporation. Fluorescence imaging revealed a high degree of spatial overlap between CheA-CFP and CheY-EYFP (Fig. S2), confirming that CheY-EYFP accurately marks the location of the chemoreceptor complex.

We have revised the manuscript accordingly (lines 119-123) and added these data as Fig. S2.

(5) The last section of the results is very problematic, regarding the rationale, the conclusions, and the novelty. As far as the rationale is concerned, I do not understand why the authors assume that "a spatial separation between the chemoreceptors and flagellar motors should not significantly impact the temporal comparison in bacterial chemotaxis". Is there any proof for that?

We apologize for the lack of clarity in our original explanation. The rationale behind the statement was initially supported by comparing the timescales of CheY-P diffusion and temporal comparison in chemotaxis. Specifically, the diffusion time for CheY-P to traverse the entire length of a bacterial cell is approximately 100 ms (refs 39&40), whereas the timescale for bacterial chemotaxis temporal comparison is on the order of seconds (ref 41).

To clarify and strengthen this argument, we have expanded the discussion as follows:

The diffusion coefficient of CheY in bacterial cells is about 10 µm2/s, which corresponds to an estimated end-to-end diffusion time on the order of 100 ms (refs 40&41). If the chemotaxis complexes were randomly distributed rather than localized, diffusion times would be even shorter. In contrast, the timescale for the chemotaxis temporal comparison is on the order of seconds (ref. 42). Additionally, a study by Fukuoka and colleagues reported that intracellular chemotaxis signal transduction requires approximately 240 ms beyond CheY or CheY-P diffusion time (ref. 41). Moreover, the intervals of counterclockwise (CCW) and clockwise (CW) rotation of the P. aeruginosa flagellar motor under normal conditions are 1-2 seconds, as determined by tethered cell or bead assays (refs. 30&43).

Taken together, these indicate that for P. aeruginosa, which moves via a run-reverse mode, the potential 100 ms reduction in response time due to co-localization of the chemotaxis complex and motor has a limited effect on overall chemotaxis timing.

We have revised the corresponding text accordingly (lines 238-245) to better explain this rationale.

More surprising for me was to read that "The signal transduction pathways in E. coli are relatively simple, and the chemotaxis response regulator CheY-P affects only the regulation of motor switching". There are degrees of complexity among signal transduction pathways in E. coli, but the chemotaxis seems to be ranked at the top. CheY is part of the adaptation. Perfect adaptation, as many other issues related to the chemotaxis pathway, which include the wide dynamic range, the robustness, the sensitivity, and the signal amplification (gain), are still largely unexplained. Hence, such assumptions are not justified.

We apologize for the confusion and imprecision in our original statements. Our intention was to convey that the chemotaxis pathway in E. coli is relatively simple compared to the more complex chemosensory systems in P. aeruginosa. We did not mean to generalize this simplicity to all signal transduction pathways in E. coli.

We acknowledge that E. coli chemotaxis is a highly sophisticated system, involving processes such as perfect adaptation, wide dynamic range, robustness, sensitivity, and signal amplification, many aspects of which remain incompletely understood. CheY indeed plays a crucial role in adaptation and motor switching regulation.

Accordingly, we have revised the original text (lines 249-255) to avoid any misunderstanding.

More perplexing is the novelty of the authors' documentation of the effect of the chemotaxis proteins on the c-di-GMP level. In 2013, Kulasekara et al. published a paper in eLife entitled "c-di-GMP heterogeneity is generated by the chemotaxis machinery to regulate flagellar motility". In the same year, Kulasekara published a paper entitled "Insight into a Mechanism Generating Cyclic di-GMP Heterogeneity in Pseudomonas aeruginosa". The authors did not cite these works and I wonder why.

We apologize for having been unaware of these important references and thank the reviewer for bringing them to our attention. We have now cited the eLife paper and the PhD thesis titled "Insight into a Mechanism Generating Cyclic di-GMP Heterogeneity in Pseudomonas aeruginosa" by Kulasekara et al.

Regarding novelty, there are key differences between our findings and those reported by Kulasekara et al. While they proposed that CheA influences c-di-GMP heterogeneity through interaction with a specific phosphodiesterase (PDE), our results demonstrate that overexpression of CheY leads to an increase in intracellular c-di-GMP levels.

We have revised the original text accordingly (lines 358-362) to clarify these distinctions.

(6) Throughout the manuscript, the authors refer to foci of fluorescent CheY as "chemoreceptor arrays". If anything, these foci signify the chemotaxis complex, not the membrane-traversing chemoreceptors.

We thank the reviewer for this clarification. We have revised the manuscript accordingly to refer to the fluorescent CheY foci as representing the chemotaxis complex rather than the chemoreceptor arrays.

Conclusions:

The manuscript addresses an interesting subject and contains interesting, but incomplete, data.

Reviewer #2 (Public Review):

Summary:

Here, the authors studied the molecular mechanisms by which the chemoreceptor cluster and flagella motor of Pseudomonas aeruginosa (PA) are spatially organized in the cell. They argue that FlhF is involved in localizing the receptors-motor to the cell pole, and even without FlhF, the two are colocalized. FlhF is known to cause the motor to localize to the pole in a different bacterial species, Vibrio cholera, but it is not involved in receptor localization in that bacterium. Finally, the authors argue that the functional reason for this colocalization is to insulate chemotactic signaling from other signaling pathways, such as cyclic-di-GMP signaling.

Strengths:

The experiments and data look to be high-quality.

Weaknesses:

However, the interpretations and conclusions drawn from the experimental observations are not fully justified in my opinion.

I see two main issues with the evidence provided for the authors' claims.

(1) Assumptions about receptor localization:

The authors rely on YFP-tagged CheY to identify the location of the receptor cluster, but CheY is a diffusible cytoplasmic protein. In E. coli, CheY has been shown to localize at the receptor cluster, but the evidence for this in PA is less strong. The authors refer to a paper by Guvener et al 2006, which showed that CheY localizes to a cell pole, and CheA (a receptor cluster protein) also localizes to a pole, but my understanding is that colocalization of CheY and CheA was not shown. My concern is that CheY could instead localize to the motor in PA, say by binding FliM. This "null model" would explain the authors' observations, without colocalization of the receptors and motor. Verifying that CheY and CheA are colocalized in PA would be a very helpful experiment to address this weakness.

We thank the reviewer for this valuable suggestion. We agree that verifying the colocalization of CheY and CheA would strengthen our conclusions. To address this, we constructed a plasmid expressing CheA-CFP and introduced it into the CheY-EYFP strain by electroporation. Fluorescence imaging revealed a high degree of spatial overlap between CheA-CFP and CheY-EYFP signals, indicating that CheY-EYFP indeed marks the location of the chemoreceptor complex rather than the flagellar motor.

We have revised the manuscript accordingly (lines 118-123) and included these results in the new Fig. S2.

(2) Argument for the functional importance of receptor-motor colocalization at the pole:

The authors argue that colocalization of the receptors and motors at the pole is important because it could keep phosphorylated CheY, CheY-p, restricted to a small region of the cell, preventing crosstalk with other signaling pathways. Their evidence for this is that overexpressing CheY leads to higher intracellular cdG levels and cell aggregation. Say that the receptors and motors are colocalized at the pole. In E. coli, CheY-p rapidly diffuses through the cell. What would prevent this from occurring in PA, even with colocalization?

We appreciate the reviewer's insightful question. The colocalization of both the signaling source (the kinase) and sink (the phosphatase) at the chemoreceptor complex at the cell pole results in a rapid decay of CheY-P concentration within approximately 0.2 µm from the cell pole, leading to a nearly uniform distribution elsewhere in the cell, as demonstrated by Vaknin and Berg (ref. 46). This spatial arrangement effectively confines high CheY-P levels to the pole region. When the motor is also localized at the cell pole, this reduces the need for elevated CheY-P concentrations throughout the cytoplasm, thereby minimizing potential crosstalk with other signaling pathways.

We have revised the manuscript accordingly (lines 280-286) to clarify this point.

Elevating CheY concentration may increase the concentration of CheY-p in the cell, but might also stress the cells in other unexpected ways. It is not so clear from this experiment that elevated CheY-p throughout the cell is the reason that they aggregate, or that this outcome is avoided by colocalizing the receptors and motor at the same pole. If localization of the receptor array and motor at one pole were important for keeping CheY-p levels low at the opposite pole, then we should expect cells in which the receptors and motor are not at the pole to have higher CheY-p at the opposite pole. According to the authors' argument, it seems like this should cause elevated cdG levels and aggregation in the delta flhF mutants with wild-type levels of CheY. But it does not look like this happened. Instead of varying CheY expression, the authors could test their hypothesis that receptor-motor colocalization at the pole is important for preventing crosstalk by measuring cdG levels in the flhF mutant, in which the motor (and maybe the receptor cluster) are no longer localized in the cell pole.

We thank the reviewer for raising the important point regarding potential cellular stress caused by elevated CheY concentrations, as well as for the suggestion to test the hypothesis using ΔflhF mutants.

First, as noted above, CheY-P concentration rapidly decreases away from the receptor complex. While deletion of flhF alters the position of the receptor complex, thereby shifting the region of high CheY-P concentration, it does not increase CheY-P levels elsewhere in the cell. Importantly, in the ΔflhF strain, the receptor complex and the motor still colocalize, so this mutant may not effectively test the role of receptor-motor colocalization in preventing crosstalk as suggested.

Regarding the possibility that elevated CheY levels stress the cells independently of CheY-P signaling, prior work in <i.E. coli by Cluzel et al. (ref. 11) showed that overexpressing CheY several-fold did not cause phenotypic changes, indicating that simple CheY overexpression alone may not be generally stressful. Furthermore, our data indicate that the increase in c-di-GMP levels and subsequent cell aggregation upon CheY overexpression is not an all-or-none switch but occurs progressively as CheY concentration rises.

To further confirm that CheY overexpression promotes aggregation through increased c-di-GMP levels, we performed additional experiments co-overexpressing CheY and a phosphodiesterase (PDE) from E. coli to reduce intracellular c-di-GMP. These experiments showed that PDE expression mitigates cell aggregation caused by CheY overexpression (Fig. S8).

We have revised the manuscript accordingly (lines 290-294) and added these new results in Fig. S8.

Reviewer #3 (Public Review):

Summary:

The authors investigated the assembly and polar localization of the chemosensory cluster in P. aeruginosa. They discovered that a certain protein (FlhF) is required for the polar localization of the chemosensory cluster while a fully-assembled motor is necessary for the assembly of the cluster. They found that flagella and chemosensory clusters always co-localize in the cell; either at the cell pole in wild-type cells or randomly-located in the cell in FlhF mutant cells. They hypothesize that this co-localization is required to keep the level of another protein (CheY-P), which controls motor switching, at low levels as the presence of high levels of this protein (if the flagella and chemosensory clusters were not co-localized) is associated with high-levels of c-di-GMP and cell aggregations.

Strengths:

The manuscript is clearly written and straightforward. The authors applied multiple techniques to study the bacterial motility system including fluorescence light microscopy and gene editing. In general, the work enhances our understanding of the subtlety of interaction between the chemosensory cluster and the flagellar motor to regulate cell motility.

Weaknesses:

The major weakness in this paper is that the authors never discussed how the flagellar gene expression is controlled in P. aeruginosa. For example, in E. coli there is a transcriptional hierarchy for the flagellar genes (early, middle, and late genes, see Chilcott and Hughes, 2000). Similarly, Campylobacter and Helicobacter have a different regulatory cascade for their flagellar genes (See Lertsethtakarn, Ottemann, and Hendrixson, 2011). How does the expression of flagellar genes in P. aeruginosa compare to other species? How many classes are there for these genes? Is there a hierarchy in their expression and how does this affect the results of the FliF and FliG mutants? In other words, if FliF and FliG are in class I (as in E. coli) then their absence might affect the expression of other later flagellar genes in subsequent classes (i.e., chemosensory genes). Also, in both FliF and FliG mutants no assembly intermediates of the flagellar motor are present in the cell as FliG is required for the assembly of FliF (see Hiroyuki Terashima et al. 2020, Kaplan et al. 2019, Kaplan et al. 2022). It could be argued that when the motor is not assembled then this will affect the expression of the other genes (e.g., those of the chemosensory cluster) which might play a role in the decreased level of chemosensory clusters the authors find in these mutants.

We thank the reviewer for the insightful comments. P. aeruginosa possesses a four-tiered transcriptional regulatory hierarchy controlling flagellar biogenesis. Within this system, fliF and fliG belong to class II genes and are regulated by the master regulator FleQ. In contrast, chemotaxis-related genes such as cheA and cheW are regulated by intracellular free FliA, and currently, there is no evidence that FliA activity is influenced by proteins like FliG.

To verify that the expression of core chemotaxis proteins was not affected by deletion of fliG, we performed Western blot analyses to compare CheY levels in wild-type, ΔfliF, and ΔfliG strains. We observed no significant differences, indicating that the reduced presence of receptor clusters in these mutants is not due to altered expression of chemotaxis proteins.

Accordingly, we have revised the manuscript (lines 341-348) and updated Fig. 3B to reflect these findings.

Recommendations for the authors:

Reviewing Editor (Recommendations For The Authors):

The reviewers comment on several important aspects that should be addressed, namely: the lack of statistical analysis; the need for clarifications regarding assumptions made regarding receptor localization; the functional importance of receptor-motor colocalization; and the need for an elaborate discussion of flagellar gene expression. Also, two reviewers pointed out the need to prove the co-localization of CheY and CheA; This is important since CheY is dynamic, shuttling back and forth from the chemotaxis complex to the base of the flagella, whereas CheA (or cheW or, even better, the receptors) is considered less dynamic and an integral part of the chemotaxis complex.

Reviewer #1 (Recommendations For The Authors):

Minor points:

Line 43: "ubiquitous" - I would choose another word.

We changed "ubiquitous" to "widespread".

Line 49: "order" - change to organize.

We changed "order" to "organize".

Line 52: "To grow and colonize within the host, bacteria have evolved a mechanism for migrating...". Motility "towards more favorable environments" is an important survival strategy of bacteria in various ecological niches, not only within the host.

We revised it to "grow and colonize in various ecological niches".

Line 72: Define F6 in "F6 pathway-related receptors".

The proteins encoded by chemotaxis-related genes collectively constitute the F6 pathway, which we have now explained in the manuscript text.

Line 72-73: Do references 17 &18 really report colocalization of the chemotaxis receptor and flagella to the same pole? If these or other reports document such colocalization, then the sentence in the Abstract "Surprisingly, we found that both are located at the same cell pole..." is not correct.

Kazunobu et al. (ref. 18) used scanning electron microscopy to preliminarily characterize the flagellation pattern of Pseudomonas aeruginosa during cell division, showing that existing flagella are located at the old pole. Zehra et al. (ref. 17), through fluorescence microscopy, observed that CheA and CheY proteins in dividing cells are typically also present at the old pole. Based on these observations, we inferred in the Introduction that the chemotaxis complex and flagellum may localize to the same cell pole.

However, this inference is indirect and lacks direct live-cell evidence of colocalization, leaving its validity to be confirmed. This uncertainty was indeed the starting point and motivation for our study.

In our work, we simultaneously visualized flagellar filaments and core chemoreceptor proteins at the single-cell level in P. aeruginosa. We characterized the assembly and spatial coordination of the chemotaxis network and flagellar motor throughout the cell cycle, providing direct evidence of their colocalization and coordinated assembly. This represents a significant advance beyond prior indirect observations and supports the novelty of our study.

Accordingly, we have revised the relevant statements in lines 71-75 of the manuscript to better reflect the current state of the literature and emphasize the novelty of our direct observations.

Line 108: "CheY has been shown to colocalize with chemoreceptors". The authors rely here (reference 29) and in other places on findings in E. coli. However, in the Introduction, they describe the many differences between the motility systems of P. aeruginosa and E. coli, e.g., the number of chemosensory systems and their spatial distribution (E. coli is a peritrichous bacterium, as opposed to the monotrichous bacterium P. aeruginosa). There seem to be proofs for colocalization of the Che and MCP proteins in P. aeruginosa, which should be cited here.

Thank you for pointing this out. Harwood's group reported that a cheY-YFP fusion strain exhibited bright fluorescent spots at the cell pole, which disappeared upon knockout of cheA or cheW-genes encoding structural proteins of the chemotaxis complex. This strongly suggests colocalization of CheY with MCP proteins in P. aeruginosa. We have now cited this study as reference 17 in the manuscript.

Figure 1B: Please replace the order of the schematic presentations, so that the cheY-egfp fusion, which is described first in the text, is at the top.

We have modified the order of related images in Fig. 1B.

Line 127: "by introducing cysteine mutations". Replace either by "by introducing cysteines" or by "by substituting several residues with cysteines".

We changed the relevant statement to "by introducing cysteines".

Line 144-145: "Given that the physiological and physical environments of both cell poles are nearly identical.". I think that also the physical, but certainly the physiological environment of the two poles is not identical. First, one is an old pole, and the other a new pole. Second, many proteins and RNAs were detected mainly or only in one of the poles of rod-shaped Gram-negative bacteria that are regarded as symmetrically dividing. Although my intuition is that the authors are correct in assuming that "it is unlikely that the unipolar distribution of the chemoreceptor array can be attributed to passive regulatory factors", relating it to the (false) identity between the poles is incorrect.

We thank the reviewer for this important correction. We agree that the physiological environments of the two poles are not identical, given that one is the old pole and the other the new pole, and that many proteins and RNAs show polar localization in rod-shaped Gram-negative bacteria. Accordingly, we have revised the original text (lines 150-152) to read:

“Despite potential differences in the physical and especially physiological environments at the two cell poles, it is unlikely that the unipolar distribution of the chemotaxis complex can be attributed to passive regulatory factors.”

Lines 151-154: "Considering the consistent colocalization pattern between chemosensory arrays and flagellar motors in P. aeruginosa". Does the word consistent relate to different reports on such colocalization or to the results in Figure 1D? In case it is the latter, then what is the word consistent based on? All together only 7 cells are presented in the 5 micrographs that compose Figure 1D (back to statistics...).

We thank the reviewer for raising this point. To clarify, the word "consistent" refers to the observation of colocalization shown in Figure 1D & Figure S3. As noted in the revised figure legend for Figure 1D, a total of 145 cells with labeled flagella were analyzed, all exhibiting consistent colocalization between flagella and chemosensory arrays. Additionally, we have included a new image showing a large field of co-localization in the wild-type strain as Figure S3 to better illustrate this consistency.

Figure 2A: Omit "Subcellular localization of" from the beginning of the caption.

We removed the relevant expression from the caption.