Reviewer #2 (Public review):

Liu et al. applied hidden Markov models (HMM) to fMRI data from 64 participants listening to audio stories. The authors identified three brain states, characterized by specific patterns of activity and connectivity, that the brain transitions between during story listening. Drawing on a theoretical framework proposed by Berwick et al. (TICS 2023), the authors interpret these states as corresponding to external sensory-motor processing (State 1), lexical processing (State 2), and internal mental representations (State 3). States 1 and 3 were more likely to transition to State 2 than between one another, suggesting that State 2 acts as a transition hub between states. Participants whose brain state trajectories closely matched those of an individual with high comprehension scores tended to have higher comprehension scores themselves, suggesting that optimal transitions between brain states facilitated narrative comprehension.

Overall, the conclusions of the paper are well-supported by the data. Several recent studies (e.g., Song, Shim, and Rosenberg, eLife, 2023) have found that the brain transitions between a small number of states; however, the functional role of these states remains under-explored. An important contribution of this paper is that it relates the expression of brain states to specific features of the stimulus in a manner that is consistent with theoretical predictions.

The correlation between narrative features and brain state expression was reliable, but relatively low (~0.03). As discussed in the manuscript, this could be due to measurement noise, as well as narrative features accounting for a small proportion of cognitive processes underlying the brain states.

A strength of the paper is that the authors repeated the HMM analyses across different tasks (Figure 5) and an independent dataset (Figure S3) and found that the data was consistently best fit by 3 brain states. Across tasks, however, the spatial regions associated with each state varied. For example, state 2 during narrative comprehension was similar to both states 2 and 3 during rest (Fig. 5A), suggesting that the organization of the three states was task dependent.

The three states identified in the manuscript correspond rather well to areas with short, medium, and long temporal timescales (see Hasson, Chen & Honey, TiCs, 2015). Given the relationship with behavior, where State 1 responds to acoustic properties, State 2 responds to word-level properties, and State 3 responds to clause-level properties, a "single-process" account where the states differ in terms of the temporal window for which one needs to integrate information over may offer a more parsimonious account than a multi-process account where the states correspond to distinct processes. This possibility is mentioned briefly in the introduction, but not developed further.

Author response:

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

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

Liu and colleagues applied the hidden Markov model on fMRI to show three brain states underlying speech comprehension. Many interesting findings were presented: brain state dynamics were related to various speech and semantic properties, timely expression of brain states (rather than their occurrence probabilities) was correlated with better comprehension, and the estimated brain states were specific to speech comprehension but not at rest or when listening to non-comprehensible speech. 

Strengths: 

Recently, the HMM has been applied to many fMRI studies, including movie watching and rest. The authors cleverly used the HMM to test the external/linguistic/internal processing theory that was suggested in comprehension literature. I appreciated the way the authors theoretically grounded their hypotheses and reviewed relevant papers that used the HMM on other naturalistic datasets. The manuscript was well written, the analyses were sound, and the results had clear implications. 

Weaknesses: 

Further details are needed for the experimental procedure, adjustments needed for statistics/analyses, and the interpretation/rationale is needed for the results. 

For the Experimental Procedure, we will provide a more detailed description about stimuli, and the comprehension test, and upload the audio files and corresponding transcriptions as the supplementary dataset. 

For statistics/analyses, we have reproduced the states' spatial maps using unnormalized activity pattern. For the resting state, we observed a state resembling the baseline state described in Song, Shim, & Rosenberg (2023). However, for the speech comprehension task, all three states were characterized by network activities varying largely from zero. In addition, we have re-generated the null distribution for behaviorbrain state correlations using circular shift. The results are largely consistent with the previous findings. We have also made some other adjustment to the analyses or add some new analyses as recommended by the reviewer. We will revise the manuscript to incorporate these changes.

For the interpretation/rationale: We will add a more detailed interpretation for the association between state occurrence and semantic coherence. Briefly speaking, higher semantic coherence may allow for the brain to better accumulate information over time.

State #2 seems to be involved in the integration of information at shorter timescales (hundreds of milliseconds) while State #3 seems to be involved in the longer timescales (seconds). 

We greatly appreciate the reviewer for the insightful comments and constructive suggestions.  

Reviewer #2 (Public review): 

Liu et al. applied hidden Markov models (HMM) to fMRI data from 64 participants listening to audio stories. The authors identified three brain states, characterized by specific patterns of activity and connectivity, that the brain transitions between during story listening. Drawing on a theoretical framework proposed by Berwick et al. (TICS 2023), the authors interpret these states as corresponding to external sensory-motor processing (State 1), lexical processing (State 2), and internal mental representations (State 3). States 1 and 3 were more likely to transition to State 2 than between one another, suggesting that State 2 acts as a transition hub between states. Participants whose brain state trajectories closely matched those of an individual with high comprehension scores tended to have higher comprehension scores themselves, suggesting that optimal transitions between brain states facilitated narrative comprehension. 

Overall, the conclusions of the paper are well-supported by the data. Several recent studies (e.g., Song, Shim, and Rosenberg, eLife, 2023) have found that the brain transitions between a small number of states; however, the functional role of these states remains under-explored. An important contribution of this paper is that it relates the expression of brain states to specific features of the stimulus in a manner that is consistent with theoretical predictions. 

(1) It is worth noting, however, that the correlation between narrative features and brain state expression (as shown in Figure 3) is relatively low (~0.03). Additionally, it was unclear if the temporal correlation of the brain state expression was considered when generating the null distribution. It would be helpful to clarify whether the brain state expression time courses were circularly shifted when generating the null. 

In the revision, we generated the null distribution by circularly shifting the state time courses. The results remain consistent with our previous findings: p = 0.002 for the speech envelope, p = 0.007 for word-level coherence, and p = 0.001 for clause-level coherence.

We note that in other studies which examined the relationship between brain activity and word embedding features, the group-mean correlation values are similarly low but statistically significant and theoretically meaningful (e.g., Fernandino et al., 2022; Oota et al., 2022). We think these relatively low correlations are primarily due to the high level of noise inherent in neural data. Brain activity fluctuations are shaped by a variety of factors, including task-related cognitive processing, internal thoughts, physiological states, as well as arousal and vigilance. Additionally, the narrative features we measured may account for only a small portion of the cognitive processes occurring during the task. As a result, the variance in narrative features can only explain a limited portion of the overall variance in brain activity fluctuations.

We will replace Figure 3 and the related supplementary figures with new ones, in which the null distribution is generated via circular shift. Furthermore, we will expand our discussion to address why the observed brain-stimuli correlations are relatively small, despite their statistical significance.

(2) A strength of the paper is that the authors repeated the HMM analyses across different tasks (Figure 5) and an independent dataset (Figure S3) and found that the data was consistently best fit by 3 brain states. However, it was not entirely clear to me how well the 3 states identified in these other analyses matched the brain states reported in the main analyses. In particular, the confusion matrices shown in Figure 5 and Figure S3 suggests that that states were confusable across studies (State 2 vs. State 3 in Fig. 5A and S3A, State 1 vs. State 2 in Figure 5B). I don't think this takes away from the main results, but it does call into question the generalizability of the brain states across tasks and populations. 

We identified matching states across analyses based on similarity in the activity patterns of the nine networks. For each candidate state identified in other analyses, we calculate the correlation between its network activity pattern and the three predefined states from the main analysis, and set the one it most closely resembled to be its matching state. For instance, if a candidate state showed the highest correlation with State #1, it was labelled State #1 accordingly. 

Each column in the confusion matrix depicts the similarity of each candidate state with the three predefined states. In Figure S3 (analysis for the replication dataset), the highest similarity occurred along the diagonal of the confusion matrix. This means that each of the three candidate states was best matched to State #1, State #2, and State #3, respectively, maintaining a one-to-one correspondence between the states from two analyses.

For the comparison of speech comprehension task with the resting and the incomprehensible speech condition, there was some degree of overlap or "confusion."

In Figure 5A, there were two candidate states showing the highest similarity to State #2. In this case, we labelled the candidate state with the strongest similarity as State #2, while the other candidate state is assigned as State #3 based on the ranking of similarity. This strategy was also applied to naming of states for the incomprehensible condition. The observed confusion supports the idea that the tripartite-state space is not an intrinsic, task-free property. To make the labeling clearer in the presentation of results, we will use a prime symbol (e.g., State #3') to indicate cases where such confusion occurred, helping to distinguish these ambiguous matches.

(3) The three states identified in the manuscript correspond rather well to areas with short, medium, and long temporal timescales (see Hasson, Chen & Honey, TiCs, 2015).

Given the relationship with behavior, where State 1 responds to acoustic properties, State 2 responds to word-level properties, and State 3 responds to clause-level properties, the authors may want to consider a "single-process" account where the states differ in terms of the temporal window for which one needs to integrate information over, rather than a multi-process account where the states correspond to distinct processes. 

The temporal window hypothesis provides a more fitting explanation for our results. Based on the spatial maps and their modulation by speech features, States #1, #2, and #3 seem to correspond to short, medium, and long processing timescales, respectively. We will update the discussion to reflect this interpretation.

We sincerely appreciate the constructive suggestions from the two anonymous reviewers, which have been highly valuable in improving the quality of the manuscript.  

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) The "Participants and experimental procedure" section deserves more details. I've checked Liu et al. (2020), and the dataset contained 43 participants aged 20-75 years, whereas this study contained data from 64 young adults and 30 old adult samples. The previous dataset seems to have two stories, whereas this study seems to have three. Please be specific, given that the dataset does not seem the same. Could the authors also include more descriptions of what the auditory stories were? For example, what were the contents, and how were they recorded? 

The citation is partially incorrect. The dataset of young adults is shared with our work published in (2022). The 64 participants listened to one of three stories told by a female college student in Mandarin, recounting her real-life experience of hiking, a graduate admission interview, and her first time taking a flight, respectively. The sample of older adults is from our work published in (2020), which includes 30 older adults and additionally 13 young adults. The stimuli in this case were two stories told by an older woman in a Chinese dialect, describing her experience in Thailand and riding a warship, respectively. Since we aim to explore whether the main results can be replicated on a different age group, we excluded the 13 young adults from the analysis. 

All the stories were recorded during fMRI scanning using a noise-canceling microphone (FOMRI-III; Optoacoustics Ltd, Or-Yehuda, Israel) positioned above the speaker’s mouth. The audio recordings were subsequently processed offline with Adobe Audition 3.0 (Adobe Systems Inc., USA) to further eliminate MRI scanner noise.

In the revised manuscript, we have updated the citation, and provided a more detailed description of the stimuli in the supplementary material. We have also uploaded the audio files along with their corresponding transcriptions to GitHub.

(2) I am curious about individual differences in comprehension scores. Did participants have less comprehension of the audio-narrated story because the story was a hard-tocomprehend narrative or because the audio quality was low? Could the authors share examples of comprehension tests? 

We believe two factors contribute to the individual differences in comprehension scores. First, the audio quality is indeed moderately lower than in dailylife story-listening conditions. This is because those stories were recorded and played during fMRI scanning. Although a noise-canceling equipment was used, there were still some noises accompanying the speech, which may have made speech perception and comprehension more difficult than usual.

Second, the comprehension test measured how much information about the story (including both main themes and details) participants could recall. Specifically, participants were asked to retell the stories in detail immediately after the scanning session. Following this free recall, the experimenters posed a few additional questions drawn from a pre-prepared list, targeting information not mentioned in their recall. If participants experienced lapses of attention or did not store the incoming information into memory promptly, they might fail to recall the relevant content. In several studies, such a task has been called a narrative recall test. However, memory plays a crucial role in real-time speech comprehension, while comprehension affects the depth of processing during memory encoding, thereby influencing subsequent recall performance. To align with prior work (e.g., Stephens et al., 2010) and our previous publications, we chose to referred to this task as narrative comprehension. 

In the revised manuscript, we have provided a detailed description about the comprehension test (Line 907-933) and share the examples on GitHub. 

(3) Regarding Figure 3, what does it mean for a state occurrence to follow semantic coherence? Is there a theoretical reason why semantic coherence was measured and related to brain state dynamics? A related empirical question is: is it more likely for the brain states to transition from one state to another when nearby time points share low semantic similarity compared to chance? 

We analyzed semantic coherence and sound envelope as they capture different layers of linguistic and acoustic structure that unfold over varying temporal scales. Changes in the sound envelope typically occur on the order of milliseconds to a few hundred milliseconds, changes in word-level semantic coherence span approximately 0.24 ± 0.15 seconds, and changes in clause-level semantic coherence extend to 3.2 ± 1.7 seconds. Previous theory and empirical studies suggest that the timescales of information accumulation vary hierarchically, progressing from early sensory areas to higher-order areas (Hasson et al., 2015; Lerner et al., 2011). Based on this work, we anticipate that the three brain states, which are respectively associated with the auditory and sensory motor network, the language network and the DMN, would be selectively modulated by these speech properties corresponding to distinct timescales. 

Accordingly, when a state occurrence aligns with (clause-level) semantic coherence, it suggests that this state is engaged in processing information accumulated at the clause level (i.e., its semantic relationship). Higher coherence facilitates better accumulation, making it more likely for the associated brain state to be activated. 

We analyzed the relationship between state transition probability and semantic coherence, but did not find significant results. Here, the transition probability was calculated as Gamma(t) – Gamma(t-1), where Gamma refers to the state occurrence probability. The lack of significant findings may be because brain state transitions are driven primarily by more slowly changing factors. Indeed, we found the average dwell time of the three states ranges from 9.66 to 15.29s, which is a much slower temporal dynamics compared to the relatively rapid shifts in acoustic/semantic properties. 

In the revised version, we have updated the Introduction to clarify the rational for selecting the three speech properties and to explore their relationship with brain dynamics (Line 111-118)

(4) When running the HMM, the authors iterated K of 2 to 10 and K = 4, 10, and 12. However, the input features of the model consist of only 9 functional networks. Given that the HMM is designed to find low-dimensional latent state sequences, the choice of the number of latent states being higher than the number of input features sounds odd to me - to my speculation, it is bound to generate almost the exact same states as 9 networks and/or duplicates of the same state. I suggest limiting the K iterations from 2 to 8. For replication with Yeo et al.'s 7 networks, K iteration should also be limited to K of less than 7, or optionally, Yeo's 7 network scheme could be replaced with a 17network scheme. 

We understand your concern. However, the determination of the number (K) of hidden states is not directly related to the number of features (in this case, the number of networks), but rather depends on the complexity of the time series and the number of underlying patterns. Given that each state corresponds to a distinct combination of the features, even a small number of features can be used to model a system with complex temporal behaviors and multiple states. For instance, for a system with n features, assuming each is a binary variable (0 or 1), there are maximally 2ⁿ possible underlying states. 

In our study, we recorded brain activity over 300 time points and used the 9 networks as features. At different time points, the brain can exhibit distinct spatial configurations, reflected in the relative activity levels of the nine networks and their interactions. To accurately capture the temporal dynamics of brain activity, it is essential to explore models that allow for more states than the number of features. We note that in other HMM studies, researchers have also explored states more than the number of networks to find the best number of hidden states (e.g., Ahrends et al., 2022; Stevner et al., 2019). 

Furthermore, Ahrends et al. (2022) suggested that “Based on the HCP-dataset, we estimate as a rule of thumb that the ratio of observations to free parameters per state should not be inferior to 200”, where free parameters per state is [𝐾 ∗(𝐾 −1)+ (𝐾 −1)+𝐾 ∗𝑁 ∗(𝑁 +1)/2]/𝐾. According to this, there should be above 10, 980 observations when the number of states (K) is 10 (the maximal number in our study) and the number of networks (N) is 9. In our group-level HMM model, there were 64 (valid runs) * 300 (TR) = 19200 observations for young adults, and 50 (valid runs) * 210 (TR) = 10500 observations for older adults. Aside from the older adults' data being slightly insufficient (4.37% less than the suggestion), all other hyperparameter combinations in this study meet the recommended number of observations. 

(5) In Figure 2, the authors write that the states' spatial maps were normalized for visualization purposes. Could the authors also show visualization of brain states that are not normalized? The reason why I ask is, for example, in Song, Shim, & Rosenberg (2023), the base state was observed which had activity levels all close to the mean (which is 0 because the BOLD activity was normalized). If the activity patterns of this brain state were to be normalized after state estimation, the base state would have looked drastically different than what is reported. 

We derived the spatial maps of the states using unnormalized activity patterns, with the BOLD signals Z-score normalized to a mean of zero. Under the speech comprehension task, the three states exhibited relatively large fluctuations in network activity levels. The activity ranges were as follows: [-0.71 to 0.51] for State #1, [-0.26 to 0.30] for State #2, and [-0.82 to 0.40] for State #3. For the resting state, we observed a state resembling the baseline state as described in Song, Shim, & Rosenberg (2023), with activity values ranging from -0.133 to 0.09. 

In the revision, we have replaced the states' spatial maps with versions showing unnormalized activity patterns. 

(6) In line 297, the authors speculate that "This may be because there is too much heterogeneity among the older adults". To support this speculation, the authors can calculate the overall ISC of brain state dynamics among older adults and compare it to the ISC estimated from younger adults.  

We analyzed the overall ISC of brain state dynamics, and found the ISC was indeed significantly lower among the older adults than that among the younger adults. We have revised this statement as follows:

These factors can diminish the inter-subject correlation of brain state dynamics— indeed, ISCs among older adults were significantly lower than those among younger adults (Figure S5)—and reduce ISC's sensitivity to individual differences in task performance (Line 321-326).

Other comments: 

(7) In Figure 4, the authors showed a significant positive correlation between head movement ISC with the best performer and comprehension scores. Does the average head movement of all individuals negatively correlate with comprehension scores, given that the authors argue that "greater task engagement is accompanied by decreased movement"? 

We examined the relationship between participants' average head movement across the comprehension task and their comprehension scores. There was no significant correlation (r = 0.041, p = 0.74). In the literature (e.g. ,Ballenghein et al., 2019) , the relationship between task engagement and head movement was also assessed at the moment-by-moment level, rather than by using time-averaged data.

Real-time head movements reflect fluctuations in task engagement and cognitive state. In contrast, mean head movement, as a static measure, fails to capture these changes, and thus is not effective in predicting task performance.

(8) The authors write the older adults sample, the "independent dataset". Technically, however, this dataset cannot be independent because they were collected at the same time by the same research group. I would advise replacing the word independent to something like second dataset or replication dataset. 

We have replaced the phrase “independent dataset” with “replication dataset”. 

(9) Pertaining to a paragraph starting in line 586: For non-parametric permutation tests, the authors note that the time courses of brain state expression were "randomly shuffled". How was this random shuffling done: was this circular-shifted randomly, or were the values within the time course literally shuffled? The latter approach, literal shuffling of the values, does not make a fair null distribution because it does not retain temporal regularities (autocorrelation) that are intrinsic to the fMRI signals. Thus, I suggest replacing all non-parametric permutation tests with random circular shifting of the time series (np. roll in python).  

In the original manuscript, the time course was literally shuffled. In the revised version, we circular-shifted the time course randomly (circshift.m in Matlab) to generate the null distribution. The results remain consistent with our previous findings: p = 0.002 for the speech envelope, p = 0.007 for word-level coherence, and p = 0.001 for clause-level coherence (Line 230-235). 

(10) The p value calculation should be p = (1+#(chance>=observed))/(1+#iterations) for one-tailed test and p = (1+#(abs(chance)>=abs(observed)))/(1+#iterations) for twotailed test. Thus, if 5,000 iterations were run and none of the chances were higher than the actual observation, the p-value is p = 1/5001, which is the minimal value it can achieve. 

Have corrected. 

(11) State 3 in Figure S2 does not resemble State 3 of the main result. Could the authors explain why they corresponded State 3 of the Yeo-7 scheme to State 3 of the nineparcellation scheme, perhaps using evidence of spatial overlap? 

The correspondence of states between the two schemes was established using evidence of state expression time course. 

To assess temporal overlap, we calculated Pearson’s correlation between each candidate state obtained by the Yeo-7 scheme and the three predefined states obtained by the nine-network parcellation scheme in terms of state expression probabilities. The time courses of the 64 participants were concatenated, resulting in 19200 (300*64) time points for each state. The one that the candidate state most closely resembled was set to be its corresponding state. For instance, if a candidate state showed the highest correlation with State #1, it was labelled State #1 accordingly. As demonstrated in the confusion matrix, each of the three candidate states was best matched to State #1, State #2, and State #3, respectively, maintaining a one-to-one correspondence between the states from the two schemes.

We also assessed the spatial overlap between the two schemes. First, a state activity value was assigned to each voxel across the whole brain (including a total of 34,892 voxels covered by both parcellation schemes). This is done for each brain state. Next, we calculated Spearman’s correlation between each candidate state obtained by the Yeo-7 scheme and the three predefined states obtained by the nine-network scheme in terms of whole-brain activities. The pattern of spatial overlap is consistent with the pattern of temporal overlap, such that each of the three candidate states was best matched to State #1, State #2, and State #3, respectively.

Author response image 1.

We noted that the networks between the two schemes are not well aligned in their spatial location, especially for the DMN (as shown below). This may lead to the low spatial overlap of State #3, which is dominated by DMN activity. Consequently, establishing state correspondence based on temporal information is more appropriate in this context. We therefore only reported the results of temporal overlap in the manuscript. 

We have added a paragraph in the main text for “Establishing state correspondence between analyses” (Line 672-699). We have also updated the associated figures (Fig.S2, Fig.S3 and Fig.5)

Author response image 2.

(12) Line 839: gamma parameter, on a step size of? 

(16) Figure 3. Please add a legend in the "Sound envelope" graph what green and blue lines indicate. The authors write Coh(t) and Coh(t, t+1) at the top and Coh(t) and Coh(t+1) at the bottom. Please be consistent with the labeling. Shouldn't they be Coh(t-1, t) and Coh(t, t+1) to be exact for both? 

Have corrected. 

(17) In line 226, is this one-sample t-test compared to zero? If so, please write it inside the parentheses. In line 227, the authors write "slightly weaker"; however, since this is not statistically warranted, I suggest removing the word "slightly weaker" and just noting significance in both States 1 and 2.  

Have corrected.

(18) In line 288, please fix "we also whether". 

Have corrected. 

(19) In Figure 2C, what do pink lines in the transition matrix indicate? Are they colored just to show authors' interests, or do they indicate statistical significance? Please write it in the figure legend.   

Yes, the pink lines indicate a meaningful trend, showing that the between-state transition probabilities are significantly higher than those in permutation.

We have added this information to the figure legend. 

Reviewer #2 (Recommendations for the authors):

(1) It is unclear how the correspondence between states across different conditions and datasets was computed. Given the spatial autocorrelation of brain maps, I recommend reporting the Dice coefficient along with a spin-test permutation to test for statistical significance.  

The state correspondence between different conditions and between the two datasets are established using evidence of spatial overlap. The spatial overlap between states was quantified by Pearson’s correlation using the activity values (derived from HMM) of the nine networks. For each candidate state identified in other analyses (for the Rest, MG and older-adult datasets), we calculate the correlation between its network activity pattern and the three predefined states from the main analysis (for the young-adults dataset), and set the one it most closely resembled to be its matching state. For instance, if a candidate state showed the highest correlation with State #1, it was labelled State #1 accordingly. 

For the comparison between the young and older adults’ datasets (as shown below), the largest spatial overlap occurred along the diagonal of the confusion matrix, with high correlation values. This means that each of the three candidate states was best matched to State #1, State #2, and State #3, respectively, maintaining a one-to-one correspondence between the states from the two datasets. As the HMM is modelled at the level of networks which lack accurate coordinates, we did not apply the spin-test to assess the statistical significance of overlap. Instead, we extracted the state activity patterns from the 1000 permutations (wherein the original BOLD time courses were circularly shifted and an HMM was conducted) for the older-adults dataset. Applying the similar state-correspondence strategy, we generated a null distribution of spatial overlap. The real overlap of the three states was greater than and 97.97%, 95.34% and 92.39% instances from the permutation (as shown below). 

Author response image 3.

For the comparison of main task with the resting and the incomprehensible speech condition, there was some degree of confusion: there were two candidate states showing the highest similarity to State #2. In this case, we labeled the most similar candidate as State #2. The other candidate was then assigned to the predefined state with which it had the second-highest correlation. We used a prime symbol (e.g., State #3') to denote cases where such confusion occurred. These findings support our conclusion that the tripartite-organization of brain states is not a task-free, intrinsic property.

When establishing the correspondence between the Yeo-7 network and the ninenetwork parcellation schemes, we primarily relied on evidence from temporal overlap measures, as a clear network-level alignment between the two parcellation schemes is lacking. Temporal overlap was quantified by calculating the correlation of state occurrence probabilities between the two schemes. To achieve this, we concatenated the time courses of 64 participants, resulting in a time series consisting of 19,200 time points (300 time points per participant) for each state. Each of the three candidate states from the Yeo-7 network scheme was best matched to State #1, State #2, and State #3 from the main analyses, respectively. To determine the statistical significance of the temporal overlap, we circular shifted each participant’s time course of state expression obtained from the Yeo-7network scheme for 1000 times. Applying the same strategy to find the matching states, we generated a null distribution of overlap. The real overlap was much higher than the instances from permutation. 

Author response image 4.

In the revision, we have provided detailed description for how the state correspondence is established and reported the statistical significance of those correspondence (Line 671-699). The associated figures have also been updated (Fig.5, Fig. S2 and Fig.S3).  

(2) Please clarify if circle-shifting was applied to the state expression time course when generating the null distribution for behavior-brain state correlations reported in Figure (3). This seems important to control for the temporal autocorrelation in the time courses.  

We have updated the results by using circle-shifting to generated the null distribution. The results are largely consistent with the previous on without circular shifting (Line 230-242). 

(3) Figure 3: What does the green shaded area around the sound envelope represent? In the caption, specify whether the red line in the null distributions indicates the mean or median R between brain state expression and narrative features. It would also be beneficial to report this value in the main text. 

The green shaded area indicated the original amplitude of speech signal, while blue line indicates the smoothed, low-frequency contour of amplitude changes over time (i.e., speech envelope). We have updated the figure and explained this in the figure caption. 

The red line in the null distributions indicates the R between brain state expression and narrative features for the real data. and reported the mean R of the permutation in the main text. 

(4) The manuscript is missing a data availability statement (https://elifesciences.org/inside-elife/51839f0a/for-authors-updates-to-elife-s-datasharing-policies). 

We have added a statement of data availability in the revision, as follows: 

“The raw and processed fMRI data are available on OpenNeuro: https://openneuro.org/datasets/ds005623. The experimental stimuli, behavioral data and main scripts used in the analyses are provided on Github. ”

(5) There is a typo in line 102 ("perceptual alalyses"). 

Have corrected. 

We sincerely thank the two reviewers for their constructive feedback, thorough review, and the time they dedicated to improving our work.

Reference: 

Ahrends, C., Stevner, A., Pervaiz, U., Kringelbach, M. L., Vuust, P., Woolrich, M. W., & Vidaurre, D. (2022). Data and model considerations for estimating timevarying functional connectivity in fMRI. Neuroimage, 252, 119026. 

Ballenghein, U., Megalakaki, O., & Baccino, T. (2019). Cognitive engagement in emotional text reading: concurrent recordings of eye movements and head motion. Cognition and Emotion. 

Fernandino, L., Tong, J.-Q., Conant, L. L., Humphries, C. J., & Binder, J. R. (2022). Decoding the information structure underlying the neural representation of concepts. Proceedings of the national academy of sciences, 119(6), e2108091119. https://doi.org/10.1073/pnas.2108091119  

Hasson, U., Chen, J., & Honey, C. J. (2015). Hierarchical process memory: memory as an integral component of information processing. Trends in Cognitive Sciences, 19(6), 304-313. 

Lerner, Y., Honey, C. J., Silbert, L. J., & Hasson, U. (2011). Topographic mapping of a hierarchy of temporal receptive windows using a narrated story [Article]. Journal of Neuroscience, 31(8), 2906-2915. https://doi.org/10.1523/JNEUROSCI.3684-10.2011  

Liu, L., Li, H., Ren, Z., Zhou, Q., Zhang, Y., Lu, C., Qiu, J., Chen, H., & Ding, G. (2022). The “two-brain” approach reveals the active role of task-deactivated default mode network in speech comprehension. Cerebral Cortex, 32(21), 4869-4884. 

Liu, L., Zhang, Y., Zhou, Q., Garrett, D. D., Lu, C., Chen, A., Qiu, J., & Ding, G. (2020). Auditory–Articulatory Neural Alignment between Listener and Speaker during Verbal Communication. Cerebral Cortex, 30(3), 942-951. https://doi.org/10.1093/cercor/bhz138

eLife Assessment

This valuable study reports on electrophysiological recording of the spiking activity of single neurons in the entopeduncular nucleus (EPN) in freely-moving mice performing an auditory discrimination task. The data show that the activity of single EPN neurons is modulated by reward and movement kinematics, with the latter further affected by task contexts (e.g. movement toward or away from a reward location). The results provide solid evidence for the conclusions. There is some ambiguity as to whether the data contain the population of EPN neurons characterized in previous studies that obtained different results. Investigations separating confounding factors would be of benefit. Nonetheless, the work is overall of interest to those who study how the basal ganglia, particularly the EPN, contribute to behavior.

Reviewer #1 (Public review):

The authors in this paper investigate the nature of the activity in the rodent EPN during a simple freely moving cue-reward association task. Given that primate literature suggest movement coding whereas other primate and rodent studies suggest mainly reward outcome coding in the EPNs, it is important try to tease apart the two views. Through careful analysis of behavior kinematics, position, and the neural activity in the EPNs, the authors reveal an interesting and complex relationship between the EPN and mouse behavior.

Strengths:

(1) The authors use a novel freely moving task to study EPN activity, which displays rich movement trajectories and kinematics. Given that previous studies have mostly looked at reward coding during head fixed behavior, this study adds a valuable dataset to the literature.

(2) The neural analysis is rich and thorough. Both single neuron level and population level (i.e. PCA) analysis are employed to reveal what EPN encodes.

Discussion:<br /> EPN is one of the major output nuclei of the basal ganglia. What information is present within EPN is still unclear, and under investigation. The authors have used electrophysiology to determine the nature of information present within EPN that is likely to be valuable to the field. Future studies should try to address whether this information is specific to certain cell types within EPN or whether there is topography within EPN that reflects the kinematic information present within EPN. This will require more careful dissection of EPN activity based on anatomy. Future experiments should also consider tasks that isolate a single limb (i.e. joystick tasks) in order to better understand the kinematic encoding of forelimb movement. This, combined with recording in forelimb encoding region of EPN, should give us insights into the nature of kinematic control of EPN. Overall, this study will be useful to inspire future investigations in the function of EPN.

Reviewer #2 (Public review):

This paper examined how the activity of neurons in the entopeduncular nucleus (EPN) of mice relates to kinematics, value, and reward. The authors recorded neural activity during an auditory cued two-alternative choice task, allowing them to examine how neuronal firing relates to specific movements like licking or paw movements, as well as how contextual factors like task stage or proximity to a goal influence the coding of kinematic and spatiotemporal features. The data shows that the firing of individual neurons is linked to kinematic features such as lick or step cycles. However, the majority of neurons exhibited activity related to both movement types, suggesting that EPN neuronal activity does not merely reflect muscle-level representations. This contradicts what would be expected from traditional action selection or action specification models of the basal ganglia.

The authors also show that spatiotemporal variables account for more variability compared to kinematic features alone. Using demixed Principal Component Analysis, they reveal that at the population level, the three principal components explaining the most variance were related to specific temporal or spatial features of the task, such as ramping activity as mice approached reward ports, rather than trial outcome or specific actions. Notably, this activity was present in neurons whose firing was also modulated by kinematic features, demonstrating that individual EPN neurons integrate multiple features. A weakness is that what the spatiotemporal activity reflects is not well specified. The authors suggest some may relate to action value due to greater modulation when approaching a reward port, but acknowledge action value is not well parametrized or separated from variables like reward expectation.

A key goal was to determine whether activity related to expected value and reward delivery arose from a distinct population of EPN neurons or was also present in neurons modulated by kinematic and spatiotemporal features. In contrast to previous studies (Hong & Hikosaka 2008 and Stephenson-Jones et al., 2016), the current data reveals that individual neurons can exhibit modulation by both reward and kinematic parameters. Two potential differences may explain this discrepancy: First, the previous studies used head-fixed recordings, where it may have been easier to isolate movement versus reward-related responses. Second, those studies observed prominent phasic responses to the delivery or omission of expected rewards - responses that are present but not common in the current paper. This suggests a possibility that the VGlut2+ EPN neurons that project to the LHb were under/not sampled, antidromic or optogenetic tagging would have been needed to confirm the identity of the populations that were recorded. Alternatively, in the head-fixed recordings, kinematic/spatial coding may have gone undetected due to the forced immobility.

Overall, this paper offers needed insight into how the basal ganglia output encodes behavior. The EPN recordings from freely moving mice clearly demonstrate that individual neurons integrate reward, kinematic, and spatiotemporal features, challenging traditional models. However, the specific relationship between the spatiotemporal activity and factors like action value remains unclear.

Author response:

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

Reviewer #1 (Public Review):

The authors in this paper investigate the nature of the activity in the rodent EPN during a simple freely moving cue-reward association task. Given that primate literature suggests movement coding whereas other primate and rodent studies suggest mainly reward outcome coding in the EPNs, it is important to try to tease apart the two views. Through careful analysis of behavior kinematics, position, and neural activity in the EPNs, the authors reveal an interesting and complex relationship between the EPN and mouse behavior.

Strengths:

(1) The authors use a novel freely moving task to study EPN activity, which displays rich movement trajectories and kinematics. Given that previous studies have mostly looked at reward coding during head-fixed behavior, this study adds a valuable dataset to the literature. (2) The neural analysis is rich and thorough. Both single neuron level and population level (i.e. PCA) analysis are employed to reveal what EPN encodes.

Thank you very much for this appreciation.

Weaknesses:

(1) One major weakness in this paper is the way the authors define the EPN neurons. Without a clear method of delineating EPN vs other surrounding regions, it is not convincing enough to call these neurons EPNs solely from looking at the electrode cannula track from Figure 2B. Indeed, EPN is a very small nucleus and previous studies like Stephenson-Jones et al (2016) have used opto-tagging of Vglut2 neurons to precisely label EPN single neurons. Wallace et al (2017) have also shown the existence of SOM and PV-positive neurons in the EPN. By not using transgenic lines and cell-type specific approaches to label these EPN neurons, the authors miss the opportunity to claim that the neurons recorded in this study do indeed come from EPN. The authors should at least consider showing an analysis of neurons slightly above or below EPN and show that these neurons display different waveforms or firing patterns.

We thank the reviewer for their comment, and we thank the opportunity to expand on the inclusion criteria of studied units after providing an explanation. 

As part of another study, we performed experiments recording in EPN with optrodes and photoidentification in PV-Cre animals. We found optoidentified units in both: animals with correct placement (within the EPN) and on those with off-target placement (within the thalamus or medial to the EPN). Thus, despite the use of Cre animals, we relied on histology to ensure correct EPN recording. We believe that the optotagging based purely on neural makers such as PV, SOM, VGLUT, VGAT would not provide a better anatomical delineation of the EPN since adjacent structures are rich in those same markers. The thalamic reticular nucleus is just dorsal to the EPN and it has been shown to express both SOM and PV (Martinez-Garcia et al., 2020). 

On the other hand, the lateral hypothalamus (just medial to the EPN) also expresses vGlut2 and SOM. Stephenson-Jones (2016), Extended Data Figure 1, panel g, shows vGluT2 and somatostatin labeling of neurons, with important expression of neurons dorsal, ventral and medial to the EPN. Thus, we believe that viral strategies relying on single neuronal markers still depend on careful histological analysis of recording sites.

A combination of neural markers or more complex viral strategies might be more suitable to delineate the EPN. As an example, for anatomical tracing Stephenson-Jones et al. 2016 performed a rabies-virus based approach involving retrogradely transported virus making use of projection sites through two injections. Two step viral approaches were also performed in Wallace, M. et al. 2017. We attempted to perform a two-step viral approach, using an anterogradely transported Cre-expressing virus (AAV1.hSyn.Cre.WPRE.hGH) injected into the striatum and a second Cre dependent ChR2 into the EPN. However, our preliminary experiments showed that this double viral approach had a stark effect decreasing the performance of animals during the task (we attempted re-training 2-3 weeks after viral infections and animals failed to turn to the contralateral side of the injections). We believe that this approach might have had a toxic effect (Zingg et al., 2017). 

To this point, a recent paper (Lazaridis et al., 2019) repeated an optogenetic experiment performed in the Stephenson-Jones et al. study, using a set of different viral approaches and concluded that increasing the activity of GPi-LHb is not aversive, as it had been previously reported. Thus, future studies attempting to increase anatomical specificity are a must, but they will require using viral approaches amenable to the behavioral paradigm.

We attempted to find properties regarding waveforms, firing rate, and firing patterns from units above or below, however, we did not find a marker that could generate a clear demarcation. We show here a figure that includes the included units in this study as well as excluded ones to show that there is a clear overlap.

Author response image 1.

Finally, we completely agree with the reviewer in that there is still room for improvement. We have further expanded the Methods section to explain better our efforts to include units recorded within the EPN. Further, we have added a paragraph within the Discussion section to point out this limitation (lines 871-876).

Methods (lines 116-131):

“Recordings. Movable microwire bundles (16 microwires, 32 micrometers in diameter, held inside a cannula, Innovative Neurophysiology, Durham, NC)] were stereotaxtically implanted just above the entopeduncular nucleus (-0.8 AP, 1.7 ML, 3.9 DV). Post surgical care included antibiotic, analgesic and antiinflammatory pharmacological treatment. After 5 days of recovery, animals were retrained for 1-2 weeks. Unitary activity was recorded for 2-6 days at each dorsoventral electrode position and the session with the best electrophysiological (signal to noise ratio (>2), stability across time) and behavioral [performance, number of trials (>220)] quality was selected. Microwire electrodes were advanced in 50 micrometer dorsoventral steps for 500 micrometers in total. After experiment completion, animals were perfused with a 4% paraformaldehyde solution. Brains were extracted, dehydrated with a 30% sucrose solution and sectioned in a cryostat into 30micron thick slices. Slices were mounted and photographed using a light microscope. Microwire tracks of the 16-microwire bundle were analyzed (Fig. 2A-B) and only animals with tracks traversing the EPN were selected (6 out of 10). Finally, we located the final position of microwire tips and inferred the dorsoventral recording position of each of the recording sessions. Only units recorded within the EPN were included.” 

Discussion (lines 871-876):

“A weakness of the current study is the lack of characterization of neuronal subtypes. An area of opportunity for future research could be to perform photo-identification of neuronal subtypes within the EPN which could contribute to the overall description of the information representation. Further, detailed anatomical viral vector strategies could aid to improve anatomical localization of recordings, reduce reliance on histological examination, and solve some current controversies (Lazaridis et al., 2019).” 

(2) The authors fail to replicate the main finding about EPN neurons which is that they encode outcome in a negative manner. Both Stephenson-Jones et al (2016) and Hong and Hikosaka (2008) show a reward response during the outcome period where firing goes down during reward and up during neutral or aversive outcome. However, Figure 2 G top panel shows that the mean population is higher during correct trials and lower during incorrect trials. This could be interesting given that the authors might try recording from another part of EPN that has not been studied before. However, without convincing evidence that the neurons recorded are from EPN in the first place (point 1), it is hard to interpret these results and reconcile them with previous studies.

We really thank the reviewer for pointing out that we need to better explain how EPN units encode outcome. We now provide an additional panel in Figure 4, its corresponding text in the results section (lines 544-562) and a new paragraph in the discussion related to this comment.

We believe that we do indeed recapitulate findings of both of Stephenson-Jones et al (2016) and Hong and Hikosaka (2008). Both studies focus on a specific subpopulation of GPi/EPN neurons that project to the lateral habenula (LHb). Stephenson-Jones et al (2016) posit that GPi-LHb neurons (which they opto-tag as vGluT2) exhibit a decreased firing rate during rewarding outcomes. Hong and Hikosaka (2008) antidromically identified LHb projecting neurons through within the GPi and found reward positive and reward negative neurons, which were respectively modulated either by increasing or decreasing their firing rate with a rewarding outcome (red and green dots on the x-axis of Figure 5A in their paper).

As the reviewer pointed out the zScore may be misleading. Therefore, in our study we also decomposed population activity on reward axis through dPCA. When marginalizing for reward in Figure 3F, we find that the weights of individual units on this axis are centered around zero, with positive and negative values (Figure 3F, right panel). Thus, units can code a rewarding outcome as either an increase or a decrease of activity. We show example units of such modulation in Figure 3-1g and h.

We had segregated our analysis of spatio-temporal and kinematic coding upon the reward coding of units in Figure 4L-M. Yet, following this comment and in an effort of further clarifying this segregation, we introduced panels with the mean zScore of units during outcome evaluation in Figure 4L.

We amended the main text to better explain these findings (lines 544-562).

“Previous reports suggest that EPN units that project to the lateral habenula encode reward as a decrease in firing rate. Thus, we wished to ask whether reward encoding units can code kinematic and spatio-temporal variables as well.

To this end, we first segregated units upon their reward coding properties: reward positive (which increased activity with reward) and reward negative units (which decreased activity with reward). We performed auROC on the 250ms after head entry comparing rewarded trials and incorrect trails (p<0.001, permutation test). Mean activity of reward insensitive, positive and negative units is shown in Fig. 4L. Next, we performed a dimensionality reduction on the coefficients of the model that best explained both contexts (kinematic + spatio-temporal model on pooled data) using UMAP (McInnes et al., 2018). We observe a continuum rather than discrete clusters (Fig. 4L). Note that individual units are color coded according to their responsivity to reward. We did not find a clear clustering either.”  

Paragraph added in the discussion (lines 749-755):

“In this study, we found that rewarding outcomes can be represented by EPN units through either an increase or a decrease in firing rate (Fig. 3F, 3-1g-h, 4L). While Stephenson-Jones et al., 2016 found that lateral habenula (LHb)-projecting neurons within the EPN of mice primarily encoded rewarding outcomes by a decrease in firing rate, Hong and Hikosaka, 2008 observed that in primates, LHb-projecting units could encode reward through either a decrease or an increase in firing rate. Thus, our results align more closely with the latter study, which also employed an operant conditioning task.”

(3) The authors say that: 'reward and kinematic doing are not mutually exclusive, challenging the notion of distinct pathways and movement processing'. However, it is not clear whether the data presented in this work supports this statement. First, the authors have not attempted to record from the entire EPN. Thus it is possible that the coding might be more segregated in other parts of EPN. Second, EPNs have previously been shown to display positive firing for negative outcomes and vice versa, something which the authors do not find here. It is possible that those neurons might not encode kinematic and movement variables. Thus, the authors should point out in the main text the possibility that the EPN activity recorded might be missing some parts of the whole EPN.

We thank the reviewer for the opportunity to expand on this topic. We believe it is certainly possible that other not-recorded regions of the EPN might exhibit greater segregation of reward and kinematics. However, we considered it worthwhile pointing out that from the dataset collected in this study reward-sensitive units encode kinematics in a similar fashion to reward-insensitive ones (Fig. 4L,M). Moreover, we asked specifically whether reward-negative units (that decrease firing rate with rewarding outcomes, as previously reported) could encode kinematics and spatio-temporal variables with different strength than reward-insensitive ones and could not find significant differences (Fig. 4M).

We did indeed find units that displayed decreased firing rate upon rewarding outcomes, as has been previously reported. We have addressed this fact more thoroughly in point (2). 

Finally, we agree with the reviewer that the dataset collected in this study is by no means exhaustive of the entire EPN and have thus included a sentence pointing this out in the Discussion section (lines 805-806):

“Given that we did not record from the entire EPN, it is still possible that another region of the nucleus might exhibit more segregation.”

(4) The authors use an IR beam system to record licks and make a strong claim about the nature of lick encoding in the EPN. However, the authors should note that IR beam system is not the most accurate way of detecting licks given that any object blocking the path (paw or jaw-dropping) will be detected as lick events. Capacitance based, closed-loop detection, or video capturing is better suited to detect individual licks. Given that the authors are interested in kinematics of licking, this is important. The authors should either point this out in the main text or verify in the system if the IR beam is correctly detecting licks using a combination of those methods.

We thank the reviewer for the opportunity of clarifying the lick event acquisition. We have experience using electrical alternatives to lickometers; however, we believe they were not best suited to this application. Closed-loop lickometers generally use a metallic grid upon which animals stand so that the loop can be closed; however, we wanted to have a transparent floor. We have found capacitance based lickometers to be useful in head-fixed conditions but have noticed that they are very dependent on animal position and proximity of other bodyparts such as limbs. Given the freely moving aspect of the task this was difficult to control. Finally, both electric alternatives for lickometers are more prone to noise and may introduce electrical artifacts that might contaminate the spiking signal. This is why we opted to use a slit in combination with an IR beam that would only fit the tongue and that forced enough protrusion such that individual licks could be monitored. Further, the slit could not fit other body-parts like the paw or jaw. We have now included a video (Supp. Video 2) showing a closeup of this behavior that better conveys how the jaw and paw do not fit inside the slit. The following text has been added in the corresponding methods section (lines 97-98):

“The lickometer slit was just wide enough to fit the tongue and deep enough to evoke a clear tongue protrusion.”

Reviewer #1 (Recommendations For The Authors):

(1)The authors should verify using opto-tagging of either Vglut2, SOM, or PV neurons whether they can see the same firing pattern. If not, the authors should address this weakness in the paper.

We thank the reviewer for this important point, we have provided a more detailed reply above.

(2)The way dPCA or PCA is applied to the data is not stated at all in the main text. Are all units from different mice combined? Or applied separately for each mouse? How does that affect the interpretation of the data? At least a brief text should be included in the main text to guide the readers.

We thank the reviewer for pointing out this important omission. We have included an explanation in the Methods section and in the Main text.

Methods (lines 182-184):

“For all population level analyses individual units recorded from all sessions and all animals were pooled to construct pseudo-simultaneous population response of combined data mostly recorded separately.”

Main text (lines 397-399):

“For population level analyses throughout the study, we pooled recorded units from all animals to construct a pseudo-simultaneous population.”

Discussion (lines 729-730):

“…(from pooled units from all animals to construct a pseudo-simultaneous population, which assumes homogeneity across subjects)”

(3) The authors argue that they do not find 'value coding' in this study. However, the authors never manipulate reward size or probability, but only the uncertainty or difficulty of the task. This might be better termed 'difficulty', and it is difficult to say whether this correlates with value in this task. For instance, mice might be very confident about the choice, even for an intermediate frequency sweep, if the mouse had waited long enough to hear the full sweep. In that case, the difficulty would not correlate with value, given that the mouse will think the value of the port it is going to is high. Thus, authors should avoid using the term value.

We agree with the reviewer. We have modified the text to specify that difficulty was the variable being studied and added the following sentence in the Discussion (lines 747-748):

“It is still possible that by modifying reward contingencies such as droplet size value coding could be evidenced.”

(4) How have the authors obtained Figure 7D bottom panel? It is unclear at all what this correlation represents. Are the authors looking at a correlation between instantaneous firing rate and lick rate during a lick bout?

We thank the reviewer for pointing out that omission. It is indeed correlation coefficient between the instantaneous firing rate and the instantaneous lick rate for a lick bout. We have included labeling in Figure 7D and pointed this out in the main text [lines 680-681]:

“Fig.7D, lower panel shows the correlation coefficient between the instantaneous firing rate and the instantaneous lick rate within a lick bout for all units.”

Reviewer #2 (Public Review):

This paper examined how the activity of neurons in the entopeduncular nucleus (EPN) of mice relates to kinematics, value, and reward. The authors recorded neural activity during an auditory-cued two-alternative choice task, allowing them to examine how neuronal firing relates to specific movements like licking or paw movements, as well as how contextual factors like task stage or proximity to a goal influence the coding of kinematic and spatiotemporal features. The data shows that the firing of individual neurons is linked to kinematic features such as lick or step cycles. However, the majority of neurons exhibited activity related to both movement types, suggesting that EPN neuronal activity does not merely reflect muscle-level representations. This contradicts what would be expected from traditional action selection or action specification models of the basal ganglia.

The authors also show that spatiotemporal variables account for more variability compared to kinematic features alone. Using demixed Principal Component Analysis, they reveal that at the population level, the three principal components explaining the most variance were related to specific temporal or spatial features of the task, such as ramping activity as mice approached reward ports, rather than trial outcome or specific actions. Notably, this activity was present in neurons whose firing was also modulated by kinematic features, demonstrating that individual EPN neurons integrate multiple features. A weakness is that what the spatiotemporal activity reflects is not well specified. The authors suggest some may relate to action value due to greater modulation when approaching a reward port, but acknowledge action value is not well parametrized or separated from variables like reward expectation.

We thank the reviewer for the comment. We indeed believe that further exploring these spatiotemporal signals is important and will be the subject of future studies.

A key goal was to determine whether activity related to expected value and reward delivery arose from a distinct population of EPN neurons or was also present in neurons modulated by kinematic and spatiotemporal features. In contrast to previous studies (Hong & Hikosaka 2008 and Stephenson-Jones et al., 2016), the current data reveals that individual neurons can exhibit modulation by both reward and kinematic parameters. Two potential differences may explain this discrepancy: First, the previous studies used head-fixed recordings, where it may have been easier to isolate movement versus reward-related responses. Second, those studies observed prominent phasic responses to the delivery or omission of expected rewards - responses largely absent in the current paper. This absence suggests a possibility that neurons exhibiting such phasic "reward" responses were not sampled, which is plausible since in both primates and rodents, these neurons tend to be located in restricted topographic regions. Alternatively, in the head-fixed recordings, kinematic/spatial coding may have gone undetected due to the forced immobility.

Thank you for raising this point. Nevertheless, there is some phasic activity associated with reward responses, which can be seen in the new panel in Figure 4L.

Overall, this paper offers needed insight into how the basal ganglia output encodes behavior. The EPN recordings from freely moving mice clearly demonstrate that individual neurons integrate reward, kinematic, and spatiotemporal features, challenging traditional models. However, the specific relationship between spatiotemporal activity and factors like action value remains unclear.

We really appreciate this reviewer for their valuable comments.

Reviewer #2 (Recommendations For The Authors):

One small suggestion is to make sure that all the panels in the figures are well annotated. I struggled in places to know what certain alignments or groupings meant because they were not labelled. An example would be what do the lines correspond to in the lower panels of Figure 2D and E. I could figure it out from other panels but it would have helped if each panel had better labelling.

Thanks for pointing this out, we have improved labelling across the figures and corrected the specific example you have pointed out.

The paper is very nice though. Congratulations!

Thank you very much.

Editor's note:

Should you choose to revise your manuscript, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

We thank the editor for the comment. A statistics table has been added.

References:

Lazaridis, I., Tzortzi, O., Weglage, M., Märtin, A., Xuan, Y., Parent, M., Johansson, Y., Fuzik, J., Fürth, D., Fenno, L. E., Ramakrishnan, C., Silberberg, G., Deisseroth, K., Carlén, M., & Meletis, K. (2019). A hypothalamus-habenula circuit controls aversion. Molecular Psychiatry, 24(9), 1351–1368. https://doi.org/10.1038/s41380-019-0369-5

Martinez-Garcia, R. I., Voelcker, B., Zaltsman, J. B., Patrick, S. L., Stevens, T. R., Connors, B. W., & Cruikshank, S. J. (2020). Two dynamically distinct circuits drive inhibition in the sensory thalamus. Nature, 583(7818), 813–818. https://doi.org/10.1038/s41586-0202512-5

McInnes, L., Healy, J., Saul, N., & Großberger, L. (2018). UMAP: Uniform Manifold Approximation and Projection. Journal of Open Source Software, 3(29), 861. https://doi.org/10.21105/joss.00861

Zingg, B., Chou, X. lin, Zhang, Z. gang, Mesik, L., Liang, F., Tao, H. W., & Zhang, L. I. (2017). AAV-Mediated Anterograde Transsynaptic Tagging: Mapping Corticocollicular Input-Defined Neural Pathways for Defense Behaviors. Neuron, 93(1), 33–47. https://doi.org/10.1016/j.neuron.2016.11.045

eLife Assessment

Kreeger et al. convincingly demonstrate that octopus cells in the mouse cochlear nucleus, previously thought to rely primarily on excitatory inputs for coincidence detection, also receive glycinergic inhibitory synaptic inputs that influence their synaptic integration. Using advanced techniques, including genetic mouse models, optogenetics, microscopy, slice physiology, and computational modeling, this important study reveals that inhibition can shunt synaptic currents and alter the timing of dendritic EPSPs, both of which are significant for auditory processing. This research broadens the understanding of octopus cells' roles in sensory processing, highlighting the importance of inhibitory inputs in shaping fast, high-frequency neural response capabilities.

Reviewer #1 (Public review):

Kreeger and colleagues have explored the balance of excitation and inhibition in the cochlear nucleus octopus cells of mice using morphological, electrophysiological and computational methods. On the surface, the conclusion, that synaptic inhibition is present, does not seem like a leap. However, the octopus cells have been in the past portrayed as lacking synaptic inhibition. This view was supported by the paucity of glycinergic fibers in the octopus cell area and the lack of apparent IPSPs. Here, Kreeger et al., used beautiful immunohistochemical and mouse genetic methods to quantify the inhibitory and excitatory boutons over the complete surface of individual octopus cells and further analyzed the proportions of the different subtypes of spiral ganglion cell inputs. I think the analysis of synaptic distribution and the origin of the excitatory inputs stands as one of the most complete descriptions of any neuron, leaving little doubt about the presence of glycinergic boutons.

Kreeger et al then examined inhibition physiologically. Recordings from these neurons are notoriously difficult to make because of the enormous leak currents that shunt membrane stimuli and currents, and complicate voltage clamp. The authors have tried to overcome these limitations using drugs to block leak conductances, and computational approaches based on realistic parameters. They conclude that dendritic inhibition can modify the size and kinetics of excitatory signals, and may play out in computations made on temporally dispersed stimuli as might be experienced during a ramp in sound frequency or complex natural sounds like vocalizations.

Reviewer #2 (Public review):

Kreeger et.al provided mechanistic evidence for flexible coincidence detection of auditory nerve synaptic inputs by octopus cells in the mouse cochlear nucleus. The octopus cells are highly specialized neurons that, with appropriate stimuli, can fire repetitively at very high rates (> 800 Hz in vivo), yield responses dominated by the onset of sound for simple stimuli, and integrate auditory nerve inputs over a wide frequency span. Previously, it was thought that octopus cells received little inhibitory input, and their integration of auditory input depended principally on temporally precise coincidence detection of excitatory auditory nerve inputs, coupled with a low input resistance established by high levels of expression of certain potassium channels and hyperpolarization-activated channels.

This study provides convincing evidence that octopus cells do in fact receive glycinergic synaptic input that can influence the efficacy of excitatory dendritic synaptic activity. By coupling selected genetic mouse models to characterize synaptic inputs and enable optogenetic stimulation of subsets of afferents, fluorescent microscopy, detailed reconstructions of the location of inhibitory synapses on the soma and dendrites of octopus cells, slice physiology, and computational modeling, they have been able to clarify the presence of functional inhibition and elucidate some of the features of the inhibitory inputs to octopus cells at a biophysical level. They also show through modeling that inhibition is predicted to both provide shunting of synaptic currents and to change the peak timing of dendritic EPSPs as they travel to the soma. Both of these effects are potentially critically important in integration in these fast, coincidence-detecting neurons, and the magnitudes of the effects could have physiological significance. Overall, this work extends thinking about the functional sensory processing roles of octopus cells beyond the pre-existing hypotheses that are focussed primarily on the coincidence detection of excitatory inputs.

The authors have addressed all of my prior concerns, including improving several aspects of the presentation. The modeling is better described, which is critical because it provides a foundation to help interpret some of the physiology and to propose specific functions.

Author response:

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

eLife assessment

This valuable work analyzes how specialized cells in the auditory cells, known as the octopus cells, can detect coincidences in their inputs at the submillisecond time scale. While previous work indicated that these cells receive no inhibitory inputs, the present study unambiguously demonstrates that these cells receive inhibitory glycinergic inputs. The physiologic impact of these inputs needs to be studied further. It remains incomplete at present but could be made solid by addressing caveats related to similar sizes of excitatory postsynaptic potentials and spikes in the octopus neurons.

We apologize for not explicitly describing our experimental methods and analyses procedures that ensure the discrimination between action potentials and EPSPs. This has been addressed in responses to reviewer comments and amended in the manuscript.

Reviewer #1 (Public Review):

Kreeger and colleagues have explored the balance of excitation and inhibition in the cochlear nucleus octopus cells of mice using morphological, electrophysiological, and computational methods. On the surface, the conclusion, that synaptic inhibition is present, does not seem like a leap. However, the octopus cells have been in the past portrayed as devoid of inhibition. This view was supported by the seeming lack of glycinergic fibers in the octopus cell area and the lack of apparent IPSPs. Here, Kreeger et al. used beautiful immunohistochemical and mouse genetic methods to quantify the inhibitory and excitatory boutons over the complete surface of individual octopus cells and further analyzed the proportions of the different subtypes of spiral ganglion cell inputs. I think the analysis stands as one of the most complete descriptions of any neuron, leaving little doubt about the presence of glycinergic boutons.

Kreeger et al then examined inhibition physiologically, but here I felt that the study was incomplete. Specifically, no attempt was made to assess the actual, biological values of synaptic conductance for AMPAR and GlyR. Thus, we don't really know how potent the GlyR could be in mediating inhibition. Here are some numbered comments:

(1) "EPSPs" were evoked either optogenetically or with electrical stimulation. The resulting depolarizations are interpreted to be EPSPs. However previous studies from Oertel show that octopus cells have tiny spikes, and distinguishing them from EPSPs is tricky. No mention is made here about how or whether that was done. Thus, the analysis of EPSP amplitude is ambiguous.

We agree that large EPSPs can be difficult to distinguish from an octopus cell’s short spikes during experiments. During analysis, we distinguished spikes from EPSPs by generating phase plots, which allow us to visualize the first derivative of the voltage trace on the y-axis and the value of the voltage on the x-axis at each moment in time. In the example shown below, four depolarizing events were electrically evoked in an octopus cell (panel A). The largest of these events (shown in orange in panels B-D) has an amplitude of ~9mV and could be a small spike. The first derivative of the voltage (panel C) reveals a bi-phasic response in the larger orange trace, where during the rising phase (mV/ms > 0) of the EPSP there is a second, sharper rising phase for the spike. Like more traditionally sized action potentials, phase plots for octopus cell spikes also reveal a sharp change in the rate of voltage change over time (Author response image 1 panel D, ✱) after the rising action of the EPSP begins to slow. EPSPs (shown in blue in panels B-D) lack the deflection in the phase plot. Not all cases were as unambiguous as this example. Therefore, our analysis only included subthreshold stimulation that unambiguously evoked EPSPs, not spikes. A brief description of this analysis has been added to the methods text (lines 625-627) and we have noted in the results section that both ChR2-evoked and electrically-evoked stimulation can produce small action potentials, which were excluded from analysis (lines 156-158).

Author response image 1.

(2) For this and later analysis, a voltage clamp of synaptic inputs would have been a simple alternative to avoid contaminating spikes or shunts by background or voltage-gated conductances. Yet only the current clamp was employed. I can understand that the authors might feel that the voltage clamp is 'flawed' because of the failure to clamp dendrites. But that may have been a good price to pay in this case. The authors should have at least justified their choice of method and detailed its caveats.

We agree that data collected using voltage-clamp would have eliminated the confound of short action potentials and avoided the influence of voltage-gated conductances. The large-diameter, and comparatively simple dendritic trees of octopus cells make them good morphological candidates for reliable voltage clamp. However, as suggested, we were concerned that the abundance of channels open at the neuron’s resting potential would make it difficult to sufficiently clamp dendrites. Ultimately, given the low input resistances of octopus cells and the fast kinetics of excitatory inputs, we determined that bad voltage clamp conditions were likely to result in unclamped synaptic events with unpredicted distortions in kinetics and attenuation (To et al. 2022; PMID: 34480986; DOI: 10.1016/j.neuroscience.2021.08.024). We therefore chose to focus our efforts on current-clamp.

Beyond the limits of both current-clamp and voltage-clamp, we chose to leave all conductances that influence EPSP dendritic propagation intact because our model demonstrates that active Kv and leak conductances shape and attenuate synaptic inputs as they travel through the dendritic tree (Supp. Fig. 4F-G). The addition of voltage-clamp recordings would not impact the conclusions we make about EPSP summation at the soma. Future studies will need to focus on a dendrite-centric view of local excitatory and inhibitory summation. For dendrite-centric experiments, dendritic voltage-clamp recordings are well suited to answer that set of questions.

(3) The modeling raised several concerns. First, there is little presentation of assumptions, and of course, a model is entirely about its assumptions. For example, what excitatory conductance amplitudes were used? The same for inhibitory conductance? How were these values arrived at? The authors note that EPSGs and IPSGs had peaks at 0.3 and 3 ms. On what basis were these numbers obtained? The model's conclusions entirely depend on these values, and no measurements were made here that could have provided them. Parenthetical reference is made to Figure S5 where a range of values are tested, but with little explanation or justification.

We apologize for not providing this information. We used our octopus neuron model to fit both EPSP and IPSP parameters to match experimental data. We have expanded the methods to include final values for the conductances (lines 649-651), which were adjusted to match experimental values seen in current-clamp recordings. We have also expanded the results section to describe each of the parameters we tuned (lines 203-222). An example of these adjustments is illustrated in Fig. 4F where the magnitude of inhibitory potentials at different conductances (100nS and 1nS) was compared to experimental data over a range of octopus cell input resistance conditions. Kinetic parameters were determined by aligning modeled PSPs to the rise times and full width at half maximum (FWHM) measurements from experiments under control and Kv block conditions. The experimental data for EPSPs and IPSPs that was used to fit the model is shown in Author response image 2 below.

Author response image 2.

(4) In experiments that combined E and I stimulation, what exactly were time courses of the conductance changes, and how 'synchronous' were they, given the different methods to evoke them? (had the authors done voltage clamp they would know the answers).

We chose to focus data collection on voltage changes at the soma under physiological conditions to better understand how excitation and inhibition integrate at the somatic compartment. Our conclusions in the combined E and I stimulation experiments require the resting membrane properties of octopus cells to be intact to make physiologically-relevant conclusions. Our current-clamp data includes the critical impact of leak, Kv, and HCN conductances on this computation. Reliable voltage-clamp would necessitate the removal of the Kv and HCN conductances that shape PSP magnitude, shape, and speed. Because it was not necessary to measure the conductances and kinetics of specific channels, we chose to use current-clamp.

Evoked IPSPs and EPSPs had cell-to-cell variability in their latencies to onset. Somatically-recorded optically-evoked inhibition under pharmacological conditions that changed cable properties had onset latencies between 2.5 and 4.3ms; electrically-evoked excitation under control conditions had latencies between 0.8 and 1.4ms. To overcome cell-to-cell timing variabilities, we presented a shuffled set of stimulation pairings that had a 3ms range of timings with 200µs intervals. As the evoked excitation and inhibition become more ‘synchronous’, the impact on EPSP magnitude and timing is greatest. Data presented in this paper was for the stimulation pairings that evokes a maximal shift in EPSP timing. On average, this occurred when the optical stimulation began ~1.2ms before electrical stimulation. Stimulation pairing times ranged between a 0ms offset and a 1.8ms offset at the extremes. An example of the shuffled stimulation pairings is shown in Author response image 3 below, and we have included information about the shuffled stimulus in the methods (lines 627-630)

Author response image 3.

(5) Figure 4G is confusing to me. Its point, according to the text, is to show that changes in membrane properties induced by a block of Kv and HCN channels would not be expected to alter the amplitudes of EPSCs and IPSCs across the dendritic expanse. Now we are talking about currents (not shunting effects), and the presumption is that the blockers would alter the resting potential and thus the driving force for the currents. But what was the measured membrane potential change in the blockers? Surely that was documented. To me, the bigger concern (stated in the text) is whether the blockers altered exocytosis, and thus the increase in IPSP amplitude in blockers is due BOTH to loss of shunting and increase in presynaptic spike width. Added to this is that 4AP will reduce the spike threshold, thus allowing more ChR2-expressing axons to reach the threshold. Figure 4G does not address this point.

These are valuable points that motivated us to improve the clarity of this figure and the corresponding text. We discussed two separate points in this paragraph and were not clear. Our intention with Figure 4G was to address concerns that using pharmacological blockers changes driving forces and may confound the measured change in magnitude of postsynaptic potentials. Membrane potentials hyperpolarized by approximately 8-10 mV after application of blockers. We corrected for this effect by adding a holding current to depolarize the neuron to its baseline resting potential. Text in the results (lines 187-190) and figure legends have been changed to clarify these points.

We also removed any discussion of presynaptic effects from this portion of the text because our description was incomplete and we did not directly collect data related to these claims. We originally wrote, “While blocking Kv and HCN allowed us to reveal IPSPs at the soma, 4-AP increases the duration of the already unphysiological ChR2-evoked presynaptic action potential (Jackman et al., 2014; DOI: 10.1523/jneurosci.4694-13.2014), resulting in altered release probabilities and synaptic properties, amongst other caveats (Mathie et al., 1998; DOI: 10.1016/S0306-3623(97)00034-7)”. Ultimately, effects on exocytosis, presynaptic excitability, or release probability are only relevant for the experiments presented in Figure 4. Figure 4 serves as evidence that synaptic release of glycine elicits strychnine-sensitive inhibitory postsynaptic potentials in octopus cells. Concerns of presynaptic effects do not carry over to the data presented in Figure 5, as Kv and HCN were not blocked in these experiments. Therefore, we have removed this portion of the text.

(6) Figure 5F is striking as the key piece of biological data that shows that inhibition does reduce the amplitude of "EPSPs" in octopus cells. Given the other uncertainties mentioned, I wondered if it makes sense as an example of shunting inhibition. Specifically, what are the relative synaptic conductances, and would you predict a 25% reduction given the actual (not modeled) values?

We agree that both shunting and hyperpolarizing inhibition could play a role in the measured EPSP changes. Because we focused data collection on voltage changes at the soma under physiological conditions, we cannot calculate the relative synaptic conductances. Together, our experimental current-clamp results paired with estimates from the model provide compelling evidence for the change we observe in EPSPs. Regardless, the relative weights of the synaptic conductances is a very interesting question, but this information is not necessary to answer the questions posed in this study, namely the impact of dendritic inhibition on the arrival of EPSPs in the soma.

(7) Some of the supplemental figures, like 4 and 5, are hardly mentioned. Few will glean anything from them unless the authors direct attention to them and explain them better. In general, the readers would benefit from more complete explanations of what was done.

We apologize for not fully discussing these figures in the results text. We have fully expanded the results section to detail the experiments and results presented in the supplement (lines 203-238).

Reviewer #2 (Public Review):

Summary:

Kreeger et.al provided mechanistic evidence for flexible coincidence detection of auditory nerve synaptic inputs by octopus cells in the mouse cochlear nucleus. The octopus cells are specialized neurons that can fire repetitively at very high rates (> 800 Hz in vivo), yield responses dominated by the onset of sound for simple stimuli, and integrate auditory nerve inputs over a wide frequency span. Previously, it was thought that octopus cells received little inhibitory input, and their integration of auditory input depended principally on temporally precise coincidence detection of excitatory auditory nerve inputs, coupled with a low input resistance established by high levels of expression of certain potassium channels and hyperpolarization-activated channels.

In this study, the authors used a combination of numerous genetic mouse models to characterize synaptic inputs and enable optogenetic stimulation of subsets of afferents, fluorescent microscopy, detailed reconstructions of the location of inhibitory synapses on the soma and dendrites of octopus cells, and computational modeling, to explore the importance of inhibitory inputs to the cells. They determined through assessment of excitatory and inhibitory synaptic densities that spiral ganglion neuron synapses are densest on the soma and proximal dendrite, while glycinergic inhibitory synaptic density is greater on the dendrites compared to the soma of octopus cells. Using different genetic lines, the authors further elucidated that the majority of excitatory synapses on the octopus cells are from type 1a spiral ganglion neurons, which have low response thresholds and high rates of spontaneous activity. In the second half of the paper, the authors employed electrophysiology to uncover the physiological response of octopus cells to excitatory and inhibitory inputs. Using a combination of pharmacological blockers in vitro cellular and computational modeling, the authors conclude that glycine in fact evokes IPSPs in octopus cells; these IPSPs are largely shunted by the high membrane conductance of the cells under normal conditions and thus were not clearly evident in prior studies. Pharmacological experiments point towards a specific glycine receptor subunit composition. Lastly, Kreeger et. al demonstrated with in vitro recordings and computational modeling that octopus cell inhibition modulates the amplitude and timing of dendritic spiral ganglion inputs to octopus cells, allowing for flexible coincidence detection.

Strengths:

The work combines a number of approaches and complementary observations to characterize the spatial patterns of excitatory and inhibitory synaptic input, and the type of auditory nerve input to the octopus cells. The combination of multiple mouse lines enables a better understanding of and helps to define, the pattern of synaptic convergence onto these cells. The electrophysiology provides excellent functional evidence for the presence of the inhibitory inputs, and the modeling helps to interpret the likely functional role of inhibition. The work is technically well done and adds an interesting dimension related to the processing of sound by these neurons. The paper is overall well written, the experimental tests are well-motivated and easy to follow. The discussion is reasonable and touches on both the potential implications of the work as well as some caveats.

Weaknesses:

While the conclusions presented by the authors are solid, a prominent question remains regarding the source of the glycinergic input onto octopus cells. In the discussion, the authors claim that there is no evidence for D-stellate, L-stellate, and tuberculoventral cell (all local inhibitory neurons of the ventral and dorsal cochlear nucleus) connections to octopus cells, and cite the relevant literature. An experimental approach will be necessary to properly rule out (or rule in) these cell types and others that may arise from other auditory brainstem nuclei. Understanding which cells provide the inhibitory input will be an essential step in clarifying its roles in the processing of sound by octopus cells.

We are glad that the reviewer agrees with the conclusions we have made and is interested in learning more about how these findings impact sound processing. We agree that defining the source of inhibition will dramatically shape our understanding of the computation octopus cells are making. However, this is not an easy task, given the small size of the octopus cell area, and will involve considerable additional work. Since the overall findings do not depend on knowing the source of inhibition, we have instead re-written the discussion to clarify the lack of evidence for intrinsic inhibitory inputs to octopus cells, in addition to presenting likely candidates. As genetic profiles of cochlear nucleus and other auditory brainstem neurons become available, we intend to make and utilize genetic mouse models to answer questions like this.

The authors showed that type 1a SGNs are the most abundant inputs to octopus cells via microscopy. However, in Figure 3 they compare optical stimulation of all classes of ANFs, then compare this against stimulation of type 1b/c ANFs. While a difference in the paired-pulse ratio (and therefore, likely release probability) can be inferred by the difference between Foxg1-ChR2 and Ntng1-ChR2, it would have been preferable to have specific data with selective stimulation of type 1a neurons.

We agree that complete genetic access to only the Ia population would have been the preferable approach, but we did not have an appropriate line when beginning these experiments. Because our results did not suggest a meaningful difference between the populations, we did not pursue further investigation once a line was available.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Besides the points mentioned in the main review:

Minor

(1) I really like the graphics and the immunohistological presentation.

(2) Lines 316-319 say that octopus cells lack things like back-propagating spikes and dendritic Ca spikes. How do you know this?

This statement was intended to be a summary of suggestions from the literature and lacked references and context as written. We have rewritten this section and clarified that our hypothesis was formed from data found in the literature (lines 334-337).

(3) Spectrograms of Figure 6A...where were these data obtained?

We recorded and visualized human-generated rhythmic tapping and high-frequency squeaking sounds using Audacity. The visualizations of rhythmic tapping and imitated vocalizations are meant to show two different types of multi-frequency stimuli we hypothesize would result in somatic summation within an octopus cell’s spike integration window, despite differences in timing. We rewrote the figure legend to explain more clearly what is shown and how it relates to the model in Figure 6.

(4) 'on-path' and 'off-path' seem like jargon that may not be clear to the average reader.

Thank you for pointing out our use of unapproachable jargon. We have replaced the term from the figure with “proximal” and “distal” inhibition. In the main text, we now describe on-path and off-path together as the effect of location of dendritic inhibition on somatically recorded EPSPs.

(5) The paper could benefit from a table of modeled values.

We have added specific details about the modelling in the text and clarified which modeled values were referenced from previous computational models and which were tuned to fit experimental data. Since most values were taken from a referenced publication, we did not add a table and instead point readers towards that source.

(6) Figure S4A-C what currents were delivered to the modeled cells?

The model cells were injected with a -0.8 nA DC current for 300 ms in current clamp mode. This information has been added to the figure legend.

(7) In that figure "scaling factors" scale exactly which channels?

Scaling factor is used to scale low-voltage activated K⁺ (ḡ_KLT), high threshold K⁺ (ḡ_KHT), fast transient K⁺ (ḡ_KA), hyperpolarization-activated cyclic nucleotide-gated HCN (ḡ_h) but not fast Na⁺ (ḡ_Na) and leak K⁺ (ḡ_leak). This information has been added to the text (lines 205-208 and 646-653).

(8) In performing and modeling Kv/HCN block, do you know how complete the level of the block is?

Since we cannot assess how complete the level of block is, we have changed the language in the text to clarify that we are reducing Kv and HCN channel conductance to the degree needed to increase resistance of the neuron (line 185).

(9) More on this Figure S4. It is hardly referred to in the text except to say that it supports that blocking the Kv/HCN channels will enhance the IPSP. Given how large the figure is, can you offer more of a conclusion than that? Also, in the synaptic model in that figure, the IPSCs are presumably happening in current-clamp conditions, and the reduction in amplitude of the IPSC (as opposed to the increase in IPSP) is due to hyperpolarization. Can you simply state that so readers can track what this figure is showing? Other similar things: what is a transfer impedance? How is it measured? What do we take from the analysis?

We have elaborated on our description of both Supp. Fig. 4 and Supp. Fig. 5 in the results section of the text (lines 203-238).

(10) Figure S5 also needs a better explanation. E.g., in C-D, what does 'average' mean? The gray is an SD of this average? You modeled a range of values...but which ones are physiological? To me, this is a key point.

We have elaborated on our description of both Supp. Fig. 4 and Supp. Fig. 5 in the results section of the text (lines 203-238).

Reviewer #2 (Recommendations For The Authors):

General:

The images and 3-D reconstructions are visually stunning, but they are not colorblind-friendly and in some cases, hard to distinguish. This shows up particularly in the green and blue colors used in Figure 1. Also, better representative images could be used for Figure 1B.

Thank you for pointing out that blue and green were difficult to distinguish in Figure 1H. We have outlined the green inhibitory puncta in this image to make them more distinguishable. We have also increased the resolution of the image in Figure 1B for better clarity. All other colors are selected from Wong, 2011 (PMID: 21850730; DOI: https://doi.org/10.1038/nmeth.1618).

Supplemental Figure 1D: The low-power view is good to have, but the CN is too small and the image appears a bit noisy. An inset showing the CN on a larger scale (higher resolution image?) would be more convincing. In this image, I see what appear to be cells in the DCN labeled, which calls into question the purity of the source of optogenetic synaptic activation. It is also difficult to tell whether there are other cells labeled in the VCN. Such inputs would still be minor, but it would be good to be very clear about the expression pattern.

To offer more information about the activity of the Ntng1^Cre line in other regions of the auditory system, we increased the resolution of the image included in Supp. Fig. 1D and have also included an additional image (Supp. Fig. 1E) of a coronal section of the cochlear nucleus complex with Ntng1-tdT labelling. This image provides additional context for the cells labeled in the DCN. The text in the figure legend has been changed to clarify that some cells in the DCN were labeled (lines 118-120).

We agree that in the Ntng1^Cre experiments, there is the possibility of minor contamination from excitatory cells that express ChR2 outside of the spiral ganglion. This is also true for our Foxg1^Cre and Foxg1^Flp experiments, because these lines label cortical cells in addition to cochlear cells. However, we do not observe direct descending inputs from the cortex into the PVCN, making contamination from other Foxg1^Cre-positive neurons unlikely. While non-cochlear inputs from the Ntng1^Cre line are possible, evidence from both lines gives us confidence that we are not capturing inputs to octopus cells outside the cochlea. Central axons from Type I spiral ganglion neurons have VGLUT1+ synaptic terminals. When comparing the overlap between VGLUT1+ terminals and Foxg1-tdT labelling, we see full coverage. That is, all VGLUT+ terminals on octopus cells are co-labelled by Foxg1^Cre-mediated expression of tdTomato. An example image is shown below. Here, an octopus cell soma is labeled with blue fluorescent Nissl stain and inputs to the cochlear nucleus complex are labeled with Foxg1^Cre-dependent tdTomato (Foxg1-tdT; magenta). We have also immunolabeled for VGLUT1 puncta in green. This eliminates the possibility that VGLUT+ cells from outside the cochlea and cortex are sources of excitation to octopus cells.

Author response image 4.

Further, we have looked at expression of Ntng1-tdT and Foxg1-EYFP together in the octopus cell area.  An example image is shown below. All Ntng1-tdT+ fibers (magenta) are also Foxg1-EYFP+ (green), suggesting that all Ntng1^Cre-targeted inputs to octopus cells are a part of the Foxg1^Cre-targeted input population, which are very likely to only be from the cochlea. We have expanded the results section to include information about the overlap in expression driven by the Ntng1^Cre and Foxg1^Flp lines.

Author response image 5.

Supplemental Figure 2 G: These are a bit hard to read. Perhaps use a different image, or provide a reference outline drawing telling us what is what.

We have used a different image with a Thy1-YFP labeled octopus cell for clarity.

In some places, the term "SGN" is used when referencing the axons and terminals within the CN, and without some context, this was occasionally confusing (SGN would seem to refer to the cell bodies). In some places in the text, it may be preferable to separate SGN, auditory nerve fibers (ANFs), and terminals, as entities for clarity.

In order to make the study accessible to a broad neuroscience audience, we refer to the neurons of the spiral ganglion and their central axon projections using one name. We understand why, for those well acquainted with the auditory periphery, condensing terminology may feel awkward. However, for those readers unfamiliar with the anatomy of the cochlea and auditory nerve, we feel that the use of “SGN central axon” makes it clear that the “auditory nerve fibers” come from neurons in the spiral ganglion. This is clarified in the first paragraph of the introduction (lines 29-31) and in the methods (line 533).

Specific: Numbers refer to the line numbers on the manuscript.

L29-31: Cochlear nucleus neurons are more general in their responses than this sentence indicates. While we can all agree that they are specialized to carry (or improve upon) the representation of these specific features of sound, they also respond more generally to sounds that might not have specific information in any of these domains. They are not silos of neural computation, and their outputs become mixed and "re-represented" well before they reach the auditory cortex. Octopus cells are no exception to this. I suggest striking most of the first paragraph, and instead using the first sentence to lead into the second paragraph, and putting the last sentence (of the current first paragraph) at the end of the second (now first) paragraph.

We agree with this assessment and have made major changes to the introduction in line with these suggestions.

L33-46: A number of points in this paragraph need references (exp. line 41).

We agree and have added references accordingly.

L43: Not sure what is meant by "fire at the onset of the sound, breaking it up into its frequency components"?

We changed this text as part of a major reworking of the introduction.

L47-66: Again more citations are needed (at the end of sentence at line 55, probably moving some of the citations from the next sentence up).

We agree and have added references accordingly.

L51: The consistent orientation of octopus cell dendrites across the ANFs has been claimed in the literature (as mentioned here), but there are some (perhaps problematic - plane of sectioning?) counterexamples from the older Golgi-stained images, and even amongst intracellularly stained cells (for example see Reccio-Spinoza and Rhode, 2020). This is important with regards to the broader hypothesis regarding traveling-wave compensation (e.g., McGinley et al; but also many others); if the cells are not all in the appropriate orientation then such compensation may be problematic. Likewise, the data from Lu et al., 2022, points towards a range of sensitivity to frequency-swept stimuli, some of which work in opposition to the traveling wave compensation hypothesis. It would seem that with the Thy1 mice, you have an opportunity to clarify the orientation. Figures 1A and 2A show a consistent dendritic orientation, assuming that these drawings are reconstructions of the cells as they were actually oriented in the tissue. Can you either comment on this or provide clearer evidence?

We are happy to offer more information about the appearances of octopus cells in our preparations. In our hands, sparsely labeled octopus cells in Thy1-YFP-H mice show consistent dendritic orientation when visualized in a 15 degree parasaggital plane, with the most diversity apparent in cells with somas located more dorsally in the octopus cell area. We hypothesize that this is due to the limited area through which the central projections of spiral ganglion neurons (i.e. ANFs) must pass through before they enter the dorsal cochlear nucleus and continue their tonotopic organization in that area.

A caveat to studies without physiological or genetic identification of octopus cells is the assumption that all neurons in the octopus cell area are octopus cells. We find, especially along the borders of the octopus cell area, that stellate cells can be seen amongst octopus cells. Because stellate cell dendrites are not oriented like octopus cell dendrites, any stellate cells misidentified as octopus cells would appear to have poorly-oriented dendrites. This may explain why some studies report this finding. In addition, it can be difficult to assess tonotopic organization because of the 3D trajectory of tightly bundled axons, which is not capturable by a single section plane. Although a parasaggital plane of sectioning captures the tonotopic axis in one part of the octopus cell area, that same plane may be perpendicular at the opposing end.

L67: canonical -> exceptional.

Thank you for the suggestion. We have made this change in the introduction.

L127: This paragraph was confusing on first reading. I don't think Supplemental Figure 1D shows the restricted pattern of expression very clearly. The "restricted to SGNs" might be better as "restricted to auditory nerve fibers" (except in the DCN, where there seem to be some scattered small cells?). A higher magnification image of the CN, but lower magnification than in panel E, would be helpful here.

To avoid confusion, we have re-written this paragraph (lines 117-127) and included a higher magnification image of the CN in a revised Supp. Fig. 1.

L168: Here, perhaps say ANFs instead of SGNs.

As above, we have decided to describe ANFs as SGN central axons to make the anatomy more accessible to people unfamiliar with cochlear anatomy.

L201-204: The IPSPs are surprisingly slow (Figures 5B, C), especially given the speed of the EPSPs/EPSCs in these cells. This is reminiscent of the asymmetry between EPSC and IPSC kinetics in bushy cells (Xie and Manis, 2014). The kinetics used in the model (3 ms; mentioned on line 624) however seem a bit arbitrary and no data is provided for the selection of that value. Were there any direct measurements of the IPSC kinetics (all of the traces in the paper are in the current clamp) that were used to justify this value?

The kinetics of the somatically-recorded IPSPs are subject to the effects of our pharmacological manipulations. EPSPs measured at the soma under control conditions are small amplitude and rapid. With pharmacological reduction of HCN and Kv channels, EPSPs are larger and slower (please see figure in response to a similar question posed by Reviewer #1). We expect that this change also occurs with the IPSP kinetics under pharmacological conditions. Our justification of kinetics has been expanded and justified in the methods section (lines 641-661).

L594: Technically, this is a -11 mV junction potential, but thanks for including the information.

We have corrected this in the text (line 618). Thank you for the close reading of all experimental and methodological details.

L595: The estimated power of the LED illumination at the focal plane should be measured and indicated here.

We measured the power of the LED illumination at the focal plane using a PM100D Compact Power and Energy Meter Console (Thorlabs), a S120C Photodiode Power Sensor (Thorlabs), and a 1000µm diameter Circular Precision Pinhole (Thorlabs). Light intensity at the focal plane ranged between 1.9 and 4.1mW/mm², corresponding to 6% and 10% intensity on the Colibri5 system. We have reported these measurements in the results section (Lines 621-622).

L609: One concern about the model is that the integration time of 25 microseconds is rather close to the relative shifts in latency. While I doubt it will make a difference (except in the number), it may be worth verifying (spot checks, at least) that running the model with a 5 or 10-microsecond step yields a similar pattern of latency shifts (e.g., Supplementary Figure 5, Figure 5).

Also, it is not clear what temperature the model was executed at (I would presume 35C); this needs to be given, and channel Q10's listed.

We realize that additional information is needed to fully understand the model and have added this to the results and the methods. The synaptic mechanism (.mod) files were obtained from Manis and Campagnola (2018) (PMID: 29331233; DOI: https://doi.org/10.1016/j.heares.2017.12.017). Q10 (3) and temperature (22°C) were also matched to parameters from Manis and Campagnola (2018). Because temperature is a critical factor for channel kinetics, we verified that our primary results remain consistent under conditions using a temperature of 35°C and a time step of 5µs, depicted below. Panel A illustrates the increase in IPSP as a function of glycine conductance under Kv+HCN block conditions at 35°C. As at 22°C, an increase in IPSP magnitude is absent in the control condition at 35°C. Panels B and C provide a direct comparison between the initial (i.e. 22°C) and suggested (i.e. 35°C) simulation conditions. Again we found that temperature does not have a major impact on the amplitude of IPSPs. Thus, results at 35°C do not change the conclusions we make from the model.

Author response image 6.

The nominal conductance densities should at least be provided in a table (supplemental, in addition to including them in the deposited code). The method for "optimization" of the conductance densities to match the experimental recordings needs to be described; the parameter space can be quite large in a model such as this. The McGinley reference needs a number.

We added a more thorough description of modeling parameters and justification of choices in the methods section of the text (lines 641-661). We have also added a reference number to the McGinley 2012 reference in the text.

I think this is required by the journal:

The model code, test results, and simulation results should be deposited in a public resource (Github would be preferable, but dryad, Zenodo, or Figshare could work), and the URL/doi for the resource provided in the manuscript. This includes the morphology swc/hoc file. The code should be in a form, and with a description, that readily allows an interested party with appropriate skills to download it and run it to generate the figures.

We will upload the code and all associated simulation files to the ModelDB repository upon publication.

eLife Assessment

In this manuscript, Abd El Hay and colleagues use an innovative behavioral assay and analysis method, together with standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons, to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. Compelling evidence is provided for a role of TRPM2 channels in warmth avoidance behavior, but it remains unclear whether this involves channel activity in the periphery or in the brain. In contrast, TRPV1 is clearly implicated at the cellular level in warmth detection. These findings are important because there is substantial ongoing discussion regarding the contribution of TRP channels to different aspects of thermo-sensation.

Reviewer #1 (Public review):

Summary:

The authors use an innovative behavior assay (chamber preference test) and standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. They find a profound effect of TRPM2 elimination in the behavioral assay, whereas the elimination of TRPV1 has the largest effect on the neuronal responses. These findings are very important, as there is substantial ongoing discussion in the field regarding the contribution of TRP channels to different aspects of thermosensation.

Strengths:

The chamber preference test is an important innovation compared to the standard two-plate test, as it depends on thermal information sampled from the entire skin, as opposed to only the plantar side of the paws. With this assay, and the detailed analysis, the authors provide strong supporting evidence for a role of TRPM2 in warmth avoidance. The conceptual framework using the Drift Diffusion Model provides a first glimpse of how this decision of a mouse to change between temperatures can be interpreted and may form the basis for further analysis of thermosensory behavior.

Weaknesses:

The authors juxtapose these behavioral data with calcium imaging data using isolated DRG neurons. As the authors acknowledge, it remains unclear whether the clear behavioral effect seen in the TRPM2 knockout animals is directly related to TRPM2 functioning as a warmth sensor in sensory neurons. The effects of the TRPM2 KO on the proportion of warmth sensing neurons are very subtle, and TRPM2 may also play a role in the behavioral assay through its expression in thermoregulatory processes in the brain. Future behavioral experiments on sensory-neuron specific TRPM2 knockout animals will be required to clarify this important point.

Reviewer #3 (Public review):

Summary and strengths:

In the manuscript, Abd El Hay et al investigate the role of thermally sensitive ion channels TRPM2 and TRPV1 in warm preference and their dynamic response features to thermal stimulation. They develop a novel thermal preference task, where both the floor and air temperature are controlled, and conclude that mice likely integrate floor with air temperature to form a thermal preference. They go on to use knockout mice and show that TRPM2-/- mice play a role in the avoidance of warmer temperatures. Using a new approach for culturing DRG neurons they show the involvement of both channels in warm responsiveness and dynamics. This is an interesting study with novel methods that generate important new information on the different roles of TRPV1 and TRPM2 on thermal behavior.

Comments on revisions:

Thanks to the authors for addressing all the points raised. They now include more details about the classifier, better place their work in context of the literature, corrected the FOVs, and explained the model a bit further. The new analysis in Figure 2 has thrown up some surprising results about cellular responses that seem to reduce the connection between the cellular and behavioral data and there are a few things to address because of this:

TRPM2 deficient responses: The differences in the proportion of TRPM2 deficient responders compared to WT are only observed at one amplitude (39C), and even at this amplitude the effect is subtle. Most surprisingly, TRPM2 deficient cells have an enhanced response to warm compared to WT mice to 33C, but the same response amplitude as WT at 36C and 39C. The authors discuss why this disconnect might be the case, but together with the lack of differences between WT and TRPM2 deficient mice in Fig 3, the data seem in good agreement with ref 7 that there is little effect of TRPM2 on DRG responses to warm in contrast to a larger effect of TRPV1. This doesn't take away from the fact there is a behavioral phenotype in the TRPM2 deficient mice, but the impact of TRPM2 on DRG cellular warm responses is weak and the authors should tone down or remove statements about the strength of TRPM2's impact throughout the manuscript, for example:<br /> "Trpv1 and Trpm2 knockouts have decreased proportions of WSNs."<br /> "this is the first cellular evidence for the involvement of TRPM2 on the response of DRG sensory neurons to warm-temperature stimuli"<br /> "we demonstrate that TRPV1 and TRPM2 channels contribute differently to temperature detection, supported by behavioural and cellular data"<br /> "TRPV1 and TRPM2 affect the abundance of WSNs, with TRPV1 mediating the rapid, dynamic response to warmth and TRPM2 affecting the population response of WSNs."<br /> "Lack of TRPV1 or TRPM2 led to a significant reduction in the proportion of WSNs, compared to wildtype cultures".

The new analysis also shows that the removal of TRPV1 leads to cellular responses with smaller responses at low stimulus levels but larger responses with longer latencies at higher stimulus levels. Authors should discuss this further and how it fits with the behavioral data.

Analysis clarification: authors state that TRPM2 deficient WSNs show "Their response to the second and third stimulus, however, are similar to wildtype WSNs, suggesting that tuning of the response magnitude to different warmth stimuli is degraded in Trpm2-/- animals." but is there a graded response in WT mice? It looks like there is in terms of the %responders but not in terms of response amplitude or AUC. Authors could show stats on the figure showing differences in response amplitude/AUC/responders% to different stimulus amplitudes within the WT group.

New discussion point: sex differences are "similar to what has been shown for an operant-based thermal choice assay (11,56)", but in their rebuttal, they mention that ref 11 did not report sex differences. 56 does. Check this.

The authors added in new text about the drift diffusion model in the results, however it's still not completely clear whether the "noise" is due to a perceptual deficit or some other underlying cause. Perhaps authors could discuss this further in the discussion.

Author response:

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

Public Reviews:  

Reviewer #1 (Public Review): 

Summary: 

The authors use an innovative behavior assay (chamber preference test) and standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. They find a profound effect of TRPM2 elimination in the behavioral assay, whereas elimination of TRPV1 has the largest effect on neuronal responses. These findings are of importance, as there is still substantial discussion in the field regarding the contribution of TRP channels to different aspects of thermosensation. 

Strengths: 

The chamber preference test is an important innovation compared to the standard two-plate test, as it depends on thermal information sampled from the entire skin, as opposed to only the plantar side of the paws. With this assay, and the detailed analysis, the authors provide strong supporting evidence for the role of TRPM2 in warmth avoidance. The conceptual framework using the Drift Diffusion Model provides a first glimpse of how this decision of a mouse to change between temperatures can be interpreted and may form the basis for further analysis of thermosensory behavior. 

Weaknesses: 

The authors juxtapose these behavioral data with calcium imaging data using isolated DRG neurons. Here, there are a few aspects that are less convincing. 

(1) The authors study warmth responses using DRG neurons after three days of culturing. They propose that these "more accurately reflect the functional properties and abundance of warm-responsive sensory neurons that are found in behaving animals." However, the only argument to support this notion is that the fraction of neurons responding to warmth is lower after three days of culture. This could have many reasons, including loss of specific subpopulations of neurons, or any other (artificial?) alterations to the neurons' transcriptome due to the culturing. The isolated DRGs are not selected in any way, so also include neurons innervating viscera not involved in thermosensation. If the authors wish to address actual changes in sensory nerves involved in warmth sensing in TRPM2 or TRPV1 KO mice without disturbing the response profile as a result of the isolation procedure, other approaches would be needed (e.g. skin-nerve recordings or in vivo DRG imaging).  

We agree that there could be several reasons as to why the responses of cultured DRGs are reduced compared to the acute/short-term cultures. It is possible ––and likely–– that transcriptional changes happen over the course of the culturing period. It is also possible that it is a mere coincidence that the 3-day cultures have a response profile more similar to the in vivo situation than the acute cultures. In the revised manuscript, we have therefore toned down the claim that the 3-day cultures mirror the native conditions more appropriately and included the sentence “However, whether 3-day cultures resemble native sensory neurons more closely than acute cultures in terms of their (transcriptional) identity is currently unknown.” (page 5). 

We now also included a section “Limitations of the study” and bring this point up there as well and acknolwedge that longer culturing periods may cause changes in the neurons and may result in a drift away from their native state. 

Nevertheless, our results clearly show that acute cultures have a response profile that is much more similar to damaged/”inflamed” neurons, irrespective of any comparison to the 3 daycultures. Therefore, we believe, it is helpful to include this data to make scientists aware that acute cultures are very different to non-inflamed native/in vivo DRG neurons that many researchers use in their experiments.

(2) The authors state that there is a reduction in warmth-sensitive DRG neurons in the TRPM2 knockout mice based on the data presented in Figure 2D. This is not convincing for the following reasons. First, the authors used t-tests (with FDR correction - yielding borderline significance) whereas three groups are compared here in three repetitive stimuli. This would require different statistics (e.g. ANOVA), and I am not convinced (based on a rapid assessment of the data) that such an analysis would yield any significant difference between WT and TRPM2 KO. Second, there seems to be a discrepancy between the plot and legend regarding the number of LOV analysed (21, 17, and 18 FOV according to the legend, compared to 18, 10, and 12 dots in the plot). Therefore, I would urge the authors to critically assess this part of the study and to reconsider whether the statement (and discussion) that "Trpm2 deletion reduces the proportion of warmth responders" should be maintained or abandoned. . 

Yes, we agree that the statistical tests indicated by the referee are more appropriate/robust for the data shown in Figures 1F, 2D, and 4G.

When we perform 2-way repeated measures ANOVA and subsequent multiple comparison test (with Dunnets correction) against Wildtype, for data shown in Fig. 2D, both the main effect (Genotype) and the interaction term (Stimulus x Genotype) are significant. The multiple comparison yields very similar result as in the current manuscript, with the difference that the TRPM2-KO data for the second stimulus (~36°C) is borderline significant (with a p-value of p=0.050).

Due to the possible dependence of the repeated temperature stimuli and the variability of each stimulus between FOVs (Fig. 2C), it is possible that a mixed-effect model that accounts for these effects is more appropriate. 

Similarly, for plots 1F and 4G, Genotype (either as main effect or as interaction with Time) is significant after a repeated measures two-way ANOVA. The multiple comparisons (with Bonferroni correction) only changed the results marginally at individual timepoints, without affecting the overall conclusions. The exception is Fig. 4G at 38°C, where the interaction of Time and Genotype is significant, but no individual timepoint-comparison is significant after Bonferroni correction.

The main difference between the results presented above and the ones presented in the manuscript is the choice of the multiple comparison correction. We originally opted for the falsediscovery rate (FDR) approach as it is less prone to Type II errors (false negatives) than other methods such as Sidaks or Bonferroni, particularly when correcting for a large number of tests.

However, we are mainly interested in whether the genotypes differ in their behavior in each temperature combination and the significant ANOVA tests for Fig. 1F and 4G support that point. The statistical test and comparison used in the original/previous version of the manuscript, comparing behavior at individual/distinct timepoints, are interesting, but less relevant (and potentially distracting), as we do not go into the details about the behavior at any given/distinct timepoint in the assay.

Therefore, and per suggestion of the reviewer, we have updated the statistics in the revised version of the manuscript. Also, we now report the correct number of FOVs in the legend. The statistical details are now found in the legends of the respective figures.

(3) It remains unclear whether the clear behavioral effect seen in the TRPM2 knockout animals is at all related to TRPM2 functioning as a warmth sensor in sensory neurons. As discussed above, the effects of the TRPM2 KO on the proportion of warmth-sensing neurons are at most very subtle, and the authors did not use any pharmacological tool (in contrast to the use of capsaicin to probe for TRPV1 in Figures S3 and S4) to support a direct involvement of TRPM2 in the neuronal warmth responses. Behavioral experiments on sensory-neuron-specific TRPM2 knockout animals will be required to clarify this important point

As mentioned above, we have toned down the correlation between the cellular and behavioral data. 

In the discussion we now clearly describe three possibilities as to why the Trpm2 knockout animals only show a subtle cellular thermal phenotype but a strong behavioral thermal preference phenotype: (i) permanent deletion of Trpm2 may result in developmental defects and/or compensatory mechanisms; (ii) The DRG population expressing Trpm2 may be more relevant for autonomic thermoregulation rather than behavioral responses to temperature; (iii) Trpm2 expression outside DRGs (possibly in the hypothalamic POA) may account for the altered thermal behavior. 

(4) The authors only use male mice, which is a significant limitation, especially considering known differences in warmth sensing between male and female animals and humans. The authors state "For this study, only male animals were used, as we aimed to compare our results with previous studies which exclusively used male animals (7, 8, 17, 43)." This statement is not correct: all four mentioned papers include behavioral data from both male and female mice! I recommend the authors to either include data from female mice or to clearly state that their study (in comparison with these other studies) only uses male mice.  

This is a valid point -- when our study started 7-8 years ago, we only used male mice (as did many other researchers) and this we would now do differently. We have now newly included a statement concerning this limitation in the “Limitations of this study” section of the manuscript. 

Nevertheless, in the studies by Tan et al. And Vandevauw et al. only male animals were used for the behavioral experiments. Yarmolinsky et al.  And Paricio-Montesinons et al. used both males and females while, as far as we can tell, only Paricio-Montesions et al. Reported that no difference was observed between the sexes. 

Wildtypes are all C57bl/6N from the provider Janvier. Generally, all lines are backcrossed to C57bl/6 mice and additionally inbreeding was altered every 4-6 generations by crossing to C57bl/6. Exactly how many times the Trp channel KOs have been backcrossed to C57bl/6 mice we cannot exactly state.

Reviewer #2 (Public Review): 

Summary: 

The authors of the study use a technically well-thought-out approach to dissect the question of how far TRPV1 and TRPM2 are involved in the perception of warm temperatures in mice. They supplement the experimental data with a drift-diffusion model. They find that TRPM2 is required to trigger the preference for 31{degree sign}C over warmer temperatures while TRPV1 increases the fidelity of afferent temperature information. A lack of either channel leads to a depletion of warm-sensing neurons and in the case of TRPV1 to a deficit in rapid responses to temperature changes. The study demonstrates that mouse phenotyping can only produce trustworthy results if the tools used to test them measure what we believe they are measuring. 

Strengths: 

The authors tackle a central question in physiology to which we have not yet found sufficient answers. They take a pragmatic approach by putting existing experimental methods to the test and refining them significantly. 

Weaknesses: 

It is difficult to find weaknesses. Not only the experimental methods but also the data analysis have been refined meticulously. There is no doubt that the authors achieved their aims and that the results support their conclusions. 

There will certainly be some lasting impact on the future use of DRG cultures with respect to (I) the incubation periods, (II) how these data need to be analyzed, and (III) the numbers of neurons to be looked at. 

As for the CPT assay, the future will have to show if mouse phenotyping results are more accurate with this technique. I'm more fond of full thermal gradient environments. However, behavioural phenotyping is still one of the most difficult fields in somatosensory research.  

We thank the referee and were happy to read that the referee finds our study valuable and insightful. 

Reviewer #3 (Public Review):  

Summary and strengths: 

In the manuscript, Abd El Hay et al investigate the role of thermally sensitive ion channels TRPM2 and TRPV1 in warm preference and their dynamic response features to thermal stimulation. They develop a novel thermal preference task, where both the floor and air temperature are controlled, and conclude that mice likely integrate floor with air temperature to form a thermal preference. They go on to use knockout mice and show that TRPM2-/- mice play a role in the avoidance of warmer temperatures. Using a new approach for culturing DRG neurons they show the involvement of both channels in warm responsiveness and dynamics. This is an interesting study with novel methods that generate important new information on the different roles of TRPV1 and TRPM2 on thermal behavior. 

Open questions and weaknesses: 

(1) Differences in the response features of cells expressing TRPM2 and TRPV1 are central and interesting findings but need further validation (Figures 3 and 4). To show differences in the dynamics and the amplitude of responses across different lines and stimulus amplitudes more clearly, the authors should show the grand average population calcium response from all responsive neurons with error bars for all 3 groups for the different amplitudes of stimuli (as has been presented for the thermal stimuli traces). The authors should also provide a population analysis of the amplitude of the responses in all groups to all stimulus amplitudes. Prior work suggests that thermal detection is supported by an enhancement or suppression of the ongoing activity of sensory fibers innervating the skin. The authors should present any data on cells with ongoing activity. 

We have now included grand average population analysis of the different groups in the revised version, this is found in Figure 2E and F. Based on the referee’s suggestion and the new analysis, we now can report a (subtle) cellular phenotype observed in DRG cultures of Trpm2 deficient animals: when averaging all warmth responses, the new analysis suggests that Trpm2-deficient cultures lack modulation of the response magnitude across the three increasing consecutive warmth stimuli (33°C, 36°C and 39°C).

Concerning the point about ongoing activity: We are not sure if it is possible in neuronal cultures to faithfully recapitulate ongoing activity. Ongoing activity has been mostly recorded in skinnerve preparations (or in older studies in other types of nerve recordings) and there are only very few studies that show ongoing activity in cultured neurons and in those instances the ongoing activity only starts in sensory neuron cultures when cultured for even longer time periods than 3 days (Ref.: doi: 10.1152/jn.00158.2018). We have very few cells that show some spontaneous activity, but these are too few to draw any conclusions. In any case, nerve fibers might be necessary to drive ongoing activity which are absent from our cultures.

(2) The authors should better place their findings in context with the literature and highlight the novelty of their findings. The introduction builds a story of a 'disconnect' or 'contradictory' findings about the role of TRPV1 and TRPM2 in warm detection. While there are some disparate findings in the literature, Tan and McNaughton (2016) show a role for TRPM2 in the avoidance of warmth in a similar task, Paricio et al. (2020) show a significant reduction in warm perception in TRPM2 and TRPV1 knock out lines and Yarmolinksy et al. (2016) show a reduction in warm perception with TRPV1 inactivation. All these papers are therefore in agreement with the authors finding of a role for these channels in warm behavior. The authors should change their introduction and discussion to more correctly discuss the findings of these studies and to better pinpoint the novelty of their own work.  

Paricio-Montesinos et al. argue that TRPM8 is crucial for the detection of warmth, as TRPM8KO animals are incapable of learning the operant task. TRPM2-KO animals and, to a smaller extent TRPV1-KO animals, have reduced sensitivity in the task, but are still capable of learning/performing the task. However, in our chamber preference assay this is reversed: TRPM2-KO animals lose the ability to differentiate warm temperatures while TRPM8 appears to play no major role. A commonality between the two studies is that while TRPV1 affects the detection of warm temperatures in the different assays, this ion channel appears not to be crucial. 

Similarly, Yarmolinsky et al. show that Trpv1-inactivation only increases the error rate in their operant assay (from ~10% to ~30%), without testing TRPM2. And Tan et al. show the importance of TRPM2 in the preference task, without testing for TRPV1. 

More generally, the choice of the assay, being either an operant task (Paricio-Montesinos et al. and Yarmolinsky et al.) or a preference assay without training of the mice (Tan et al. and our data here), might be important and different TRP receptors may be relevant for different types of temperature assays, which we have now included at the end of the discussion section in the revised manuscript. While our results generally agree with the previous studies, they add a different perspective on the analysis of the behavior (with correlation to cellular data). We now edited the manuscript to highlight the advances more clearly. 

Nevertheless, we believe that a discrepancy between cellular and behavioral data in the former studies exists and we kept this in the introduction. We hope that our data and suggestions of more nuanced analysis of cellular and behavioral responses, in particular also differences in their kinetics, may be helping to guide future studies.  

(3) The responses of 60 randomly selected cells are shown in Figure 2B. But, looking at the TRPM2-/- data, warm responses appear more obvious than in WTs and the weaker responders of the WT group appear weaker than the equivalent group in the TRPV1-/- and TRPM2-/- data. This does not necessarily invalidate the results, but it may suggest a problem in the data selection. Because the correct classification of warm-sensitive neurons is central to this part of the study more validation of the classifier should be presented. For example, the authors could state if they trained the classifier using equal amounts of cells, show some randomly selected cells that are warm-insensitive for all genotypes, and show the population average responses of warm-insensitive neurons.  

The classifier was trained on a balanced dataset of 1000 (500 responders and 500 nonresponders), manually labelled traces across all 5 temperature stimuli. The prediction accuracy was 98%. We have now described more clearly how the classifier was trained (See Materials and Methods) and include examples of responders and non-responders, the population averages of each class as well as a confusion matrix of the classification in the revised manuscript (Suppl. Figure 4A and B).

(4) The interpretation of the main behavioral results and justification of the last figure is presented as the result of changes in sensing but differences in this behavior could be due to many factors and this needs clarification and discussion. (i) The authors mention that 'crucially temperature perception is not static' and suggest that there are fluctuating changes in perception over time and conclude that their modelling approach helps show changes in temperature detection. They imply that temperature perceptual threshold changes over time, but the mouse could just as easily have had exactly the same threshold throughout the task but their motivation (or some other cognitive variable) might vary causing them to change chamber. The authors should correct this. (ii) Likewise, from their fascinating and high-profile prior work the authors suggest a model of internal temperature sensing whereby TRPM2 expression in the hypothalamus acts as an internal sensory of body temperature. Given this, and the slow time course of the behavior in chambers with different ambient temperatures, couldn't the reason for the behavioral differences be due to central changes in hypothalamic processing rather than detection by skin temperature? If TRPM2-/- were selectively ablated from the skin or the hypothalamus (these experiments are not necessary for this paper) it might be possible to conclude whether sensation or body temperature is more likely the root cause of these effects but, without further experiments it is tough to conclude either way. (iii) Because the ambient temperature is controlled in this behavior, another hypothesis is that warm avoidance could be due to negative valence associated with breathing warm air, i.e. a result of sensation within the body in internal pathways, rather than sensing from the external skin. Overall, the authors should tone down conclusions about sensation and present a more detailed discussion of these points.  

We are sorry that the statement including the phrase “crucially temperature perception is not static” was ambiguous; We have now deleted this statement and instead included different possibilities as to why mice may switch from one chamber to the other stochastically. 

As the referee mentioned, it is possible that some other variable (motivation etc.) makes the mouse change the chamber; Nevertheless, we hypothesize that this variable (whatever it might be) is still modulated by temperature (at least this would be the likeliest explanation that we see).

As for the aspect of internal/hypothalamic temperature sensing and its dependence on Trpm2: we have included this possibility in the discussion in the manuscript. 

As for the point of negative valence mediated by breathing in warm air: yes, presumably this could also be possible. The aspect of valence is in interesting aspect by itself: would the mice be rather repelled from the (uncomfortable) hot plate or more attracted to the (more comfortable) thermoneutral plate, or both? Something to elucidate in a different study.

(5) It is an excellent idea to present a more in-depth analysis of the behavioral data collected during the preference task, beyond 'the mouse is on one side or the other'. However, the drift-diffusion approach is complex to interpret from the text in the results and the figures. The results text is not completely clear on which behavioral parameters are analyzed and terms like drift, noise, estimate, and evidence are not clearly defined. Currently, this section of the paper slightly confuses and takes the paper away from the central findings about dynamics and behavioral differences. It seems like they could come to similar conclusions with simpler analysis and simpler figures. 

We have now reassessed the description of the drift diffusion model and explain it more clearly, this can be found on page 5 – 8. We have considered whether it will be better to introduce the drift diffusion model at the beginning of the study, subsequent to Figure 1 but we believe this to better suited at the end, because, indeed, the cellular results (and differences in kinetic response parameters observed in DRG cultures of Trpv1 KO mice) prompted us to assess the behavior in this way. Thus, the order of experiments presented here, represents also more the natural path the study took. 

(6) In Figure 2D the % of warm-sensitive neurons are shown for each genotype. Each data point is a field of view, however, reading the figure legend there appear to be more FOVs than data points (eg 10 data points for the TRPV1-/- but 17 FOVs). The authors should check this. 

We have checked and corrected the number of FOVs mentioned in the legend, and the number shown in the Figure 2D and its legend are now in agreement. 

(7) Can the authors comment on why animals with over-expression of TRPV1 spend more time in the warmest chamber to start with at 38C and not at 34C?  

This is an interesting observation that we did not consider before. A closer look at Figure 4H reveals that the majority of the TRPV1-OX animals, have a proportionally long first visit to the 38°C room. We can only speculate why this is the case. We cannot rule out that this a technical shortcoming of the assay and how we conduced it – but we did not observe this for the wildtype mice, thus it is rather unlikely a technical problem. It is possible that this is a type of “freezing-” (or “startle-“) behavior when the animals first encounter the 38°C temperature. Freezing behaviors in mice can be observed when sudden/threatening stimuli are applied. It is possible that, in the TRPV1-overexpressing animals, the initial encounter with 38°C leads to activation of a larger proportion of cells (compared to WT controls), possibly signaling a “threatening” stimulus, and thus leading to this startle effect. However, such a claim would require additional experiments to test such a hypothesis more rigorously.

eLife Assessment

This study presents valuable evidence concerning the potential for naturalistic movie-viewing fMRI experiments to reveal some features that are correlated with the functional and topographical organization of the developing visual system in awake infants and toddlers. The data are compelling given the difficulty of studying this population, the methodology is original and validated, and the evidence supporting the conclusions is convincing and in line with prior research using resting-state and awake task-based fMRI. This study will be of interest to cognitive neuroscientists and developmental psychologists, and in particular those interested in using fMRI to investigate brain organisation in pediatric and clinical populations with limited tolerance to fMRI.

Reviewer #2 (Public review):

Summary:

This manuscript reports analyses of fMRI data from infants and toddlers watching naturalistic movies. Visual areas in the infant brain show distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. The pattern of activity in visual regions contains some features predicted by the regions' retinotopic responses. The revised version of the manuscript provides additional validation of the methodology, and clarifies the claims. As a result, the data provide clear support for the claims.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. Using these data position the authors show that activity evoked by movies, in infants' visual areas, is correlated with the regions' retinopic response. The revised manuscript validates this methodology, using adult data. The revised manuscript also shows that an infant's movie watching data is not sufficient or optimal to predict their visual areas' retinotopic responses; anatomical alignment with a group of previous participants provides more accurate prediction of a new participant's retinotopic response.

Weaknesses:

A key step in the analysis of the movie-watching data is the selection of independent components of the movie evoked response that resemble retinotopic spatial patterns. While the trained researcher was unlikely to be biased by this infant's own retinotopy, he/she was actively looking for ICs that resemble average patterns of retinotopic response. To show that these ICs didn't arise by chance (i.e. in noise), the authors proposed an additional analysis in the revised manuscript, by misaligning the functional and anatomical data for a subset of participants. This only partially confirms the reliability of the original components, since when the (new) coder tried to be conservative to avoid false components, he/she identified just over half of the 'true' components (13 vs 22 estimated over the group of 6 infants).

Author response:

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

eLife Assessment

This study presents valuable findings on the potential of short-movie viewing fMRI protocol to explore the functional and topographical organization of the visual system in awake infants and toddlers. Although the data are compelling given the difficulty of studying this population, the evidence presented is incomplete and would be strengthened by additional analyses to support the authors' claims. This study will be of interest to cognitive neuroscientists and developmental psychologists, especially those interested in using fMRI to investigate brain organisation in pediatric and clinical populations with limited fMRI tolerance.

We are grateful for the thorough and thoughtful reviews. We have provided point-bypoint responses to the reviewers’ comments, but first, we summarize the major revisions here. We believe these revisions have substantially improved the clarity of the writing and impact of the results.

Regarding the framing of the paper, we have made the following major changes in response to the reviews:

(1) We have clarified that our goal in this paper was to show that movie data contains topographic, fine-grained details of the infant visual cortex. In the revision, we now state clearly that our results should not be taken as evidence that movies could replace retinotopy and have reworded parts of the manuscript that could mislead the reader in this regard.

(2) We have added extensive details to the (admittedly) complex methods to make them more approachable. An example of this change is that we have reorganized the figure explaining the Shared Response Modelling methods to divide the analytic steps more clearly.

(3) We have clarified the intermediate products contributing to the results by adding 6 supplementary figures that show the gradients for each IC or SRM movie and each infant participant.

In response to the reviews, we have conducted several major analyses to support our findings further:

(1) To verify that our analyses can identify fine-grained organization, we have manually traced and labeled adult data, and then performed the same analyses on them. The results from this additional dataset validate that these analyses can recover fine-grained organization of the visual cortex from movie data.

(2) To further explore how visual maps derived from movies compare to alternative methods, we performed an anatomical alignment control analysis. We show that high-quality maps can be predicted from other participants using anatomical alignment.

(3) To test the contribution of motion to the homotopy analyses, we regressed out the motion effects in these analyses. We found qualitatively similar results to our main analyses, suggesting motion did not play a substantial role.

(4) To test the contribution of data quantity to the homotopy analyses, we correlated the amount of movie data collected from each participant with the homotopy results. We did not find a relationship between data quantity and the homotopy results. 

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Ellis et al. investigated the functional and topographical organization of the visual cortex in infants and toddlers, as evidenced by movie-viewing data. They build directly on prior research that revealed topographic maps in infants who completed a retinotopy task, claiming that even a limited amount of rich, naturalistic movie-viewing data is sufficient to reveal this organization, within and across participants. Generating this evidence required methodological innovations to acquire high-quality fMRI data from awake infants (which have been described by this group, and elsewhere) and analytical creativity. The authors provide evidence for structured functional responses in infant visual cortex at multiple levels of analyses; homotopic brain regions (defined based on a retinotopy task) responded more similarly to one another than to other brain regions in visual cortex during movie-viewing; ICA applied to movie-viewing data revealed components that were identifiable as spatial frequency, and to a lesser degree, meridian maps, and shared response modeling analyses suggested that visual cortex responses were similar across infants/toddlers, as well as across infants/toddlers and adults. These results are suggestive of fairly mature functional response profiles in the visual cortex in infants/toddlers and highlight the potential of movie-viewing data for studying finer-grained aspects of functional brain responses, but further evidence is necessary to support their claims and the study motivation needs refining, in light of prior research.

Strengths:

- This study links the authors' prior evidence for retinotopic organization of visual cortex in human infants (Ellis et al., 2021) and research by others using movie-viewing fMRI experiments with adults to reveal retinotopic organization (Knapen, 2021).

- Awake infant fMRI data are rare, time-consuming, and expensive to collect; they are therefore of high value to the community. The raw and preprocessed fMRI and anatomical data analyzed will be made publicly available.

We are grateful to the reviewer for their clear and thoughtful description of the strengths of the paper, as well as their helpful outlining of areas we could improve.

Weaknesses:

- The Methods are at times difficult to understand and in some cases seem inappropriate for the conclusions drawn. For example, I believe that the movie-defined ICA components were validated using independent data from the retinotopy task, but this was a point of confusion among reviewers. 

We acknowledge the complexity of the methods and wish to clarify them as best as possible for the reviewers and the readers. We have extensively revised the methods and results sections to help avoid potential misunderstandings. For instance, we have revamped the figure and caption describing the SRM pipeline (Figure 5).

To answer the stated confusion directly, the ICA components were derived from the movie data and validated on the (completely independent) retinotopy data. There were no additional tasks. The following text in the paper explains this point:

“To assess the selected component maps, we correlated the gradients (described above) of the task-evoked and component maps. This test uses independent data: the components were defined based on movie data and validated against task-evoked retinotopic maps.” Pg. 11

In either case: more analyses should be done to support the conclusion that the components identified from the movie reproduce retinotopic maps (for example, by comparing the performance of movie-viewing maps to available alternatives (anatomical ROIs, group-defined ROIs). 

Before addressing this suggestion, we want to restate our conclusions: features of the retinotopic organization of infant visual cortex could be predicted from movie data. We did not conclude that movie data could ‘reproduce’ retinotopic maps in the sense that they would be a replacement. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously[23] found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses[27], here we find that functional alignment is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

As per the reviewer’s suggestion and alluded to in the paragraph above, we have created anatomically aligned visual maps, providing an analogous test to the betweenparticipant analyses like SRM. We find that these maps are highly similar to the ground truth. We describe this result in a new section of the results:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment > functional alignment: ∆_{Fisher Z} M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Also, the ROIs used for the homotopy analyses were defined based on the retinotopic task rather than based on movie-viewing data alone - leaving it unclear whether movie-viewing data alone can be used to recover functionally distinct regions within the visual cortex.

We agree with the reviewer that our approach does not test whether movie-viewing data alone can be used to recover functionally distinct regions. The goal of the homotopy analyses was to identify whether there was functional differentiation of visual areas in the infant brain while they watch movies. This was a novel question that provides positive evidence that these regions are functionally distinct. In subsequent analyses, we show that when these areas are defined anatomically, rather than functionally, they also show differentiated function (e.g., Figure 2). Nonetheless, our intention was not to use the homotopy analyses to define the regions. We have added text to clarify the goal and novelty of this analysis.

“Although these analyses cannot define visual maps, they test whether visual areas have different functional signatures.” Pg. 6

Additionally, even if the goal were to define areas based on homotopy, we believe the power of that analysis would be questionable. We would need to use a large amount of the movie data to define the areas, leaving a low-powered dataset to test whether their function is differentiated by these movie-based areas.

- The authors previously reported on retinotopic organization of the visual cortex in human infants (Ellis et al., 2021) and suggest that the feasibility of using movie-viewing experiments to recover these topographic maps is still in question. They point out that movies may not fully sample the stimulus parameters necessary for revealing topographic maps/areas in the visual cortex, or the time-resolution constraints of fMRI might limit the use of movie stimuli, or the rich, uncontrolled nature of movies might make them inferior to stimuli that are designed for retinotopic mapping, or might lead to variable attention between participants that makes measuring the structure of visual responses across individuals challenging. This motivation doesn't sufficiently highlight the importance or value of testing this question in infants. Further, it's unclear if/how this motivation takes into account prior research using movie-viewing fMRI experiments to reveal retinotopic organization in adults (e.g., Knapen, 2021). Given the evidence for retinotopic organization in infants and evidence for the use of movie-viewing experiments in adults, an alternative framing of the novel contribution of this study is that it tests whether retinotopic organization is measurable using a limited amount of movie-viewing data (i.e., a methodological stress test). The study motivation and discussion could be strengthened by more attention to relevant work with adults and/or more explanation of the importance of testing this question in infants (is the reason to test this question in infants purely methodological - i.e., as a way to negate the need for retinotopic tasks in subsequent research, given the time constraints of scanning human infants?).

We are grateful to the reviewer for giving us the opportunity to clarify the innovations of this research. We believe that this research contributes to our understanding of how infants process dynamic stimuli, demonstrates the viability and utility of movie experiments in infants, and highlights the potential for new movie-based analyses (e.g., SRM). We have now consolidated these motivations in the introduction to more clearly motivate this work:

“The primary goal of the current study is to investigate whether movie-watching data recapitulates the organization of visual cortex. Movies drive strong and naturalistic responses in sensory regions while minimizing task demands[12, 13, 24] and thus are a proxy for typical experience. In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion[25–27]. Movies have been useful in awake infant fMRI for studying event segmentation[28], functional alignment[29], and brain networks[30]. However, this past work did not address the granularity and specificity of cortical organization that movies evoke. For example, movies evoke similar activity in infants in anatomically aligned visual areas[28], but it remains unclear whether responses to movie content differ between visual areas (e.g., is there more similarity of function within visual areas than between31). Moreover, it is unknown whether structure within visual areas, namely visual maps, contributes substantially to visual evoked activity. Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity – rather than anatomy – and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses[27, 32–34].” Pg. 3-4

Furthermore, the introduction culminates in the following statement on what the analyses will tell us about the nature of movie-driven activity in infants:

“These three analyses assess key indicators of the mature visual system: functional specialization between areas, organization within areas, and consistency between individuals.” Pg. 5

Furthermore, in the discussion we revisit these motivations and elaborate on them further:

[Regarding homotopy:] “This suggests that visual areas are functionally differentiated in infancy and that this function is shared across hemispheres[31].” Pg. 19

[Regarding ICA:] “This means that the retinotopic organization of the infant brain accounts for a detectable amount of variance in visual activity, otherwise components resembling these maps would not be discoverable.” Pg. 19–20

[Regarding SRM:] “This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45].” Pg. 21

Additionally, we have expanded our discussion of relevant work that uses similar methods such as the excellent research from Knapen (2021) and others:

“In adults, movies and resting-state data have been used to characterize the visual cortex in a data-driven fashion[25-27].” Pg. 4

“We next explored whether movies can reveal fine-grained organization within visual areas by using independent components analysis (ICA) to propose visual maps in individual infant brains[25,26,35,42,43].” Pg. 9

Reviewer #2 (Public Review):

Summary:

This manuscript shows evidence from a dataset with awake movie-watching in infants, that the infant brain contains areas with distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. However, substantial new analyses would be required to support the novel claim that movie-watching data in infants can be used to identify retinotopic areas or to capture within-area functional organization.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. These data position the authors to test their novel claim, that movie-watching data in infants can be used to identify retinotopic areas.

Weaknesses:

To claim that movie-watching data can identify retinotopic regions, the authors should provide evidence for two claims:

- Retinotopic areas defined based only on movie-watching data, predict retinotopic responses in independent retinotopy-task-driven data.

- Defining retinotopic areas based on the infant's own movie-watching response is more accurate than alternative approaches that don't require any movie-watching data, like anatomical parcellations or shared response activation from independent groups of participants.

We thank the reviewer for their comments. Before addressing their suggestions, we wish to clarify that we do not claim that movie data can be used to identify retinotopic areas, but instead that movie data captures components of the within and between visual area organization as defined by retinotopic mapping. We recognize that this was not clear in our original manuscript and have clarified this point throughout, including in this section of the discussion:

“To be clear, we are not suggesting that movies work well enough to replace a retinotopy task when accurate maps are needed. For instance, even though ICA found components that were highly correlated with the spatial frequency map, we also selected some components that turned out to have lower correlations. Without knowing the ground truth from a retinotopy task, there would be no way to weed these out. Additionally, anatomical alignment (i.e., averaging the maps from other participants and anatomically aligning them to a held-out participant) resulted in maps that were highly similar to the ground truth. Indeed, we previously[23] found that adult-defined visual areas were moderately similar to infants. While functional alignment with adults can outperform anatomical alignment methods in similar analyses[27], here we find that functional alignment with infants is inferior to anatomical alignment. Thus, if the goal is to define visual areas in an infant that lacks task-based retinotopy, anatomical alignment of other participants’ retinotopic maps is superior to using movie-based analyses, at least as we tested it.” Pg. 21

In response to the reviewer’s suggestion, we compare the maps identified by SRM to the averaged, anatomically aligned maps from infants. We find that these maps are highly similar to the task-based ground truth and we describe this result in a new section:

“We performed an anatomical alignment analog of the functional alignment (SRM) approach. This analysis serves as a benchmark for predicting visual maps using taskbased data, rather than movie data, from other participants. For each infant participant, we aggregated all other infant or adult participants as a reference. The retinotopic maps from these reference participants were anatomically aligned to the standard surface template, and then averaged. These averages served as predictions of the maps in the test participant, akin to SRM, and were analyzed equivalently (i.e., correlating the gradients in the predicted map with the gradients in the task-based map). These correlations (Table S4) are significantly higher than for functional alignment (using infants to predict spatial frequency, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.44, CI=[0.32–0.58], p<.001; using infants to predict meridians, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.61, CI=[0.47–0.74], p<.001; using adults to predict spatial frequency, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.31, CI=[0.21–0.42], p<.001; using adults to predict meridians, anatomical alignment < functional alignment: ∆_{Fisher Z} M=0.49, CI=[0.39–0.60], p<.001). This suggests that even if SRM shows that movies can be used to produce retinotopic maps that are significantly similar to a participant, these maps are not as good as those that can be produced by anatomical alignment of the maps from other participants without any movie data.” Pg. 16–17

Note that we do not compare the anatomically aligned maps with the ICA maps statistically. This is because these analyses are not comparable: ICA is run withinparticipant whereas anatomical alignment is necessarily between-participant — either infant or adults. Nonetheless, an interested reader can refer to the Table where we report the results of anatomical alignment and see that anatomical alignment outperforms ICA in terms of the correlation between the predicted and task-based maps.

Both of these analyses are possible, using the (valuable!) data that these authors have collected, but these are not the analyses that the authors have done so far. Instead, the authors report the inverse of (1): regions identified by the retinotopy task can be used to predict responses in the movies. The authors report one part of (2), shared responses from other participants can be used to predict individual infants' responses in the movies, but they do not test whether movie data from the same individual infant can be used to make better predictions of the retinotopy task data, than the shared response maps.

So to be clear, to support the claims of this paper, I recommend that the authors use the retinotopic task responses in each individual infant as the independent "Test" data, and compare the accuracy in predicting those responses, based on:

-  The same infant's movie-watching data, analysed with MELODIC, when blind experimenters select components for the SF and meridian boundaries with no access to the ground-truth retinotopy data.

-  Anatomical parcellations in the same infant.

-  Shared response maps from groups of other infants or adults.

-  (If possible, ICA of resting state data, in the same infant, or from independent groups of infants).

Or, possibly, combinations of these techniques.

If the infant's own movie-watching data leads to improved predictions of the infant's retinotopic task-driven response, relative to these existing alternatives that don't require movie-watching data from the same infant, then the authors' main claim will be supported.

These are excellent suggestions for additional analyses to test the suitability for moviebased maps to replace task-based maps. We hope it is now clear that it was never our intention to claim that movie-based data could replace task-based methods. We want to emphasize that the discoveries made in this paper — that movies evoke fine-grained organization in infant visual cortex — do not rely on movie-based maps being better than alternative methods for producing maps, such as the newly added anatomical alignment.

The proposed analysis above solves a critical problem with the analyses presented in the current manuscript: the data used to generate maps is identical to the data used to validate those maps. For the task-evoked maps, the same data are used to draw the lines along gradients and then test for gradient organization. For the component maps, the maps are manually selected to show the clearest gradients among many noisy options, and then the same data are tested for gradient organization. This is a double-dipping error. To fix this problem, the data must be split into independent train and test subsets.

We appreciate the reviewer’s concern; however, we believe it is a result of a miscommunication in our analytic strategy. We have now provided more details on the analyses to clarify how double-dipping was avoided. 

To summarize, a retinotopy task produced visual maps that were used to trace both area boundaries and gradients across the areas. These data were then fixed and unchanged, and we make no claims about the nature of these maps in this paper, other than to treat them as the ground truth to be used as a benchmark in our analyses. The movie data, which are collected independently from the same infant in the session, used the boundaries from the retinotopy task (in the case of homotopy) or were compared with the maps from the retinotopy task (in the case of ICA and SRM). In other words, the statement that “the data used to generate maps is identical to the data used to validate those maps” is incorrect because we generated the maps with a retinotopy task and validated the maps with the movie data. This means no double dipping occurred.

Perhaps a cause of the reviewer’s interpretation is that the gradients used in the analysis are not clearly described. We now provide this additional description:  “Using the same manually traced lines from the retinotopy task, we measured the intensity gradients in each component from the movie-watching data. We can then use the gradients of intensity in the retinotopy task-defined maps as a benchmark for comparison with the ICA-derived maps.” Pg. 10

Regarding the SRM analyses, we take great pains to avoid the possibility of data contamination. To emphasize how independent the SRM analysis is, the prediction of the retinotopic map from the test participant does not use their retinotopy data at all; in fact, the predicted maps could be made before that participant’s retinotopy data were ever collected. To make this prediction for a test participant, we need to learn the inversion of the SRM, but this only uses the movie data of the test participant. Hence, there is no double-dipping in the SRM analyses. We have elaborated on this point in the revision, and we remade the figure and its caption to clarify this point:

We also have updated the description of these results to emphasize how double-dipping was avoided:

“We then mapped the held-out participant's movie data into the learned shared space without changing the shared space (Figure 5c). In other words, the shared response model was learned and frozen before the held-out participant’s data was considered.

This approach has been used and validated in prior SRM studies[45].” Pg. 14

The reviewer suggests that manually choosing components from ICA is double-dipping. Although the reviewer is correct that the manual selection of components in ICA means that the components chosen ought to be good candidates, we are testing whether those choices were good by evaluating those components against the task-based maps that were not used for the ICA. Our statistical analyses evaluate whether the components chosen were better than the components that would have been chosen by random chance. Critically: all decisions about selecting the components happen before the components are compared to the retinotopic maps. Hence there is no double-dipping in the selection of components, as the choice of candidate ICA maps is not informed by the ground-truth retinotopic maps. We now clarify what the goal of this process is in the results:

“Success in this process requires that 1) retinotopic organization accounts for sufficient variance in visual activity to be identified by ICA and 2) experimenters can accurately identify these components.” Pg. 10

The reviewer also alludes to a concern that the researcher selecting the maps was not blind to the ground-truth retinotopic maps from participants and this could have influenced the results. In such a scenario, the researcher could have selected components that have the gradients of activity in the places that the infant has as ground truth. The researcher who made the selection of components (CTE) is one of the researchers who originally traced the areas in the participants approximately a year prior to the identification of ICs. The researcher selecting the components didn’t use the ground-truth retinotopic maps as reference, nor did they pay attention to the participant IDs when sorting the IC components. Indeed, they weren’t trying to find participant specific maps per se, but rather aimed to find good candidate retinotopic maps in general. In the case of the newly added adult analyses, the ICs were selected before the retinotopic mapping was reviewed or traced; hence, no knowledge about the participant-specific ground truth could have influenced the selection of ICs. Even with this process from adults, we find results of comparable strength as we found in infants, as shown below. Nonetheless, there is a possibility that this researcher’s previous experience of tracing the infant maps could have influenced their choice of components at the participant-specific level. If so, it was a small effect since the components the researcher selected were far from the best possible options (i.e., rankings of the selected components averaged in the 64th percentile for spatial frequency maps and the 68th percentile for meridian maps). We believe all reasonable steps were taken to mitigate bias in the selection of ICs.

Reviewer #3 (Public Review):

The manuscript reports data collected in awake toddlers recording BOLD while watching videos. The authors analyse the BOLD time series using two different statistical approaches, both very complex but do not require any a priori determination of the movie features or contents to be associated with regressors. The two main messages are that 1) toddlers have occipital visual areas very similar to adults, given that an SRM model derived from adult BOLD is consistent with the infant brains as well; 2) the retinotopic organization and the spatial frequency selectivity of the occipital maps derived by applying correlation analysis are consistent with the maps obtained by standard and conventional mapping.

Clearly, the data are important, and the author has achieved important and original results. However, the manuscript is totally unclear and very difficult to follow; the figures are not informative; the reader needs to trust the authors because no data to verify the output of the statistical analysis are presented (localization maps with proper statistics) nor so any validation of the statistical analysis provided. Indeed what I think that manuscript means, or better what I understood, may be very far from what the authors want to present, given how obscure the methods and the result presentation are.

In the present form, this reviewer considers that the manuscript needs to be totally rewritten, the results presented each technique with appropriate validation or comparison that the reader can evaluate.

We are grateful to the reviewer for the chance to improve the paper. We have broken their review into three parts: clarification of the methods, validation of the analyses, and enhancing the visualization.

Clarification of the methods

We acknowledge that the methods we employed are complex and uncommon in many fields of neuroimaging. That said, numerous papers have conducted these analyses on adults (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017) and non-human primates (Arcaro & Livingstone, 2017; Moeller et al., 2009). We have redoubled our efforts in the revision to make the methods as clear as possible, expanding on the original text and providing intuitions where possible. These changes have been added throughout and are too vast in number to repeat here, especially without context, but we hope that readers will have an easier time following the analyses now. 

Additionally, we updated Figures 3 and 5 in which the main ICA and SRM analyses are described. For instance, in Figure 3’s caption we now add details about how the gradient analyses were performed on the components: 

“We used the same lines that were manually traced on the task-evoked map to assess the change in the component’s response. We found a monotonic trend within area from medial to lateral, just like we see in the ground truth.” Pg. 11

Regarding Figure 5, we reconsidered the best way to explain the SRM analyses and decided it would be helpful to partition the diagram into steps, reflecting the analytic process. These updates have been added to Figure 5, and the caption has been updated accordingly.

We hope that these changes have improved the clarity of the methods. For readers interested in learning more, we encourage them to either read the methods-focused papers that debut the analyses (e.g., Chen et al., 2015), read the papers applying the methods (e.g., Guntupalli et al., 2016), or read the annotated code we publicly release which implements these pipelines and can be used to replicate the findings.

Validation of the analyses

One of the requests the reviewer makes is to validate our analyses. Our initial approach was to lean on papers that have used these methods in adults or primates (e.g., Arcaro, & Livingstone, 2017; Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Moeller et al., 2009) where the underlying organization and neurophysiology is established. However, we have made changes to these methods that differ from their original usage (e.g., we used SRM rather than hyperalignment, we use meridian mapping rather than traveling wave retinotopy, we use movie-watching data rather than rest). Hence, the specifics of our design and pipeline warrant validation. 

To add further validation, we have rerun the main analyses on an adult sample. We collected 8 adult participants who completed the same retinotopy task and a large subset of the movies that infants saw. These participants were run under maximally similar conditions to infants (i.e., scanned using the same parameters and without the top of the head-coil) and were preprocessed using the same pipeline. Given that the relationship between adult visual maps and movie-driven (or resting-state) analyses has been shown in many studies (Beckman et al., 2005; Butt et al., 2015; Guntupalli et al., 2016; Haak & Beckman, 2018; Knapen, 2021; Lu et al., 2017), these adult data serve as a validation of our analysis pipeline. These adult participants were included in the original manuscript; however, they were previously only used to support the SRM analyses (i.e., can adults be used to predict infant visual maps). The adult results are described before any results with infants, as a way to engender confidence. Moreover, we have provided new supplementary figures of the adult results that we hope will be integrated with the article when viewing it online, such that it will be easy to compare infant and adult results, as per the reviewer’s request. 

As per the figures and captions below, the analyses were all successful with the adult participants: 1) Homotopic correlations are higher than correlations between comparable areas in other streams or areas that are more distant within stream. 2) A multidimensional scaling depiction of the data shows that areas in the dorsal and ventral stream are dissimilar. 3) Using independent components analysis on the movie data, we identified components that are highly correlated with the retinotopy task-based spatial frequency and meridian maps. 4) Using shared response modeling on the movie data, we predicted maps that are highly correlated with the retinotopy task-based spatial frequency and meridian maps.

These supplementary analyses are underpowered for between-group comparisons, so we do not statistically compare the results between infants and adults. Nonetheless, the pattern of adult results is comparable overall to the infant results. 

We believe these adult results provide a useful validation that the infant analyses we performed can recover fine-grained organization.

Enhancing the visualization

The reviewer raises an additional concern about the lack of visualization of the results. We recognize that the plots of the summary statistics do not provide information about the intermediate analyses. Indeed, we think the summary statistics can understate the degree of similarity between the components or predicted visual maps and the ground truth. Hence, we have added 6 new supplementary figures showing the intensity gradients for the following analyses: 1. spatial frequency prediction using ICA, 2. meridian prediction using ICA, 3. spatial frequency prediction using infant SRM, 4. meridian prediction using infant SRM, 5. spatial frequency prediction using adult SRM, and 6. meridian prediction using adult SRM.

We hope that these visualizations are helpful. It is possible that the reviewer wishes us to also visually present the raw maps from the ICA and SRM, akin to what we show in Figure 3A and 3B. We believe this is out of scope of this paper: of the 1140 components that were identified by ICA, we selected 36 for spatial frequency and 17 for meridian maps. We also created 20 predicted maps for spatial frequency and 20 predicted meridian maps using SRM. This would result in the depiction of 93 subfigures, requiring at least 15 new full-page supplementary figures to display with adequate resolution. Instead, we encourage the reader to access this content themselves: we have made the code to recreate the analyses publicly available, as well as both the raw and preprocessed data for these analyses, including the data for each of these selected maps.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) As mentioned in the public review, the authors should consider incorporating relevant adult fMRI research into the Introduction and explain the importance of testing this question in infants.

Our public response describes the several citations to relevant adult research we have added, and have provided further motivation for the project.

(2) The authors should conduct additional analyses to support their conclusion that movie data alone can generate accurate retinotopic maps (i.e., by comparing this approach to other available alternatives).

We have clarified in our public response that we did not wish to conclude that movie data alone can generate accurate retinotopic maps, and have made substantial edits to the text to emphasize this. Thus, because this claim is already not supported by our analyses, we do not think it is necessary to test it further.

(3) The authors should re-do the homotopy analyses using movie-defined ROIs (i.e., by splitting the movie-viewing data into independent folds for functional ROI definition and analyses).

As stated above, defining ROIs based on the movie content is not the intended goal of this project. Even if that were the general goal, we do not believe that it would be appropriate to run this specific analysis with the data we collected. Firstly, halving the data for ROI definition (e.g., using half the movie data to identify and trace areas, and then use those areas in the homotopy analysis to run on the other half of data) would qualitatively change the power of the analyses described here. Secondly, we would be unable to define areas beyond hV4/V3AB with confidence, since our retinotopic mapping only affords specification of early visual cortex. Thus we could not conduct the MDS analyses shown in Figure 2.

(4) If the authors agree that a primary contribution of this study and paper is to showcase what is possible to do with a limited amount of movie-viewing data, then they should make it clearer, sooner, how much usable movie data they have from infants. They could also consider conducting additional analyses to determine the minimum amount of fMRI data necessary to reveal the same detailed characteristics of functional responses in the visual cortex.

We agree it would be good to highlight the amount of movie data used. When the infant data is first introduced in the results section, we now state the durations:

“All available movies from each session were included (Table S2), with an average duration of 540.7s (range: 186--1116s).” Pg. 5

Additionally, we have added a homotopy analysis that describes the contribution of data quantity to the results observed. We compare the amount of data collected with the magnitude of same vs. different stream effect (Figure 1B) and within stream distance effect (Figure 1C). We find no effect of movie duration in the sample we tested, as reported below:

“We found no evidence that the variability in movie duration per participant correlated with this difference [of same stream vs. different stream] (r=0.08, p=.700).” Pg. 6-7

“There was no correlation between movie duration and the effect (Same > Adjacent: r=-0.01, p=.965, Adjacent > Distal: r=-0.09, p=.740).” Pg. 7

(5) If any of the methodological approaches are novel, the authors should make this clear. In particular, has the approach of visually inspecting and categorizing components generated from ICA and movie data been done before, in adults/other contexts?

The methods we employed are similar to others, as described in the public review.

However, changes were necessary to apply them to infant samples. For instance, Guntupalli et al. (2016) used hyperalignment to predict the visual maps of adult participants, whereas we use SRM. SRM and hyperalignment have the same goal — find a maximally aligned representation between participants based on brain function — but their implementation is different. The application of functional alignment to infants is novel, as is their use in movie data that is relatively short by comparison to standard adult data. Indeed, this is the most thorough demonstration that SRM — or any functional alignment procedure — can be usefully applied to infant data, awake or sleeping. We have clarified this point in the discussion.

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45], which may prove especially useful for infant fMRI[52].” Pg. 21

(6) The authors found that meridian maps were less identifiable from ICA and movie data and suggest that this may be because these maps are more susceptible to noise or gaze variability. If this is the case, you might predict that these maps are more identifiable in adult data. The authors could consider running additional analyses with their adult participants to better understand this result.

As described in the manuscript, we hypothesize that meridian maps are more difficult to identify than spatial frequency maps because meridian maps are a less smooth, more fine-grained map than spatial frequency. Indeed, it has previously been reported (Moeller et al., 2009) that similar procedures can result in meridian maps that are constituted by multiple independent components (e.g., a component sensitive to horizontal orientations, and a separate component sensitive to vertical components). Nonetheless, we have now conducted the ICA procedure on adult participants and again find it is easier to identify spatial frequency components compared to meridian maps, as reported in the public review.

Minor corrections:

(1) Typo: Figure 3 title: "Example retintopic task vs. ICA-based spatial frequency maps.".

Fixed

(2) Given the age range of the participants, consider using "infants and toddlers"? (Not to diminish the results at all; on the contrary, I think it is perhaps even more impressive to obtain awake fMRI data from ~1-2-year-olds). Example: Figure 3 legend: "A) Spatial frequency map of a 17.1-monthold infant.".

We agree with the reviewer that there is disagreement about the age range at which a child starts being considered a toddler. We have changed the terms in places where we refer to a toddler in particular (e.g., the figure caption the reviewer highlights) and added the phrase “infants and toddlers” in places where appropriate. Nonetheless, we have kept “infants” in some places, particularly those where we are comparing the sample to adults. Adding “and toddlers” could imply three samples being compared which would confuse the reader.

(3) Figure 6 legend: The following text should be omitted as there is no bar plot in this figure: "The bar plot is the average across participants. The error bar is the standard error across participants.".

Fixed

(4) Table S1 legend: Missing first single quote: Runs'.

Fixed

Reviewer #2 (Recommendations For The Authors):

I request that this paper cite more of the existing literature on the fMRI of human infants and toddlers using task-driven and resting-state data. For example, early studies by (first authors) Biagi, Dehaene-Lambertz, Cusack, and Fransson, and more recent studies by Chen, Cabral, Truzzi, Deen, and Kosakowski.

We have added several new citations of recent task-based and resting state studies to the second sentence of the main text:

“Despite the recent growth in infant fMRI[1-6], one of the most important obstacles facing this research is that infants are unable to maintain focus for long periods of time and struggle to complete traditional cognitive tasks[7].”

Reviewer #3 (Recommendations For The Authors):

In the following, I report some of my main perplexities, but many more may arise when the material is presented more clearly.

The age of the children varies from 5 months to about 2 years. While the developmental literature suggests that between 1 and 2 years children have a visual system nearly adult-like, below that age some areas may be very immature. I would split the sample and perhaps attempt to validate the adult SRM model with the youngest children (and those can be called infants).

We recognize the substantial age variability in our sample, which is why we report participant-specific data in our figures. While splitting up the data into age bins might reveal age effects, we do not think we can perform adequately powered null hypothesis testing of the age trend. In order to investigate the contribution of age, larger samples will be needed. That said, we can see from the data that we have reported that any effect of age is likely small. To elaborate: Figures 4 and 6 report the participant-specific data points and order the participants by age. There are no clear linear trends in these plots, thus there are no strong age effects.

More broadly, we do not think there is a principled way to divide the participants by age. The reviewer suggests that the visual system is immature before the first year of life and mature afterward; however, such claims are the exact motivation for the type of work we are doing here, and the verdict is still out. Indeed, the conclusion of our earlier work reporting retinotopy in infants (Ellis et al., 2021) suggests that the organization of the early visual cortex in infants as young as 5 months — the youngest infant in our sample — is surprisingly adult-like.

The title cannot refer to infants given the age span.

There is disagreement in the field about the age at which it is appropriate to refer to children as infants. In this paper, and in our prior work, we followed the practice of the most attended infant cognition conference and society, the International Congress of Infant Studies (ICIS), which considers infants as those aged between 0-3 years old, for the purposes of their conference. Indeed, we have never received this concern across dozens of prior reviews for previous papers covering a similar age range. That said, we understand the spirit of the reviewer’s comment and now refer to the sample as “infants and toddlers” and to older individuals in our sample as “toddlers” wherever it is appropriate (the younger individuals would fairly be considered “infants” under any definition).

Figure 1 is clear and an interesting approach. Please also show the average correlation maps on the cortical surface.

While we would like to create a figure as requested, we are unsure how to depict an area-by-area correlation map on the cortical surface. One option would be to generate a seed-based map in which we take an area and depict the correlation of that seed (e.g., vV1) with all other voxels. This approach would result in 8 maps for just the task-defined areas, and 17 maps for anatomically-defined areas. Hence, we believe this is out of scope of this paper, but an interested reader could easily generate these maps from the data we have released.

Figure 2 results are not easily interpretable. Ventral and dorsal V1-V3 areas represent upper or lower VF respectively. Higher dorsal and ventral areas represent both upper and lower VF, so we should predict an equal distance between the two streams. Again, how can we verify that it is not a result of some artifacts?

In adults, visual areas differ in their functional response properties along multiple dimensions, including spatial coding. The dorsal/ventral stream hypothesis is derived from the idea that areas in each stream support different functions, independent of spatial coding. The MDS analysis did not attempt to isolate the specific contribution of spatial representations of each area but instead tested the similarity of function that is evoked in naturalistic viewing. Other covariance-based analyses specifically isolate the contribution of spatial representations (Haak et al., 2013); however, they use a much more constrained analysis than what was implemented here. The fact that we find broad differentiation of dorsal and ventral visual areas in infants is consistent with adults (Haak & Beckman, 2018) and neonate non-human primates (Arcaro & Livingstone, 2017). 

Nonetheless, we recognize that we did not mention the differences in visual field properties across areas and what that means. If visual field properties alone drove the functional response then we would expect to see a clustering of areas based on the visual field they represent (e.g., hV4 and V3AB should have similar representations). Since we did not see that, and instead saw organization by visual stream, the result is interesting and thus warrants reporting. We now mention this difference in visual fields in the manuscript to highlight the surprising nature of the result.

“This separation between streams is striking when considering that it happens despite differences in visual field representations across areas: while dorsal V1 and ventral V1 represent the lower and upper visual field, respectively, V3A/B and hV4 both have full visual field maps. These visual field representations can be detected in adults[41]; however, they are often not the primary driver of function[39]. We see that in infants too: hV4 and V3A/B represent the same visual space yet have distinct functional profiles.” Pg. 8

The reviewer raises a concern that the MDS result may be spurious and caused by noise. Below, we present three reasons why we believe these results are not accounted for by artifacts but instead reflect real functional differentiation in the visual cortex. 

(1) Figure 2 is a visualization of the similarity matrix presented in Figure S1. In Figure S1, we report the significance testing we performed to confirm that the patterns differentiating dorsal and ventral streams — as well as adjacent areas from distal areas — are statistically reliable across participants. If an artifact accounted for the result then it would have to be a kind of systematic noise that is consistent across participants.

(2) One of the main sources of noise (both systematic and non-systematic) with infant fMRI is motion. Homotopy is a within-participant analysis that could be biased by motion. To assess whether motion accounts for the results, we took a conservative approach of regressing out the framewise motion (i.e., how much movement there is between fMRI volumes) from the comparisons of the functional activity in regions. Although the correlations numerically decreased with this procedure, they were qualitatively similar to the analysis that does not regress out motion:

“Additionally, if we control for motion in the correlation between areas --- in case motion transients drive consistent activity across areas --- then the effects described here are negligibly different (Figure S5).” Pg. 7

(3) We recognize that despite these analyses, it would be helpful to see what this pattern looks like in adults where we know more about the visual field properties and the function of dorsal and ventral streams. This has been done previously (e.g., Haak & Beckman, 2018), but we have now run those analyses on adults in our sample, as described in the public review. As with infants, there are reliable differences in the homotopy between streams (Figure S1). The MDS results show that the adult data was more complex than the infant data, since it was best described by 3 dimensions rather than 2. Nonetheless, there is a rotation of the MDS such that the structure of the ventral and dorsal streams is also dissociable. 

Figure 3 also raises several alternative interpretations. The spatial frequency component in B has strong activity ONLY at the extreme border of the VF and this is probably the origin of the strong correlation. I understand that it is only one subject, but this brings the need to show all subjects and to report the correlation. Also, it is important to show the putative average ICA for retinotopy and spatial frequencies across subjects and for adults. All methods should be validated on adults where we have clear data for retinotopy and spatial frequency.

The reviewer notes that the component in Figure 3 shows strong negative response in the periphery. It is often the case, as reported elsewhere (Moeller et al., 2009), that ICA extracts portions of visual maps. To make a full visual map would require combining components into a composite (e.g., a component that has a high response in the periphery and another component that has a high response in the fovea). If we were to claim that this component, or others like it, could replace the need for retinotopic mapping, then we would want to produce these composite maps; however, our conclusion in this project is that the topographic information of retinotopic maps manifest in individual components of ICA. For this purpose, the analysis we perform adequately assesses this topography.

Regarding the request to show the results for all subjects, we address this in the public response and repeat it here briefly: we have added 6 new figures to show results akin to Figure 3C and D. It is impractical to show the equivalent of Figure 3A and B for all participants, yet we do release the data necessary to see to visualize these maps easily.

Finally, the reviewer suggests that we validate the analyses on adult participants. As shown in Figure S3 and reported in the public response, we now run these analyses on adult participants and observe qualitatively similar results to infants.

How much was the variation in the presumed spatial frequency map? Is it consistent with the acuity range? 5-month-old infants should have an acuity of around 10c/deg, depending on the mean luminance of the scene.

The reviewer highlights an important weakness of conducting ICA: we cannot put units on the degree of variation we see in components. We now highlight this weakness in the discussion:

“Another limitation is that ICA does not provide a scale to the variation: although we find a correlation between gradients of spatial frequency in the ground truth and the selected component, we cannot use the component alone to infer the spatial frequency selectivity of any part of cortex. In other words, we cannot infer units of spatial frequency sensitivity from the components alone.” Pg. 20

Figure 5 pipeline is totally obscure. I presumed that I understood, but as it is it is useless. All methods should be clearly described, and the intermediate results should be illustrated in figures and appropriately discussed. Using such blind analyses in infants in principle may not be appropriate and this needs to be verified. Overall all these techniques rely on correlation activities that are all biased by head movement, eye movement, and probably the dummy sucking. All those movements need to be estimated and correlated with the variability of the results. It is a strong assumption that the techniques should work in infants, given the presence of movements.

We recognize that the SRM methods are complex. Given this feedback, we remade Figure 5 with explicit steps for the process and updated the caption (as reported in the public review).

Regarding the validation of these methods, we have added SRM analyses from adults and find comparable results. This means that using these methods on adults with comparable amounts of data as what we collected from infants can predict maps that are highly similar to the real maps. Even so, it is not a given that these methods are valid in infants. We present two considerations in this regard. 

First, as part of the SRM analyses reported in the manuscript, we show that control analyses are significantly worse than the real analyses (indicated by the lines on Figure 6). To clarify the control analysis: we break the mapping (i.e., flip the order of the data so that it is backwards) between the test participant and the training participants used to create the SRM. The fact that this control analysis is significantly worse indicates that SRM is learning meaningful representations that matter for retinotopy. 

Second, we believe that this paper is a validation of SRM for infants. Infant fMRI is a nascent field and SRM has the potential to increase the signal quality in this population. We hope that readers will see these analyses as a proof of concept that SRM can be used in their work with infants. We have stated this contribution in the paper now.

“Additionally, we wish to test whether methods for functional alignment can be used with infants. Functional alignment finds a mapping between participants using functional activity -- rather than anatomy -- and in adults can improve signal-to-noise, enhance across participant prediction, and enable unique analyses[27,32-34].” Pg. 4

“This is initial evidence that functional alignment may be useful for enhancing signal quality, like it has in adults[27,32,33], or revealing changing function over development[45].” Pg. 21

Regarding the reviewer’s concern that motion may bias the results, we wish to emphasize the nature of the analyses being conducted here: we are using data from a group of participants to predict the neural responses in a held-out participant. For motion to explain consistency between participants, the motion would need to be timelocked across participants. Even if motion was time-locked during movie watching, motion will impair the formation of an adequate model that can contain retinotopic information. Thus, motion should only hurt the ability for a shared response to be found that can be used for predicting retinotopic maps. Hence, the results we observed are despite motion and other sources of noise.

What is M??? is it simply the mean value??? If not, how it is estimated?

M is an abbreviation for mean. We have now expanded the abbreviation the first time we use it.

Figure 6 should be integrated with map activity where the individual area correlation should be illustrated. Probably fitting SMR adult works well for early cortical areas, but not for more ventral and associative, and the correlation should be evaluated for the different masks.

With the addition of plots showing the gradients for each participant and each movie (Figures S10–S13) we hope we have addressed this concern. We additionally want to clarify that the regions we tested in the analysis in Figure 6 are only the early visual areas V1, V2, V3, V3A/B, and hV4. The adult validation analyses show that SRM works well for predicting the visual maps in these areas. Nonetheless, it is an interesting question for future research with more extensive retinotopic mapping in infants to see if SRM can predict maps beyond extrastriate cortex.

Occipital masks have never been described or shown.

The occipital mask is from the MNI probabilistic structural atlas (Mazziotta et al., 2001), as reported in the original version and is shared with the public data release. We have added the additional detail that the probabilistic atlas is thresholded at 0% in order to be liberally inclusive. 

“We used the occipital mask from the MNI structural atlas[63] in standard space -- defined liberally to include any voxel with an above zero probability of being labelled as the occipital lobe -- and used the inverted transform to put it into native functional space.” Pg. 27–28

Methods lack the main explanation of the procedures and software description.

We hope that the additions we have made to address this reviewer’s concerns have provided better explanations for our procedures. Additionally, as part of the data and code release, we thoroughly explain all of the software needed to recreate the results we have observed here.

eLife Assessment

Using genomic data from ancient and modern samples, this important study investigates the genomic history of cattle in Iberia, focusing on the admixture between domestic cattle and their wild ancestors, aurochs. The authors present convincing evidence for interbreeding between domestic cattle and wild aurochs since the Neolithic period, although the evidence of sex-biased introgression is weak. The authors also show that the aurochs ancestry in cattle stabilized at ~20% since ~4000 years ago and continues into modern breeds; however, the aurochs ancestry is not heightened in a modern breed of Spanish fighting bulls that are bred for aggressiveness. The work will be of interest to evolutionary biologists and quantitative geneticists who seek to understand the genomic history and genetic basis of trait variation of domesticated animals.

Reviewer #2 (Public review):

Summary:

In this paper, the authors investigated the admixture history of domestic cattle since they were introduced into Iberia, by studying genomic data from 24 ancient samples dated to ~2000-8000 years ago and comparing them to modern breeds. They aimed to (1) characterize genomic variation of skeletal remains and concordance (or discordance) with morphological features; (2) test for hybridization between wild aurochs and domestic cattle; (3) test for correlation between genetic ancestry and stable isotope levels (which are indicative of ecological niche); and (4) test for previously hypothesized higher aurochs ancestry in a modern breed of fighting bulls.

Strengths:

Overall, this study collects valuable new data and tests several important hypotheses regarding the evolutionary history and genomic variation of domestic cattle in Iberia, such as admixture between domestic and wild populations, and correlation between genome-wide aurochs ancestry and aggressiveness.

Weaknesses:

Most conclusions are well supported by the data presented, with the strengths and caveats of each analysis clearly explained. The presence of admixed individuals in prehistorical periods strongly support hybridization between wild and domestic populations, although the evidence for sex-biased introgression and ecological niche sharing is relatively weak. Lastly, the authors presented convincing evidence for relatively constant aurochs ancestry across all modern breeds, including the Lidia breed that has been bred for aggressiveness for centuries.

Major comments:

As the authors pointed out, a major limitation of this study is uncertainty in the "population identity" for most sampled individuals (i.e., whether an individual belonged to the domesticated or wild herd when they were alive). Based on chronology, morphology and genetic data, it is clear the Mesolithic samples from the Artusia and Mendandia sites are bona fide aurochs, but the "population identities" of individuals from the other two sites are much less certain. Indeed, archeological and morphological evidence from El Portalon supports the presence of both domestic animals and wild aurochs, which is echoed by the inter-individual heterogeneity in genetic ancestry. Despite the strong evidence of hybridization, it is unclear whether these admixed individuals were raised in the domestic population or lived in the wild population and hunted, limiting the authors' ability to draw conclusions regarding the direction of gene flow.

In general, detecting sex-bias admixture is an inherently challenging problem, especially given limited data. The differential ancestry proportions (estimated by f4 ratios) on autosomes and X chromosome are indicative of sex-biased hybridization and consistent with previous mtDNA results and other non-genetic data. However, as shown in Fig 3, the confidence intervals of X and autosomal estimates overlap for all but a couple of individuals, despite the overall trend of the point estimates. Moreover, even if there is significant difference, it only suggests existence of sex-bias but does not speak to the extent (unless further quantitative argument is made). Statements such as "it was mostly aurochs males who contributed wild ancestry to domestic herds" is too strong and may be interpreted as extreme bias. The authors did a good job noting the caveats of this analysis and down-toned the statement in the main text, but claims regarding sex-bias hybridization that use the phrase "mostly" in the abstract and discussion need to be further weakened.

The stable isotope analysis is very under-powered, due to issues of categorization of wild vs domestic Bos, as discussed by the authors. Although the considerable overlap in stable isotope values between domestic and wild groups is consistent with shared ecological niche, but the absence of evidence (ie significant difference between groups) is not evidence of absence. Two alternative, non-mutually exclusive scenarios are (1) prevalent errors in classification of wild vs domestic individuals; (2) different ecological niches share similar isotope profiles. Thus, the claim "suggesting that wild and domesticated groups often did not occupy different niches in Iberia" is still too strong.

Reviewer #3 (Public review):

Summary:

Günther and colleagues leverage ancient DNA data to track the genomic history of one of the most important farm animals (cattle) in Iberia, a region showing peculiarities both in terms of cultural practices as well as a climatic refugium during the LGM, the latter of which could have allowed the survival of endemic lineages. They document interesting trends of hybridisation with wild aurochs over the last 8-9 millennia, including a stabilisation of auroch ancestry ~4000 years ago, at ~20%, a time coincidental with the arrival of domestic horses from the Pontic steppe. Modern breeds such as the iconic Lidia used in bullfighting or bull running retain a comparable level of auroch ancestry.

Strengths:

The generation of ancient DNA data has been proven crucial to unravel the domestication history of traditional livestock, and this is challenging due to the environmental conditions of the Iberian peninsula, less favourable to DNA preservation. The authors leverage samples unearthed from key archaeological sites in Spain, including the karstic system of Atapuerca. Their results provide fresher insights into past management practices and permit characterisation of significant shifts in hybridization with wild aurochs.

Comments on revisions:

The authors have satisfactorily addressed my previous concerns. Last questions:

- How many MCMC iterations were run for Structf4? Can they show the likelihood of the last 10% of MCMC iterations? The results seem way too different for K = 4 vs. K = 5, but only for moo014 and moo019.

- I guess the authors also lack an "a" superindex in Table 1 for moo019.

- That Gyu2-related ancestry appears systematically for K=5 suggests that the Caucasus-related ancestry was already present in the pool that led to domesticates. Is it not important to discuss the implications of this possibility, for future analyses?

- If monophyletic, why choose between Bed3 and CPC98 if both could be combined as a single population to further reduce qpAdm and f4 confidence intervals?

- Why not combine all auroch Iberian samples as a single population for testing gene flow from this whole group of samples to ancient Iberian cattle? Would be the resulting coverage still too low?

- What is subindex 1 in the denominator of the f4 ratio (main methods)?

Thanks for your efforts

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

My main concern is the use of the 700K SNP dataset. This set of SNPs suffers from a heavy ascertainment bias, which can be seen in the PCA in the supplementary material where all the aurochs cluster in the center within the variation of cattle. Given the coverage of some of the samples, multiple individuals would have less than 10K SNP covered. The majority of these are unlikely to be informative here given that they would just represent fixed positions between taurine and indicine or SNPs mostly variable in milk cattle breeds. The authors would get a much better resolution (i.e. many more SNPs to work with their very low genome coverage data) using the 1000 bull genome project VCF data set:

https://www.ebi.ac.uk/ena/browser/view/PRJEB42783 which based on whole genome resequencing data from many cattle. This will certainly help with improving the resolution of qpAdm and f4 analysis, which have huge confidence intervals in most cases. Right now some individuals have huge confidence intervals ranging from 0 to 80% auroch ancestry...

We thank the reviewer for this suggestion. We repeated our analyses with a SNP panel from Run 6 of the 1000 Bulls project presented in Naval-Sanchez et al 2020. This panel reduced standard errors and narrowed down confidence intervals for the ancient samples. Another consequence is that more single-source qpAdm models can now be rejected highlighting the abundance of hybridization. For our comparison to modern breeds, we still use the 700K dataset as it provides a set of different modern European cattle breeds.

I agree with the authors that qpAdm is likely to give quite a noisy estimate of ancestry here (likely explain part of the issue I mentioned above). Although qpAdm is good for model testing here for ancestry proportion the authors instead could use an explicit f4 ratio - this would allow them to specify a model which would make the result easier to interpret.

We have added ancestry estimates from f4 ratios to the manuscript and display them together with qpAdm and Struct-f4 (as suggested by reviewer #3) in our new Table 1. We decided to keep all three different estimates to illustrate that results are not consistent for all analyses. An additional feature of qpAdm is the possibility that two source models can be rejected and additional ancestries can be identified.

The interpretation of the different levels of allele sharing on X vs autosome being the result of sex-bias admixture is not very convincing. Could these differences simply be due to a low recombination rate on the X chromosome and/or lower effective population size, which would lead to less efficient purifying selection?

Following this comment (and another comment referring to the X chromosome analysis by reviewer #2), we decided to remove sex bias from the title of our study and add more information on the caveats of this analysis. While estimating ancestry on the X chromosome can be difficult, we also add that our patterns are consistent with what has been suggested based on ancient mitochondrial data (Verdugo et al 2019). For Neolithic Anatolia, it has been suggested that the insemination of domestic cows by auroch bulls has been intentional or even ritual (Peters et al 2012). A recent parallel archaeogenomic study also concluded sex-biased introgression from autosomal, X-chromosomal and Y-chromosomal data (Rossi et al 2024). As our results are consistent with these previous studies as well as the lower differentiation of modern breeds on the X chromosome (da Fonseca et al 2019), we still consider the general pattern of our results valid even if the exact extent of sex bias is difficult to assess.

The authors suggest that 2 pop model rejection in some domestic population might be due to indicine ancestry, this seems relatively straightforward to test.

We had already performed this analysis of modeling their ancestry from three sources using qpAdm. The results are shown in Supplementary Table S6 and we now refer to this more explicitly in the text: “The presence of indicine ancestry can be confirmed in a qpAdm analysis using three sources resulting in fitting models for all breeds (Supplementary Table S6).”

The first sentence of the paper is a bit long-winded, also dogs were domesticated before the emergence of farming societies.

We rephrased the first sentence to “Domestication of livestock and crops has been the dominant and most enduring innovation of the transition from a hunter-gathering lifestyle to farming societies.”

It would be good to be specific about the number of genomes and coverage info in the last paragraph of the intro.

This information is included in the first paragraph of the results section and we decided to not duplicate the numbers in the preceding introduction paragraph to retain a flow for the readers.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors investigated the admixture history of domestic cattle since they were introduced into Iberia, by studying genomic data from 24 ancient samples dated to ~2000-8000 years ago and comparing them to modern breeds. They aimed to (1) test for introgression from (local) wild aurochs into domestic cattle; (2) characterize the pattern of admixture (frequency, extent, sex bias, directionality) over time; (3) test for correlation between genetic ancestry and stable isotope levels (which are indicative of ecological niche); and (4) test for the hypothesized higher aurochs ancestry in a modern breed of fighting bulls.

Strengths:

Overall, this study collects valuable new data that are useful for testing interesting hypotheses, such as admixture between domestic and wild populations, and correlation between genome-wide aurochs ancestry and aggressiveness.

Thank you for highlighting the importance of our study and the potential of our dataset.

Weaknesses:

Most conclusions are partially supported by the data presented. The presence of admixed individuals in prehistorical periods supports the hypothesized introgression, although this conclusion needs to be strengthened with an analysis of potential contamination. The frequency, sex-bias, and directionality of admixture remain highly uncertain due to limitations of the data or issues with the analysis. There is considerable overlap in stable isotope values between domestic and wild groups, indicating a shared ecological niche, but variation in classification criteria for domestic vs wild groups and in skeletal elements sampled for measurements significantly weakens this claim. Lastly, the authors presented convincing evidence for relatively constant aurochs ancestry across all modern breeds, including the Lidia breed which has been bred for aggressiveness for centuries. My specific concerns are outlined below.

Contamination is a common concern for all ancient DNA studies. Contamination by modern samples is perhaps unlikely for this specific study of ancient cattle, but there is still the possibility of cross-sample contamination. The authors should estimate and report contamination estimates for each sample (based on coverage of autosomes and sex chromosomes, or heterozygosity of Y or MT DNA). Such contamination estimates are particularly important to support the presence of individuals with admixed ancestry, as a domestic sample contaminated with a wild sample (or vice versa) could appear as an admixed individual.

We thank the reviewer for this suggestion. Due to our low coverage data, we focused on estimating contamination from the mitochondrial data by implementing the approach used by Green et al (2008). We make the code for this step available on Github. While most samples displayed low levels of contamination, we identified one sample (moo013a) with a surprisingly high (~50%) level of contamination which was excluded from further analysis.

A major limitation of this study is uncertainty in the "population identity" for most sampled individuals (i.e., whether an individual belonged to the domesticated or wild herd when they were alive). Based on chronology, morphology, and genetic data, it is clear the Mesolithic samples from the Artusia and Mendandia sites are bona fide aurochs, but the identities of individuals from the other two sites are much less certain. Indeed, archeological and morphological evidence from El Portalon supports the presence of both domestic animals and wild aurochs, which is echoed by the inter-individual heterogeneity in genetic ancestry. Based on results shown in Fig 1C and Fig 2 it seems that individuals moo017, moo020, and possibly moo012a are likely wild aurochs that had been hunted and brought back to the site by humans. Although the presence of individuals (e.g., moo050, moo019) that can only be explained by two-source models strongly supports that interbreeding happened (if cross-contamination is ruled out), it is unclear whether these admixed individuals were raised in the domestic population or lived in the wild population and hunted.

The reviewer is pointing out an important topic, the unknown identity of the studied individuals. We have revised the text making clear that we do not know whether the individuals were hunted or herded. At the same time, their genomic ancestry speaks for itself showing that there was hybridization between wild and domestic and that different individuals carried different degrees of wild ancestry. In the revised version, we have added the unknown identity as well as the fact that our results can be affected by both, changes in human hunting and herding practices over time. Regardless of the exact identity of the individuals, our results can still be seen as (a) evidence for hybridization and (b) changes in human practices (hunting and/or herding) and their relationship to bovids over time.

Such uncertainty in "population identity" limits the authors' ability to make conclusions regarding the frequency, sex bias, and directionality of gene flow between domestic and wild populations. For instance, the wide range of ancestry estimates in Neolithic and Chalcolithic samples could be interpreted as evidence of (1) frequent recent gene flow or (2) mixed practices of herding and hunting and less frequent gene flow. Similarly, the statement about "bidirection introgression" (on pages 8 and 11) is not directly supported by data. As the genomic, morphological, and isotope data cannot confidently classify an individual as belonging to the domesticated or wild population, it seems impossible to conclude the direction of gene flow (if by "bidirection introgression" the authors mean something other than "bidirectional gene flow", they need to clearly explain this before reaching the conclusion.)

We have removed “bidirectional introgression” from the text and replaced it with the more neutral term “hybridization”. Furthermore, we used the revision to mention at several places in the text that it is not clear whether the sequenced individuals were hunted and herded and that the observed pattern likely reflects changes in both hunting and herding practices.

The f4 statistics shown in Fig 3B are insufficient to support the claim regarding sex-biased hybridization, as the f4 statistic values are not directly comparable between the X chromosome and autosomes. Because the effective population size is different for the X chromosome and autosomes (roughly 3:4 for populations with equal numbers of males and females), the expected amount of drift is different, hence the fraction of allele sharing (f4) is expected to be different. In fact, the observation that moo004 whose autosomal genome can be modeled as 100% domestic ancestry still shows a higher f4 value for the X chromosome than autosomes hints at this issue. A more robust metric to test for sex-biased admixture is the admixture proportion itself, which can be estimated by qpAdm or f4-ratio (see Patterson et al 2012). However, even with this method, criticism has been raised (e.g., Lazaridis and Reich 2017; Pfennig and Lachance, 2023). In general, detecting sex-bias admixture is a tough problem.

In response to this comment and another comment by reviewer #1, we decided to remove sex bias from the title. In the revised version of our study, we have now switched this analysis from f4 statistics to comparing f4 ratios between the X chromosome and autosomes (Figure 3). Furthermore, we have added more information on the caveats of this analysis citing the articles mentioned by the reviewer. At the same time, we highlight that our patterns are consistent with what has been suggested based on ancient mitochondrial data (Verdugo et al 2019). Unfortunately, the low coverage data does not allow to call Y chromosomal haplotypes which would also allow an analysis of the paternal lineage. But our results are consistent with additional examples from the literature: For Neolithic Anatolia, it has been suggested that the insemination of domestic cows by auroch bulls has been intentional or even ritual (Peters et al 2012) and there is a lower differentiation of modern breeds on the X chromosome (da Fonseca et al 2019). A recent parallel archaeogenomic study also concluded sex-biased introgression from autosomal, X-chromosomal and Y-chromosomal data (Rossi et al 2024). Similar to the broader hybridization signal, our interpretation does not depend on the estimates for single individuals as we describe the broader pattern. As our results are consistent with previous results based on other types of data, we still consider the general pattern of our results valid even if the exact extent of sex bias is difficult to assess.

In general, the stable isotope analysis seems to be very underpowered, due to the issues of variation in classification criteria and skeletal sampling location discussed by the authors in supplementary material. The authors claimed a significant difference in stable nitrogen isotope between (inconsistently defined) domestic cattle and wild aurochs, but no figures or statistics are presented to support this claim. Please describe the statistical method used and the corresponding p-values. The authors can consider including a figure to better show the stable isotope results.

In combination with updated tables, we have added a supplementary figure showing the stable isotope results (S9). In light of the reanalysis of the genetic data, we have reassessed the genetic models used to assign species in the stable isotope analysis. We have provided more details of the statistical methods used and the p-values are given in the supplementary materials. There is a significant difference in the nitrogen isotope values when comparing B. taurus and B. primigenius (identified on morphology) but no other comparisons are significant at the p = 0.05 threshold. The reviewer highlights what we have mentioned in the supplementary material regarding the varied skeletal elements used for stable isotope analysis and the difficulty of assigning a species identity (as this depends on what criteria are used; morphological or some kind of genetic threshold of ancestry). Indeed, how to identify the species is at the heart of the paper. Given that identity could be defined in many ways, we have used 3 different genetic models to reflect this and the morphological categories, to help explore different possible scenarios. The reviewer is correct to point out that some of this analysis is not helped by the variety of skeletal elements used, but we have been careful not to over-interpret the results. The only samples that have nitrogen values higher than one standard deviation from the mean are domestic cattle, so it is not unreasonable to suggest that only domestic cattle have high nitrogen isotope values.

Reviewer #3 (Public Review):

Summary:

Günther and colleagues leverage ancient DNA data to track the genomic history of one of the most important farm animals (cattle) in Iberia, a region showing peculiarities both in terms of cultural practices as well as a climatic refugium during the LGM, the latter of which could have allowed the survival of endemic lineages. They document interesting trends of hybridisation with wild aurochs over the last 8-9 millennia, including a stabilisation of auroch ancestry ~4000 years ago, at ~20%, a time coincidental with the arrival of domestic horses from the Pontic steppe. Modern breeds such as the iconic Lidia used in bullfighting or bull running retain a comparable level of auroch ancestry.

Strengths:

The generation of ancient DNA data has been proven crucial to unravel the domestication history of traditional livestock, and this is challenging due to the environmental conditions of the Iberian peninsula, less favourable to DNA preservation. The authors leverage samples unearthed from key archaeological sites in Spain, including the karstic system of Atapuerca. Their results provide fresher insights into past management practices, and permit characterisation of significant shifts in hybridization with wild aurochs.

We thank the reviewer for their positive assessment of our work and for highlighting the strength and potential of the study.

Weaknesses:

- Treatment of post-mortem damage: the base quality of nucleotide transitions was recalibrated down to a quality score of 2, but for 5bp from the read termini only. In some specimens (e.g. moo022), the damage seems to extend further. Why not use dedicated tools (e.g. mapDamage), or check the robustness by conditioning on nucleotide transversions?

We agree that using such a non-standard data preparation approach requires some testing. Since our main analyses are all based on f statistics, we compared f4 statistics and f4 ratios of our rescaled base quality data with data only using transversion sites. While estimates are highly correlated, the data set reduced to transversions produces larger confidence intervals in f4 ratios due to the lower number of sites. Consequently, we decided to use the rescaled data for all analyses displayed in main figures. We also prefer not to perform reference based rescaling as implemented in mapDamage as it might be sensitive to mapping bias (Günther & Nettelblad 2019).

- Their more solid analyses are based on qpAdm, but rely on two single-sample donor populations. As the authors openly discuss, it is unclear whether CPC98 is a good proxy for Iberian aurochs despite possibly forming a monophyletic clade (the number of analysed sites is simply too low to assess this monophyly; Supplementary Table S2). Additionally, it is also unclear whether Sub1 was a fully unadmixed domestic specimen, depleted of auroch ancestry. The authors seem to suggest themselves that sex-biased introgression may have already taken place in Anatolia ("suggesting that sex-biased processes already took place prior to the arrival of cattle to Iberia").

We expanded the discussion on this topic but removed the analysis of whether European aurochs form a clade due to the low number of sites. We do highlight that a recent parallel study on aurochs genomes confirmed that Western European aurochs form a clade, probably even originating from an Iberian glacial refugium (Rossi et al 2024). Even if minor structure in the gene pool of European aurochs might affect our quantitative results, it should not drive the qualitative pattern. The same should be the case for Sub1 as our tests would detect additional European aurochs ancestry that was not present in Sub1. The corresponding paragraph now reads:

“A limitation of this analysis is the availability of genomes that can be used as representatives of the source populations as we used German and British aurochs to represent western European aurochs ancestry and a single Anatolian Neolithic to represent the original domestic cattle that was introduced into Europe. Our Mesolithic Iberian aurochs contained too little endogenous DNA to be used as a proxy aurochs reference and all Neolithic and Chalcolithic samples estimated with predominantly aurochs ancestry (including the 2.7x genome of moo014) already carry low (but significant) levels of domestic ancestry. However, the fact that all of these aurochs samples carried P mitochondria strongly suggests that western European aurochs can be considered monophyletic. Furthermore, a recent parallel study also concluded that Western European aurochs all form a clade (27). The Anatolian Sub1 might also not be depleted of any European aurochs ancestry and could not fully represent the original European Neolithic gene pool as also indicated by qpAdm and Struct-f4 identifying small proportions of other Asian ancestries in some Iberian individuals.

While these caveats should affect our quantitative estimates of European aurochs ancestry, they should not drive the qualitative pattern as our tests would still detect any excess European aurochs ancestry that was not present in Neolithic Anatolia.”

Alternatively, I recommend using Struct-f4 as it can model the ancestry of all individuals together based on their f4 permutations, including outgroups and modern data, and without the need to define pure "right" and "left" populations such as CPC98 and Sub1. It should work with low-coverage data, and allows us to do f4-based MDS plots as well as to estimate ancestry proportions (including from ghost populations).

We thank the reviewer for this suggestion. We added Struct-f4 as an analysis but observed that it would not converge in an individual-based analysis due to the low coverage of most of our samples. We added Struct-f4 results for samples with >0.1X to the new Table 1, the results are similar to the results obtained using f4 ratios and (to a lower degree) the qpAdm results.

- In the admixture graph analyses (supplementary results), the authors use population groups based on a single sample. If these samples are pseudohaploidised (or if coverage is insufficient to estimate heterozygosity - and it is at least for moo004 and moo014), f3 values are biased, implying that the fitted graph may be wrong. The graph shown in Fig S7 is in fact hard to interpret. For example, the auroch Gyu2 from Anatolia but not the auroch CPC98 also from Anatolia received 62% of ancestry from North Africa? The Neolithic samples moo004 and moo014 also show the same shocking disparity. I would consider re-doing this analysis with more than a sample per population group

There seems to be some confusion relating to the sample identity in these figures. CPC98 is British and not Anatolian while Gyu2 is from the Caucasus and not Anatolia which would explain why they are different. Furthermore, moo004 is mostly of domestic ancestry while, moo014 is mostly of European aurochs ancestry according to our other analyses, which should explain why they also behave differently in this analysis. To avoid confusion and since this is a supplementary analysis from which we are not drawing any major conclusions, we decided to remove the graphs and the analysis from the study.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Fig 3A: The red regression line is misleading. It seems to show that the average aurochs ancestry fraction has been steadily decreasing since ~8000 years ago, but the "averaging" is not meaningful as not all samples necessarily represent domestic cattle remains and the sample size is rather small. In other words, the samples are just a small, random collection of domestic and wild animals, and the average ancestry is subject to large sampling noise. I would suggest removing the regression line (along with the associated confidence interval) in this figure. It would also be helpful to label the samples with their IDs and morphology in the plot for cross-reference with other figures. Also, it is said in the legend that "Modern Iberian breeds... are added around date 0 with some vertical jitter". Do the authors mean "horizontal jitter" instead?

Thank you for noticing this! We have removed the regression line and corrected the figure legend.

Fig 2 vs Fig 3A: are the error bars the same in these two plots? They seem to be highly similar, if not identical, but the legends read very differently ("95% confidence interval by block-jackknife vs. on standard error"). Please explain.

The figure legends have been corrected.

Fig 3B: What do the error bars in Fig 3B mean? 95% confidence interval or one standard error? Please clarify in the legend.

We have removed this figure and replaced it with a different way of displaying the results (now Figure 3). We ensured that the error bars are displayed consistently across figures.

According to the f4 statistics shown in Fig 1C and Fig 3B, moo012b carries a relatively high amount of domestic ancestry. How is this compatible with the observation in Fig 2 that this individual can be modeled with 100% aurochs (i.e., aurochs as the single source)? Does this simply reflect the low genome coverage?

moo012b is indeed one of the lowest coverage samples in our has at <0.02x sequencing depth. Even in our revised analysis using more sites, there is a discrepancy between the results of f4 statistics and qpAdm (suggesting mostly domestic ancestry) and f4 ratio suggesting mostly aurochs ancestry (Figure 1C and Table 1). We believe that this highlights the sensitivity of different methods to assumptions about the relationships of sources and potential “outgroups” which might not be well resolvable with low coverage data and in the presence of potentially complex admixture. Our general results, however, do not depend on the estimates for single individuals as our interpretations are based on the general pattern.

I don't fully understand the rationale behind the statement "However, at some point, the herding practices must have changed since modern Iberian breeds show approximately 20-25% aurochs ancestry". Can the stable ancestry fraction from 4000 years to the present (relative to the highly variable ancestry before) reflect of discontinuation of hunting rather than changes in herding practices?

We agree that this statement was not justified here, we rephrased the sentence to “In fact, from the Bronze Age onwards, most estimates overlap with the approximately 25% aurochs ancestry in modern Iberian cattle” and generally tried to make the text more nuanced on the issue of herding and hunting practices.

Reviewer #3 (Recommendations For The Authors):

Thanks for this interesting piece of work. The results are clearly presented, and I have no additional concerns other than those reflected in the public report, except perhaps:

(i) trying to use more informative sample names (eg. including the date and location). It may facilitate reading without going back and forth to the table "Sample List".

We have now added a main table listing our post-Mesolithic samples together with their age, site and estimated aurochs ancestry proportions. We hope that his table makes it easier for readers to follow our sample IDs.

(ii) Briefly describe in the main the age of aurochs and Sub1 not generated in this study.

Fixed.

eLife Assessment

This study reveals the important role of upstream open reading frames (uORFs) in limiting the translational variability of downstream coding sequences. Through a combination of computational simulations, comparative analyses of translation efficiency across different developmental stages in two closely related Drosophila species, and manipulative, experimental validation of translation buffering by an uORF for a gene, the authors provide convincing evidence supporting their conclusions. This work will be of broad interest to molecular biologists and geneticists.

Reviewer #1 (Public review):

Summary:<br /> The authors set out to explore the role of upstream open reading frames (uORFs) in stabilizing protein levels during Drosophila development and evolution. By utilizing a modified ICIER model for ribosome translation simulations and conducting experimental validations in Drosophila species, the study investigates how uORFs buffer translational variability of downstream coding sequences. The findings reveal that uORFs significantly reduce translational variability, which contributes to gene expression stability across different biological contexts and evolutionary timeframes.

Strengths:<br /> (1) The study introduces a sophisticated adaptation of the ICIER model, enabling detailed simulation of ribosomal traffic and its implications for translation efficiency.<br /> (2) The integration of computational predictions with empirical data through knockout experiments and translatome analysis in Drosophila provides a compelling validation of the model's predictions.<br /> (3) By demonstrating the evolutionary conservation of uORFs' buffering effects, the study provides insights that are likely applicable to a wide range of eukaryotes.

Weaknesses:<br /> (1) Although the study is technically sound, it does not clearly articulate the mechanisms through which uORFs buffer translational variability. A clearer hypothesis detailing the potential molecular interactions or regulatory pathways by which uORFs influence translational stability would enhance the comprehension and impact of the findings.<br /> (2) The study could be further improved by a discussion regarding the evolutionary selection of uORFs. Specifically, it would be beneficial to explore whether uORFs are favored evolutionarily primarily for their role in reducing translation efficiency or for their capability to stabilize translation variability. Such a discussion would provide deeper insights into the evolutionary dynamics and functional significance of uORFs in genetic regulation.

Reviewer #2 (Public review):

uORFs, short open reading frames located in the 5' UTR, are pervasive in genomes. However, their roles in maintaining protein abundance are not clear. In this study, the authors propose that uORFs act as "molecular dam", limiting the fluctuation of the translation of downstream coding sequences. First, they performed in silico simulations using an improved ICIER model, and demonstrated that uORF translation reduces CDS translational variability, with buffering capacity increasing in proportion to uORF efficiency, length, and number. Next, they analzed the translatome between two related Drosophila species, revealing that genes with uORFs exhibit smaller fluctuations in translation between the two species and across different developmental stages within the same specify. Moreover, they identified that bicoid, a critical gene for Drosophila development, contains a uORF with substantial changes in translation efficiency. Deleting this uORF in Drosophila melanogaster significantly affected its gene expression, hatching rates, and survival under stress condition. Lastly, by leveraging public Ribo-seq data, the authors showed that the buffering effect of uORFs is also evident between primates and within human populations. Collectively, the study advances our understanding of how uORFs regulate the translation of downstream coding sequences at the genome-wide scale, as well as during development and evolution.

The conclusions of this paper are mostly well supported by data, but some definitions and data analysis need to be clarified and extended.

(1) There are two definitions of translation efficiency (TE) in the manuscript: one refers to the number of 80S ribosomes that complete translation at the stop codon of a CDS within a given time interval, while the other is calculated based on Ribo-seq and mRNA-seq data (as described on Page 7, line 209). To avoid potential misunderstandings, please use distinct terms to differentiate these two definitions.

(2) Page 7, line 209: "The translational efficiencies (TEs) of the conserved uORFs were highly correlated between the two species across all developmental stages and tissues examined, with Spearman correlation coefficients ranging from 0.478 to 0.573 (Fig. 2A)." However, the authors did not analyze the correlation of translation efficiency of conserved CDSs between the two species, and compare this correlation to the correlation between the TEs of CDSs. These analyzes will further support the authors conclusion regarding the role of conserved uORFs in translation regulation.

(3) Page 8, line 217: "Among genes with multiple uORFs, one uORF generally emerged as dominant, displaying a higher TE than the others within the same gene (Fig. 2C)." The basis for determining dominance among uORFs is not explained and this lack of clarification undermines the interpretation of these findings.

(4) According to the simulation, the translation of uORFs should exhibit greater variability than that of CDSs. However, the authors observed significantly fewer uORFs with significant TE changes compared to CDSs. This discrepancy may be due to lower sequencing depth resulting in fewer reads mapped to uORFs. Therefore, the authors may compare this variability specifically among highly expressed genes.

(5) If possible, the author may need to use antibodies against bicoid to test the effect of ATG deletion on bicoid expression, particularly under different developmental stages or growth conditions. According to the authors' conclusions, the deletion mutant should exhibit greater variability in bicoid protein abundance. This experiment could provide strong support for the proposed mechanisms.

eLife Assessment

This important study of regulatory elements and gene expression in the craniofacial region of the fat-tailed dunnart shows that, compared to placental mammals, marsupial craniofacial tissue develops in a precocious manner, with enhancer regulatory elements as primary driver of this difference. While the results are overall solid, addressing concerns regarding the liftover methods in the context of low conservation of alignable enhancers between dunnart and mouse would benefit the work, enhancing its value for uncovering mechanisms that drive heterochronic processes and as a reference for future mammalian evolution studies.

Reviewer #1 (Public review):

Summary:

Cook et al. have presented an important study on the transcriptomic and epigenomic signature underlying craniofacial development in marsupials. Given the lack of a dunnart genome, the authors also prepared long and short-read sequence datasets to assemble and annotate a novel genome to allow for the mapping of RNAseq and ChIPseq data against H3K4me3 and H3K27ac, which allowed for the identification of putative promoter and enhancer sites in dunnart. They found that genes proximal to these regulatory loci were enriched for functions related to bone, skin, muscle and embryonic development, highlighting the precocious state of newborn dunnart facial tissue. When compared with mouse, the authors found a much higher proportion of promoter regions aligned between species than for enhancer regions, and subsequent profiling identified regulatory elements conserved across species and are important for mammalian craniofacial development. In contrast, the identification of dunnart-specific enhancers and patterns of RNA expression further confirm the precocious state of muscle development, as well as for sensory system development, in dunnart suggesting that early formation of these features are critical for neonate marsupials likely to assist with detecting and responding to cues that direct the joeys to the mother's teat after birth. This is one of the few epigenomic studies performed in marsupials (of any organ) and the first performed in fat-tailed dunnart (also of any organ). Marsupials are emerging as an important model for studying mammalian development and evolution and the authors have performed a novel and thorough analysis, impressively including the assembly of a new marsupial reference genome that will benefit many future studies.

Strengths:

The study provides multiple pieces of evidence supporting the important role enhancer elements play in mammalian phenotypic evolution, namely the finding of a lower proportion of peaks present in both dunnart and mouse for enhancers than for promoters, and dunnart showing more genes uniquely associated with it's active enhancers than any other combination of mouse and dunnart samples, whereas this pattern was less pronounced than for promoter-associated genes. In addition, rigorous parameters were used for the cross-species analyses to identify the conserved regulatory elements and the dunnart-specific enhancers. For example, for the results presented in Figure 1, I agree that it is a little surprising that the average promoter-TSS distance is greater than that for enhancers, but that this could be related to the possible presence of unannotated transcripts between genes. The authors addressed this well by examining the distribution of promoter-TSS distances and using proximal promoters (cluster #1) as high confidence promoters for downstream analyses.

The genome assembly method was thorough, using two different long read methods (Pacbio and ONT) to generate the long reads for contig and scaffold construction, increasing the quality of the final assembled genome.

Weaknesses:

Biological replicates of facial tissue were collected at a single developmental time point of the fat-tailed dunnart within the first postnatal day (P0), and analysed this in the context of similar mouse facial samples from the ENCODE consortium at six developmental time points, where previous work from the authors have shown that the younger mouse samples (E11.5-12.5) approximately corresponds to the dunnart developmental stage (Cook et al. 2021). However, it would be useful to have samples from at least one older dunnart time point, for example, at a developmental stage equivalent to mouse E15.5. This would provide additional insight into the extent of accelerated face development in dunnart relative to mouse, i.e. how long do the regulatory elements that activated early in dunnart remain active for and does their function later influence other aspects of craniofacial development?

The authors refer to the development of the CNS being delayed in marsupials relative to placental mammals, however, evidence shows how development of the dunnart brain (whole brain or cortex) is protracted compared to mouse, by a factor of at least 2 times, rather than delayed per se (Workman et al. 2013; Paolino et al. 2023). In addition, there is evidence that cortical formation and cell birth may begin at approximately the same stage across species equivalent to the neonate period in dunnart (E10.5 in mouse), and that shortly after this at the stage equivalent to mouse E12.5, the dunnart cortex shows signs of advanced neurogenesis followed by a protracted phase of neuronal maturation (Paolino et al. 2023). Therefore, it is possible that marsupial CNS development appears delayed relative to mouse but instead begins at the same stage and then proceeds to develop on a different timing scale.

Reviewer #2 (Public review):

This study by Cook and colleagues utilizes genomic techniques to examine gene regulation in the craniofacial region of the fat-tailed dunnart at perinatal stages. Their goal is to understand how accelerated craniofacial development is achieved in marsupials compared to placental mammals.

The authors employ state-of-the-art genomic techniques, including ChIP-seq, transcriptomics, and high-quality genome assembly, to explore how accelerated craniofacial development is achieved in marsupials compared to placental mammals. This work addresses an important biological question and contributes a valuable dataset to the field of comparative developmental biology. The study represents a commendable effort to expand our understanding of marsupial development, a group often underrepresented in genomic studies.

The dunnart's unique biology, characterized by a short gestation and rapid craniofacial development, provides a powerful model for examining developmental timing and gene regulation. The authors successfully identified putative regulatory elements in dunnart facial tissue and linked them to genes involved in key developmental processes such as muscle, skin, bone, and blood formation. Comparative analyses between dunnart and mouse chromatin landscapes suggest intriguing differences in deployment of regulatory elements and gene expression patterns.

Strengths

(1) The authors employ a broad range of cutting-edge genomic tools to tackle a challenging model organism. The data generated - particularly ChIP-seq and RNA-seq from craniofacial tissue - are a valuable resource for the community, which can be employed for comparative studies. The use of multiple histone marks in the ChIP-seq experiments also adds to the utility of the datasets.

(2) Marsupial occupy an important phylogenetic position, but they remain an understudied group. By focusing on the dunnart, this study addresses a significant gap in our understanding of mammalian development and evolution. Obtaining enough biological specimens for these experiments studies was likely a big challenge that the authors were able to overcome.

(3) The comparison of enhancer landscapes and transcriptomes between dunnarts and can serve as the basis of subsequent studies that will examine the mechanisms of developmental timing shifts. The authors also carried out liftover analyses to identify orthologous enhancers and promoters in mice and dunnart.

Weaknesses and Recommendations

(1) The absence of genome browser tracks for ChIP-seq data makes it difficult to assess the quality of the datasets, including peak resolution and signal-to-noise ratios. Including browser tracks would significantly strengthen the paper by provide further support for adequate data quality.

(2) The first two figures of the paper heavily rely in gene orthology analysis, motif enrichment, etc, to describe the genomic data generated from the dunnart. The main point of these figures is to demonstrate that the authors are capturing the epigenetic signature of the craniofacial region, but this is not clearly supported in the results. The manuscript should directly state what these analyses aim to accomplish - and provide statistical tests that strengthen confidence on the quality of the datasets.

(3) The observation that "promoters are located on average 106 kb from the nearest TSS" raises significant concerns about the quality of the ChIP-seq data and/or genome annotation. The results and supplemental information suggest a combination of factors, including unannotated transcripts and enhancer-associated H3K4me3 peaks - but this issue is not fully resolved in the manuscript. The authors should confirm that this is not caused by spurious peaks in the CHIP-seq analysis - and possibly improve genome annotation with the transcriptomic datasets presented on the study.

(4) The comparison of gene regulation between a single dunnart stage (P1) and multiple mouse stages lacks proper benchmarking. Morphological and gene expression comparisons should be integrated to identify equivalent developmental stages. This "alignment" is essential for interpreting observed differences as true heterochrony rather than intrinsic regulatory differences.

(5) The low conservation of putative enhancers between mouse and dunnart (0.74-6.77%) is surprising given previous reports of higher tissue-specific enhancer conservation across mammals. The authors should address whether this low conservation reflects genuine biological divergence or methodological artifacts (e.g., peak-calling parameters or genome quality). Comparisons with published studies could contextualize these findings.

(6) Focusing only on genes associated with shared enhancers excludes potentially relevant genes without clear regulatory conservation. A broader analysis incorporating all orthologous genes may reveal additional insights into craniofacial heterochrony.

In conclusion, this study provides an important dataset for understanding marsupial craniofacial development and highlights the potential of genomic approaches in non-traditional model organisms. However, methodological limitations, including incomplete genome annotation and lack of developmental benchmarking weaken the robustness and of the findings. Addressing these issues would significantly enhance the study's utility to the field and its ability to support the study's central conclusion that dunnart-specific enhancers drive accelerated craniofacial development.

eLife Assessment

This study provides important insights into how a specific brain region controls innate responses to odors, showing that different parts of this region govern behaviors related to attraction and aversion. The findings are convincing and supported by a combination of well-executed experimental approaches, including genetic manipulations and neural activity mapping, though the evidence could be strengthened by addressing certain methodological concerns, such as clarifying the rationale for specific experimental choices and exploring alternative techniques.

Reviewer #1 (Public review):

Summary:

This study by Howe and colleagues investigates the role of the posterolateral cortical amygdala (plCoA) in mediating innate responses to odors, specifically attraction and aversion. By combining optogenetic stimulation, single-cell RNA sequencing, and spatial analysis, the authors identify a topographically organized circuit within plCoA that governs these behaviors. They show that specific glutamatergic neurons in the anterior and posterior regions of plCoA are responsible for driving attraction and avoidance, respectively, and that these neurons project to distinct downstream regions, including the medial amygdala and nucleus accumbens, to control these responses.

Strengths:

The major strength of the study is the thoroughness of the experimental approach, which combines advanced techniques in neural manipulation and mapping with high-resolution molecular profiling. The identification of a topographically organized circuit in plCoA and the connection between molecularly defined populations and distinct behaviors is a notable contribution to understanding the neural basis of innate motivational responses. Additionally, the use of functional manipulations adds depth to the findings, offering valuable insights into the functionality of specific neuronal populations.

Weaknesses:

There are some weaknesses in the study's methods and interpretation. The lack of clarity regarding the behavior of the mice during head-fixed imaging experiments raises the possibility that restricted behavior could explain the absence of valence encoding at the population level. Furthermore, while the authors employ chemogenetic inhibition of specific pathways, the rationale for this choice over optogenetic inhibition is not fully addressed, and this could potentially affect the interpretation of the results. Additionally, the choice of the mplCoA for manipulation, rather than the more directly implicated anterior and posterior subregions, is not well-explained, which could undermine the conclusions drawn about the topographic organization of plCoA.

Despite these concerns, the work provides significant insights into the neural circuits underlying innate behaviors and opens new avenues for further research. The findings are particularly relevant for understanding the neural basis of motivational behaviors in response to sensory stimuli, and the methods used could be valuable for researchers studying similar circuits in other brain regions. If the authors address the methodological issues raised, this work could have a substantial impact on the field, contributing to both basic neuroscience and translational research on the neural control of behavior.

Reviewer #2 (Public review):

Summary:

The manuscript by the Root laboratory and colleagues describes how the posterolateral cortical amygdala (plCoA) generates valenced behaviors. Using a suite of methods, the authors demonstrate that valence encoding is mediated by several factors, including spatial localization of neurons within the plCoA, glutamatergic markers, and projection. The manuscript shows convincingly that multiple features (spatial, genetic, and projection) contribute to overall population encoding of valence. Overall, the authors conduct many challenging experiments, each of which contains the relevant controls, and the results are interpreted within the framework of their experiments.

Strengths:

-For a first submission the manuscript is well constructed, containing lots of data sets and clearly presented, in spite of the abundance of experimental results.<br /> -The authors should be commended for their rigorous anatomical characterizations and post-hoc analysis. In the field of circuit neuroscience, this is rarely done so carefully, and when it is, often new insights are gleaned as is the case in the current manuscript.<br /> -The combination of molecular markers, behavioral readouts and projection mapping together substantially strengthen the results.<br /> -The focus on this relatively understudied brain region in the context is valence is well appreciated, exciting and novel.

Weaknesses:

-Interpretation of calcium imaging data is very limited and requires additional analysis and behavioral responses specific to odors should be considered. If there are neural responses behavioral epochs and responses to those neuronal responses should be displayed and analyzed.<br /> -The effect of odor habituation is not considered.<br /> -Optogenetic data in the two subregions relies on very careful viral spread and fiber placement. The current anatomy results provided should be clear about the spread of virus in A-P, and D-V axis, providing coordinates for this, to ensure readers the specificity of each sub-zone is real.<br /> -The choice of behavioral assays across the two regions doesn't seem balanced and would benefit from more congruency,<br /> -Rationale for some of the choices of photo-stimulation experiment parameters isn't well defined.

Reviewer #3 (Public review):

Summary:

Combining electrophysiological recording, circuit tracing, single cell RNAseq, and optogenetic and chemogenetic manipulation, Howe and colleagues have identified a graded division between anterior and posterior plCoA and determined the molecular characteristics that distinguish the neurons in this part of the amygdala. They demonstrate that the expression of slc17a6 is mostly restricted to the anterior plCoA whereas slc17a7 is more broadly expressed. Through both anterograde and retrograde tracing experiments, they demonstrate that the anterior plCoA neurons preferentially projected to the MEA whereas those in the posterior plCoA preferentially innervated the nucleus accumbens. Interestingly, optogenetic activation of the aplCoA drives avoidance in a spatial preference assay whereas activating the pplCoA leads to preference. The data support a model that spatially segregated and molecularly defined populations of neurons and their projection targets carry valence specific information for the odors. The discoveries represent a conceptual advance in understanding plCoA function and innate valence coding in the olfactory system.

Strengths:

The strongest evidence supporting the model comes from single cell RNASeq, genetically facilitated anterograde and retrograde circuit tracing, and optogenetic stimulation. The evidence clear demonstrates two molecularly defined cell populations with differential projection targets. Stimulating the two populations produced opposite behavioral responses.

Weaknesses:

There are a couple of inconsistencies that may be addressed by additional experiments and careful interpretation of the data.

Stimulating aplCoA or slc17a6 neurons results in spatial avoidance, and stimulating pplCoA or slc17a7 neurons drives approach behaviors. On the other hand, the authors and others in the field also show that there is no apparent spatial bias in odor-driven responses associated with odor valence. This discrepancy may be addressed better. A possibility is that odor-evoked responses are recorded from populations outside of those defined by slc17a6/a7. This may be addressed by marking activated cells and identifying their molecular markers. A second possibility is that optogenetic stimulation activates a broad set of neurons that and does not recapitulate the sparseness of odor responses. It is not known whether sparsely activation by optogenetic stimulation can still drive approach of avoidance behaviors.

The authors show that inhibiting slc17a7 neurons blocks approaching behaviors toward 2-PE. Consistent with this result, inhibiting NAc projection neurons also inhibits approach responses. However, inhibiting aplCOA or slc17a6 neurons does not reduce aversive response to TMT, but blocking MEA projection neurons does. The latter two pieces of evidence are not consistent with each other. One possibility is that the MEA projecting neurons may not be expressing slc17a6. It is not clear that the retrogradely labeling experiments what percentage of MEA- and NAC-projecting neurons express slc17a6 and slc17a7. It is possible that neurons expressing neither VGluT1 nor VGluT2 could drive aversive or appetitive responses. This possibility may also explain that silencing slc17a6 neurons does not block avoidance.

eLife Assessment

This important manuscript presents a thorough analysis of trans-specific polymorphism (TSP) in Major Histocompatibility Complex gene families across primates. The analysis makes the most of currently available genomic data and methods to substantially increase the amount and evolutionary time that TSPs can be observed, but both false negative TSPs due to missing genes at the assembly and/or annotation level, as well as false positives due to read mismapping with missing paralogs, could be assessed and discussed more. Overall the evidence provided is convincing, and the manuscript may benefit from discussing the future use of more complete assemblies made from long reads to reduce the occurrence of both missing and false TSPs.

Reviewer #1 (Public review):

Summary:

MHC (Major Histocompatibility Complex) genes have long been mentioned as cases of trans-species polymorphism (TSP), where alleles might have their most recent common ancestor with alleles in a different species, rather than other alleles in the same species (e.g., a human MHC allele might coalesce with a chimp MHC allele, more recently than the two coalesce with other alleles in either species). This paper provides a more complete estimate of the extent and ages of TSP in primate MHC loci. The data clearly support deep TSP linking alleles in humans to (in some cases) old world monkeys, but the amount of TSP varies between loci.

Strengths:

The authors use publicly available datasets to build phylogenetic trees of MHC alleles and loci. From these trees they are able to estimate whether there is compelling support for Trans-species polymorphisms (TSPs) using Bayes Factor tests comparing different alternative hypotheses for tree shape. The phylogenetic methods are state-of-the-art and appropriate to the task.

The authors supplement their analyses of TSP with estimates of selection (e.g., dN/dS ratios) on motifs within the MHC protein. They confirm what one would suspect: classical MHC genes exhibit stronger selection at amino acid residues that are part of the peptide binding region, and non-classical MHC exhibit less evidence of selection. The selected sites are associated with various diseases in GWAS studies.

Weaknesses:

An implication drawn from this paper (and previous literature) is that MHC has atypically high rates of TSP. However, rates of TSP are not estimated for other genes or gene families, so readers have no basis of comparison. No framework to know whether the depth and frequency of TSP is unusual for MHC family genes, relative to other random genes in the genome, or immune genes in particular. I expect (from previous work on the topic), that MHC is indeed exceptional in this regard, but some direct comparison would provide greater confidence in this conclusion.

Given the companion paper's evidence of genic gain/loss, it seems like there is a real risk that the present study under-estimates TSP, if cases of TSP have been obscured by the loss of the TSP-carrying gene paralog from some lineages needed to detect the TSP. Are the present analyses simply calculating rates of TSP of observed alleles, or are you able to infer TSP rates conditional on rates of gene gain/loss?

Figure 5 (and 6) provide regression model fits (red lines in panel C) relating evolutionary rates (y axis not labeled) to site distance from the peptide binding groove, on the protein product. This is a nice result. I wonder, however, whether a linear model (as opposed to non-linear) is the most biologically reasonable choice, and whether non-linear functions have been evaluated. The authors might consider generalized additive models (GAMs) as an alternative that relaxes linearity assumptions.

The connection between rapidly evolving sites, and disease associations (lines 382-3) is very interesting. However, this is not being presented as a statistical test of association. The authors note that fast-evolving amino acids all have at least one association: but is this really more disease-association than a random amino acid in the MHC? Or, a randomly chosen polymorphic amino acid in MHC? A statistical test confirming an excess of disease associations would strengthen this claim.

Reviewer #2 (Public review):

Summary

In this study, the authors characterized population genetic variation in the MHC locus across primates and looked for signals of long-term balancing selection (specifically trans-species polymorphism, TSP) in this highly polymorphic region. To carry out these tasks, they used Bayesian methods for phylogenetic inference (i.e. BEAST2) and applied a new Bayesian test to quantify evidence supporting monophyly vs. transspecies polymorphism for each exon across different species pairs. Their results, although mostly confirmatory, represent the most comprehensive analyses of primate MHC evolution to date and novel findings or possible discrepancies are clearly pointed out. However, as the authors discuss, the available data are insufficient to fully capture primates' MHC evolution.

Strengths of the paper include: using appropriate methods and statistically rigorous analyses; very clear figures and detailed description of the results methods that make it easy to follow despite the complexity of the region and approach; a clever test for TSP that is then complemented by positive selection tests and the protein structures for a quite comprehensive study.

That said, weaknesses include: lack of information about how many sequences are included and whether uneven sampling across taxa might results in some comparisons without evidence for TSP; frequent reference to the companion paper instead of summarizing (at least some of) the critical relevant information (e.g., how was orthology inferred?); no mention of the quality of sequences in the database and whether there is still potential effects of mismapping or copy number variation affecting the sequence comparison.

Reviewer #3 (Public review):

Summary

The study uses publicly available sequences of classical and non-classical genes from a number of primate species to assess the extent and depth of TSP across the primate phylogeny. The analyses were carried out in a coherent and, in my opinion, robust inferential framework and provided evidence for ancient (even > 30 million years) TSP at several classical class I and class II genes. The authors also characterise evolutionary rates at individual codons, map these rates onto MHC protein structures, and find that the fastest evolving codons are extremely enriched for autoimmune and infectious disease associations.

Strengths

The study is comprehensive, relying on a large data set, state-of-the-art phylogenetic analyses and elegant tests of TSP. The results are not entirely novel, but a synthesis and re-analysis of previous findings is extremely valuable and timely.

Weaknesses

I've identified weaknesses in several areas (details follow in the next section):<br /> - Inadequate description and presentation of the data used<br /> - Large parts of the results read like extended figure captions, which breaks the flow.<br /> - Older literature on the subject is duly cited, but the authors don't really discuss their findings in the context of this literature.<br /> - The potential impact of mechanisms other than long-term maintenance of allelic lineages by balancing selection, such as interspecific introgression and incorrect orthology assessment, needs to be discussed.

eLife Assessment

This valuable study presents a resource for researchers using Drosophila to study neural circuits, in the form of a collection of split-Gal4 lines with an online search engine, which will facilitate the mapping of neuronal circuits. The evidence is convincing to demonstrate the utility of these new tools, and of the search engine, for understanding expression patterns in adults and larvae, and differences between the sexes. These resources will be of broad interest to Drosophila researchers in the field of neurobiology.

Reviewer #1 (Public review):

Summary:

Meissner et al describe an update on the collection of split-GAL4 lines generated by a consortium led by Janelia Research Campus. This follows the same experimental pipeline described before and presents as a significant increment to the present collection. This will strengthen the usefulness and relevance of "splits" as a standard tool for labs that already use this tool and attract more labs and researchers to use it.

Strengths:

This manuscript presents a solid step to establish Split-GAL4 lines as a relevant tool in the powerful Drosophila toolkit. Not only the raw number of available lines contribute to the relevance of this tool in the "technical landscape" of genetic tools, but additional features of this effort contribute to the successful adoption. These include:

(1) A description of expression patterns in the adult and larvae, expanding the "audience" for these tools<br /> (2) A classification of line combination according to quality levels, which provides a relevant criterion while deciding to use a particular set of "splits".<br /> (3) Discrimination between male and female expression patterns, providing hints regarding the potential role of these gender-specific circuits.<br /> (4) The search engine seems to be user-friendly, facilitating the retrieval of useful information.<br /> (5) An acknowledgement of the caveats and challenges that splits (like any other genetic tool) can carry.<br /> Overall, the authors employed a pipeline that maximizes the potential of the Split-GAL4 collection to the scientific community.

Weaknesses:

My concerns were resolved regarding the existence of caveats while using these tools that researchers should be aware of, particularly those using them for the first time.

Reviewer #2 (Public review):

Summary:

This manuscript describes the creation and curation of a collection of genetic driver lines that specifically label small numbers of neurons, often just a single to handful of cell types, in the central nervous system of the fruit fly, Drosophila melanogaster. The authors screened over 77,000 split hemidriver combinations to yield a collection of 3060 lines targeting a range of cell types in the adult Drosophila central nervous system and 1373 lines characterized in third-instar larvae. These genetic driver lines have already contributed to several important publications and will no doubt continue to do so. It is a truly valuable resource that represents the cooperation of several labs throughout the Drosophila community.

Strengths:

The authors have thoughtfully curated and documented the lines that they have created, so that they may be maximally useful to the greater community. This documentation includes confocal images of neurons labeled by each driver line and when possible, a list of cell types labeled by the genetic driver line and their identity in an EM connectome dataset. The authors have also made available some information from the other lines they created and tested but deemed not specific or strong enough to be included as part of the collection. This additional resource will be a valuable aid for those seeking to label cell types that may not be included in the main collection.

The added revisions help to clarify important points relating to the creation of the lines, which lines were included as part of this specific collection, and caveats to be mindful of when using any of the described lines. These revisions will increase the manuscript's utility to users who may be less familiar with this resource.

Weaknesses:

The major weakness, which is also in some ways a strength, is the stringent requirement that lines that be included be highly specific across the CNS. As a result, the lines that are part of this specific collection are sparse and specific but also limited in which cell types they cover. Doubtless there are many missing cell types.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Meissner et al describe an update on the collection of split-GAL4 lines generated by a consortium led by Janelia Research Campus. This follows the same experimental pipeline described before and presents as a significant increment to the present collection. This will strengthen the usefulness and relevance of "splits" as a standard tool for labs that already use this tool and attract more labs and researchers to use it.

Strengths:

This manuscript presents a solid step to establish Split-GAL4 lines as a relevant tool in the powerful Drosophila toolkit. Not only does the raw number of available lines contribute to the relevance of this tool in the "technical landscape" of genetic tools, but additional features of this effort contribute to the successful adoption. These include:

(1) A description of expression patterns in the adult and larvae, expanding the "audience" for these tools

(2) A classification of line combination according to quality levels, which provides a relevant criterion while deciding to use a particular set of "splits".

(3) Discrimination between male and female expression patterns, providing hints regarding the potential role of these gender-specific circuits.

(4) The search engine seems to be user-friendly, facilitating the retrieval of useful information.

Overall, the authors employed a pipeline that maximizes the potential of the Split-GAL4 collection to the scientific community.

Weaknesses:

The following aspects apply:

The use of split-GAL4 lines has improved tremendously the genetic toolkit of Drosophila and this manuscript is another step forward in establishing this tool in the genetic repertoire that laboratories use. Thus, this would be a perfect opportunity for the authors to review the current status of this tool, addressing its caveats and how to effectively implement it into the experimental pipeline.

(1) While the authors do bring up a series of relevant caveats that the community should be aware of while using split-GAL4 lines, the authors should take the opportunity to address some of the genetic issues that frequently arise while using the described genetic tools. This is particularly important for laboratories that lack the experience using split-GAL4 lines and wish to use them. Some of these issues are covertly brought up, but not entirely clarified.

First, why do the authors (wisely) rescreen the lines using UAS-CsChrimson-mVenus? One reason is that using another transgene (such as UAS-GFP) and/or another genomic locus can drive a different expression pattern or intensities. Although this is discussed, this should be made more explicit and the readers should be aware of this.

Second, it would be important to include a discussion regarding the potential of hemidriver lines to suffer from transvection effects whenever there is a genetic element in the same locus. These are serious issues that prevent a more reliable use of split-GAL4 lines that, once again, should be discussed.

We added additional explanatory text to the discussion.

(2) The authors simply mention that the goal of the manuscript is to "summarize the results obtained over the past decade.". A better explanation would be welcomed in order to understand the need of a dedicated manuscript to announce the availability of a new batch of lines when previous publications already described the Split-GAL4 lines. At the extreme, one might question why we need a manuscript for this when a simple footnote on Janelia's website would suffice.

We added an additional mention of the cell type split-GAL4 collection at the relevant section and added more emphasis on the curation process adding value to the final selections. We feel that the manuscript is useful to document the methods used for the contained analysis and datasets and gives a starting point to the reader to go through the many split-GAL4 publications and images.

Reviewer #2 (Public Review):

Summary: This manuscript describes the creation and curation of a collection of genetic driver lines that specifically label small numbers of neurons, often just a single to handful of cell types, in the central nervous system of the fruit fly, Drosophila melanogaster. The authors screened over 77,000 split hemidriver combinations to yield a collection of 3060 lines targeting a range of cell types in the adult Drosophila central nervous system and 1373 lines characterized in third-instar larvae. These genetic driver lines have already contributed to several important publications and will no doubt continue to do so. It is a truly valuable resource that represents the cooperation of several labs throughout the Drosophila community.

Strengths:

The authors have thoughtfully curated and documented the lines that they have created, so that they may be maximally useful to the greater community. This documentation includes confocal images of neurons labeled by each driver line and when possible, a list of cell types labeled by the genetic driver line and their identity in an EM connectome dataset. The authors have also made available some information from the other lines they created and tested but deemed not specific or strong enough to be included as part of the collection. This additional resource will be a valuable aid for those seeking to label cell types that may not be included in the main collection.

Weaknesses:

None, this is a valuable set of tools that took many years of effort by several labs. This collection will continue to facilitate important science for years to come.

We thank the reviewer for their positive feedback.

Reviewer #3 (Public Review):

Summary:

The manuscript by Meissner et al. describes a collection of 3060 Drosophila lines that can be used to genetically target very small numbers of brain cells. The collection is the product of over a decade of work by the FlyLight Project Team at the Janelia Research Campus and their collaborators. This painstaking work has used the intersectional split-Gal4 method to combine pairs of so-called hemidrivers into driver lines capable of highly refined expression, often targeting single cell types. Roughly one-third of the lines have been described and characterized in previous publications and others will be described in manuscripts still in preparation. They are brought together here with many new lines to form one high-quality collection of lines with exceptional selectivity of expression. As detailed in the manuscript, all of the lines described have been made publicly available accompanied by an online database of images and metadata that allow researchers to identify lines containing neurons of interest to them. Collectively, the lines include neurons in most regions of both the adult and larval nervous systems, and the imaging database is intended to eventually permit anatomical searching that can match cell types targeted by the lines to those identified at the EM level in emerging connectomes. In addition, the manuscript introduces a second, freely accessible database of raw imaging data for many lower quality, but still potentially useful, split-Gal4 driver lines made by the FlyLight Project Team.

Strengths:

Both the stock collection and the image databases are substantial and important resources that will be of obvious interest to neuroscientists conducting research in Drosophila. Although many researchers will already be aware of the basic resources generated at Janelia, the comprehensive description provided in this manuscript represents a useful summary of past and recent accomplishments of the FlyLight Team and their collaborators and will be very valuable to newcomers in the field. In addition, the new lines being made available and the effort to collect all lines that have been generated that have highly specific expression patterns is very useful to all.

Weaknesses:

The collection of lines presented here is obviously somewhat redundant in including lines from previously published collections. Potentially confusing is the fact that previously published split-Gal4 collections have also touted lines with highly selective expression, but only a fraction of those lines have been chosen for inclusion in the present manuscript. For example, the collection of Shuai et al. (2023) describes some 800 new lines, many with specificity for neurons with connectivity to the mushroom body, but only 168 of these lines were selected for inclusion here. This is presumably because of the more stringent criteria applied in selecting the lines described in this manuscript, but it would be useful to spell this out and explain what makes this collection different from those previously published (and those forthcoming).

We added more description of how this collection is focused on the best cell-type-specific lines across the CNS. An important requirement for inclusion was this degree of specificity across the CNS, while many prior publications had a greater emphasis on lines with a narrower focus of specificity.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Luckily for us, genetics is for the most part an exact science. However, there's still some "voodoo" in a lot of genetic combinations that the authors should disclose and be as clear as possible in the manuscript. This allows for the potential users to gauge expectations and devise a priori alternative plans.

We attempted to comprehensively cover the caveats inherent in our genetic targeting approach.

Minor points:

(1) The authors mention that fly age should be controlled as expression can vary. Is there any reference to support this claim?

We added a reference describing driver expression changes over development.

(2) There should be a citation for "Flies were typically 1-5 days old at dissection for the cell type collection rescreening, 1-8 days old for other non-MCFO crosses and 3-8 days old for MCFO".

We clarified that these descriptions were of our experimental preparations, not describing other citable work.

Reviewer #3 (Recommendations For The Authors):

General Points:

Overall, the manuscript is very clear, but there are a couple of points where more explicit information would be useful. One of these is with respect to the issue of selectivity of targeting. The cell type specificity of lines is often referred to, but cell types can range from single pairs of neurons to hundreds of indistinguishable neurons with similar morphology and function. It would be useful if the authors explained whether their use of the term "cell type" distinguishes cell type from cell number. It would also be useful if lines that target many neurons of a single cell type were identified.

We added further discussion of cell types vs. cell numbers. Our labeling strategy was not optimized for counting cell numbers labeled by each line. We believe EM studies are best positioned to comprehensively evaluate the number of cells making up each type.

The second point relates to vagueness about the intended schedule for providing resources that will match (or allow matching of) neurons to the connectome. For example, on pp. 5-6 it is stated that: "In the future all of the neurons in these lines will be uniquely identified and linked to neurons reconstructed in the electron microscopy volume of the larva" but no timeline is provided. Similarly, for the adult neurons it is stated on p. 4 that: "Anatomical searching for comparison to other light microscopy (LM) and EM data is being made available." A more explicit statement about what resources are and are not yet available, a timeline for full availability, and an indication of how many lines currently have been matched to EM data would be helpful.

During the review and revision period we have made progress on processing the images in the collection. We updated the text with the current status and anticipated timeline for completion.

Specific Points:

p. 4 "Although the lines used for these comparisons are not a random sample, the areas of greatest difference are in the vicinity of previously described sexual dimorphisms..." In the vicinity of is a very vague statement of localization. A couple of examples of what is meant here would be useful.

We added example images to Figure 3.

p. 5 "...may have specific expression outside our regions of interest." It's not clear what "our regions of interest" refers to here. Please clarify.

We clarified that we were referring to the regions studied in the publications listed in Table 1.

p. 5 "...lines that were sparse in VNC but dirty in the brain or SEZ..." A more quantitative descriptor than "dirty" would be helpful.

We unfortunately did not quantify the extent of undesired brain/SEZ expression, but attempted to clarify the statement.

p. 6 "...the images are being made instantly searchable for LM and EM comparisons at NeuronBridge..." Here again it is hard to know what is meant by "being made instantly searchable." How many have been made searchable and what is the bottleneck in making the rest searchable?

We updated the text as described above. The bottleneck has been available processing capacity for the hundreds of thousands of included images.

Figure 1 Supplemental File 2: The movie is beautiful, but it seems more useful as art than as a reference. Perhaps converting it to a pdf of searchable images for each line would make it more useful.

We replaced the movie with a searchable PDF.

Fig. 2(B) legend: "Other lines may have more than two types." It is not clear what "other lines" are being referred to.

As part of making the quality evaluation more robust, we scored lines for the clear presence of three or more cell types. We updated the text accordingly.

Fig. 2(C): Presumably the image shown is an example of variability in expression rather than weakness, but it is hard to know without a point of comparison. Perhaps show the expression patterns of other samples? Or describe briefly in the legend what other samples looked like?

We added Figure 2 - figure supplement 1 with examples of variable expression in a split-GAL4 line.

eLife Assessment

This important study reports on PI3KR mutations and a paradoxical mechanism of PI3KR signaling. The strength of evidence for the study is mostly convincing, as conclusions are supported by a variety of mutational strategies and cellular systems to look at interactions among signaling pathways.

Reviewer #1 (Public review):

Summary:

This study provides convincing data showing that expression of the PIK3R1(deltaExon11) dominant negative mutation in Activated PI3K Delta Syndrome 1/2 (APDS1/2) patient-derived cells reduces AKT activation and p110δ protein levels. Using a 3T3-L1 model cell system, the authors show that overexpressed p85α(deltaExon 11) displays reduced association with the p110α catalytic subunit but strongly interacts with Irs1/2. Overexpression of PIK3R1 dominant negative mutants inhibit AKT phosphorylation and reduce cellular differentiation of preadipocytes. The experimental design, interpretation, and quantification broadly support the authors' conclusions, which establishes a new paradigm that warrants future studies.

Strengths:

The strength of this study is the clear results derived from Western blots analysis of cell signaling markers (e.g. pAKT1), and co-immunoprecipitation of PI3K holoenzyme complexes and associated regulatory factors (e.g. Irs1/2). The authors analyze a variety of PIK3R1 mutants (i.e. deltaExon11, E489K, R649W, and Y657X), which reveals a range of phenotypes that support the proposed model for dominant negative activity. The use of clonal cell lines with doxycycline induced expression of the PIK3R1 mutants (deltaExon 11, R649W, and Y657X) provides convincing experimental data concerning the relationship between p85α mutant expression and AKT phosphorylation in vivo. This approach for overexpression is excellent and should be utilized more broadly by cell biologists. The authors convincingly show that p85α(deltaExon11, R649W, or Y657X) is unable to associate with p110α but instead more strongly associates with Irs1/2 compared to wild type p85α. Overall, this article does a great job of motivating future studies of SHORT and APDS2 PIK3R1 mutants expressed from their endogenous loci (e.g. knock-in mice).

Weaknesses:

The limitations for this study lie in the complexity of the cell signaling pathway under investigation, rather than a lack of rigor by the authors. Future experimentation will help reconcile the cell type specific differences (e.g. APDS2 patient derived cells vs. the 3T3-L1 cell model system) in PIK3R1 mutant behavior reported by the authors. This is also intimately linked to variable expression of PIK3R1 mutants and cell-type specific regulatory factors. Although beyond the scope of this work, an unbiased proteomic study that broadly evaluates the cell signaling landscape could provide a more holistic understanding of the APDS2 and SHORT mutants compared to a candidate-based approach. Additional structural biochemistry of the p110α/p85α(deltaExon 11) complex is needed to explain why PIK3R1 mutant regulatory subunits do not strongly associate with the p110 catalytic subunit. A more comprehensive biochemical analysis of p110α/p85α, p110β/p85α, and p110δ/p85α mutant protein complexes will also be necessary to explain various cell signaling phenotypes. A minor limitation of this study is the use of single end point assays to measure PI3K lipid kinase activity in the presence of one regulatory input (i.e. RTK-derived pY peptide). An expanded biochemical analysis of purified mutant PI3K complexes across the canonical membrane signaling landscape will be important for deciphering how competition between wild-type and mutant regulatory subunits are regulated in different cell signaling contexts.

Reviewer #2 (Public review):

Patsy R. Tomlinson et al; investigated the impact of different p85 alpha variants associated with SHORT syndrome or APDS2 on insulin mediated signaling in dermal fibroblasts and preadipocytes. They perform this study as APDS2 patients oftern present with features of SHORT syndrome. They found no evidence of hyperactive PI3K signalling monitored by pAKT in a APDS2 patient-derived dermal fibroblast cells. In these cells p110 alpha protein levels were comparable to levels in control cells, however, p110 delta protein levels were strongly reduced. Remarkably, the truncated APDS2-causal p85 alpha variant was less abundant in these cells than p85 alpha wildtype. Afterwards they studied the impact of ectopically expressed p85 alpha variants on insulin mediated PI3K signaling in 3T3-L1 preadipocytes. Interestingly they found that the truncated APDS2-causal p85 alpha variant impaired insulin induced signaling. Using immunoprecipitation of p110 alpha they did not find truncated APDS2-causal p85 alpha variant in p110 alpha precipitates. Furthermore, by immunoprecipitating IRS1 and IRS2 they observed that the truncated APDS2-causal p85 alpha variant was very abundant in IRS1 and IRS2 precipitates, even in the absence of insulin stimulation. These important findings add in an interesting way possible mechanistic explanation for the growing number of APDS2 patients described with features of SHORT syndrome.

Strengths:

Based on state-of-the-art functional studies, the authors show that the p85 alpha variant responsible for APDS2, known to be associated with increased PI3K-delta signaling, can attenuate PI3K-alpha signalling in preadipocytes, providing a possible mechanistic explanation for the growing number of APDS2 patients with features of SHORT syndrome.

Weaknesses:

The proposed paradigm is based on one cell line derived from an APDS2 patient and an overexpressing system. The investigation of a larger number of cell lines derived from APDS2 patients would further substantiate the conclusion.

Author response:

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

eLife Assessment

The authors identify new mechanisms that link a PIK3R1 mutant to cellular signaling and division in Activated PI3 Kinase Delta Syndrome 1 and 2 (APDS1/2). The conclusion that this mutant serves as a dominant negative form of the protein, impacting PI3K complex assembly and IRS/AKT signaling, is important, and the evidence from constitutive and inducible systems in cultured cells is convincing. Nevertheless, there are several limitations relating to differences between cell lines and expression systems, as well as more global characterization of the protein interaction landscape, which would further enhance the work.

We are pleased by this fair assessment, while noting that this work relates to APDS2 (PIK3R1-related) rather than APDS1 (PIK3CD-related). Our findings we believe are clear, but the observation that studies including more global proteomics/phosphoproteomics in cells expressing mutants at endogenous levels would add further insight is well made. We hope that this report may motivate such studies by laboratories with wider access to primary cells from patients and knock-in mice.

Public Reviews

Reviewer #1 (Public Review):

Summary:

This study provides convincing data showing that expression of the PIK3R1(delta Exon11) dominant negative mutation in Activated PI3K Delta Syndrome 1/2 (APDS1/2) patient-derived cells reduces AKT activation and p110δ protein levels. Using a 3T3-L1 model cell system, the authors show that overexpressed p85α delta Exon 11) displays reduced association with the p110α catalytic subunit but strongly interacts with Irs1/2. Overexpression of PIK3R1 dominant negative mutants inhibits AKT phosphorylation and reduces cellular differentiation of preadipocytes. The strength of this article is the clear results derived from Western blots analysis of cell signaling markers (e.g. pAKT1), and co-immunoprecipitation of PI3K holoenzyme complexes and associated regulatory factors (e.g. Irs1/2). The experimental design, interpretation, and quantification broadly support the authors' conclusions.

Strengths:

The authors analyze a variety of PIK3R1 mutants (i.e. delta Exon11, E489K, R649W, and Y657X), which reveals a range of phenotypes that support the proposed model for dominant negative activity. The use of clonal cell lines with doxycycline-induced expression of the PIK3R1 mutants (DExon 11, R649W, and Y657X) provides convincing experimental data concerning the relationship between p85α mutant expression and AKT phosphorylation in vivo. The authors convincingly show that p85α delta Exon11, R649W, or Y657X) is unable to associate with p110α but instead more strongly associates with Irs1/2 compared to wild type p85α. This helps explain why the authors were unable to purify the recombinant p110α/p85α delta Exon 11) heterodimeric complex from insect cells.

Weaknesses:

Future experimentation will be needed to reconcile the cell type specific differences (e.g. APDS2 patient-derived cells vs. the 3T3-L1 cell model system) in PIK3R1 mutant behavior reported by the authors.

This is a fair comment. It has been established for many years that relative protein levels even of wild type PIK3CA and PIK3R1 gene products influence sensitivity of PI3K to growth factor stimulation. Such issues of stoichiometry become exponentially more complicated when the numerous potential interactions among the full repertoire of Class 1 PI3K regulatory subunits (3 splice variants of PIK3R1, and also PIK3R2 and PIK3R3) and corresponding catalytic subunits (PIK3CA, PIK3CB, PIK3CD) are considered, and when different activities and stabilities of PIK3R1 mutants are added to the mix. It thus seems obvious to us that different levels of expression of different mutants in different cellular contexts will have different signalling consequences. We establish a paradigm in this paper using an overexpression system, and we strongly agree that this merits further investigation in a wider variety of primary cells (or cells with knock in at the endogenous locus), where available.

An unbiased proteomic study that broadly evaluates the cell signaling landscape could provide a more holistic understanding of the APDS2 and SHORT mutants compared to a candidate-based approach.

We agree. This would be highly informative, but we think would best be carried out in both “metabolic” and “immune” cells with endogenous levels of expression of SHORT or APDS2 PIK3R1 mutants. These are not all currently available to us, and require follow up studies.

Additional biochemical analysis of p110α/p85α delta Exon 11 complex is needed to explain why this mutant regulatory subunit does not strongly associate with the p110 catalytic subunit.

We agree. We present this observation in our overexpression system, which is clear and reproducible, even though somewhat surprising. The failure to bind p110a is likely not absolute, as sufficient p110a-p85a^DEx11 was synthesised in vitro in a prior study to permit structural and biochemical studies, although a series of technical workarounds were required to generate enough heterodimeric PI3K to study in vitro given the manifest instability of the complex, particularly when concentrated (PMID 28167755). We already note in discussion that p85a can homodimerize and bind PTEN, likely among other partners, and it may be that the APDS2 deletion strongly favours binding to proteins that effectively compete with p110a. However this requires further study of the wider interactome of the mutant PIK3R1, which, as noted above, are beyond the scope of the current study.

It remains unclear why p85α delta Exon 11 expression reduces p110δ protein levels in APDS2 patient-derived dermal fibroblasts.

We caution that we only had the opportunity to study dermal fibroblasts cultured from a single APDS2 patient, as noted in the paper, and so replication of this finding in future will be of interest. Nevertheless the observation is robust and reproducible in these cells, and we agree that this apparently selective effect on p110d  is not fully explained. Having said that, it has been observed previously that heterodimers of the DEx11 p85a variant with either p110a or p110d are unstable, and when the unstable complexes were eventually synthesised, p110a and p110d were demonstrated to show differences in engagement with the mutant p85, with greater disruption of inhibitory interactions observed for p110d (PMID 28167755). It is thus not a great stretch to imagine that as well as disinhibiting p110d more, the DEx11 p85a variant also destabilises the p85a-p110d complex more, potentially explaining its near disappearance in cells with low baseline p110d expression. Following on from the preceding question and response, however, is an alternative explanation, based on the 3T3-L1 overexpression studies in this paper, wherein we were unable to demonstrate binding of p110a by DEx11 p85a. If, in any given cellular context, the mutant p85 could bind p110d but not p110a, then the destabilising effect would be observed only for p110d. So in summary, we believe the selective effect on p110d is explained by differences in binding kinetics and heterodimer stability for different DEx11 p85a-containing complexes. The net effect of these differences may vary among cell types depending on relative levels of subunit expression.

This study would benefit from a more comprehensive biochemical analysis of the described p110α/p85α, p110β/p85α, and p110δ/p85α mutant protein complexes. The current limitation of this study to the use of a single endpoint assay to measure PI3K lipid kinase activity in the presence of a single regulatory input (i.e. RTK-derived pY peptide). A broader biochemical analysis of the mutant PI3K complexes across the canonical signaling landscape will be important for establishing how competition between wild-type and mutant regulatory subunits is regulated in different cell signaling pathways.

We agree that a wider analysis of upstream inputs and downstream network would be of interest, though as noted above the ultimate functional consequences of mutants will be an amalgam of any differential signalling effects of complexes that are stable enough to function, and differential effects of mutant p85a on the kinetics of distinct heterodimer assembly and stability. In this paper we seek to suggest a paradigm worthy of further, deeper assessment. We note that the search space here is large indeed (A. different cell types with differing profiles of PI3K subunit expression B. Multiple upstream stimuli and C. Multiple downstream outputs, with timecourse of responses an additional important factor to consider). These studies are realistically beyond the scope of the current work, but we hope that further studies, as suggested by the reviewer, follow.

Reviewer #2 (Public Review)

Summary:

Patsy R. Tomlinson et al; investigated the impact of different p85alpha variants associated with SHORT syndrome or APDS2 on insulin-mediated signaling in dermal fibroblasts and preadipocytes. They find no evidence of hyperactive PI3K signalling monitored by pAKT in APDS2 patient-derived dermal fibroblast cells. In these cells p110alpha protein levels were comparable to levels in control cells, however, the p110delta protein levels were strongly reduced. Remarkably, the truncated APDS2-causal p85alpha variant was less abundant in these cells than p85alpha wildtype. Afterwards, they studied the impact of ectopically expressed p85alpha variants on insulin-mediated PI3K signaling in 3T3-L1 preadipocytes. Interestingly they found that the truncated APDS2-causal p85alpha variant impaired insulin-induced signaling. Using immunoprecipitation of p110alpha they did not find truncated APDS2-causal p85alpha variant in p110alpha precipitates. Furthermore, by immunoprecipitating IRS1 and IRS2, they observed that the truncated APDS2-causal p85alpha variant was very abundant in IRS1 and IRS2 precipitates, even in the absence of insulin stimulation. These important findings add in an interesting way possible mechanistic explanation for the growing number of APDS2 patients described with features of SHORT syndrome.

Strengths:

Based on state-of-the-art functional investigation the authors propose indicating a loss-of-function activity of the APDS2-disease causing p85alpha variant in preadipocytes providing a possible mechanistic explanation for the growing number of APDS2 patients described with features of SHORT syndrome.

Weaknesses:

Related to Figure 1: PIK3R1 expression not only by Western blotting but also by quantifying the RNA transcripts, e.g. mutant and wildtype transcripts, was not performed. RNA expression analysis would further strengthen the suggested impaired stabilization/binding.

It is not completely clear to us how further PIK3R1 mRNA analysis would enhance the points we seek to make. Perhaps the reviewer’s point is that changes in protein expression could be explained by reduced transcription rather than having anything to do with altered protein turnover? As shown in Figure 1 supplemental figure 1, sequencing cDNA from each of the primary cell lines studied indicates that both mutant and WT alleles are expressed at or close to 50% of the total mRNA for PIK3CA or PIK3R1 as relevant. While this is not strictly quantitative, allied to prior evidence that these are dominant alleles which require to be expressed to exert their effect, with no evidence for altered mRNA expression of these variants in prior studies, we don’t believe any further quantification of mRNA expression would add value.

Related to Figure 2

As mentioned by the authors in the manuscript the expression of p110delta but also p110beta in 3T3-L1 preadipocytes ectopically expressing p85alpha variants has not been analyzed.

We agree that such determination would have been a useful addition to the study, but regretfully it was not undertaken in these modified 3T3-L1 cells at the time of study. However independent bulk RNAseq studies of the founder 3T3-L1 cells from which the stably transduced cells were generated, undertaken as part of an unrelated study, revealed the following relative levels of endogenous expression of PI3K subunit mRNA:

Author response table 1.

We have not determined endogenous protein expression, and so have left the text of the discussion unchanged, simply noting that we have not formally assessed protein expression of p110d/p110b. However these transcriptomic findings suggest that p110d protein is likely either undetectable, or else present at extremely low levels compared to endogenous p110a. p110b also appears to be expressed at a much lower level than p110a. In our studies overexpressing mutant PIK3R1 and assessing insulin action, we believe we are largely or perhaps entirely assaying the effect of the mutants on p110a, in keeping with the fact that genetic and pharmacological studies have firmly established that it is p110a that is responsible for mediating the metabolic actions of insulin in adipose tissue and preadipocytes including 3T3-L1 (e.g. PMID 16647110). Indeed, to quote from this study, in 3T3-L1 “… inhibitors of p110b (TGX-115 and TGX-286) and p110d (IC87114 and PIK-23) had no effect on the insulin-stimulated phosphorylation of any protein in the PI3-K pathway.”

We have added the following sentence to the discussion:

“The current study has limitations. We have studied primary cells from only a single APDS2 patient, and in the 3T3-L1 cell model, we did not determine whether p110d protein could be detected. If not, this could explain the lack of detectable AKT phosphorylation with induction of Pik3r1 DEx11.  Indeed, previous pharmacological studies in 3T3-L1 adipocytes has shown that selective inhibition of p110d or p110b does not alter insulin-induced phosphorylation of any protein studied in the PI3-K pathway, attesting to the dominance of p110a in insulin action in this cell model (Knight et al, 2006).” 

Furthermore, a direct comparison of the truncated APDS2-causal p85alpha variant with SHORT syndrome-causal p85alpha variants in regard to pAKT level, and p85alpha expression level has not been performed.

These investigations would further strengthen the data.

The cell lines conditionally expressing SHORT syndrome variants have been reported already, as cited (PMID: 27766312). Remarkably, the degree of inhibition of insulin-stimulated signalling is actually less pronounced for the SHORT syndrome variants than for the overexpressed APDS2 variant, as seen in the excerpt from the prior paper below. In this prior paper the maximum insulin concentration used, 100nM, was the concentration used in the current study. While overexpression of the APDS2 p85a variant ablated the response to insulin entirely, it is still seen in the prior study, albeit at a clearly reduced level.

Related to Figure 3

The E489K and Y657X p85alpha variants should be also tested in combination with p110delta in the PI3K activity in vitro assay. This would help to further decipher the overall impact, especially of the E489K variant.

We agree that this would make our data more complete, but for logistical reasons (primarily available personnel) we were compelled to constrain the number of p85-p110 combinations we studied. We elected to prioritise the PIK3R1 R649W variant as by far the most common causal SHORT syndrome variant, and as the variant showing the “cleanest” functional perturbation, namely severely impaired or absent ability to dock to phosphotyrosines in cognate proteins.  The paradox that we sought to explain in this paper, namely the phenotypic combination of gain-of-function APDS2 with loss-of-function SHORT syndrome features holds only for APDS2 PIK3R1 variants, and so while it is interesting to document that the canonical SHORT syndrome variant also inhibits PI3Kb and PI3Kd activation in vitro, this was not the main purpose of our study.

Reviewer #1 (Recommendations For The Authors):

Points of clarification and suggestions for improving the manuscript:

(1) Explain whether there are any PIK3R1-independent genetic alterations in the APDS2 and PROS-derived cell lines. For example, are there differences in the karyotype of mutant cell lines compared to wild-type cells?

Karyotypic abnormalities are not an established feature of either PROS or APDS2, and the patients from whom cells were derived were documented to be of normal karyotype. Karyotypic abnormalities acquired during cell culture would not be unprecedented, but confirming normal karyotypes in primary cell lines where there is no specific reason to suppose any alteration exceeds normal expectations for primary cell studies, and so this has not been undertaken.

(2) When introducing the APDS2-associated PIK3R1 mutation (lines 126-128), the authors describe both the exon 11 skipping and in-frame deletions. I recommend rewording this sentence to say exon 11 skipping results in an in-frame deletion of PIK3R1. The current wording makes it seem like APDS2-derived cells contain two genetic perturbations: (1) exon 11 skipping and (2) in-frame deletion. Include a diagram in Figure 1 to help explain the location of the mutations being studied in relationship to the PIK3R1 gene sequence and domains (i.e. nSH2, iSH2, cSH2). The description of the exon 11 skipping and in-frame deletions (lines 126-128) would benefit from having a complementary figure that diagrams the location of these mutations in the PIK3R1 gene.

On review we agree that clarity of description could be enhanced. We have now edited these lines as follows:

“We began by assessing dermal fibroblasts cultured from a previously described woman with APDS2 due to the common causal PIK3R1 mutation. This affects a splice donor site and causes skipping of exon 11, leading to an in-frame deletion of 42 amino acids (434-475 inclusive) in the inter-SH2 domain, which is shared by all PIK3R1 isoforms (Patient A.1 in (Lucas et al., 2014b))(Figure 1 figure supplement 1).”

We have moreover introduced a further figure element including a schematic of all PIK3R1 mutations reported in the current study (new Figure 1 figure supplement 1)

(3) For Figure 2, I recommend including a cartoon that illustrates the experimental design showing the induced expression of PIK3R1 mutants, R649W and Y657X, in the background of the wild-type endogenous gene expression.

Such a figure element has now been generated and included as Figure 2 figure supplement 1, duly called out in the results section where appropriate.

(4) For the data plotted in Figure 1B-1C, please clarify whether the experiments represent a single patient or all 3-4 patients shown in Figure 1A.

Each datapoint shown represents one of the patients in the immunoblots, with all patients included. Each point in turn is the mean from 3 independent experiments. We have added the following to the Figure legend:

“(B)-(E) quantification of immunoblot bands from 3 independent experiments shown for phosphoAKT-S473, phosphoAKT-T308, p110d and p110a respectively. Each point represents data from one of the patient cell lines in the immunoblots. Paired datapoints +/- insulin are shown in (B) and (C), and dotted lines mark means.”

(5) I recommend rewording the following sentence: "Given this evidence that APDS2-associated PIK3R1 delta Exon 11 potently inhibits PI3Kα when overexpressed in 3T3-L1 preadipocytes," to say "... potently inhibits PI3Kα signaling when overexpressed in 3T3-L1 preadipocytes." The data shown in Figures 1 and 2 do not support a direct biochemical inhibition of PI3Kα lipid kinase activity by p85α (delta Exon 11).

This edit has been made.

(6) Provide more discussion concerning the percentage of humans with APDS2 or SHORT syndrome that contain the mutations discussed in this paper. How strong is the genotype-phenotype link for these diseases? Are these diseases inherited or acquired through environmental stresses?

Both APDS2 and SHORT syndrome are very well established, highly penetrant and stereotyped monogenic disease. APDS is defined by the presence of activating PIK3R1 mutations such as the one studied here (by far the commonest causal mutation).  SHORT syndrome clinically has some superficial resemblance to other human genetic syndrome including short stature, but when careful attention is paid to characteristic features it is nearly universally attributable to loss-of-function PIK3R1 mutations with the single exception of one case in which a putatively pathogenic PKCE mutation was described (PMID: 28934384). Although both syndromes are monogenic it is often not accurate to refer to them as inherited, as, particularly in SHORT syndrome, de novo mutations (i.e. not found in either parent) are common. Environmental modifiers of phenotypes have not been described. To the introduction has now been added the comment that both conditions are highly penetrant and monogenic.

(7) The data presented in Figure 5 would benefit from additional discussion and citations that describe the molecular basis of the interaction between PI3K and Irs1/2. What studies have previously established this is a direct protein-protein interactions? Are there PI3K mutants that don't interact with Irs1/2 that can be included as a negative control? Alternatively, the authors can simply reference other papers to support the mechanism of interaction.

There is a voluminous literature dating back to the early 1990s documenting the mode of interaction of PI3K with Irs1/2. Relevant papers have now been cited as requested:

p85-Irs1 binding: PMID 1332046 (White lab, PNAS 1992)

p85-Irs2 binding: PMID 7675087 (White lab, Nature 1995)

“This may be important, as p85a mediates recruitment of PI3K to activated tyrosine kinase receptors and their tyrosine phosphorylated substrates, including the insulin-receptor substrate proteins Irs1 (PMID 1332046) and Irs2 (PMID 7675087).”

Regarding PI3K mutants that don't interact with Irs1/2, the SHORT syndrome mutant R649W which we include in this study is perhaps the best example of this, so it is both disease-causing and functions as such a negative control.

(8) To see the effect of the dominant negative delta Exon 11, the truncated p85α needs to be super stoichiometric to the full-length p85α (Figure 2 - Supplemental Figure 2). This is distinct from the results in Figure 1 showing the ADPS2-derived dermal fibroblast express 5-10x lower levels of p85α delta Exon 11 compared to full-length p85α (Figure 1A), but still strongly inhibits pAKT S473 and T308 (Figure 1B-1C). The manuscript would benefit from more discussion concerning the cell type specific differences in phenotypes. Alternatively, do the APDS2-derived dermal fibroblasts have other genetic perturbations that are not accounted for that potentially modulate cell signaling differently compared to 3T3-L1 preadipocytes?

The reviewer is astute to point out this apparent contrast. First of all, we have no reason to suppose there is any specific, PI3K-modifying genetic perturbation present in the primary dermal fibroblasts studied, although of course the genetic background of these cells is very distinct to that of 3T3-L1 mouse embryo fibroblasts. Related to such background differences, however, substantial variability is usually apparent in insulin-responsiveness even of healthy control dermal fibroblasts. This means that caution should be exercised in extrapolating from studies of the primary cells of a single individual. To illustrate this, we point the reviewer to our 2016 study in which we extensively studied the dermal fibroblasts of a proband with SHORT syndrome due to PIK3R1 Y657X:

From this study we conclude that A. WT controls show quite substantial variation in insulin-stimulated AKT phosphorylation and B. even the SHORT syndrome p85a Y657X variant, expressed at higher levels that WT p85a in dermal fibroblasts, does not produce an obvious decrease in insulin-stimulated AKT phosphorylation, despite extensive evidence from other human cell studies and knock-in mice that it does indeed impaired insulin action in metabolic tissues. For both these reasons we are not convinced that the lower insulin-induced AKT phosphorylation we described in Figure 1 should be overinterpreted until reproduced in other studies with primary cells from further APDS2 patients. This is why we did not comment more extensively on this. We now add the following qualifier in results:

“Despite this, no increase in basal or insulin-stimulated AKT phosphorylation was seen in APDS2 cells compared to cells from wild-type volunteers or from people with PROS and activating PIK3CA mutations H1047L or H1047R (Fig 1A-C, Fig 1 figure supplement 3A,B). Although insulin-induced AKT phosphorylation was lower in fibroblasts from the one APDS2 patient studied compared to controls, we have previously reported extensive variability in insulin-responsiveness of primary dermal fibroblasts from WT controls. Moreover even primary cells from a patient expressing high levels of the SHORT syndrome-associated p85a Y657X did not show attenuated insulin action, so we do not believe the reduced insulin action in APDS2 cells in the current study should be overinterpreted until reproduced in further APDS2 cells.”

Nevertheless we remind the reviewer that the main purpose of our primary cell experiment was to determine if there were any INCREASE in basal PI3K activity, or any difference in p110a or p110d protein levels, and we regard our findings in these regards to be clear.

The manuscript would benefit from additional explanation concerning why the E489K, R649W, and Y657X are equivalent substitutes for the characterization of p110α/p85α delta Exon 11). Perhaps a more explicit description of these mutations in relationship to the location of p85α delta Exon 11) mutation would help. I recommend including a diagram in Figure 3 showing the position of the delta Exon 11, E489K, R649W, and Y657X mutations in the PIK3R1 coding sequence. B. Also, please clarify whether all three holoenzyme complexes were biochemically unstable (i.e. p110α/p85α, p110β/p85α, p110δ/p85α) when p85α delta Exon 11) was expressed in insect cells.

A. Whether or not E489K, R649W and Y657X are “equivalent” to the APDS2 mutant is not really a meaningful issue here. These mutants are being studied because they cause SHORT syndrome without immunodeficiency, while the APDS2 mutant causes APDS2 often with features of SHORT syndrome. That is, it is naturally occurring mutations and the associated genotype-phenotype correlation that we seek to understand. Of the 3 SHORT syndrome causal mutations chosen, R649W is by far the commonest, effectively preventing phosphotyrosine binding, Y657X has the interesting attribute that it can be discriminated from full length p85 on immunoblots due to its truncation, and is moreover a variant that we have studied in cells and mice before, while the rarer E489K is an interesting SHORT syndrome variant as it is positioned more proximally in the p85a protein than most SHORT syndrome causal variants. All variants studied are now illustrated in the new Figure 1 figure supplement 1. B. Regarding stability of PI3K heterodimers containing the APDS2 p85a variant, we tried extensively to purify p110a and p110d complexes without success despite several approaches to optimise production. We did not try to synthesise the p110b-containing complex.

(10) I recommend presenting the results in Figure 4 before Figure 3 because it provides a good rationale for why it's difficult to purify the p110α/p85α delta Exon 11) holoenzyme from insect cells.

This would be true of p110d were studied in Figure 4 but it is not. Figure 4 looks instead at effects on p110a of heterologous overexpression of mutant p85, is a natural lead in to the ensuing figures 5 and 6, and we do not agree it would add value or enhance flow to swap Figures 3 and 4.

(11) The authors show that overexpression of the p85α delta Exon 11) did not result in p110α/p85α delta Exon 11) complex formation based on co-immunoprecipitation. Do the authors get the same result when they co-immunoprecipitation p110α/p85α and p110δ/p85α in the APDS2-derived dermal fibroblasts used in Figure 1A?

This is an interesting question but not an experiment we have done. It is not unfeasible, but generating enough cells to undertake IP experiments of this nature in dermal fibroblasts is a significant undertaking, and with finite resources available and only one primary cell line to study we elected not to pursue this.

Details in Methods section:

(1) Include catalog numbers and vendors for reagents (e.g. lipids, PhosSTOP, G-Dynabeads, etc.). There is not enough information provided to reproduce this work.

We have now added all vendors and catalogue numbers where relevant.

(2) Concerning the stated lipid composition (5/10/15/45/20/5 %) in the liposome preparation protocol. Please clarify whether these numbers represent molar percentages or mg/mL percentages.

We have now added that this is expressed as “(wt/vol)”

(3) What is the amino acid sequence of the PDGFR (pY2) peptide used for the PI3K activity assay?

This assay has been published and references with detailed methods are cited. For clarity, however we now say:

“PI(3,4,5)P3 production was measured by modified PI3-Kinase activity fluorescence polarisation assay (Echelon Biosciences, Salt Lake City, UT, USA). 10μL reactions in 384-well black microtitre plates used 1mM liposomes containing 50μM PI(4,5)P2, optimised concentrations of purified PI3K proteins, 100μM ATP, 2mM MgCl2, with or without 1μM tyrosine bisphosphorylated 33-mer peptide derived from mouse PDGFRβ residues 735-767, including phosphotyrosine at positions 740 and 751 (“pY2”; 735-ESDGGYMDMSKDESIDYVPMLDMKGDIKYADIE-767;  Cambridge peptides).”

(4) Include a Supplemental file containing a comprehensive description of the plasmids and coding sequencing used in this study.

Such a supplemental file has been created and is included as Table 2

Minor points of clarification, citations, and typos:

(1) Clarify why Activated PI3K Delta Syndrome 1 (APDS1) is thus named APDS2. See lines 71-72 of the introduction. Also see line 89: "...is common in APDS2, but not in APDS1." Briefly describe the difference between APDS1 and APDS2?

This is described in the introduction, but we apologise if our wording was not sufficiently clear. We have tried now to remove any ambiguity:

“Some PIK3R1 mutations reduce basal inhibition of catalytic subunits, usually due to disruption of the inhibitory inter-SH2 domain, and are found in cancers (Philp et al, 2001) and vascular malformations with overgrowth(Cottrell et al, 2021). In both diseases, hyperactivated PI3Ka, composed of heterodimers of PIK3R1 products and p110a, drives pathological growth. Distinct inter-SH2 domain PIK3R1 mutations, mostly causing skipping of exon 11 and deletion of residues 434-475, hyperactivate PI3Kd in immune cells, causing highly penetrant monogenic immunodeficiency (Deau et al, 2014; Lucas et al, 2014b). This phenocopies the immunodeficiency caused by genetic activation of p110d itself, which is named Activated PI3K Delta Syndrome 1 (APDS1) (Angulo et al, 2013; Lucas et al, 2014a). The PIK3R1-related syndrome, discovered shortly afterwards, is thus named APDS2.”

(2) Figure legend 1. Clarify reference to "Figure EV2".

(3) Figure legend 2. Clarify reference to "Figure EV3".

(4) Figure legend 3. Clarify reference to "Figure EV5".

Thank you for pointing out this oversight, arising from failure to update nomenclature fully between versions. “EV” figures actually are the figure supplements in the submission. All labels have now been updated.

(5) For Figure 1 - supplemental figure 1C, indicate experimental conditions on the blot (e.g. -/+ insulin).

This is now added

(6) Figure 4B, y-axis. Clarify how data was quantified. Perhaps reword "(% WT without DOX)" for clarity.

We have left the Y axis label as it is, but have added the following to the figure legend:

“(B) Quantification of immunoblot bands from immunoprecipitates from 3 independent experiments, expressed as a percentage relative to the intensity of the band in WT cells without doxycycline exposure.”

(7) In the results section (lines 117-124), please explicitly state whether the described mutations are homo- or heterozygous.

All mutations are heterozygous, as now explicitly stated

(8) I recommend spelling out the SHORT and APDS2 acronyms in the abstract to make this study more accessible.

We respectfully disagree that such spelling out in the abstract would improve accessibility. Both acronyms are clunky and wordy and are more likely to obscure meaning by squeezing out other words in the abstract. APDS is already spelled out in the introduction, and we now add the following for SHORT syndrome:

“More surprisingly, phenotypic overlap is reported between APDS2 and SHORT syndrome. SHORT syndrome, named for the characteristic developmental features (Short stature, Hyperextensibility, Hernia, Ocular depression, Rieger anomaly, and Teething delay) is caused by loss of PI3Ka function due to disruption of the phosphotyrosine-binding C-terminal SH2 domain (Chudasama et al, 2013; Dyment et al, 2013; Thauvin-Robinet et al, 2013).”

(9) I recommend explaining in more detail or rewording the following jargon/terms to make the writing more accessible to a broad audience: "reduced linear growth" (line 83) and "larger series" (line 86). I assume "reduced linear growth" is height.

Edited as follows:

“It  features short stature, insulin resistance, and dysmorphic features (Avila et al, 2016). In recent years, both individual case reports (Bravo Garcia-Morato et al, 2017; Petrovski et al, 2016; Ramirez et al, 2020; Szczawinska-Poplonyk et al, 2022) and larger case series (Elkaim et al, 2016; Jamee et al, 2020; Maccari et al, 2023; Nguyen et al, 2023; Olbrich et al, 2016; Petrovski et al., 2016) have established that many people with APDS2 have overt features of SHORT syndrome, while, more generally, linear growth impairment is common in APDS2, but not in APDS1.”

(10) For clarity, reword lines 214-215 to read, "No increase in p110α levels was seen on conditional overexpression of wild-type or R649W p85α."

Change made, thank you

(11) Figure 6A - Western blot label says, "657X" instead of "Y657X."

Now corrected

(12) Lines 214-215: For clarity, reword the sentence to say, "No increase in p110α was seen on conditional overexpression...".

REPEAT OF POINT 10 ABOVE

(13) Clarify what interactions are being competed for in the following statement: "... delta Ex11 may exert its inhibitory action by competing with PI3K holoenzyme" (lines 237-238). Are you referring to the interaction between p110α and p85α or the interaction between p110α/p85α and another protein?

We have endeavoured to clarify by editing as follows:

“As APDS2 p85a DEx11 does not appear to displace wild-type p85a from p110a despite strong overexpression, it is likely that there are high levels of truncated p85a unbound to p110a in the cell. This may be important, as p85a mediates recruitment of PI3K to activated tyrosine kinase receptors and their tyrosine phosphorylated substrates, including the insulin-receptor substrate proteins Irs1 and Irs2. Excess free regulatory subunits compete with heterodimeric PI3K holoenzyme for binding to these phosphotyrosines (Ueki et al., 2002), raising the possibility that excess free, truncated APDS2 p85a DEx11 may exert its inhibitory action similarly by outcompeting PI3K holoenzyme for phosphotyrosine binding.”

(14) Provide more information about the following statement and how it relates to the mutations in this study: "Homozygous truncating PIK3R1 mutations abolishing p85α expression while preserving p55α and p50α produce agammaglobulinaemia" (lines 271-272). The manuscript would benefit from a more explicit description of the nature of these mutations.

This wording seems to us to be explicit, however we agree that a schematic of PIK3R1 genotype-phenotype correlation, as requested elsewhere, would help readers. Such a schematic is now included as Figure 1 figure supplement 1.

(15) Typo on line 299: "unclike".

Corrected.

(16) The data presented in this study support a model in which p85α (DExon 11) expression functions as a dominant negative. Please clarify why in the discussion section you explain that p85α (DExon 11) activates PI3K. For example, "...skipping of exon 11, were shown in 2014 to activate PI3K..." (lines 290-291), "...activate PI3Kδ on one hand..." (line 309); "...APDS2 mutations in PIK3R1 has mixed consequences, producing greater hyperactivation of p110δ than p110α" (lines 354-355).

We do not entirely understand the reviewer’s question and thus request here. p85α (DExon 11) activates PI3Kd in immune cells and in vitro, and this is accepted, based on numerous reports, to be the mechanism underlying immunodeficiency. We do not challenge this, and cite evidence for any such claims in our report. The dominant negative activity we describe here towards PI3Ka activation is based not on inhibition of mutant-containing heterodimer, but rather on destabilisation of and/or competition with heterodimeric WT holoenzyme. This is the basis of the model we present; that is, a finely balanced competition between enzymic activation and mutant holoenzyme destabilisation and competition of mutant free p85a with WT holoenzyme, whose net effect likely differs among cells and tissues, most likely based on the repertoire and proportions of PI3K subunit expression. If the reviewer has specific suggestions for us that will make this point clearer still we should be happy to consider them.

(17) Provide references for the statements in lines 349-353 of the discussion.

This brief closing paragraph is a succinct recap and summary of the key points made throughout the manuscript and thoroughly referenced therein. We prefer to keep this section clean to maximise clarity, but are happy to copy references from the various other places in the manuscript to back up these assertions if this is preferred by the editorial team. Current text:

“In summary, it is already established that: A. genetic activation of PIK3CD causes immunodeficiency without disordered growth, while B. inhibition of PIK3R1 recruitment to RTKs and their substrates impairs growth and insulin action, without immunodeficiency, despite all catalytic subunits being affected and C. loss of p85 alone causes immunodeficiency.”

Reviewer #2 (Recommendations For The Authors):

In the abstract line 42 I would rather talk from SHORT syndrome like features.

Some patients do indeed meet the criteria for SHORT syndrome, but there is a spectrum. We have thus added this qualification and removed “short stature” to maintain the word count, as this is itself a SHORT syndrome-like feature.

Line 74 It would be helpful for the reader to give the amino-acid exchange and affected position of this single case.

We agree. Now added.

Furthermore, an illustration indicating the location of the different PIK3R1 variants on the p85 alpha level would be helpful for the reader.

As noted above such a figure element is now included as Figure 1 figure supplement 1 and duly called out in the text

The sentence in lines 298-300 makes no sense to me. Do you mean, unlike APDS1 murine models?

We agree, on review, that this paragraph is convoluted and makes a simple observation complex. We have rewritten now in what we hope is a more accessible style:

“Thus, study of distinct PIK3R1-related syndromes shows that established loss-of-function PIK3R1 mutations produce phenotypes attributable selectively to impaired PI3Ka hypofunction, while activating mutations produce phenotypes attributable to selectively increased PI3Kd signalling. Indeed, not only do such activating mutations not produce phenotypes attributable to PI3Ka activation, but they surprisingly have features characteristic of impaired PI3Ka function.”

Line 321 I propose including the notion of different cells: “The balance between expression and signalling in different cells may be a fine one ...”

This change has been made

Line 352 C. loss replace with complete loss.

“C.” actually denotes the last in a list after “A.” and “B.”. We have now used bold to emphasise this, but we imagine house style may dictate how we approach this.

eLife Assessment

This important study provides insights into the physiological role of RIPK1 in liver physiology, particularly during short-term fasting. The discovery that RIPK1 deficiency sensitizes the liver to acute injury and hepatocyte apoptosis is based on convincing evidence, highlighting the importance of RIPK1 in maintaining liver homeostasis under metabolic stress. The work will be of relevance to anyone studying liver pathologies.

Reviewer #1 (Public review):

This study presents an investigation into the physiological functions of RIPK1 within the context of liver physiology, particularly during short-term fasting. Through the use of hepatocyte-specific Ripk1-deficient mice (Ripk1Δhep), the authors embarked on an examination of the consequences of Ripk1 deficiency in hepatocytes under fasting conditions. They discovered that the absence of RIPK1 sensitized the liver to acute injury and hepatocyte apoptosis during fasting, a finding of significant interest given the crucial role of the liver in metabolic adaptation. Employing a combination of transcriptomic profiling and single-cell RNA sequencing techniques, the authors uncovered intricate molecular mechanisms underlying the exacerbated proinflammatory response observed in Ripk1Δhep mice during fasting. While the investigation offers valuable insights into the consequences of Ripk1 deficiency in hepatocytes during fasting conditions, there appears to be a primarily descriptive nature to the study with a lack of clear connection between the experiments. Thus, a stronger focus is warranted, particularly on understanding the dialogue between hepatocytes and macrophages. Moreover, the data would benefit from reinforcement through additional experiments such as Western blotting, flow cytometry, and rescue experiments, which would offer a more quantitative aspect to the findings. By incorporating these enhancements, the study could achieve a more comprehensive understanding of the underlying mechanisms and ultimately strengthen the overall impact of the research.

Comments on revision:

The authors have addressed my comments accordingly.

Reviewer #2 (Public review):

Summary:

Zhang et al. analyzed the functional role of hepatocyte RIPK1 during metabolic stress, particularly its scaffold function rather than kinase function. They show that Ripk1 knockout sensitizes the liver to cell death and inflammation in response to short-term fasting, a condition that would not induce obvious abnormality in wild-type mice.

Strengths:

The findings are based on a knockout mouse model and supported by bulk RNA-seq and scRNA-seq. The work consolidates the complex role of RIPK1 in metabolic stress.

Comments on revision:

The authors have addressed my concerns. The added experiments consolidated the findings. I do not have further comments.

Author response:

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

eLife Assessment

The study presents valuable findings on the role of RIPK1 in maintaining liver homeostasis under metabolic stress. Strengths include the intriguing findings that RIPK1 deficiency sensitizes the liver to acute liver injury and apoptosis, but because the conclusions require additional experimental support, the evidence is incomplete.

We are truly grateful, and wish to express our sincere acknowledgement to the reviewer and the editor for the time and effort spent in reviewing our manuscript. We highly appreciate the thorough and constructive comments, which can greatly improve our manuscript. We have conducted new experiments to address the reviewer’s concerns. We also carefully checked and changed our manuscript according to the constructive suggestions by the reviewer. Hopefully we have adequately addressed all the concerns. In the revised manuscript version, changes are highlighted in yellow. Please find the detailed point-to-point responses below. 

Public Reviews:

Reviewer #1 (Public Review):

This study presents an investigation into the physiological functions of RIPK1 within the context of liver physiology, particularly during short-term fasting. Through the use of hepatocyte-specific Ripk1-deficient mice (Ripk1Δhep), the authors embarked on an examination of the consequences of Ripk1 deficiency in hepatocytes under fasting conditions. They discovered that the absence of RIPK1 sensitized the liver to acute injury and hepatocyte apoptosis during fasting, a finding of significant interest given the crucial role of the liver in metabolic adaptation. Employing a combination of transcriptomic profiling and single-cell RNA sequencing techniques, the authors uncovered intricate molecular mechanisms underlying the exacerbated proinflammatory response observed in Ripk1Δhep mice during fasting. While the investigation offers valuable insights into the consequences of Ripk1 deficiency in hepatocytes during fasting conditions, there appears to be a primarily descriptive nature to the study with a lack of clear connection between the experiments. Thus, a stronger focus is warranted, particularly on understanding the dialogue between hepatocytes and macrophages. Moreover, the data would benefit from reinforcement through additional experiments such as Western blotting, flow cytometry, and rescue experiments, which would offer a more quantitative aspect to the findings. By incorporating these enhancements, the study could achieve a more comprehensive understanding of the underlying mechanisms and ultimately strengthen the overall impact of the research.

We thank the reviewer for the encouraging comments and helpful suggestions. We agree with the reviewer that additional experiments could reinforce our findings. Therefore, we conducted additional experiments including flow cytometry, western blotting, and using kinase-dead mutant mice to further investigate the underlying mechanisms. We carefully addressed every comment by the reviewer as indicated below.

Detailed major concerns:

(1) Related to Figure 1.

It is imperative to ensure consistency in the number of animals analyzed across the different graphs. The current resolution of the images appears to be low, resulting in unsharp visuals that hinder the interpretation of data beyond the presence of "white dots". To address this issue, it is recommended to enhance the resolution of the images and consider incorporating zoom-in features to facilitate a clearer visualization of the observed differences. Moreover, it would be beneficial to include a complete WB analysis for the cell death pathways analyzed. These adjustments will significantly improve the clarity and interpretability of Figure 1.

Thanks very much for the constructive advice. We carefully checked the number of animals and make sure that the animal number were consistent within different figures. We further updated the figures with incorporating zoom-in features in updated Figure 1, and the resolution of the figures were greatly improved. Western blot analysis were also included in updated Supplementary Figure 1.

(2) Related to Figure 2.

It is essential to ensure consistency in the number of animals analyzed across the different graphs, as indicated by n=6 in the figure legend (similar to Figure 1). Additionally, it is crucial to distinguish between male and female subjects in the dot plots to assess any potential gender-based differences, which should be consistent throughout the paper. To achieve this, the dots plot should be harmonized to clearly differentiate between males and females and investigate if there are any disparities between the genders. Moreover, it is imperative to correlate hepatic inflammation with the activation of Kupffer cells, infiltrating monocytes, and/or hepatic stellate cells (HSCs). Therefore, conducting flow cytometry would be instrumental in achieving this correlation. Additionally, the staining for Ki67 appears to be non-specific, showing a granular pattern reminiscent of bile crystals rather than the expected nuclear staining of hepatocytes or immune cells. It is crucial to ensure specific staining for Ki67, and conducting in vitro experiments on primary hepatocytes could further elucidate the proliferation process. These experiments are relatively straightforward to implement and would provide valuable insights into the mechanisms underlying hepatic inflammation and proliferation.

Thanks very much for the helpful advice. First, we corrected the number of animals analyzed in different graphs and make sure that the number of animals listed in the figure legend were consistent with the graphs in all figures. Second, to distinguish the results between male and female mice, blue represents male mice, pink represents female mice, and green represents RIPK1 kinase inactivated mice. The majority of results were obtained from male mice, and our results indicated that there was no difference between male and female mice herein.

The percentages of immune cell subpopulations isolated from mouse liver tissue were determined. The results were consistent with single cell analysis that greater number of  macrophages were recruited into the liver tissue in Ripk1^Δhep upon 12-hour fasting (updated Figure 4F&G).

To confirm the results of Ki67, we first detected the transcriptional expression of Ki67 using real-time qPCR, and the results were consistent with the protein expression measured by immunohistochemical analysis. The percentage of Ki67⁺ cells in liver cells were also detected, and there was significantly more Ki67⁺ cells in Ripk1^Δhep mouse liver than WT control mouse upon 12-hour fasting. Taken together, our transcriptional analysis, immunohistochemical analysis as well as flow cytometry data indicated that Ki67 expression was higher in Ripk1^Δhep mice than Ripk1^fl/fl mice. (updated Figure 2). 

(3) Related to Figure 3 & related to Figure 4.

The immunofluorescence data presented are not entirely convincing and are insufficient to conclusively demonstrate the recruitment of monocytes. Previous suggestions for flow cytometry studies remain pertinent and are indeed necessary to bolster the robustness of the data and conclusions. Conducting flow cytometry analyses would provide more accurate and quantitative assessments of monocyte recruitment, ensuring the reliability of the findings and strengthening the overall conclusions of the study. Regarding the single-cell RNA sequencing analysis presented in the manuscript, it's worth questioning its relevance and depth of information provided. While it successfully identifies a quantitative difference in the cellular composition of the liver between control and knockout mice, it may fall short in elucidating the intricate interactions between different cell populations, which are crucial for understanding the underlying mechanisms of hepatic inflammation. Therefore, I propose considering alternative bioinformatic analyses, such as CellPhone-CellChat, which could potentially provide a more comprehensive understanding of the cellular dynamics and interactions within the liver microenvironment. By examining the dialogue between different cell clusters, these analyses could offer deeper insights into the functional consequences of Ripk1 deficiency in hepatocytes and its impact on hepatic inflammation during fasting.

Thanks very much for the constructive suggestion. We agree with the reviewer that conducting flow cytometry analyses would provide accurate and quantitative assessments of monocyte recruitment, ensuring the reliability of the findings. Following the advice, both WT and Ripk1^Δhep mice were fasted for 12 hour and then single hepatic cells were isolated and analyzed by flow cytometry. As indicated in updated Figure 4F&G, the percentage of F4/80⁺CD11b⁺ cells were significantly higher in Ripk1^Δhep compared with WT control mice, confirming that more monocytes were recruited into the liver.

Additionally, we performed CellChat analysis on the single-cell transcriptomic data. As shown in updated Figures 4H-J, both the number of ligand-receptor pairs and the interaction strength among the eight cell types were significantly increased in Ripk1^Δhep mice, particularly the interactions between macrophages and other cell types. Network analysis indicated that inflammation and proliferation signals were amplified in Ripk1^Δhep mice. Consistent with the bulk RNA sequencing data, SAA signaling was upregulated in the hepatocytes of Ripk1^Δhep mice (updated Figure 4K). SAA has been found to play a role in regulating immune responses and tumor development. Based on these findings, we speculate that fasting-induced liver injury in RIPK1 knockout mice may exacerbate the inflammatory response in liver tissue through enhanced SAA signaling. The above data analysis and interpretation were included in the updated Figure 4&S4 and line 421 - 443.

(4) Related to Figure 5.

What additional insights do the data from Figure 5 provide compared to the study published in Nat Comms, which demonstrated that RIPK1 regulates starvation resistance by modulating aspartate catabolism (PMID: 34686667)?

Thank you very much for your constructive suggestion. As noted by the reviewer, this study (PMID: 34686667) primarily focuses on metabolomic analyses of Ripk1^-/- neonatal mouse brain tissue and Ripk1^-/- MEF cells. The authors propose that Ripk1 regulates starvation resistance by modulating aspartate catabolism.

In our study, the global metabolic changes induced by fasting were monitored. Fastinginduced lipolysis in peripheral adipose tissue leads to hepatic lipid accumulation, and excessive deposition of free fatty acids has been shown to induce endoplasmic reticulum (ER) stress in the liver. Data from Figure 5 demonstrate that administering the ER stress inhibitor 4-PBA effectively mitigated fasting-induced liver injury and inflammatory responses in Ripk1^Δhep mice. Our findings suggest that ER stress plays a critical role in fasting-induced liver injury and inflammation in Ripk1^Δhep mice.

(5) Related to Figure 6.

The data presented in Figure 7 are complementary and do not introduce new mechanistic insights.

Thank you very much for your insightful suggestion. As you mentioned, the AAV-TBG-Cre-mediated liver-specific RIPK1 knockout mice offer complementary validation of the results obtained from Ripk1^Δhep mice. Moreover, TBG is a promoter that is exclusively expressed in mature hepatocytes, while the ALB promoter is active not only in mature hepatocytes but also in precursor cells and cholangiocytes. Therefore, we think that the inclusion of AAV-TBG-Cre further strengthens our finding that RIPK1 in hepatocytes is responsible for fasting-induced liver injury and inflammatory responses.

(6) Related to Figure 7.

The data from Figure 7 suggest that RIPK1 in hepatocytes is responsible for the observed damage. However, it has been previously demonstrated that inhibition of RIPK1 activity in macrophages protects against the development of MASLD (PMID: 33208891). One possible explanation for these findings could be that the overreaction of macrophages to fasting, coupled with the absence of RIPK1 in hepatocytes (an indirect effect), contributes to the observed damage. Considering this, complementing hepatocytes with a kinase-dead version of RIPK1 could be a valuable approach to further refine the molecular aspect of the study. This would allow for a more precise investigation into the specific role of RIPK1's scaffolding or kinase function in response to starvation in hepatocytes. Such experiments could provide additional insights into the mechanisms underlying the observed effects and help delineate the contributions of RIPK1 in different cell types to metabolic stress responses.

Thank you very much for the constructive suggestion. We fully agree with the reviewer that employing a RIPK1 kinase-inactive mutant mice could precisely investigate the specific roles of RIPK1's scaffolding and kinase functions in hepatocyte responses to starvation, respectively. In accordance with this advice, we established a 12-hour fasting model using Ripk1^WT/WT and Ripk1^K45A/K45A mice, which were previously established and confirmed with the inactivity of RIPK1 kinase activity. As demonstrated in updated Supplementary Figure 2, these mice did not show significant liver damage or inflammatory responses after 12 hours of fasting. These findings suggest that the liver damage and inflammatory response induced by fasting in Ripk1^Δhep mice may not be contributed by the kinase activity of RIPK1.  

Reviewer #2 (Public Review):

Summary:

Zhang et al. analyzed the functional role of hepatocyte RIPK1 during metabolic stress, particularly its scaffold function rather than kinase function. They show that Ripk1 knockout sensitizes the liver to cell death and inflammation in response to short-term fasting, a condition that would not induce obvious abnormality in wild-type mice.

Strengths:

The findings are based on a knockout mouse model and supported by bulk RNA-seq and scRNA-seq. The work consolidates the complex role of RIPK1 in metabolic stress.

Weaknesses:

However, the findings are not novel enough because the pro-survival role of RIPK1 scaffold is well-established and several similar pieces of research already exist. Moreover, the mechanism is not very clear and needs additional experiments.

We thank the reviewer for the encouraging comments and helpful suggestions. Here we conducted additional experiments including flow cytometry, western blotting, and using kinase-dead mutant mice to further investigate the underlying mechanisms. We carefully addressed every comment by the reviewer as indicated below.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(7) I recommend that the authors consider reassessing their results, particularly with regards to elucidating the dialogue between macrophages and hepatocytes, as this could further strengthen the study's conclusions.

Thank you very much for your constructive suggestion. We conducted additional experiments, including flow cytometry and western blotting, to reassess our findings. Furthermore, to clarify the interactions between cells, we employed CellChat for a more in-depth analysis of the single-cell sequencing results. In the revised manuscript version, changes are highlighted in yellow. In this study, we demonstrated that the specific deletion of RIPK1 in hepatocytes exacerbated the liver's vulnerability to metabolic disturbances, such as short-term fasting and high-fat diet feeding, resulting in increased liver damage, apoptosis, inflammation, and compensatory proliferation. The data indicate that fasting-induced liver injury in RIPK1 knockout mice of hepatic parenchymal cells may exacerbate the inflammatory response in liver tissue through enhanced SAA signaling. In summary, we revealed a novel physiological role of RIPK1 as a scaffold in maintaining liver homeostasis during fasting and other nutritional disturbances.

(8) It would be beneficial for the authors to address the minor weaknesses identified in the study, such as ensuring consistency in the number of animals analyzed across different graphs and enhancing the resolution of images to improve data clarity.

Thank you for the suggestion. In the revised manuscript, we have addressed these minor weaknesses, and we checked the consistency in the number of animals in different graphs, as well as enhanced the resolution of all images.

(9) I encourage the authors to incorporate additional experiments, such as Western blotting and flow cytometry, to provide a more quantitative assessment of the observed effects and enhance the robustness of their conclusions.

Thank you for your insightful suggestion. We completely agree with the reviewer that incorporating flow cytometry and western blotting would strengthen the robustness of our conclusions. We conducted flow cytometry analysis and western blotting and the results were listed in updated Supplementary Figure 1, Figure 2, Figure 4 and Supplementary Figure 4.

(10) Furthermore, the authors may consider conducting complementary experiments, such as rescue experiments involving complementing hepatocytes with a kinase-dead version of RIPK1, to further refine the molecular aspect of the study and elucidate the specific roles of RIPK1's scaffolding or kinase function in response to starvation.

Thank you very much for your constructive suggestion. As shown in updated Supplementary Figure 2, we conducted fasting experiments using RIPK1 kinase-dead mice. These findings suggest that the liver damage and inflammatory response induced by fasting in Ripk1^Δhep mice may not contributed by the kinase activity of RIPK1.

Reviewer #2 (Recommendations For The Authors):

Major:

(11) What is the upsteam signal for RIPK1? The study investigated the change induced by short-term fasting which is metabolic stress. Although RIPK1 knockout promotes cell death and inflammation, how it is involved in this condition is unclear. RIPK1 is never reported as a metabolic sensor and its function is typically downstream of TNFR1 as well as other death receptors such as Fas, TRAIL-R1, TRAIL-R2. Thus, it's probable that metabolic stress induces the expression and secretion of some ligand of the above receptors. Although TNFα expression is upregulated on both mRNA and protein levels, it could not be concluded that TNFα is the upsteam signal for RIPK1 because expression difference does not always lead to fuctional role. In addition, a recent study, which is also reference 33, reports that knockout of TNFR1/2 does not protect against 18 h liver ischemia, a condition that is similar to the present study. Therefore, the link between the metabolic fluctuation and RIPK1 function is elusive and should be addressed. The expression difference analysis should be extended to other relevant ligands. A functional study using neutralizing antibodies in RIPK1ΔHep mice is encouraged. At least, this should be discussed in the discussion section.

Thank you very much for your insightful comments. The upstream signals of RIPK1 remains a significant area of scientific inquiry. Fasting, as one of the main causes of metabolic stress, is known to trigger a series of physiological changes, including but not limited to decreased blood glucose levels, hepatic glycogen depletion, increased production of hepatic glucose and ketone bodies, adipose tissue lipolysis, and the influx and accumulation of free fatty lipids in the liver. It is well-established that the elevated lipid influx and hepatic accumulation during fasting may cause lipotoxicity stress for liver. To investigate whether the elevated free fatty acids influx might act as the signal to induce cytotoxicity, we isolated primary hepatocytes but observed that a significant number of cells underwent spontaneous death during the isolation and perfusion processes. To address this question, we utilized CRISPR-Cas9 technology to generate Ripk1^-/- AML12 cells, as illustrated in Author response image 1A.

To mimic hepatic lipid accumulation induced by short-term fasting, we treated the cells with palmitic acid (PA) or oleic acid (OA) for 12 hours in vitro. Our results indicated a significant increase in cell death among Ripk1^-/- AML12 cells after PA treatment compared to WT control cells (Author response image 1B). As shown in Author response image 1C, we also observed a marked increase in caspase-3 activity in Ripk1^-/- AML12 cells following PA treatment.

Collectively, our results highlight the crucial role of RIPK1 in hepatocytes in maintaining the liver's adaptive capacity to counteract lipotoxicity induced by metabolic stress. These in vitro results were not included in the manuscript; however, we addressed them in the discussion section (line 593 - 597). If the reviewer suggest, we would like to incorporate in our manuscript.

Author response image 1.

(12) What is the exact relationship between ER stress and RIPK1? In Figure 5A and Figure 6B, Ripk1 knockout only slightly promotes the expression of ER stress markers. The evidence of RIPK1 leading to ER stress is limited in the literature and poorly supported in this study. Also in reference 33, the hypothesis is proposed that ER stress leads to death receptor upregulation and activation, which induces RIPK1 activation. Although the ER stress inhibitor showed good efficacy in rescue experiments, it could not determine whether RIPK1 deficiency leads to ER stress-associated phenotype or ER stress leads to death receptor activation and RIPK1 deficiency-associated phenotype. If RIPK1 deficiency leads to ER stress, the possible mechanism should be investigated.

Thank you very much for your insightful comments. As the reviewer noted, the specific relationship between endoplasmic reticulum (ER) stress and RIPK1 remains unclear. However, our data, along with findings from other studies (Piccolis M et al., Mol Cell. 2019; Geng Y et al., Hepatol Int. 2021), suggest that fasting-induced lipolysis in peripheral adipose tissue leads to hepatic lipid accumulation. Additionally, excessive deposition of free fatty acids has been shown to induce ER stress in the liver. One possible explanation is that ER stress may trigger the upregulation and activation of death receptors, and the scaffold function of RIPK1 may play a protective and checkpoint role in this process. ER stress during the fasting might locate upstream of RIPK1. This could help explain why short-term fasting results in liver damage in Ripk1^Δhep mice while control mice remain unaffected. Moreover, the inhibition of ER stress using 4-PBA can effectively alleviate this damage.

Minor:  

(13) The study starts directly from functional experiments. However, it should be firstly explored whether RIPK1 expression or activation is modulated in wild-type mice.

Thank you very much for your insightful observation. Previous studies showed that RIPK1 deficiency in hepatocytes does not impact the growth and development of mice, indicating that RIPK1 is dispensable for proper liver development and homeostasis (Filliol A et al., Cell Death Dis. 2016). Furthermore, we did not observe any changes in RIPK1 levels in wild-type mice induced by fasting across different experimental batches. In our bulk transcriptomic analysis, the expression of RIPK1 was not changed before and after 12-hour fasting in Ripk1^fl/fl mice. Therefore, we focused our attention on the function of RIPK1 and started our study directly with functional experiments.

(14) Knockout of RIPK1 deprived both its scaffold function and kinase function. It is encouraged to explore whether blocking RIPK1 kinase activity influences the outcome of metabolic stress.

Thank you for your insightful suggestion. To investigate the role of RIPK1 kinase activity in response to metabolic stress, we added fasting experiments using RIPK1 kinaseinactive mice in the updated Supplementary Figure 2, in which blocking RIPK1 kinase activity does not affect the outcome of metabolic stress.

(15) In Figure 1, the number of TUNEL+ cells is about 2 times of c-casp3. What is the possible reason?

Thank you for your careful reading. Indeed, the number of TUNEL⁺ cells in Figure 1 is twice that of cleaved-caspase-3⁺ cells. There are two possible reasons. First, we speculate that this discrepancy may be attributed to the higher sensitivity of the TUNEL assay compared to the cleaved-caspase-3 assay. Secondly, TUNEL assay detects DNA fragmentation, indicating that these cells are in a pre-apoptotic state or poised to undergo apoptosis. In contrast, cleaved-caspase-3 specifically identifies cells that have already committed to the apoptotic pathway, whereas TUNEL assay could detects all types of apoptosis, but the mechanisms of apoptosis may involve more than just cleaved-caspase3.

(16) Infiltrated innate immune cells could lead to hepatocyte death. Is the hepatocyte death in this study partially caused by immune cells?

Many thanks for the advice. As outlined in the response to the 11th comment from the second reviewer, our findings indicate that metabolic stress induced by short-term fasting is the primary cause of hepatocyte death. Additionally, we demonstrate that infiltrated innate immune cells may also play a partial role in hepatocyte death through subsequent cascade reactions.

(17) Could the in vivo results be consolidated by in vitro experiments on primary mouse hepatocytes? This would be helpful to answer question 4.

Thank you for your helpful comments. As demonstrated in the response to the 11th comment by the second reviewer, we attempted to conduct in vitro experiments using primary hepatocytes. However, during the isolation and perfusion processes, we observed that a significant number of cells underwent spontaneous death. To address this issue, we utilized CRISPR-Cas9 technology to generate Ripk1^-/- AML12 cells, in which a significant increase in cell death among Ripk1^-/- AML12 cells after palmitic acid (PA) treatment compared to WT control cells. We also observed a marked increase in caspase-3 activity in Ripk1^-/- AML12 cells following PA treatment.

(18) RIPK1 scaffold function is associated with NF-kB signal. Is NF-kB signal transduction influenced by Ripk1 deficiency? If so, to what extent does it contribute to the observed phynotype? If not, what is the direct downstream effect of Ripk1 deficiency?

Thank you very much for your insightful perspective. As reported by Clucas J et al., RIPK1 serves as a scaffold for downstream NF-κB signaling through the ubiquitin chains generated by its ubiquitination (Clucas J et al., Nat Rev Mol Cell Biol. 2023). The deficiency of RIPK1 in hepatic parenchymal cells can disrupt NF-κB signaling and impair its pro-survival functions, resulting in increased cell death in response to stress. Our current findings suggest that the RIPK1-NF-κB axis serves as a crucial scaffold platform essential for the liver's adaptation to metabolic fluctuations. Any inappropriate inactivation or deletion of components within this scaffold disrupts the delicate balance between cell death, inflammation, and normal function, making the liver susceptible to metabolic changes, ultimately leading to liver damage, hepatic inflammation, and compensatory proliferation.

(19) In Figure 6B, the 'RIP' should be changed to 'RIPK1'.

Thank you for your careful observation. We have corrected "RIP" to "RIPK1" in updated Figure 6B.

(20) For Western blot results, the blot height should be at least the lane width to reveal additional signals and the molecular weight as well as unspecific signals should be denoted.

Thank you for your valuable advice. We appreciate your suggestions regarding the western blot results. We went through the previous western blot results and did not find any additional nonspecific signals. We added the molecular weights in the updated figures Figure 5, Figure 6 and Supplementary Figure 1.

eLife Assessment

This important collection of over 800 new cell type-specific driver lines will be an invaluable resource for researchers studying associative learning in Drosophila. Thoroughly characterized and well documented, this collection will permit researchers to selectively target neurons that deliver information to, or receive it from, the memory center of the fly brain called the Mushroom Body. Given the wealth of new drivers and the genetic access they provide to over 300 cell types, this compelling work will be of interest not only to researchers studying the mechanisms of associative learning but more generally to those dissecting sensorimotor circuits in the fly nervous system.

Reviewer #1 (Public Review):

Summary:

The emergence of Drosophila EM connectomes has revealed numerous neurons within the associative learning circuit. However, these neurons are inaccessible for functional assessment or genetic manipulation in the absence of cell-type-specific drivers. Addressing this knowledge gap, Shuai et al. have screened over 4000 split-GAL4 drivers and correlated them with identified neuron types from the "Hemibrain" EM connectome by matching light microscopy images to neuronal shapes defined by EM. They successfully generated over 800 split-GAL4 drivers and 22 split-LexA drivers covering a substantial number of neuron types across layers of the mushroom body associative learning circuit. They provide new labeling tools for olfactory and non-olfactory sensory inputs to the mushroom body; interneurons connected with dopaminergic neurons and/or mushroom body output neurons; potential reinforcement sensory neurons; and expanded coverage of intrinsic mushroom body neurons. Furthermore, the authors have optimized the GR64f-GAL4 driver into a sugar sensory neuron-specific split-GAL4 driver and functionally validated it as providing a robust optogenetic substitute for sugar reward. Additionally, a driver for putative nociceptive ascending neurons, potentially serving as optogenetic negative reinforcement, is characterized by optogenetic avoidance behavior. The authors also use their very large dataset of neuronal anatomies, covering many example neurons from many brains, to identify neuron instances with atypical morphology. They find many examples of mushroom body neurons with altered neuronal numbers or mistargeting of dendrites or axons and estimate that 1-3% of neurons in each brain may have anatomic peculiarities or malformations. Significantly, the study systematically assesses the individualized existence of MBON08 for the first time. This neuron is a variant shape that sometimes occurs instead of one of two copies of MBON09, and this variation is more common than that in other neuronal classes: 75% of hemispheres have two MBON09's, and 25% have one MBON09 and one MBON08. These newly developed drivers not only expand the repertoire for genetic manipulation of mushroom body-related neurons but also empower researchers to investigate the functions of circuit motifs identified from the connectomes. The authors generously make these flies available to the public. In the foreseeable future, the tools generated in this study will allow important advances in the understanding of learning and memory in Drosophila.

Strengths:

(1) After decades of dedicated research on the mushroom body, a consensus has been established that the release of dopamine from DANs modulates the weights of connections between KCs and MBONs. This process updates the association between sensory information and behavioral responses. However, understanding how the unconditioned stimulus is conveyed from sensory neurons to DANs, and the interactions of MBON outputs with innate responses to sensory context remains less clear due to the developmental and anatomic diversity of MBONs and DANs. Additionally, the recurrent connections between MBONs and DANs are reported to be critical for learning. The characterization of split-GAL4 drivers for 30 major interneurons connected with DANs and/or MBONs in this study will significantly contribute to our understanding of recurrent connections in mushroom body function.

(2) Optogenetic substitutes for real unconditioned stimuli (such as sugar taste or electric shock) are sometimes easier to implement in behavioral assays due to the spatial and temporal specificity with which optogenetic activation can be induced. GR64f-GAL4 has been widely used in the field to activate sugar sensory neurons and mimic sugar reward. However, the authors demonstrate that GR64f-GAL4 drives expression in other neurons not necessary for sugar reward, and the potential activation of these neurons could introduce confounds into training, impairing training efficiency. To address this issue, the authors have elaborated on a series of intersectional drivers with GR64f-GAL4 to dissect subsets of labeled neurons. This approach successfully identified a more specific sugar sensory neuron driver, SS87269, which consistently exhibited optimal training performance and triggered ethologically relevant local searching behaviors. This newly characterized line could serve as an optimized optogenetic tool for sugar reward in future studies.

(3) MBON08 was first reported by Aso et al. 2014, exhibiting dendritic arborization into both ipsilateral and contralateral γ3 compartments. However, this neuron could not be identified in the previously published Drosophila brain connectomes. In the present study, the existence of MBON08 is confirmed, occurring in one hemisphere of 35% of imaged flies. In brains where MBON08 is present, its dendrite arborization disjointly shares contralateral γ3 compartments with MBON09. This remarkable phenotype potentially serves as a valuable resource for understanding the stochasticity of neurodevelopment and the molecular mechanisms underlying mushroom body lobe compartment formation.

Reviewer #2 (Public Review):

Summary:

The article by Shuai et al. describes a comprehensive collection of over 800 split-GAL4 and split-LexA drivers, covering approximately 300 cell types in Drosophila, aimed at advancing the understanding of associative learning. The mushroom body (MB) in the insect brain is central to associative learning, with Kenyon cells (KCs) as primary intrinsic neurons and dopaminergic neurons (DANs) and MB output neurons (MBONs) forming compartmental zones for memory storage and behavior modulation. This study focuses on characterizing sensory input as well as direct upstream connections to the MB both anatomically and, to some extent, behaviorally. Genetic access to specific, sparsely expressed cell types is crucial for investigating the impact of single cells on computational and functional aspects within the circuitry. As such, this new and extensive collection significantly extends the range of targeted cell types related to the MB and will be an outstanding resource to elucidate MB-related processes in the future.

Strengths:

The work by Shuai et al. provides novel and essential resources to study MB-related processes and beyond. The resulting tools are publicly available and, together with the linked information, will be foundational for many future studies. The importance and impact of this tool development approach, along with previous ones, for the field cannot be overstated. One of many interesting aspects arises from the anatomical analysis of cell types that are less stereotypical across flies. These discoveries might open new avenues for future investigations into how such asymmetry and individuality arise from development and other factors, and how it impacts the computations performed by the circuitry that contains these elements.

Reviewer #3 (Public Review):

Summary:

Previous research on the Drosophila mushroom body (MB) has made this structure the best-understood example of an associative memory center in the animal kingdom. This is in no small part due to the generation of cell-type specific driver lines that have allowed consistent and reproducible genetic access to many of the MB's component neurons. The manuscript by Shuai et al. now vastly extends the number of driver lines available to researchers interested in studying learning and memory circuits in the fly. It is an 800-plus collection of new cell-type specific drivers target neurons that either provide input (direct or indirect) to MB neurons or that receive output from them. Many of the new drivers target neurons in sensory pathways that convey conditioned and unconditioned stimuli to the MB. Most drivers are exquisitely selective, and researchers will benefit from the fact that whenever possible, the authors have identified the targeted cell types within the Drosophila connectome. Driver expression patterns are beautifully documented and are publicly available through the Janelia Research Campus's Flylight database where full imaging results can be accessed. Overall, the manuscript significantly augments the number of cell type-specific driver lines available to the Drosophila research community for investigating the cellular mechanisms underlying learning and memory in the fly. Many of the lines will also be useful in dissecting the function of the neural circuits that mediate sensorimotor circuits.

Strengths:

The manuscript represents a huge amount of careful work and leverages numerous important developments from the last several years. These include the thousands of recently generated split-Gal4 lines at Janelia and the computational tools for pairing them to make exquisitely specific targeting reagents. In addition, the manuscript takes full advantage of the recently released Drosophila connectomes. Driver expression patterns are beautifully illustrated side-by-side with corresponding skeletonized neurons reconstructed by EM. A comprehensive table of the new lines, their split-Gal4 components, their neuronal targets, and other valuable information will make this collection eminently useful to end-users. In addition to the anatomical characterization, the manuscript also illustrates the functional utility of the new lines in optogenetic experiments. In one example, the authors identify a specific subset of sugar reward neurons that robustly promotes associative learning.

Author response:

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

Comments on revised version: 

Overall, I thought the authors addressed my comments well with the possible exception of what is actually new here. This was the most important thing that I thought should be included in the revision. Although the authors rewrote the paragraph describing the lines presented in the paper, I still can't tell exactly which ones haven't been previously published. Their revised paragraph says that 40 lines have been "previously used," but Supplemental Table 1 shows references for over 200 of the lines, which sounds more reasonable based on papers that have come out. 

We have modified the text in line 112-120 as below.

“Supplementary File 1 lists 859 lines (including split-LexA) and their detailed information, such as genotype, expression specificity, matched EM cell type(s), and recommended driver for each cell type. A small subset of 47 lines from this collection have been previously used in studies (Aso et al., 2023; Dolan et al., 2019; Gao et al., 2019; Scaplen et al., 2021; Schretter et al., 2020; Takagi et al., 2017; Xie et al., 2021; Yamada et al., 2023).”

For 842 lines among the 859 lines listed in Supplementary File 1, this study is the primary citation for future papers for the following reason: 

In 2021 December, we deposited the confocal images of new split-GAL4 lines at Janelia Flylight website (http://www.janelia.org/split-gal4) without a publication to describe annotation of expression patterns, and we already started sharing the lines without restrictions. In 2023 September, we released the preprint of this study at bioRxiv (doi: https://doi.org/10.1101/2023.09.15.557808). Up to this point, 47 lines have been used in other studies. In Supplementary File 1, 30 of them attribute the citation credit to both this study and other papers, because this 2023 preprint was cited as the primary citation in those papers. Similarly, the omni paper to summarize all the eWort of generating split-GAL4 lines by Janelia Flylight team (https://doi.org/10.7554/eLife.98405.1) cite many lines from this paper. However, since this summary paper did not provide additional information such as functional characterization by behavioral experiments, we did not include it in Supplementary File 1 to clarify that this study is the primary citation for these lines. The remaining 17 lines were published before 2021. We included them for the convenience of users, and we attributed the primary citation to the already published papers. 

Also, in the revised paragraph they state that "All transgenic lines newly generated in this study are listed in Supplementary File 2" but that table lists only the 36 LexA hemidriver lines! Confusingly, this comment cites the same 8 references as are cited for the 40 line that they say were previously published. I am thus only more confused about how many previously uncharacterized lines are presented in this paper. 

We modified the text as below to clarify that “new lines” indicate LexA or DBD lines but not new combination of already published AD and DBD lines. We removed the 8 citations, which were mistakenly placed in the previous manuscript.

“The newly generated LexA, Gal4DBD and LexADBD lines are listed in Supplementary File 2. “

eLife Assessment

This paper presents useful results that extend our understanding of how the visual cortex encodes temporal structure, providing new information about sequence representations in the upper layers of the visual cortex. The evidence for prediction errors is solid, however, support for other claims regarding sparsification and simplification of activity following training is incomplete. The main concerns pertain to the confounds associated with restricted ordering within blocks that does not allow for separate plasticity mechanisms operating on different time scales.

Reviewer #1 (Public review):

Summary:

Knudstrup et al. use two-photon calcium imaging to measure neural responses in the mouse primary visual cortex (V1) in response to image sequences. The authors presented mice with many repetitions of the same four-image sequence (ABCD) for four days. Then on the fifth day, they presented unexpected stimulus orderings where one stimulus was either omitted (ABBD) or substituted (ACBD). After analyzing trial-averaged responses of neurons pooled across multiple mice, they observed that stimulus omission (ABBD) caused a small, but significant, strengthening of neural responses but observed no significant change in the response to stimulus substitution (ACBD). Next, they performed population analyses of this dataset. They showed that there were changes in the correlation structure of activity and that many features about sequence ordering could be reliably decoded. This second set of analyses is interesting and exhibited larger effect sizes than the first results about predictive coding. However, concerns about the design of the experiment temper my enthusiasm.

The most recent version of this manuscript makes a few helpful changes (entirely in supplemental figures--the main text figures are unchanged). It does not resolve any of the larger weaknesses of the experimental design, or even perform single-neuron tracking in the one case where it was possible (between similar FOVs shown in Supplemental Figure 1).

Strengths:

(1) The topic of predictive coding in the visual cortex is exciting, and this task builds on previous important work by the senior author (Gavornik and Bear 2014) where unexpectedly shuffling sequence order caused changes in LFPs recorded from visual cortex.

(2) Deconvolved calcium responses were used appropriately here to look at the timing of the neural responses.

(3) Neural decoding results showing that the context of the stimuli could be reliably decoded from trial-averaged responses were interesting. But I have concerns about how the data was formatted for performing these analyses.

Weaknesses:

(1) All analyses were performed on trial-averaged neural responses that were pooled across mice (except for Supplementary Figure 6, see below). Owing to differences between subjects in behavior, experimental preparation quality, and biological variability, it seems important to perform most analyses on individual datasets to assess how behavioral training might differently affect each animal.

In the most recent draft, a single-mouse analysis was added for Figure 4C (Supplementary Figure 6). This effect of "representational drift" was not statistically quantified in either the single-mouse results or in the main text figure panel. Moreover, the apparent correlational drift could be accounted for by a reduction in SNR as a consequence of photobleaching.

(2) The correlation analyses presented in Figure 3 (labeled the second Figure 2 in the text) should be conducted on a single-animal basis. Studying population codes constructed by pooling across mice, particularly when there is no behavioral readout to assess whether learning has had similar effects on all animals, appears inappropriate to me. If the results in Figure 3 hold up on single animals, I think that is definitely an interesting result.

In the most recent draft, this analysis was still not performed on single mice. I was referring to the "decorrelation of responses" analysis in Figure 3, not the "representational drift" analysis in Figure 4. See my comments on Supplementary Figure 6 above.

(3) On Day 0 and Day 5, the reordered stimuli are presented in trial blocks where each image sequence is shown 100 times. Why wasn't the trial ordering randomized as was done in previous studies (e.g. Gavornik and Bear 2014)? Given this lack of reordering, did neurons show reduced predictive responses because the unexpected sequence was shown so many times in quick succession? This might change the results seen in Figure 2, as well as the decoder results where there is a neural encoding of sequence order (Figure 4). It would be interesting if the Figure 4 decoder stopped working when the higher order block structure of the task were disrupted.

In the rebuttal letter for the most recent draft, the authors refer to recent work in press (Hosmane et al. 2024) suggesting that because sleep may be important for plastic changes between sessions, they do not expect much change to be apparent within a session. However, they admit that this current study is too underpowered to know for sure--and do not cite or mention this yet unpublished work in the manuscript itself.

As a control, I would be interested to at least know how much variance in neural responses is observed between intermediate "training" sessions with identical stimuli, e.g. between Day 1 and Day 4, but this is not possible as imaging was not performed on these days.

Despite being referred to as "similar" I do not think early and late responses are clearly shown--aside from the histograms comparing "early traces" to "all traces" which include early traces in Figure 5B and Figure 6A. Showing variance in single-cell responses would be helpful to add in Supplementary Figure 3 and Supplementary Figure 4.

(4) A primary advantage of using two-photon calcium imaging over other techniques like extracellular electrophysiology is that the same neurons can be tracked over many days. This is a standard approach that can be accomplished by using many software packages-including Suite2P (Pachitariu et al. 2017), which is what the authors already used for the rest of their data preprocessing. The authors of this paper did not appear to do this. Instead, it appears that different neurons were imaged on Day 0 (baseline) and Day 5 (test). This is a significant weakness of the current dataset.

In the most recent draft, this concern has not been mitigated. Despite Supplementary Figure 1 showing similar FOVs, mostly different neurons were still extracted. In all other sessions, it is not reported how far apart the other recorded FOVs were from each other.

The rebuttal comment that the PE statistic is computed on an individual cell within-session basis is reasonable. Moreover, the bootstrapped version of the PE analysis in Supplementary Figure 8 is an improvement of the main analysis in the paper. As a control, it would have been helpful to compute the stability of the PE ratio statistics between training days (e.g. between day 1 and day 4). How much change would have been observed when none is expected? Unfortunately, imaging was not performed on these training days so this analysis will not be readily possible to perform. Moreover, the PE statistic requires averaging across cells and trials and is therefore very likely to wash out many interesting effects. Even if it is the population response that is changing, why would it be the arithmetic mean that changes in particular vs. some other projection of the population activity? The experimental and analysis design of the paper here remains weak in my mind.

Reviewer #2 (Public review):

Knudstrup and colleagues investigate response to short and rapid sequences of stimuli in layer 2/3 of mouse visual cortex. To quote the authors themselves: "the work continues the recent tradition of providing ambiguous support for the idea that cortical dynamics are best described by predictive coding models". Unfortunately, the ambiguity here is largely a result of the choice of experimental design and analysis, and the data provide only incomplete support for the authors' conclusions.

The authors have addressed some of the concerns of the first revision. However, many still remain.

(1) From the first review: "There appears to be some confusion regarding the conceptual framing of predictive coding. Assuming the mouse learns to expect the sequence ABCD, then ABBD does not probe just for negative prediction errors, and ACBD not just positive prediction errors. With ABBD, there is a combination of a negative prediction error for the missing C in the 3rd position, and a positive prediction error for B in 3rd. Likewise, with ACBD, there is negative prediction error for the missing B at 2nd and missing C at 3rd, and a positive prediction error for the C in 2nd and B in 3rd. Thus, the authors' experimental design does not have the power to isolate either negative or positive prediction errors. Moreover, looking at the raw data in Figure 2C, this does not look like an "omission" response to C, more like a stronger response to a longer B. The pitch of the paper as investigating prediction error responses is probably not warranted - we see no way to align the authors' results with this interpretation."

The authors acknowledge in their response that this is a problem, but do not appear to discuss this in the manuscript. This should be fixed.

(2) From the first review: "Recording from the same neurons over the course of this paradigm is well within the technical standards of the field, and there is no reason not to do this. Given that the authors chose to record from different neurons, it is difficult to distinguish representational drift from drift in the population of neurons recorded. "

The authors respond by pointing out that what they mean by "drift" is within day changes. This has been clarified. However, the analyses in Figures 3 and 5 still are done across days. Figure 3: "Experience modifies activity in PCA space ..." and figure 5: "Stimulus responses shift with training". Both rely on comparisons of population activity across days. This concern remains unchanged here. It would probably be best to remove any analysis done across days - or use data where the same neurons were tracked. Performing chronic two-photon imaging experiments without tracking the same neurons is simply bad practice (assuming one intends to do any analysis across recording sessions).

(3) From the first revision: "The block paradigm to test for prediction errors appears ill chosen. Why not interleave oddball stimuli randomly in a sequence of normal stimuli? The concern is related to the question of how many repetitions it takes to learn a sequence. Can the mice not learn ACBD over 100x repetitions? The authors should definitely look at early vs. late responses in the oddball block. Also the first few presentations after block transition might be potentially interesting. The authors' analysis in the paper already strongly suggests that the mice learn rather rapidly. The authors conclude: "we expected ABCD would be more-or-less indistinguishable from ABBD and ACBD since A occurs first in each sequence and always preceded by a long (800 ms) gray period. This was not the case. Most often, the decoder correctly identified which sequence stimulus A came from." This would suggest that whatever learning/drift could happen within one block did indeed happen and responses to different sequences are harder to interpret."

Again, the authors acknowledge the problem and state that "there is no indication that this is a learned effect". However, they provide no evidence for this and perform no analysis to mitigate the concern.

(4) Some of the minor comments also appear unaddressed and uncommented. E.g. the response amplitudes are still shown in "a.u." instead of dF/F or z-score or spikes.

Reviewer #3 (Public review):

Summary:

This work provides insights into predictive coding models of visual cortex processing. These models predict that visual cortex neurons will show elevated responses when there are unexpected changes to learned sequential stimulus patterns. This model is currently controversial, with recent publications providing conflicting evidence. In this work, the authors test two types of unexpected pattern variations in layer 2/3 of the mouse visual cortex. They show that pattern omission evokes elevated responses, in favor of a predictive coding model, but find no evidence for prediction errors with substituted patterns, which conflicts with both prior results in L4, and with the expectations of a predictive coding model. They also report that with sequence training, responses sparsify and decorrelate, but surprisingly find no changes in the ability of an ideal observer to decode stimulus identity or timing.

These results are an important contribution to the understanding of how temporal sequences and expectations are encoded in the primary visual cortex

Comments on revisions:

In this revision, the authors address several of the concerns in the original manuscript. However, the primary issue, raised by all three reviewers, was the block design of the experiments. This design makes disentangling the effects of any rapid (within block) plasticity from any longer term (across days) plasticity-which nominally is the subject of the paper-extremely difficult.

Although it may be the case that re-running the experiments with an interleaved design is beyond the scope of this paper, unfortunately, the revised manuscript still does not adequately discuss this potential confound. The authors note that stimulus A in ABCD, ABBD, and ACBD could be distinguished on day 0, indicating that within block changes do occur. In both the original and revised manuscript this finding is discussed in terms of representational drift, but the authors fail to discuss how such within block plasticity may impact their primary findings of prediction error effects.

This remains a significant concern with the revised manuscript.

Many of the other issues in the original manuscript have been addressed, and in these areas the revised manuscript is both clearer and more accurately reflects the presented data. The additional analyses and controls shown in the supplemental figures aid in the interpretation of the findings.

Author response:

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

Reviewer #1:

(1) All analyses were performed on trial-averaged neural responses that were pooled across mice. Owing to differences between subjects in behavior, experimental preparation quality, and biological variability, it seems important to perform at least some analyses on individual analyses to assess how behavioral training might differently affect each animal.

In order to image at a relatively fast rate (30Hz) appropriate to the experimental conditions, we restricted our imaging to a relatively small field of view (412x412um with 512x512 pixels). This entails a smaller number of ROIs per animal, which can lead to an unbalanced distribution of cells responsive to different stimuli for individual fields-of-view. We used the common approach of pooling across animals (Homann et al., 2021; Kim et al., 2019) to overcome limitations imposed by sampling a smaller number of cells per animal. In response to this comment, we included supplemental analyses (Sup.Fig. 6) showing that representational drift (which was not performed on trial-averaged data) looks substantially the same (albeit nosier) for individual animals as at the population level. Additional analyses (PE ratio, etc.) were difficult since the distribution of cells selective for individual stimuli is unbalanced between individual animals and few mice have multiple cells representing all of the different stimuli.

(2) The correlation analyses presented in Figure 3 (labeled the second Figure 2 in the text) should be conducted on a single-animal basis. Studying population codes constructed by pooling across mice, particularly when there is no behavioral readout to assess whether learning has had similar effects on all animals, appears inappropriate to me. If the results in Figure 3 hold up on single animals, I think that is definitely an interesting result.

We repeated the correlation analysis performed on mice individually and included them in the supplement (Supp. Fig. 6). The overall result generally mirrors the result found by pooling across animals.

(3) On Day 0 and Day 5, the reordered stimuli are presented in trial blocks where each image sequence is shown 100 times. Why wasn't the trial ordering randomized as was done in previous studies (e.g. Gavornik and Bear 2014)? Given this lack of reordering, did neurons show reduced predictive responses because the unexpected sequence was shown so many times in quick succession? This might change the results seen in Figure 2, as well as the decoder results where there is a neural encoding of sequence order (Figure 4). It would be interesting if the Figure 4 decoder stopped working when the higher-order block structure of the task was disrupted.

Our work builds primarily on previous studies (Gavornik & Bear, 2014; Price et al., 2023) that demonstrated clear changes in neural responses over days while employing a similar block structure. Notably, Price et al. found that trial number (within a block) was not a significant factor in the generation of prediction-error responses which strongly suggests short-term plasticity does not play a significant role in shaping responses within the block structure. This finding is consistent with our previous LFP recordings which have not revealed any significant plasticity occurring within a training session, a conclusion bolstered by a collaborative work currently in press (Hosmane et al. 2024, Sleep) revealing the requirement for sleep in sequence plasticity expression.

It is possible that layer 2/3 adapts to sequences more rapidly than layer 4/5. While manual inspection does not reveal an obvious difference between early and late blocks in this dataset, the n for this subset is too small to draw firm conclusions. It is our view that the block structure provides the strongest comparison to previous work, but agree it would be interesting to randomize or fully interleave sequences in future studies to determine what effect, if any, short-term changes might have. 

(4) A primary advantage of using two-photon calcium imaging over other techniques like extracellular electrophysiology is that the same neurons can be tracked over many days. This is a standard approach that can be accomplished by using many software packages-including Suite2P (Pachitariu et al. 2017), which is what the authors already used for the rest of their data preprocessing. The authors of this paper did not appear to do this. Instead, it appears that different neurons were imaged on Day 0 (baseline) and Day 5 (test). This is a significant weakness of the current dataset.

The hypothesis being tested was whether expectation violations, as described in Keller & Mrsic-Flogel 2018, exist under a multi-day sequence learning paradigm. For this, tracking cells across days is not necessary as our PE metric compared responses of individual neurons to multiple stimuli within a single session. Given the speed/FOV tradeoff discussed above, we wanted to consider all cells irrespective of whether they were visible/active or trackable across days, especially since we would expect cells that learn to signal prediction errors to be inactive on day 0 and not selected by our segmentation algorithm. Though we did not compare the responses of single cells before/after training, we did analyze cells from the same field of view on days 0 and 5 (see Supp.Fig. 1) and not distinct populations.

Reviewer #2:

(1) There appears to be some confusion regarding the conceptual framing of predictive coding.

Assuming the mouse learns to expect the sequence ABCD, then ABBD does not probe just for negative prediction errors, and ACBD is not just for positive prediction errors. With ABBD, there is a combination of a negative prediction error for the missing C in the 3rd position, and a positive prediction error for B in the 3rd. Likewise, with ACBD, there is a negative prediction error for the missing B at 2nd and missing C at 3rd, and a positive prediction error for the C in 2nd and B in 3rd. Thus, the authors' experimental design does not have the power to isolate either negative or positive prediction errors. Moreover, looking at the raw data in Figure 2C, this does not look like an "omission" response to C, but more like a stronger response to a longer B. The pitch of the paper as investigating prediction error responses is probably not warranted - we see no way to align the authors' results with this interpretation.

The reviewer has identified a real problem with the framing of “positive” and “negative” prediction errors in context of sensory stimuli where substitution simultaneously introduces unexpected “positive” violation and “negative” omission. Simply put, even if there are separate mechanisms to represent positive and negative errors, there may be no way to isolate the positive response experimentally since an unexpected input always replaces the unseen expected input. For example, had a cell fired solely to ACBD (and not during either ABCD or ABCD), then whether it was signaling the unexpected occurrence of C or the unexpected absence of B would be inherently ambiguous. In either case, such a cell would have been labeled as C-responsive, and its activity would have been elevated compared with ABCD and would have been included in our substitution-type analysis of prediction errors. We accept that there is some ambiguity regarding the description in this particular case, but overall, this cell’s activity pattern would have informed the PE analysis for which the result was essentially null for the substitution-type violation ACBD.

Omission, in which the sensory input does not change, may experimentally isolate the negative response though this is only true if there is a temporal expectation of when the change should have occurred. If A is predicting B in an ordinal sense but there is no expectation of when B will occur with respect to A, changing the duration of A would not be expected to produce an error signal since at any point in time B might still be coming and the expectation is not broken until something other than B occurs. With respect specifically to ABBD in our experiments, it is correct that the learned error responses take the form of stronger, sustained responses to B during the time C was expected. This is still in contrast to day 0 in which activation decays after a transient response to ABBD. The data shows that responses during an omitted element are altered with training and take the form of elevated responses to ABBD on day 5.As we say in our discussion, this is somewhat ambiguous evidence of prediction errors since it does emerges only with training and is generally consistent with the hypothesis being tested though it takes a different form than we expected it to.

(2) Related to the interpretation of the findings, just because something can be described as a prediction error does not mean it is computed in (or even is relevant to) the visual cortex. To the best of our knowledge, it is still unclear where in the visual stream the responses described here are computed. It is possible that this type of computation happens before the signals reach the visual cortex, similar to mechanisms predicting moving stimuli already in the retina (https://pubmed.ncbi.nlm.nih.gov/10192333/). This would also be consistent with the authors' finding (in previous work) that single-cell recordings in V1 exhibit weaker sequence violation responses than the author's earlier work using LFP recordings.

Our work was aimed at testing the specific hypothesis that PE responses, at the very least, exist in L2/3—a hypothesis that is well-supported under different experimental paradigms (often multisensory mismatch). Our aim was to test this idea under a sequence learning paradigm and connect it with previously found PE responses in L4. We don’t claim that it is the only place in which prediction errors may be computed or useful, especially since (as you mentioned), there is evidence for such responses in layer 4. But it is fundamentally important to predictive processing that we determine whether PE responses can be found in layer 2/3 under this passive sequence learning paradigm, whether or not they reflect upstream processes, feedback from higher areas, or entirely local computations. Our aim was to establish some baseline evidence for or against predictive processing accounts of L2/3 activity during passive exposure to visual sequences.

(3) Recording from the same neurons over the course of this paradigm is well within the technical standards of the field, and there is no reason not to do this. Given that the authors chose to record from different neurons, it is difficult to distinguish representational drift from drift in the population of neurons recorded.

Our discussion of drift refers to changes occurring within a population of neurons over the course of a single imaging session. We have added clarifying language to the manuscript to make this clear. Changes to the population-level encoding of stimuli over days are treated separately and with different analytical tools. Re. tracking single across days, please see the response to Reviewer #1, comment 4.

(4) The block paradigm to test for prediction errors appears ill-chosen. Why not interleave oddball stimuli randomly in a sequence of normal stimuli? The concern is related to the question of how many repetitions it takes to learn a sequence. Can the mice not learn ACBD over 100x repetitions? The authors should definitely look at early vs. late responses in the oddball block. Also, the first few presentations after the block transition might be potentially interesting. The authors' analysis in the paper already strongly suggests that the mice learn rather rapidly. The authors conclude: "we expected ABCD would be more-or-less indistinguishable from ABBD and ACBD since A occurs first in each sequence and always preceded by a long (800 ms) gray period.

This was not the case. Most often, the decoder correctly identified which sequence stimulus A came from." This would suggest that whatever learning/drift could happen within one block did indeed happen and responses to different sequences are harder to interpret.

This work builds on previous studies that used a block structure to drive plasticity across days. We previously tested whether there are intra-block effects and found no indication of changes occurring within a block or withing a session (please see the response to Reviewer #1, comment 3 for further discussion). Observed drift does complicate comparison between blocks. There is no indication in our data that this is a learned effect, though future experiments could test this directly.

(5) Throughout the manuscript, many of the claims are not statistically tested, and where they are the tests do not appear to be hierarchical (https://pubmed.ncbi.nlm.nih.gov/24671065/), even though the data are likely nested.

We have modified language throughout the manuscript to be more precise about our claims. We used pooled data between mice and common parametric statistics in line with published literature. The referenced paper offers a broad critique of this approach, arguing that it increases the possibility of type 1 errors, though it is not clear to us that our experimental design carries this risk particularly since most of our results were negative. To address the specific concern, however we performed a non-parametric hierarchical bootstrap analysis (https://pmc.ncbi.nlm.nih.gov/articles/PMC7906290/) that re-confirmed the statistical significance of our positive results, see Supplemental Figure 8.

(6) The manuscript would greatly benefit from thorough proofreading (not just in regard to figure references).

We apologize for the errors in the manuscript. We caught the issue and passed on a corrected draft, but apparently the uncorrected draft was sent for review. The re-written manuscript addresses all identified issues.

(7) With a sequence of stimuli that are 250ms in length each, the use of GCaMP6s appears like a very poor choice.

We started our experiments using GCaMP6f but ultimately switched to GCaMP6s due to its improved sensitivity, brightness, and accuracy in spike detection (Huang et al., 2021). When combined with deconvolution (Pachitariu et al., 2018; Pnevmatikakis et al., 2016), we found GCaMP6s provides the most complete and accurate view of spiking within 40ms time bins. The inherent limitations of calcium imaging are more likely to be addressed using electrophysiology rather than a faster sensor in future studies.

(8) The data shown are unnecessarily selective. E.g. it would probably be interesting to see how the average population response evolves with days. The relevant question for most prediction error interpretations would be whether there are subpopulations of neurons that selectively respond to any of the oddballs. E.g. while the authors state they "did" not identify a separate population of omission-responsive neurons, they provide no evidence for this. However, it is unclear whether the block structure of the experiments allows the authors to analyze this.

We concluded that there is no clear dedicated subpopulation of omission-responding cells by inspecting cells with large PE responses (i.e., ABBD, see supplemental figure 3). Out of the 107 B-responsive cells on day 5, only one appeared to fire exclusively during the omitted stimulus. Average traces for all B-responsive cells are included in the supplement and we have updated the manuscript accordingly. Similarly, a single C-responsive cell was found with an apparently unique substitution error profile (ABCD and ACBD , supplemental figure 4).

Our primary concern was to make sure that days 0 and 5 had the highest quality fields-of-view. In work leading up to this study, there were concerns that imaging on all intermediate days resulted in a degradation of quality due to photobleaching. We agree that an analysis of intermediate days would be interesting, but it was excluded due to these concerns. 

Reviewer #3:

(1) Experimental design using a block structure. The use of a block structure on test days (0 and 5) in which sequences were presented in 100 repetition blocks leads to several potential confounds. First, there is the potential for plasticity within blocks, which could alter the responses and induce learned expectations. The ability of the authors to clearly distinguish blocks 1 and 2 on Day 0 with a decoder suggests this change over time may be meaningful.

Repeating the experiments with fully interleaved sequences on test days would alleviate this concern. With the existing data, the authors should compare responses from the first trials in a block to the last trials in a block.

This block design likely also accounts for the ability of a decoder to readily distinguish stimulus A in ABCD from A in ABBD. As all ABCD sequences were run in a contiguous block separate from ABBD, the recent history of experience is different for A stimuli in ABCD versus ABBD. Running fully interleaved sequences would also address this point, and would also potentially mitigate the impact of drift over blocks (discussed below).

As described in other responses, the block structure was chosen to align more closely with previous studies. We take the overall point though, and future studies will employ the suggested randomized or interleaved structure in addition to block structures to investigate the effects of short-term plasticity.

(2) The computation of prediction error differs significantly for omission as opposed to substitutions, in meaningful ways the authors do not address. For omission errors, PE compares the responses of B1 and B2 within ABBD blocks. These responses are measured from the same trial, within tens of milliseconds of each other. In contrast, substitution PE is computed by comparing C in ABCD to C in ACBD. As noted above, the block structure means that these C responses were recorded in different blocks, when the state of the brain could be different. This may account for the authors' detection of prediction error for omission but not substitution. To address this, the authors should calculate PE for omission using B responses from ABCD.

We performed the suggested analysis (i.e., ABBD vs ABCD) prior to submission but omitted it from the draft for brevity (the effect was the same as with ABBD vs ABBD). We have added the results of standardizing with ABCD as supplementary figure 3.

(3) The behavior of responses to B and C within the trained sequence ABCD differs considerably, yet is not addressed. Responses to B in ABCD potentiate from d0-> d5, yet responses to C in the same sequence go down. This suggests there may be some difference in either the representation of B vs C or position 2 vs 3 in the sequence that may also be contributing to the appearance of prediction errors in ABBD but not ACBD. The authors do not appear to consider this point, which could potentially impact their results. Presenting different stimuli for A,B,C,D across mice would help (in the current paper B is 75 deg and C is 165 deg in all cases). Additionally, other omissions or substitutions at different sequence positions should be tested (eg ABCC or ABDC).

We appreciate the suggestion. Ideally, we could test many different variants, but practical concerns regarding the duration of the imaging sessions prevented us from testing other interesting variations (such as ABCC) in the current study. We are uncertain as to how we should interpret the overall depressed response to element C seen on day 5, but since the effect is shared in both ABCD and ACBD, we don’t think it affected our PE calculations. 

(4) The authors' interpretation of their PCA results is flawed. The authors write "Experience simplifies activity in principal component space". This is untrue based on their data. The variance explained by the first set of PCs does not change with training, indicating that the data is not residing in a lower dimensional ("simpler") space. Instead, the authors show that the first 5 PCs better align with their a priori expectations of the stimulus structure, but that does not mean these PCs necessarily represent more information about the stimulus (and the fact that the authors fail to see an improvement in decoding performance argues against this case). Addressing such a question would be highly interesting, but is lacking in the current manuscript. Without such analysis, referring to the PCs after training as "highly discretized" and "untangled" are largely meaningless descriptions that lack analytical support.

We meant the terms “simpler”, “highly-discretized”, and “untangled” as qualitative descriptions of changes in covariance structure that occurred despite the maintenance of overall dimensionality. As the reviewer notes, the obvious changes in PC space appear to have had practically no effect on decodability or dimensionality, and we found this surprising and worth describing.

(5) The authors report that activity sparsifies, yet provide only the fraction of stimulus-selective cells. Given that cell detection was automated in a manner that takes into account neural activity (using Suite2p), it is difficult to interpret these results as presented. If the authors wish to claim sparsification, they need to provide evidence that the total number of ROIs drawn on each day (the denominator for sparseness in their calculation) is unbiased. Including more (or less) ROIs can dramatically change the calculated sparseness.

The authors mention sparsification as contributing to coding efficiency but do not test this. Training a decoder on variously sized subsets of their data on days 0 and 5 would test whether redundant information is being eliminated in the network over training.

First, we provide evidence for sparseness using a visual responsiveness metric in addition to stimulus-selectivity. Second, it is true that Suite2p’s segmentation is informed by activity and therefore may possibly omit cells with very minimal activity. However, we detected a comparable number of cells on day 5 (n=1500) to day 0 (1368). We reportedly roughly half as many cells are stimulus-selective on day 5 compared with day 0. In order for that to have been a result of biased ROI segmentation, we would have needed to have detected closer to 2600 cells on day 5 rather than 1500.  Therefore, we consider any bias in the segmentation to have had little effect on the main findings.

(6) The authors claim their results show representational drift, but this isn't supported in the data. Rather they show that there is some information in the structure of activity that allows a decoder to learn block ID. But this does not show whether the actual stimulus representations change, and could instead reflect an unrelated artifact that changes over time (responsivity, alertness, bleaching, etc). To actually assess representational drift, the authors should directly compare representations across blocks (one could train a decoder on block 1 and test on blocks 2-5). In the absence of this or other tests of representational drift over blocks, the authors should remove the statement that "These findings suggest that there is a measurable amount of representational drift".

“To actually assess representational drift, the authors should directly compare representations across blocks (one could train a decoder on block 1 and test on blocks 25)”: This is the exact analysis that was performed. Additionally, our analysis of pairwise correlations directly measures representational drift.

“But this does not show whether the actual stimulus representations change, and could instead reflect an unrelated artifact that changes over time (responsivity, alertness, bleaching, etc)”: We have repeated the decoder analysis using normalized population vectors (Supplementary Figure 5) which we believe directly addresses whether the observed drift is due to photobleaching or alertness that would affect the overall magnitudes of response vectors.

Our analysis of block decoding reflects decoders trained on individual stimulus elements, and we show the average over all such decodings (we have clarified this in the text). For example, we trained a decoder on ABCD presentations from block 1 and tested only against ABCD from other blocks, which I believe is the test being suggested by the reviewer. Furthermore, we do show that representational similarity for all stimulus elements reduces gradually and more-or-less monotonically as the time between presentations increases. We believe this is a fairly straightforward test of representational drift as has been reported and used elsewhere (Deitch et al., 2021).

(7) The authors allude to "temporal echoes" in a subheading. This term is never defined, or substantiated with analysis, and should be removed.

We hoped the term ‘temporal echo’ would be understood in the context of rebounding activity during gray periods as supported by analysis in figure 6a. We have eliminated the wording in the updated manuscript.

eLife Assessment

This paper addresses an important topic (normative trajectory modelling), seeking to provide a method aiming to accurately reflect the individual deviation of longitudinal/temporal change compared to the normal temporal change characterized based on a pre-trained population normative model. The evidence provided for the new methods is solid.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors provide a method aiming to accurately reflect the individual deviation of longitudinal/temporal change compared to the normal temporal change characterized based on pre-trained population normative model (i.e., a Bayesian linear regression normative model), which was built based on cross-sectional data. This manuscript aims at solving a recently identified problem of using normative models based on cross-sectional data to make inferences about longitudinal change.

Strengths:

The efforts of this work make a good contribution to addressing an important question of normative modeling. With the greater availability of cross-sectional studies for normative modeling than longitudinal studies, and the inappropriateness of making inferences about longitudinal subject-specific changes using these cross-sectional data-based normative models, it's meaningful to try to address this gap from the aspect of methodological development.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors provide a method aiming to accurately reflect the individual deviation of longitudinal/temporal change compared to the normal temporal change characterized based on pre-trained population normative model (i.e., a Bayesian linear regression normative model), which was built based on cross-sectional data. This manuscript aims at solving a recently identified problem of using normative models based on cross-sectional data to make inferences about longitudinal change.

Strengths:

The efforts of this work make a good contribution to addressing an important question of normative modeling. With the greater availability of cross-sectional studies for normative modeling than longitudinal studies, and the inappropriateness of making inferences about longitudinal subject-specific changes using these cross-sectional data-based normative models, it's meaningful to try to address this gap from the aspect of methodological development.

In the 1st revision, the authors added a simulation study to show how the performance of the classification based on z-diff scores relatively changes with different disruptions (and autocorrelation). Unfortunately, in my view this is insufficient as it only shows how the performance of using z-diff score relatively changes in different scenarios. I would suggest adding the comparison of performance to using the naïve difference in two simple z-scores to first show its better performance, which should also further highlight the inappropriate use of simple z-scores in inferring within-subject longitudinal changes.

Thank you for the suggestion for additional comparison, which we have now implemented in the simulated methods comparison, see Figure 2 and the extended text of Section 2.1.4 Simulation study.

Specifically, we have revised the simulation section to not only illustrate the performance of our z-diff method under various scenarios but also to include a direct comparison with a naïve approach that subtracts two z-scores.

The updated results demonstrate that, compared to the naïve method, the z-diff score consistently maintains a fixed false-positive rate, making it a more robust and controllable approach. Additionally, we show that under conditions of high autocorrelation, the z-diff method is significantly more sensitive in detecting smaller changes than the subtraction method. Importantly, our analysis of a sample from our dataset indicates that high autocorrelation is a prevalent characteristic in real-world data, further supporting the utility of the z-diff method.

We believe that these findings strengthen the case for adopting the z-diff method and underscore the limitations of more intuitive approaches, which, while simple, lack mathematical rigour.

Additionally, Figure 1 is hard to read and obtain the actual values of the performance measure. I would suggest reducing it to several 2-dimensional figures. For example, for several fixed values of rho, how the performance changes with different values of the true disruption (and also adding the comparison to the naïve method (difference in two z-scores)).

We believe that the Reviewer meant Figure 2; indeed, the 3-dimensional visualization, while attractive to some, may have been difficult to read, so we have now replaced it with several 2-dimensional figures as requested.

I would also suggest changing the title to reflect that the evaluation of "intra-subject" longitudinal change is the method's focus.

Thanks for the suggestion. We have now implemented it by changing the title to Using normative models pre-trained on cross-sectional data to evaluate intra-individual longitudinal changes in neuroimaging data.

We hope the changes implemented fulfill the expectations of the Reviewer.

eLife Assessment

Yonk and colleagues provide a valuable, timely, and in-depth study showcasing the role of thalamostriatal inputs in learning and action selection. After characterizing the synaptic properties of these inputs onto different striatal cell types in vitro, they provide solid evidence that posterior medial thalamic nucleus (POm) terminals in striatum are activated during reward expectation and arousal. The overall function of this pathway and the degree to which results are confounded by viral contamination of surrounding nuclei and movements remain open questions.

Reviewer #1 (Public review):

Summary:

This work aims at understanding the role of thalamus POm in dorsal lateral striatum (DLS) projection in learning a sensorimotor associative task. The authors first confirm that POm forms "en passant" synapses with some of the DLS neuronal subtypes. They then perform a go/no-go associative task that consists of the mouse learning to discriminate between two different textures and to associate one of them with an action. During this task they either record the activity of the POm to DLS axons using endoscopy or silence their activity. They report that POm axons in the DLS are activated around the sensory stimulus but that the activity is not modulated by the reward. Last, they showed that silencing the POm axons at the level of DLS slows down learning the task.

The authors show convincing evidence of projections from POm to DLS and that POm inputs to DLS code for whisking whatever the outcome of the task is. However, their results do not allow to conclude if more neurones are recruited during the learning process or if the already activated fibres get activated more strongly. Last, because POm fibres in the DLS are also projecting to S1, silencing the POm fibres in the DLS could have affected inputs in S1 as well and therefore, the slowdown in acquiring the task is not necessarily specific to the POm to DLS pathway.

Strengths:

One of the main strengths of the paper is to go from slice electrophysiology to behaviour to get an in-depth characterization of one pathway. The authors did a comprehensive description of the POm projections to the DLS using transgenic mice to unambiguously identify the DLS neuronal population. They also used a carefully designed sensorimotor association task, and they exploited the results in depth.

It is a very nice effort to have measured the activity of the axons in the DLS not only after the mice have learned the task but throughout the learning process. It shows the progressive increase of activity of POm axons in the DLS, which could imply that there is a progressive strengthening of the pathway. The results show convincingly that POm axons in the DLS are not activated by the outcome of the task but by the whisker activity, and that this activity in average increases with learning.

Weaknesses:

One of the main targets of the striatum from thalamic input are the cholinergic neurons that weren't investigated here, is there information that could be provided?

It is interesting to know that the POm projects to all neuronal types in the DLS, but this information is not used further down the manuscript so the only take-home message of Figure 1 is that the axons that they image or silence in the DLS are indeed connected to DLS neurons and not just passing fibres. In this line, are these axons the same as the ones projecting to S1? If this is the case, why would we expect a different behaviour of the axon activity at the DLS level compared to S1?

The authors used endoscopy to measure the POm axons in the DLS activity, which makes it impossible to know if the progressive increase of POm response is due to an increase of activity from each individual neurons or if new neurons are progressively recruited in the process.

The picture presented in Figure 4 of the stimulation site is slightly concerning as there are hardly any fibres in neocortical layer 1 while there seems to be quite a lot of them in layer 4, suggesting that the animal here was injected in the VB. This is especially striking as the implantation and projection sites presented in Figure 1 and 2 are very clean and consistent with POm injection.

Comment after review: The weaknesses remain as concerns have not been addressed. The dataset is interesting but the interpretation, due partly to the lack of control (especially relative to VPM contamination), is difficult.

Reviewer #2 (Public review):

Summary:

Yonk and colleagues show that the posterior medial thalamus (POm), which is interconnected with sensory and motor systems, projects directly to major categories of neurons in the striatum, including direct and indirect pathway MSNs, and PV interneurons. Activity in POm-striatal neurons during a sensory-based learning task indicates a relationship between reward expectation and arousal. Inhibition of these neurons slows reaction to stimuli and overall learning. This circuit is positioned to feed salient event activation to the striatum to set the stage for effective learning and action selection.

Strengths:

The results are well presented and offer interesting insight into an understudied thalamostriatal circuit. In general, this work is important as part of a general need for an increased understanding of thalamostriatal circuits in complex learning and action selection processes, which have generally received less attention than corticostriatal systems.

Weaknesses:

There could be a stronger connection between the connectivity part of the data - showing that POm neurons context D1, D2, and PV neurons in striatum but with some different properties - and the functional side of the project. One wonders whether the POm neurons projecting to these subtypes or striatal neurons have unique signaling properties related to learning, or if there is a uniform, bulk signal sent to striatum. This is not a weakness per se, as it's reasonable for these questions to be answered in future papers.

All the in vivo activity-related conclusions stem from data from just 5 mice, which is a relatively small sample set. Optogenetic groups are also on the small side.

Comments on revisions:

The revision has a lot of thoughtful discussion added. I think overall the paper is more thorough and will also be a nice set up for a number of future research questions.

Reviewer #3 (Public review):

Yonk and colleagues investigate the role of the thalamostriatal pathway. Specifically, they studied the interaction of the posterior thalamic nucleus (PO) and the dorsolateral striatum in the mouse. First, they characterize connectivity by recording DLS neurons in in vitro slices and optogenetically activating PO terminals. PO is observed to establish depressing synapses onto D1 and D2 spiny neurons as well as PV neurons. Second, the image PO axons are imaged by fiber photometry in mice trained to discriminate textures. Initially, no trial-locked activity is observed, but as the mice learn PO develops responses timed to the audio cue that marks the start of the trial and precedes touch. PO does appear to encode the tactile stimulus type or outcome. Optogenetic suppression of PO terminals in striatum slow task acquisition. The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing.

A great strength of this paper is its timeliness. Thalamostriatal processing has received almost no attention in the past, and the field has become very interested in the possible functions of PO. Additionally, the experiments exploit multiple cutting-edge techniques.

There seem to be some technical/analytical weaknesses. The in vitro experiments appear to have some contamination of nearby thalamic nuclei by the virus delivering the opsin, which could change the interpretation. Some of the statistical analysis of these data also appear inappropriate. The correlative analysis of Pom activity in vivo, licking, and pupil could be more convincingly done.

The bigger weakness is conceptual - why should striatal circuitry need "priming" by thalamus in order to process sensory stimuli? Why would such circuitry even be necessary? Why is a sensory signal from cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? It is unclear from the experiments that the thalamostriatal pathway exists for priming sensory processing. In fact the optogenetic suppression of the thalamostriatal pathway seems to speak against that idea.

Comments on revisions:

The authors have only tweaked the Discussion and not necessarily in ways that addressed our previous comments. They could have fairly easily analyzed the effect of distance of recording from injection site and compared subsets of data depending on contamination beyond PO (my comments 1 and 2) or effects of movements (3 and 4). Minimally, they could have given caveats in the Results and Discussion about these, and I would strongly encourage them to be explicit about the caveats. The analyses would probably be better.

The suggestion that the effects have something to do with priming (5), seems a grasp for function of the circuit.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This work aims to understand the role of thalamus POm in dorsal lateral striatum (DLS) projection in learning a sensorimotor associative task. The authors first confirm that POm forms "en passant" synapses with some of the DLS neuronal subtypes. They then perform a go/no-go associative task that consists of the mouse learning to discriminate between two different textures and to associate one of them with an action. During this task, they either record the activity of the POm to DLS axons using endoscopy or silence their activity. They report that POm axons in the DLS are activated around the sensory stimulus but that the activity is not modulated by the reward. Last, they showed that silencing the POm axons at the level of DLS slows down learning the task.

The authors show convincing evidence of projections from POm to DLS and that POm inputs to DLS code for whisking whatever the outcome of the task is. However, their results do not allow us to conclude if more neurons are recruited during the learning process or if the already activated fibres get activated more strongly. Last, because POm fibres in the DLS are also projecting to S1, silencing the POm fibres in the DLS could have affected inputs in S1 as well and therefore, the slowdown in acquiring the task is not necessarily specific to the POm to DLS pathway.

We thank the reviewer for these constructive comments. The points are addressed below.  

Strengths:

One of the main strengths of the paper is to go from slice electrophysiology to behaviour to get an in-depth characterization of one pathway. The authors did a comprehensive description of the POm projections to the DLS using transgenic mice to unambiguously identify the DLS neuronal population. They also used a carefully designed sensorimotor association task, and they exploited the results in depth.

It is a very nice effort to have measured the activity of the axons in the DLS not only after the mice have learned the task but throughout the learning process. It shows the progressive increase of activity of POm axons in the DLS, which could imply that there is a progressive strengthening of the pathway. The results show convincingly that POm axons in the DLS are not activated by the outcome of the task but by the whisker activity, and that this activity on average increases with learning.

Weaknesses:

One of the main targets of the striatum from thalamic input are the cholinergic neurons that weren't investigated here, is there information that could be provided?

This is true of the parafascicular (Pf) thalamic nucleus, which has been well studied in this context. However, there is much less known about the striatal projections of other thalamic nuclei, including POm, and their inputs to cholinergic neurons. Anatomical tracing evidence from Klug et al. (2018), which mapped brain-wide inputs to striatal cholinergic (ChAT) interneurons, suggests that Pf provides the majority of thalamic innervation of striatal ChAT neurons compared to other thalamic nuclei. Many other thalamic nuclei, including POm, showed very little of no labeling, suggesting weak innervation of ChAT interneurons. However, it is possible that these thalamic nuclei, including POm, do provide functional innervation of ChAT interneurons that is not sufficiently assessed by anatomical tracing. Understanding the innervation patterns of POm-striatal projections beyond the three cell types we have studied here would be an important area of further study.

It is interesting to know that the POm projects to all neuronal types in the DLS, but this information is not used further down the manuscript so the only take-home message of Figure 1 is that the axons that they image or silence in the DLS are indeed connected to DLS neurons and not just passing fibres. In this line, are these axons the same as the ones projecting to S1? If this is the case, why would we expect a different behaviour of the axon activity at the DLS level compared to S1?

Tracing of single POm axons by Ohno et al. (2012) indicated that POm axons form a branched collateral that innervates striatum, while the main axon continues in the rostral-dorsal direction to innervate cortex. We think it is reasonable, based on the morphology, that our optogenetic suppression experiment restricted the suppression of glutamate release to this branch and avoided the other branches of the axon that project to cortex. However, testing this would require monitoring S1 activity during the POm-striatal axon suppression, which we did not do in this study.

It is a very interesting question whether there could be different axon activity behavior in striatum versus S1. There is surprising evidence that POm synaptic terminals are different sizes in S1 and M1 and show different synaptic physiological properties depending on these cortical projection targets (Casas-Torremocha et al., 2022). Based on this, it is possible that POm-striatal synapses show distinct properties compared to cortex; however, this will need to be tested in future work.

The authors used endoscopy to measure the POm axons in the DLS activity, which makes it impossible to know if the progressive increase of POm response is due to an increase of activity from each individual neuron or if new neurons are progressively recruited in the process.

This is a good point. It would be necessary to perform chronic two-photon imaging of POm neurons (or chronic electrophysiological recordings) to determine whether the activity of individual neurons increased versus whether individual neuron activity levels remained similar but new neurons became active with learning. Even under baseline conditions, it is not known in detail what fraction of the population of POm neurons is active during sensory processing or behavior, highlighting how much is still to be discovered in this exciting area of neuroscience.

The picture presented in Figure 4 of the stimulation site is slightly concerning as there are hardly any fibres in neocortical layer 1 while there seems to be quite a lot of them in layer 4, suggesting that the animal here was injected in the VB. This is especially striking as the implantation and projection sites presented in Figures 1 and 2 are very clean and consistent with POm injection.

Although this image was selected to demonstrate the position of the POm injection site and optical fiber implant above striatal axons, the reviewer is correct that there appears to be mixed labeling of axons in L4 and L5a. In some cases, there was expression slightly outside the border of POm (see Fig. 1B, right), which might explain the cortical innervation pattern in this figure. While cortically bound VPM axons pass through the striatum, they do not form synaptic terminals until reaching the cortex (Hunnicutt et al., 2016). If, as may be the case, inhibitory opsins suppress release of neurotransmitter at synaptic terminals more effectively than action potential propagation in axons, it may be likely that optogenetic suppression of POm-striatal terminals is more effective than suppression of action potentials in off-target-labelled VPM axons of passage. Ideally, we could compare effects of suppression of POm-striatal synapses with POm-cortical synapses and VPM-cortical synapses, but this was outside the bandwidth of the present study.

Reviewer #2 (Public Review):

Summary:

Yonk and colleagues show that the posterior medial thalamus (POm), which is interconnected with sensory and motor systems, projects directly to major categories of neurons in the striatum, including direct and indirect pathway MSNs, and PV interneurons. Activity in POm-striatal neurons during a sensory-based learning task indicates a relationship between reward expectation and arousal. Inhibition of these neurons slows reaction to stimuli and overall learning. This circuit is positioned to feed salient event activation to the striatum to set the stage for effective learning and action selection.

Strengths:

The results are well presented and offer interesting insight into an understudied thalamostriatal circuit. In general, this work is important as part of a general need for an increased understanding of thalamostriatal circuits in complex learning and action selection processes, which have generally received less attention than corticostriatal systems.

Weaknesses:

There could be a stronger connection between the connectivity part of the data - showing that POm neurons context D1, D2, and PV neurons in the striatum but with some different properties - and the functional side of the project. One wonders whether the POm neurons projecting to these subtypes or striatal neurons have unique signaling properties related to learning, or if there is a uniform, bulk signal sent to the striatum. This is not a weakness per se, as it's reasonable for these questions to be answered in future papers.

We are very interested to understand the potentially distinct learning-related synaptic and circuit changes that potentially occur at the POm synapses with D1- and D2-SPNs and PV interneurons, and other striatal cell types. We agree that this would be an important topic for further investigation.

All the in vivo activity-related conclusions stem from data from just 5 mice, which is a relatively small sample set. Optogenetic groups are also on the small side.

We appreciate this point and agree that higher N can be important for observing robust effects. A factor of our experiments that helped reduce the number of animals used was the longitudinal design, with repeated measures in the same subjects. This allowed for the internal control of comparing learning effects in the same subject from naïve to expert stages and therefore increased robustness. Even with relatively small group sizes, results were statistically significant, suggesting that the use of more mice was unnecessary, which we considered consistent with best practice in the use of animals in research. We also note that our group sizes were consistent with other studies in the field.  

Reviewer #3 (Public Review):

Yonk and colleagues investigate the role of the thalamostriatal pathway. Specifically, they studied the interaction of the posterior thalamic nucleus (PO) and the dorsolateral striatum in the mouse. First, they characterize connectivity by recording DLS neurons in in-vitro slices and optogenetically activating PO terminals. PO is observed to establish depressing synapses onto D1 and D2 spiny neurons as well as PV neurons. Second, the image PO axons are imaged by fiber photometry in mice trained to discriminate textures. Initially, no trial-locked activity is observed, but as the mice learn PO develops responses timed to the audio cue that marks the start of the trial and precedes touch. PO does appear to encode the tactile stimulus type or outcome. Optogenetic suppression of PO terminals in striatum slow task acquisition. The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing.

A great strength of this paper is its timeliness. Thalamostriatal processing has received almost no attention in the past, and the field has become very interested in the possible functions of PO. Additionally, the experiments exploit multiple cutting-edge techniques.

There seem to be some technical/analytical weaknesses. The in vitro experiments appear to have some contamination of nearby thalamic nuclei by the virus delivering the opsin, which could change the interpretation. Some of the statistical analyses of these data also appear inappropriate. The correlative analysis of Pom activity in vivo, licking, and pupil could be more convincingly done.

The bigger weakness is conceptual - why should striatal circuitry need "priming" by the thalamus in order to process sensory stimuli? Why would such circuitry even be necessary? Why is a sensory signal from the cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? It is unclear from the experiments that the thalamostriatal pathway exists for priming sensory processing. In fact, the optogenetic suppression of the thalamostriatal pathway seems to speak against that idea.

We thank the reviewer for these constructive comments. The points are addressed below.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

Do POm neurons innervate CINs also? The connection between the PF thalamus and CINs is mentioned in a couple of places - one question is how unique are the input patterns for the POm versus adjacent sensorimotor thalamic regions, including the PF? This isn't a weakness per se but knowing the answer to that question would help in forming a more complete picture of how these different thalamostriatal circuits do or do not contribute uniquely to learning and action selection.

Anatomical tracing evidence from Klug et al. (2018), which mapped brain-wide inputs to striatal cholinergic (ChAT) interneurons, suggests that Pf provides the majority of thalamic innervation of striatal ChAT neurons compared to other thalamic nuclei. Many other thalamic nuclei, including POm, showed very little or no labeling, suggesting weak innervation of ChAT interneurons. However, it is possible that these thalamic nuclei, including POm, do provide functional innervation of ChAT interneurons that is not sufficiently assessed by anatomical tracing.

Another difference between Pf and other thalamic nuclei (likely including POm) comes from anatomical tracing evidence (Smith et al., 2014; PMID: 24523677) which indicates that Pf inputs form the majority of their synapses onto dendritic shafts of SPNs, while other thalamic nuclei form synapses onto dendritic spines. Understanding the innervation patterns of POm-striatal projections beyond the three cell types we have studied here, including ChAT neurons and subcellular localization, would be an important area of further study.

It would be useful to know to what extent these POm-striatum neurons are activated generally during movement, versus this discrimination task specifically.

We agree that distinguishing general movement-related activity from task-specific activity would be very useful. Earlier work (Petty et al., 2021) showed a close relationship between POm neuron activity, spontaneous (task-free) whisker movements, and pupil-indexed arousal in head-restrained mice. Oram et al. (2024; PMID: 39003286) recently recorded VPM and POm in freely moving mice during natural movements, finding that activity of both nuclei correlated with head and whisker movements. These studies indicate that POm is generally coactive with exploratory head and whisker movements.

During task performance, the situation may change with training and attentional effects. For example, Petty and Bruno (2024) (https://elifesciences.org/reviewed-preprints/97188) showed that POm activity correlates more closely with task demands than tactile or visual stimulus modality. Our data indicate that POm axonal signals are increased at trial start during anticipation of tactile stimulus delivery and through the sensory discrimination period, then decrease to baseline levels during licking and water reward collection (Fig. 3). Results of Petty and Bruno (2024) together with ours suggest that POm is particularly active during the context of behaviorally relevant task performance. Thus, we think it is likely that, while pupil dilation indexes general movement and arousal, POm activity is more specific to movement and arousal associated with task engagement and behavioral performance. We have strengthened this point in the Discussion.

Many of the data panels and text for legends/axes are quite small, and the stroke on line art is quite faint - overall figures could be improved from a readability standpoint.

We thank the reviewer for their careful attention to the figures. 

Reviewer #3 (Recommendations For The Authors):

Major

(1) Page 4, the Results regarding PSP and distance from injection site. The r-squared is the wrong thing to look at to test for a relationship. One should look at the p-value on the coefficient corresponding to the slope. The p-value is probably significant given the figures, in which case there may be a relationship contrary to what is stated. All the low r-squared value says is that, if there is a relationship, it does not explain a lot of the PSP variability.

We thank the reviewer for alerting us this oversight. We have included the p value (p = 0.0293) in the figure and legend, and indicated that the relationship is “small but significant”.

(2) Figure 1B suggests that the virus injections extend beyond POm and into other thalamic structures. Do any of the results change if the injections contaminating other nuclei are excluded from the analysis? I am not suggesting the authors change the figures/analyses. I am simply suggesting they double-check.

We selected for injections that were predominantly expressing in POm as determined by post-hoc histological analysis (see Fig. 1, right). As above, we think that axons of passage that do not form striatal synapses are less likely to be suppressed than axons with terminals; however, this would need to be determined in further experiments. Because the preponderance of expression is within POm, we think the results would be similar even with a stricter selection criterion. 

(3) The authors conclude that POm and licking are not correlated (bottom of page 6 pertaining to Figures 3A-F). The danger of these analyses is that they assume that GCaMP8 is a perfect linear reporter of POm spikes. The reliability of GCaMP8 has been quantified in some cell types, but not thalamic neurons, which have relatively higher firing rates.

The reviewer is correct that the relationship between GCaMP8 fluorescence changes and spiking has not been sufficiently characterized in thalamic neurons, and that this would be important to do.

What if the indicator is simply saturated late into the trial (after the average reaction time)? It would look like there is no response and one would conclude no correlation, but there could be a very strong correlation.

While saturation is worthy of concern, the signal dynamics here argue against this possibility. The reason is that the signal increased in the early part of the trial and decreased by the end. If saturation was an issue, this would have been apparent during the initial increase. When the signal decreased in amplitude at the end of the trial, this indicates that the signal is not saturated because it is returning from a point closer to its maximum (and is becoming less saturated).

Also, what happens between trials? Are the correlations the same, stronger, weaker? Ideally, the authors would analyze the data during and between trials.

Between trials the signal did not show further changes in baseline beyond what was displayed at the start and end of behavioral trials. There were no consistent increases or decreases in signals between trials, except perhaps during strong whisking bouts. This is anecdotal because we did not analyze between-trial data. However, it is interesting and important to note that signals increased dramatically in amplitude from naïve, early learning to expert behavioral performance (Fig. 3), highlighting that POm-axonal signals relate to behavioral engagement and performance rather than spontaneous behaviors.  

(4) Axonal activity could also appear more correlated with the pupil than licking because pupil dynamics are slow like the dynamics of calcium indicators. These kernels could artificially inflate the correlation. Ideally, the authors could consider these temporal effects. Perhaps they could deconvolve the temporal profiles of calcium and pupil before correlating? Or equivalently incorporate the profiles into their analysis?

We analyzed the lick probability histograms, which had a temporal profile similar to the calcium signals (Fig. 3D,E), ruling out concerns about effects of temporal effects on correlations. It is also worth noting that we observed changes in correlations between calcium signals and pupil with learning stage (Fig. 3I), even though the temporal profiles (signal dynamics) are not changing. Thus, temporal effects of the signals themselves are not the driver of correlations, but rather the changes in relative timing between calcium signals and pupil, as occur with learning.

(5) The authors conclude that PO provides a "behaviorally relevant arousal-related signal" and that this signal "primes" striatal circuitry for sensory processing. The data here support the first part. It is not clear that the data support the second part, largely because it is vague what "priming" of sensory processing or "a key role in the initial stages of action selection (p.9) even means here. Why would such circuitry even be necessary? Why is a sensory signal from the cortex insufficient? Why should the animal more slowly learn the task? How does this fit with existing ideas of striatal plasticity? Some conceptual proposals from the authors, even if speculative and not offered as a conclusion, would be helpful.

We appreciate these good points and have added further consideration and revision of the concept of priming and potential roles in an extensively revised Discussion section.

(6) The photometry shows that PO turns on about 2 seconds before the texture presentation. PO's activity seems locked to the auditory cue, not the texture (Figure 2). This means that the attempt to suppress the thalamostriatal pathway with JAWS (Figure 4) is rather late, isn't it? Some PO signals surely go through. This seems to contradict the idea of priming above. It would be good if the authors could factor this into their narrative. Perhaps labelling the time of the auditory cue in Figure 4C would also be helpful.

The start of texture presentation (movement of the texture panel toward the mouse) and auditory cue occur at the same time. To clarify this, we added a label “start tone” in Figure 4C and also in Figure 2C.

For optogenetic (JAWS) suppression, we intentionally chose a time window between start tone onset and texture presentation, because our photometry experiments showed that this was when the preponderance of the signal occurred. However, the reviewer is correct that our chosen optogenetic suppression (JAWS) onset occurs shortly after the photometry signal has already started, potentially leaving the early photometry signal un-suppressed. Our motivation for choosing a restricted time window surrounding the texture presentation time was 1) to minimize illumination and potential heating of brain tissue; 2) to target a time window that avoids the auditory cue but covers stimulus presentation. We did not want to extend the duration of the suppression to before the trial started, because this could produce task-non-specific effects, such as distraction or loss of attention before the start of the trial.

Even if some signal were getting through before suppression, we don’t think this contradicts the possibility of ‘priming’, because the process underlying priming would still be disrupted even if not totally suppressed. This would alter the temporal relationship between POm-striatal inputs and further corticostriatal inputs (from S1 and M1 cortex, for example). We have included further consideration of these points and possible relation to the priming concept in the Discussion.

Minor

(1) Page 5, "the sensitivity metric is artificially increased". What do you mean "artificially"? The mice are discriminating better. It is true that either a change in HR or FAR can cause the sensitivity metric to change, but there is nothing artificial or misleading about this.

We removed the word artificial and clarified our definition of behaviorally Expert in this context:

“Mice were considered Expert once they had reached ≥ 0.80 Hit Rate and ≤ 0.30 FA Rate for two consecutive sessions in lieu of a strict sensitivity (d’) threshold; we found this definition more intuitive because d’ is enhanced as Hit Rate and FA Rate approach their extremes (0 or 1)”

(2) Page 7, "Upon segmentation (Figure S4G-J)". Do you mean "segregation by trial outcome"?

Corrected.

(3) Page 9, "POm projections may have discrete target-specific functions, such that POm-striatal inputs may play a distinct role in sensorimotor behavior compared to POm-cortical inputs". Would POm-cortical inputs not also be sensorimotor? The somatosensory cortex contains a lot of corticostriatal cells. It also has various direct and indirect links to the motor cortex as well.

We have clarified the wording here to convey the possibility that POm signals could be received and processed differently by striatal versus cortical circuitry, and have moved this statement to later in the discussion for better elaboration.

(4) The Methods state that male and female mice were used. Why not say how many of each and whether or not there are any sex-specific differences?

We added the following information to the Methods:

The number of male and female mice were as follows, by experiment type: 6 male, 4 female (electrophysiology); 3 male, 2 female (fiber photometry); 4 male, 5 female (optogenetics). Data were not analyzed for sex differences.

eLife Assessment

Somatostatin-expressing neurons of the entopeduncular nucleus (EPNSst+) provide a limbic output of the basal ganglia and co-release GABA and Glutamate in their projection to the lateral habenula, a structure that is key for reward-based learning. Combining fiber photometry and computational modeling, the authors provide compelling evidence that EPNSst+ neural activity represents movement, choice direction and reward outcomes in a probabilistic switching task but, surprisingly, neither chronic genetic silencing of these neurons nor selectively elimination glutamate release affected behavioral performance in well-trained animals. This valuable study shows that despite its representation of key task variables, EPNSst+ neurons are dispensable for ongoing performance in a task requiring outcome monitoring to optimize reward. This work will be of interest to those interested in neural circuits, learning, and/or decision making.

Reviewer #1 (Public review):

Summary:

In this series of studies, Locantore et al. investigated the role of SST-expressing neurons in the entopeduncular nucleus (EPNSst+) in probabilistic switching tasks, a paradigm that requires continued learning to guide future actions. In prior work, this group had demonstrated EPNSst+ neurons co-release both glutamate and GABA and project to the lateral habenula (LHb), and LHb activity is also necessary for outcome evaluation necessary for performance in probabilistic decision-making tasks. Previous slice physiology works have shown that the balance of glutamate/GABA co-release is plastic, altering the net effect of EPN on downstream brain areas and neural circuit function. The authors used a combination of in vivo calcium monitoring with fiber photometry and computational modelling to demonstrate that EPNSst+ neural activity represents movement, choice direction and reward outcomes in their behavioral task. However, viral-genetic manipulations to synaptically silence these neurons or selectively eliminate glutamate release had no effect on behavioral performance in well-trained animals. The authors conclude that despite their representation of task variables, EPN Sst+ neuron synaptic output is dispensable for task performance.

Strengths and Weaknesses:

Overall, the manuscript is exceptionally scholarly, with a clear articulation of the scientific question and a discussion of the findings and their limitations. The analyses and interpretations are careful and rigorous. This review appreciates the thorough explanation of the behavioral modelling and GLM for deconvolving the photometry signal around behavioral events, and the transparency and thoroughness of the analyses in the supplemental figures. This extra care has the result of increasing the accessibility for non-experts, and bolsters confidence in the results. To bolster a reader's understanding of results, we suggest it would be interesting to see the same mouse represented across panels (i.e. Fig 1 F-J, Supp 1 F,K etc i.e via inclusion of faint hash lines connecting individual data points across variables. Additionally, Fig 3E demonstrates that eliminating the 'reward' and 'choice and reward' terms from the GLM significantly worsens model performance; to demonstrate the magnitude of this effect, it would be interesting to include a reconstruction of the photometry signal after holding out of both or one of these terms, alongside the 'original' and 'reconstructed' photometry traces in panel D. This would help give context for how the model performance degrades by exclusion of those key terms. Finally, the authors claimed calcium activity increased following ipsilateral movements. However, figure 3C clearly shows that both SXcontra and SXisi increase beta coefficients. Instead, the choice direction may be represented in these neurons, given that beta coefficients increase following CXipsi and before SEipsi, presumably when animals make executive decisions. Could the authors clarify their interpretation on this point? Also, it is not clear if there is a photometry response related to motor parameters (i.e. head direction or locomotion, licking), which could change the interpretation of the reward outcome if it is related to a motor response; could the authors show photometry signal from representative 'high licking' or 'low licking' reward trials, or from spontaneous periods of high. Vs low locomotor speeds (if the sessions are recorded) to otherwise clarify this point?

There are a few limitations with the design and timing of the synaptic manipulations that would improve the manuscript if discussed or clarified. The authors take care to validate the intersectional genetic strategies: Tetanus Toxin virus (which eliminates synaptic vesicle fusion) or CRISPR editing of Slc17a6, which prevents glutamate loading into synaptic vesicles. The magnitude of effect in the slice physiology results are striking. However, this relies on co-infection of a second AAV to express channelrhodopsin for the purposes of validation, and it is surely the case that there will not be 100% overlap between the proportion of cells infected. Alternative means of glutamate packaging (other VGluT isoforms, other transporters etc) could also compensate for the partial absence of VGluT2, which should be discussed. The authors do not perform a complimentary experiment to delete GABA release (i.e. via VGAT editing), which is understandable, given the absence of an effect with the pan-synaptic manipulation. A more significant concern is the timing of these manipulations as the authors acknowledge. The manipulations are all done in well-trained animals, who continue to perform during the length of viral expression. Moreover, after carefully showing that mice use different strategies on the 70/30 version vs the 90/10 version of the task, only performance on the 90/10 version is assessed after the manipulation. Together, the observation that EPNsst activity does not alter performance on a well learned, 90/10 switching task decreases the impact of the findings, as this population may play a larger role during task acquisition or under more dynamic task conditions. Additional experiments could be done to strengthen the current evidence, although the limitations is transparently discussed by the authors.

Finally, intersectional strategies target LHb-projecting neurons, although in the original characterization it is not entirely clear that the LHb is the only projection target of EPNsst neurons. A projection map would help clarify this point.

Overall, the authors used a pertinent experimental paradigm and common cell-specific approaches to address a major gap in the field, which is the functional role of glutamate/GABA co-release from the major basal ganglia output nucleus in action selection and evaluation. The study is carefully conducted, their analyses are thorough, and the data are often convincing and thought-provoking. However, the limitations of their synaptic manipulations with respect to the behavioral assays reduces generalizability and to some extent the impact of their findings.

Comments on the latest version:

Specifically, they have included more thorough analyses to address several concerns related to interpreting activity patterns of EPSst+ neurons. The authors clearly point out that calcium activity increased during ipsilateral movements, and the increase was statistically larger during the choice phase (Figure 2 supplement 1F-G), indicating that these neurons may represent movement and additional factors (e.g. executive decision-making). Correspondingly, we appreciate the thorough explanation of using a GLM model to determine which behavioural variables contribute to observed physiological signals and adding the example reconstructed signal with direction and reward variables omitted in Figure 3 supplements 1 and 2.

Although no new manipulation experiment is added to the manuscript, the authors respond to common critiques related to testing the behavioural effect after the manipulations in well-trained mice. The discussion related to technical limitations, possible compensatory mechanisms and alternative interpretations is thorough and overall satisfying. Based on the behaviour modeling results, the authors speculate that animals need to integrate more evidence from the past to guide choice in a more uncertain environment (70/30 version), instead of adopting a 'win-stay, lose-shift' strategy in the more deterministic 90/10 version. The authors expand the discussion, but the possibility that EPNSst+ neurons contribute to task performance in well-trained animals under uncertainty is not directly tested. Along with other alternative explanations discussed in the manuscript, we think the paper is valuable literature for future studies to understand the basal ganglia circuits in learning and decision-making.

Reviewer #2 (Public review):

Summary:

This paper aimed to determine the role EP sst+ neurons play in a probabilistic switching task.

Strengths:

- The in vivo recording of the EP sst+ neurons activity in the task is one of the strongest parts of this paper. Previous work had recorded from the EP-LHb population in rodents and primates in head fixed configurations, the recordings of this population in a freely moving context is a valuable addition to these studies and has highlighted more clearly that these neurons respond both at the time of choice and outcome.

- The use of a refined intersectional technique to record specifically the EP sst+ neurons is also an important strength of the paper. This is because previous work has shown that there are two genetically different types of glutamatergic EP neurons that project to the LHb. Previous work had not distinguished between these types in their recordings so the current results showing that the bidirectional value signaling is present in the EP sst+ population is valuable.

Weaknesses:

- One of the main weaknesses of the paper is to do with how the effect of the EP sst+ neurons on the behavior was assessed.

o All the manipulations (blocking synaptic release and blocking glutamatergic transmission) are chronic and more importantly the mice are given weeks of training after the manipulation before the behavioral effect is assessed. This means that as the authors point out in their discussion the mice will have time to adjust to the behavioral manipulation and compensate for the manipulations. The results do show that mice can adapt to these chronic manipulations and that the EP sst+ are not required to perform the task. What is unclear is whether the mice have compensated for the loss of EP sst+ neurons and whether they play a role in the task under normal conditions. Acute manipulations or chronic manipulations without additional training would be needed to assess this.

o Another weakness is that the effect of the manipulations was assessed in the 90/10 contingency version of the task. Under these contingencies, mice integrate past outcomes over fewer trials to determine their choice and animals act closer to a simple win-stay-lose switch strategy. Due to this it is unclear if the EP sst+ neurons would play a role in the task when they must integrate over a larger number of conditions in the less deterministic 70/30 version of the task. Indeed it is not clear that lesioning any other regions involved in evaluation of action outcomes such as VTA dopamine neurons, that encode reward prediction errors, would have any deficit when assessed in this way. Due to this, it's not clear if the mice have adapted to solve the task without evaluating action outcomes at all and are just acting in a more deterministic lose switch manner that would not presumably involve any of the circuitry in evaluating action outcomes.

- The authors conclude that they do not see any evidence for bidirectional prediction errors. It is not possible to conclude this. First, they see a large response in the EP sst+ neurons to the omission of an expected reward. This is what would be expected of a negative reward prediction error. There are much more specific well controlled tests for this that are commonplace in head-fixed and freely moving paradigms that could be tested to probe this. The authors do look at the effect of previous trials on the response and do not see strong consistent results, but this is not a strong formal test of what would be expected of a prediction error, either a positive or negative. The other way they assess this is by looking at the size of the responses in different recording sessions with different reward contingencies. They claim that the size of the reward expectation and prediction error should scale with the different reward probabilities. If all the reward probabilities were present in the same session this should be true as lots of others have shown for RPE. Because however this data was taken from different sessions it is not expected that the responses should scale, this is because reward prediction errors have been shown to adaptively scale to cover the range of values on offer (Tobler et al., Science 2005). A better test of positive prediction error would be to give a larger than expected reward on a subset of trials. Either way there is already evidence that responses reflect a negative prediction error in their data and more specific tests would be needed to formally rule in or out prediction error coding especially as previous recordings have shown it is present in previous primate and rodent recordings.

- There are a lot of variables in the GLM that occur extremely close in time such as the entry and exit of a port. If two variables occur closely in time and are always correlated it will be difficult if not impossible for a regression model to assign weights accurately to each event. This is not a large issue, but it is misleading to have regression kernels for port entry and exits unless the authors can show these are separable due to behavioral jitter or a lack of correlation under specific conditions, which does not seem to be the case.

Reviewer #3 (Public review):

Summary:

The authors find that Sst-EPN neurons, which project to the lateral habenula, encode information about response directionality (left vs right) and outcome (rewarded vs unrewarded). Surprisingly, chronic impairment of vesicular signaling in these neurons onto their LHb targets did not impair probabilistic choice behavior.

Strengths:

Strengths of the current work include extremely detailed and thorough analysis of data at all levels, not only of the physiological data, but also an uncommonly thorough analysis of behavioral response patterns.

Weaknesses:

In this revised manuscript, the authors have addressed my earlier critiques.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this series of studies, Locantore et al. investigated the role of SST-expressing neurons in the entopeduncular nucleus (EPNSst+) in probabilistic switching tasks, a paradigm that requires continued learning to guide future actions. In prior work, this group had demonstrated EPNSst+ neurons co-release both glutamate and GABA and project to the lateral habenula (LHb), and LHb activity is also necessary for outcome evaluation necessary for performance in probabilistic decision-making tasks. Previous slice physiology works have shown that the balance of glutamate/GABA co-release is plastic, altering the net effect of EPN on downstream brain areas and neural circuit function. The authors used a combination of in vivo calcium monitoring with fiber photometry and computational modeling to demonstrate that EPNSst+ neural activity represents movement, choice direction, and reward outcomes in their behavioral task. However, viral-genetic manipulations to synaptically silence these neurons or selectively eliminate glutamate release had no effect on behavioral performance in well-trained animals. The authors conclude that despite their representation of task variables, EPN Sst+ neuron synaptic output is dispensable for task performance.

Strengths and Weaknesses:

Overall, the manuscript is exceptionally scholarly, with a clear articulation of the scientific question and a discussion of the findings and their limitations. The analyses and interpretations are careful and rigorous. This review appreciates the thorough explanation of the behavioral modeling and GLM for deconvolving the photometry signal around behavioral events, and the transparency and thoroughness of the analyses in the supplemental figures. This extra care has the result of increasing the accessibility for non-experts, and bolsters confidence in the results.

(1) To bolster a reader's understanding of results, we suggest it would be interesting to see the same mouse represented across panels (i.e. Figures 1 F-J, Supplementary Figures 1 F, K, etc i.e via the inclusion of faint hash lines connecting individual data points across variables.

Thank you for the suggestion. The same mouse is now represented in Fig 1 and Fig 1—Figure Supplement 1 as a darkened circle so it can be followed across different panels. Photometry from this mouse was used as sample date in Figure 2b and Figure 2—figure supplement 1a-b.

(2) Additionally, Figure 3E demonstrates that eliminating the 'reward' and 'choice and reward' terms from the GLM significantly worsens model performance; to demonstrate the magnitude of this effect, it would be interesting to include a reconstruction of the photometry signal after holding out of both or one of these terms, alongside the 'original' and 'reconstructed' photometry traces in panel D. This would help give context for how the model performance degrades by exclusion of those key terms.

We have now added analyses and reconstructed photometry signals from GLMs excluding important predictors in Figure 3—figure supplement 1 and 2. We use the model where both “Direction and reward” were omitted as predictors for the GLM and showed photometry reconstructions aligned to behavioral events used for the full model (Figure 3—figure supplement 1) and partial model (Figure 3—figure supplement 2) to compare model performance.  

(3) Finally, the authors claimed calcium activity increased following ipsilateral movements. However, Figure 3C clearly shows that both SXcontra and SXipsi increase beta coefficients. Instead, the choice direction may be represented in these neurons, given that beta coefficients increase following CXipsi and before SEipsi, presumably when animals make executive decisions. Could the authors clarify their interpretation on this point?

We observe that calcium activity increases during ipsilateral choices as the animal moves toward the ipsilateral side port (e.g. CX_ipsi to SE_ipsi; Fig 2C and Fig 3C). The animal also makes other ipsiversive movements not during the “choice” phase of a trial such as when it is returning to the center port following a contralateral choice (e.g. SX_Contra to CE; Fig 2—figure supplement 1F and Fig 3C). We also observe an increase in calcium activity during these ipsiversive movements (e.g. SX_Contra to CE), but they are not as large as those observed during the choice phase (Fig 2—figure supplement 1G). Therefore, during the choice phase of a trial, activity contains signals related to ipsilateral movement and additional factors (e.g. executive decision making).    

(4) Also, it is not clear if there is a photometry response related to motor parameters (i.e. head direction or locomotion, licking), which could change the interpretation of the reward outcome if it is related to a motor response; could the authors show photometry signal from representative 'high licking' or 'low licking' reward trials, or from spontaneous periods of high vs. low locomotor speeds (if the sessions are recorded) to otherwise clarify this point?

Unfortunately, neither licks nor locomotion were recorded during the behavioral sessions when photometry was recorded. In Figure 2—figure supplement 1a we now show individual trials sorted by trial duration (time elapsed between CE and SE) to illustrate the dynamics of the photometry signal on fast vs slow trials within a session.  

(5) There are a few limitations with the design and timing of the synaptic manipulations that would improve the manuscript if discussed or clarified. The authors take care to validate the intersectional genetic strategies: Tetanus Toxin virus (which eliminates synaptic vesicle fusion) or CRISPR editing of Slc17a6, which prevents glutamate loading into synaptic vesicles. The magnitude of effect in the slice physiology results is striking. However, this relies on the co-infection of a second AAV to express channelrhodopsin for the purposes of validation, and it is surely the case that there will not be 100% overlap between the proportion of cells infected.

For the Tet-tox experiments in Figure 4 we estimate approximately 70±15% of EP^Sst+ neurons expressed Tet-tox based on our histological counts and published stereological counts in EP (Miyamoto and Fukuda, 2015). It is true that channelrhodopsin expression will not overlap 100% with cells infected by the other virus, indeed our in vitro synaptic physiology shows small residual postsynaptic currents following optogenetic stimulation either from incomplete blockade of synaptic release or neurons that expressed channelrhodopsin but not Tettx (Figure 4—figure supplement 1J-K). The same is shown for CRISPR mediated deletion of Slc17a6 (Fig 5 – Fig supplement 1J-K).  

(6) Alternative means of glutamate packaging (other VGluT isoforms, other transporters, etc) could also compensate for the partial absence of VGluT2, which should be discussed.

While single cell sequencing (Wallace et al, 2017) has shown EP^Sst+ neurons do not express Slc17a7/8 (vGlut1 or vGlut3) it is possible that these genes could be upregulated following CRISPR mediated deletion of Slc17a6, however we do not see evidence of this with our in vitro synaptic physiology (EPSCs are significant suppressed, Figure 5 – Fig supplement 1J-K) and therefore can conclude it is highly unlikely to occur to a significant degree in our experiments. This is now included in the Discussion.

(7) The authors do not perform a complimentary experiment to delete GABA release (i.e. via VGAT editing), which is understandable, given the absence of an effect with the pan-synaptic manipulation. A more significant concern is the timing of these manipulations as the authors acknowledge. The manipulations are all done in well-trained animals, who continue to perform during the length of viral expression. Moreover, after carefully showing that mice use different strategies on the 70/30 version vs the 90/10 version of the task, only performance on the 90/10 version is assessed after the manipulation. Together, the observation that EPNsst activity does not alter performance on a well-learned, 90/10 switching task decreases the impact of the findings, as this population may play a larger role during task acquisition or under more dynamic task conditions. Additional experiments could be done to strengthen the current evidence, although the limitation is transparently discussed by the authors.

As mentioned above, it is possible that a requirement for EP^Sst+ neurons could be revealed if the experiment was conducted with different parameters (either different reward probabilities, fluctuating reward probabilities within a session, or withholding additional training during viral expression). It is difficult to predict which version of the task, if any, would be most likely to reveal a requirement for EP^Sst+ neurons based on our results. We favor testing for EP^Sst+ function using a new behavioral paradigm that allows us to carefully examine task learning following EP manipulations in an independent study.

(8) Finally, intersectional strategies target LHb-projecting neurons, although in the original characterization, it is not entirely clear that the LHb is the only projection target of EPNsst neurons. A projection map would help clarify this point.

In a previous study we confirmed that EP^Sst+ neurons project exclusively to the LHb using cell-type specific rabies infection and examining all reported downstream regions for axon collaterals (Wallace et al 2017, Suppl. Fig 6F-G). When EP^Sst+ neurons were labeled we did not observe axon collaterals in known targets of EP such as ventro-antero lateral thalamus, red nucleus, parafasicular nucleus of the thalamus, or the pedunculopontine tegmental nucleus, only in the LHb. Additionally, using single cell tracing techniques, others have shown EP neurons that exclusively project to the LHb (Parent et al, 2001).

Overall, the authors used a pertinent experimental paradigm and common cell-specific approaches to address a major gap in the field, which is the functional role of glutamate/GABA co-release from the major basal ganglia output nucleus in action selection and evaluation. The study is carefully conducted, their analyses are thorough, and the data are often convincing and thought-provoking. However, the limitations of their synaptic manipulations with respect to the behavioral assays reduce generalizability and to some extent the impact of their findings.

Reviewer #2 (Public Review):

Summary:

This paper aimed to determine the role EP sst+ neurons play in a probabilistic switching task.

Strengths:

The in vivo recording of the EP sst+ neuron activity in the task is one of the strongest parts of this paper. Previous work had recorded from the EP-LHb population in rodents and primates in head-fixed configurations, the recordings of this population in a freely moving context is a valuable addition to these studies and has highlighted more clearly that these neurons respond both at the time of choice and outcome.

The use of a refined intersectional technique to record specifically the EP sst+ neurons is also an important strength of the paper. This is because previous work has shown that there are two genetically different types of glutamatergic EP neurons that project to the LHb. Previous work had not distinguished between these types in their recordings so the current results showing that the bidirectional value signaling is present in the EP sst+ population is valuable.

Weaknesses:

(1) One of the main weaknesses of the paper is to do with how the effect of the EP sst+ neurons on the behavior was assessed.

(a) All the manipulations (blocking synaptic release and blocking glutamatergic transmission) are chronic and more importantly the mice are given weeks of training after the manipulation before the behavioral effect is assessed. This means that as the authors point out in their discussion the mice will have time to adjust to the behavioral manipulation and compensate for the manipulations. The results do show that mice can adapt to these chronic manipulations and that the EP sst+ are not required to perform the task. What is unclear is whether the mice have compensated for the loss of EP sst+ neurons and whether they play a role in the task under normal conditions. Acute manipulations or chronic manipulations without additional training would be needed to assess this.

Unfortunately, when mice are given a three week break from behavioral training (the time required to allow for adequate viral expression) behavioral performance on the task (p(highport), p(switch), trial number, trial time, etc.) is significantly degraded. Animals do eventually recover to previous performance levels, but this takes place during a 4-5 day “relearning” period. Here we sought to examine if EP^Sst+ neurons are required for continued task performance and chose to continue to train the animals following viral injection to avoid the “relearning” period that occurs following an extended break from behavioral training which may have made it difficult to interpret changes in behavioral performance due to the viral manipulation vs relearning.  

Acute manipulations were not used because we planned to compare complete synaptic ablation (Tettx) and single neurotransmitter ablation (CRISPR Slc17a6) over similar time courses and we know of no acute manipulation that could achieve single neurotransmitter ablation. 

(b) Another weakness is that the effect of the manipulations was assessed in the 90/10 contingency version of the task. Under these contingencies, mice integrate past outcomes over fewer trials to determine their choice and animals act closer to a simple win-stay-lose switch strategy. Due to this, it is unclear if the EP sst+ neurons would play a role in the task when they must integrate over a larger number of conditions in the less deterministic 70/30 version of the task.

It is possible that a requirement for EP^Sst+ neurons could be revealed if the experiment was conducted with different parameters (either different reward probabilities, fluctuating reward probabilities within a session, or withholding additional training during viral expression). It is difficult to predict which version of the task, if any, would be most likely to reveal a requirement for EP^Sst+ neurons based on our results. We favor testing for EP^Sst+ function using a new behavioral paradigm that allows us to carefully examine task learning following EP manipulations in an independent study.

The authors show an intriguing result that the EP sst+ neurons are excited when mice make an ipsilateral movement in the task either toward or away from the center port. This is referred to as a choice response, but it could be a movement response or related to the predicted value of a specific action. Recordings while mice perform movement outside the task or well-controlled value manipulations within the session would be needed to really refine what these responses are related to.

If activity of EP^Sst+ neurons included a predicted value component, we would expect to see a change in activity during ipsilateral movements when the previous trial was rewarded vs unrewarded. This is examined in Fig 2—figure suppl. 2C, where we compare EP^Sst+ responses during ipsilateral trials when the previous trials were either rewarded (blue) or unrewarded (gray). We show that EP^Sst+ activity prior to side port entry (SE) is identical in these two trial types indicating that EP^Sst+ neurons do not show evidence of predicted value of an action in this context. Therefore, we conclude that increased EP^Sst+ activity during ipsilateral trials is primarily related to ipsilateral movement following CX (we call this the “choice” phase of the trial). We also show that other ipsiversive movements outside of the “choice” phase of a trial (such as the return to center port following a contralateral trial) show a smaller but significant increase in activity (Figure 2—figure supplement 1F-G). Therefore, whereas the activity observed during ipsilateral choice contains signals related to ipsilateral movement and additional factors, our data suggest that predicted value is not one of those factors. We will clarify this point and our definition of “choice” in the narrative.  

(2) The authors conclude that they do not see any evidence for bidirectional prediction errors. It is not possible to conclude this. First, they see a large response in the EP sst+ neurons to the omission of an expected reward. This is what would be expected of a negative reward prediction error. There are much more specific well-controlled tests for this that are commonplace in head-fixed and freely moving paradigms that could be tested to probe this. The authors do look at the effect of previous trials on the response and do not see strong consistent results, but this is not a strong formal test of what would be expected of a prediction error, either a positive or negative. The other way they assess this is by looking at the size of the responses in different recording sessions with different reward contingencies. They claim that the size of the reward expectation and prediction error should scale with the different reward probabilities. If all the reward probabilities were present in the same session this should be true as lots of others have shown for RPE. Because however this data was taken from different sessions it is not expected that the responses should scale, this is because reward prediction errors have been shown to adaptively scale to cover the range of values on offer (Tobler et al., Science 2005). A better test of positive prediction error would be to give a larger-than-expected reward on a subset of trials. Either way, there is already evidence that responses reflect a negative prediction error in their data and more specific tests would be needed to formally rule in or out prediction error coding especially as previous recordings have shown it is present in previous primate and rodent recordings.

We do not conclude that we see no evidence for RPE and the reviewer is correct in stating that a large increase in EP^Sst+ activity following omission of an expected reward would be expected of a negative reward prediction error. However, this observation alone is not strong enough evidence that EP^Sst+ neurons signal RPE. When we looked for additional evidence of RPE within our experiments we did not find consistent demonstrations of its existence in our data. When performing photometry measurements of dopamine release in the striatum, RPE signals are readily observed with a task identical to ours using trial history to as a modifier of reward prediction (Chantranupong, et al 2023). Of course, there could be a weaker more heterogeneous RPE signal in EP^Sst+ neurons that we cannot detect with our methods. As we state in the discussion, RPE signals may be present in a subset of individual neurons (as observed in Stephenson-Jones et al, 2016 and Hong and Hikosaka, 2008) which are below our detection threshold using fiber photometry. Additionally, Hong and Hikosaka, 2008 show that LHb-projecting GPi neurons show both positive and negative reward modulations which may obscure observation of RPE signals with photometry recordings that arise from population activity of genetically defined neurons.   

(3) There are a lot of variables in the GLM that occur extremely close in time such as the entry and exit of a port. If two variables occur closely in time and are always correlated it will be difficult if not impossible for a regression model to assign weights accurately to each event. This is not a large issue, but it is misleading to have regression kernels for port entry and exits unless the authors can show these are separable due to behavioral jitter or a lack of correlation under specific conditions, which does not seem to be the case.

It is true that two variables that are always correlated are redundant in a GLM. For example, center entry (CE) and center exit (CX) occur in quick succession in most trials and are highly correlated (Figure 1C). For this reason, when only one is removed as a predictor from the model but not the other there is a very small change in the MSE of the fit (Figure 3E, -CE or -CX). However, when both are removed model performance decreases further indicating that center-port nose-pokes do contribute to model performance (Figure 3E, -CE/CX). Due to the presence/absence of reward following side port entry there is substantial behavioral jitter (due to water consumption in rewarded trials) that the SE and SX are not always correlated, therefore the model performs worse when either are omitted alone, but even worse still when both SE/SX are omitted together (Figure 3E, -SE/SX). We will update Figure 3 and the narrative to make this more explicit.

Reviewer #3 (Public Review):

Summary:

The authors find that Sst-EPN neurons, which project to the lateral habenula, encode information about response directionality (left vs right) and outcome (rewarded vs unrewarded). Surprisingly, impairment of vesicular signaling in these neurons onto their LHb targets did not impair probabilistic choice behavior.

Strengths:

Strengths of the current work include extremely detailed and thorough analysis of data at all levels, not only of the physiological data but also an uncommonly thorough analysis of behavioral response patterns.

Weaknesses:

Overall, I saw very few weaknesses, with only two issues, both of which should be possible to address without new experiments:

(1) The authors note that the neural response difference between rewarded and unrewarded trials is not an RPE, as it is not affected by reward probability. However, the authors also show the neural difference is partly driven by the rapid motoric withdrawal from the port. Since there is also a response component that remains different apart from this motoric difference (Figure 2, Supplementary Figure 1E), it seems this is what needs to be analyzed with respect to reward probability, to truly determine whether there is no RPE component. Was this done?

We thank the reviewer for this comment, we believe this is particularly important for unrewarded trials as SE and SX occur in rapid succession. In Figure 2—figure supplement 2A-B we now show the photometry signal from Rewarded and Unrewarded ipsilateral trials aligned to SX for different reward probabilities. We quantify the signals for different reward probabilities during a 500ms window immediately prior to SX but find no differences between groups.  

(2) The current study reaches very different conclusions than a 2016 study by Stephenson-Jones and colleagues despite using a similar behavioral task to study the same Sst-EPN-LHb circuit. This is potentially very interesting, and the new findings likely shed important light on how this circuit really works. Hence, I would have liked to hear more of the authors' thoughts about possible explanations of the differences. I acknowledge that a full answer might not be possible, but in-depth elaboration would help the reader put the current findings in the context of the earlier work, and give a better sense of what work still needs to be done in the future to fully understand this circuit.

For example, the authors suggest that the Sst-EPN-LHb circuit might be involved in initial learning, but play less of a role in well-trained animals, thereby explaining the lack of observed behavioral effect. However, it is my understanding that the probabilistic switching task forces animals to continually update learned contingencies, rendering this explanation somewhat less persuasive, at least not without further elaboration (e.g. maybe the authors think it plays a role before the animals learn to switch?).

Also, as I understand it, the 2016 study used manipulations that likely impaired phasic activity patterns, e.g. precisely timed optogenetic activation/inhibition, and/or deletion of GABA/glutamate receptors. In contrast, the current study's manipulations - blockade of vesicle release using tetanus toxin or deletion of VGlut2, would likely have blocked both phasic and tonic activity patterns. Do the authors think this factor, or any others they are aware of, could be relevant?

We have added further discussion of the Stephenson-Jones, et al 2016 study as well as the Lazaridis, et al 2019 study which shows no effect of phasic stimulation of EP when specifically manipulating EP^Sst+ (vGat+/vGlut2+) neurons rather than vGlut2+ neurons as in the Stephenson-Jones study.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In some places, there seems to be a mismatch between referenced figures and texts. For example:

(1) The authors described that 'This increase in activity was seen for all three reward probabilities tested (90/10, 80/20, and 70/30) and occurred while the animal was engaged in ipsiversive movements as similar increases were observed following side exit (SX) on contralateral trials as the animal was moving from the contralateral side port back to the center port (Figure 2-Figure Supplement 1c)', but supplement 1c is not about calcium dynamics around the SX event. I presume they mean Figure 2-Figure Supplement 1d.

Yes, this will be corrected in the revised manuscript.

(2) The authors explained that increased EPSst+ neuronal activity following an unrewarded outcome was partially due to the rapid withdrawal of the animal's snout following an unrewarded outcome however, differences in rewarded and unrewarded trials were still distinguishable when signals were aligned to side port exit indicating that these increases in EPSst+ neuronal activity on unrewarded trials were a combination of outcome evaluation (unrewarded) and side port withdrawal occurring in quick succession (SX, Figure 2 - Figure Supplement 1d). I presume that they mean Figure 2 - Figure Supplement 1e.

Yes, this will be corrected in the revised manuscript.

Minor suggestions related to specific figure presentation are below:

Figure 2 and supplement figures:

(1) Figure 2B: the authors may consider presenting outcome-related signals recorded from all trials, including both ipsilateral and contralateral events, and align signals to SE when reward consumption presumably begins, rather than aligning to CE.

We have added sample recordings from ipsilateral and contralateral trials and sorted them by trial duration to allow for clearer presentation of activity following CE and SE (Figure 2—figure supplement 1a-b).

(2) The authors described that 'This increase in activity was seen for all three reward probabilities tested (90/10, 80/20, and 70/30) and occurred while the animal was engaged in ipsiversive movements as similar increases were observed following side exit (SX) on contralateral trials as the animal was moving from the contralateral side port back to the center port (Figure 2-Figure Supplement 1c)', but supplement 1c is not about calcium dynamics around the SX event. I presume they mean Figure 2-Figure Supplement 1d.

Yes, this will be corrected in the revised manuscript.

(3) The authors explained that increased EPSst+ neuronal activity following an unrewarded outcome was partially due to the rapid withdrawal of the animal's snout following an unrewarded outcome however, differences in rewarded and unrewarded trials were still distinguishable when signals were aligned to side port exit indicating that these increases in EPSst+ neuronal activity on unrewarded trials were a combination of outcome evaluation (unrewarded) and side port withdrawal occurring in quick succession (SX, Figure 2 -Figure Supplement 1d). I presume that they mean Figure 2 -Figure Supplement 1e.

Yes, this will be corrected in the revised manuscript.

Figure 3 and supplement figures:

(1) Figure 3C-F: it is hard to compare the amplitude of calcium signals between different behaviour events without a uniform y-axis.

The scale for the y-axis on Figure 3C-D is uniform for all panels. Figure 3E is also uniform for all boxplots. The reviewer may be referring to Figure 2C-F, but the y-axis for all of the photometry data is uniform for all panels and the horizontal line represents zero. The y-axis for the quantification on the right of each panel is scaled to the max/min for each comparison.

(2) Figure 3E is difficult to follow. The authors explained that the 'SE' variable is generated by collapsing the ipsilateral and contralateral port entries, and hence the variable has no choice of direction information. I assumed that the 'SX', 'CE', and 'CX' variables are generated similarly. It is not clear if this is the case for the 'side', 'centre' and 'choice' variables. The authors explained that 'omitting center port entry/exit together or individually also resulted in decreased GLM performance but to a smaller degree than the omission of choice direction (Figure 3e, "-Center")'. My understanding is that they created the Centre variable by collapsing ipsilateral and contralateral centre port entry/exit together. The Centre variable should have no choice of direction information. How is the Center variable generated differently from omitting centre port entry/exit together? I would ask the authors to explain the model and different variables a bit more thoroughly in the text.

We apologize for the confusion. All ten variables used to train the full GLM are listed in Fig. 3C. In Figure 3E variable(s) were omitted to test how they contributed to GLM performance (data labeled “None” is the full model with all variables). Omitted variables are now defined as follows: -Rew = Rew+Unrew removed, -Direction = Ipsi/Contra designation removed and collapsed into CE, CX, SE, SX, -Direction & Rew = Ipsi/Contra info removed from all variables + Rew/Unrew removed, -CE/CX = Ipsi/Contra CE and CX removed, -CE = Ipsi/contra CE removed, -CX = Ipsi/contra CX removed, -SE/SX = Ipsi/Contra SE and SX removed, -SE = Ipsi/contra SE removed, -SX = Ipsi/contra SX removed. This clarification has also been added to the Generalized Linear Model section of Materials and Methods.

Figure 5 and supplement figures:

There are no representative and summary figures show the specificity and efficiency of oChief-tdTomato or Tetx-GFP expression. Body weight changes following virus injection are not well described.

A representative image of Tettx GFP expression are shown in Fig. 4A and percent of infected EP^Sst+ neurons is described in the text (70±15.1% (mean±SD), 1070±230 neurons/animal, n=6 mice). Most oChief-tdTom animals were used for post-hoc electrophysiology experiments and careful quantification of viral expression was not possible. However, Slc17a6 deletion was confirmed in these animals (Fig. 5 – Fig supplement 1J-K) to confirm the manipulation was effective in the experimental group. A representative image of oChief-tdTom expression is shown in Fig. 5A.

We now mention the body weight changes observed following Tettx injection in the narrative.

Reviewer #2 (Recommendations For The Authors):

(1) In the RFLR section you state that "this variable decays...", a variable can't decay only the value of a variable can change. Also, it is not mentioned what variable is being discussed. There are lots of variables in the model so this should be made clear.

We now state, “This variable (β) changes over trials and is updated with new evidence from each new trial’s choice and outcome with an additional bias towards or away from its most recent choice (Figure 1-figure supplement 2A-C).”

(2) I couldn't find in the results section, or the methods section the details for the Tet tx experiments, were mice trained and tested on 90/10 only? Were they trained while the virus was expressing etc? This should be added.

In the methods section we state, ”For experiments where we manipulated synaptic release in EP^Sst+ neurons (Figures 4-5) we trained mice (reward probabilities 90/10, no transparent barrier present) to the following criteria for the 5 days prior to virus injection: 1) p(highport) per session was greater than or equal to 0.80 with a variance less than 0.003, 2) p(switch) per session was less than or equal to 0.15 with a variance less than 0.001, 3) the p(left port) was between 0.45-0.55 with a variance less than 0.005, and 4) the animal performed at least 200 trials in a session. The mean and variance for these measurements was calculated across the five session immediately preceding surgery. The criterion were determined by comparing performance profiles in separate animals and chosen based on when animals first showed stable and plateaued behavioral performance. Following surgery, mice were allowed to recover for 3 days and then continued to train for 3 weeks during viral expression. Data collected during the 5 day pre-surgery period was then compared to data collected for 10 sessions following the 3 weeks allotted for viral expression (i.e. days 22-31 post-surgery).”

Reviewer #3 (Recommendations For The Authors):

(1) The kernel in Figure 3C shows an activation prior to CE on "contra" trials that is not apparent in Figure 2C which shows no activation prior to CE on either contra or ipsi trials. Given that movement directionality prior to CE is dictated by the choice on the PREVIOUS trial, is the "contra" condition in 3C actually based on the previous trial? If so, this should be clarified.

On most “contra” trials the animal is making an ipsiversive movement just prior to CE as it returns to the center from the contralateral side-port (as most trials are no “switch” trials). Therefore, an increase in activity is expected and shown most clearly following SX for contralateral trials in Fig 2 –Fig suppl 1F. A significant increase in activity prior to CE on contra trials compared to ipsi trials can also be seen in Fig 2C, its just not as large a change as the increase observed following CE for ipsi. trials. The comparison between activity observed during the two types of ipsiversive movements is now shown directly in Figure 2—figure supplement 1G.

(2) Paragraph 7 of the discussion uses a phrase "by-in-large", which probably should be "by and large".

Thank you for the correction.

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

Readers would also benefit from coding individual data points by sex and noting N/sex.

Sex breakdown has been added to figure legends for each experiment, full statistical reporting is now also include in the figure legends.

eLife Assessment

Cav2 voltage-gated calcium channels play key roles in regulating synaptic strength and plasticity. In contrast to mammals, invertebrates like Drosophila encode a single Cav2 channel, raising questions on how diversity in Cav2 is achieved from a single gene. Here, the authors present solid evidence that two alternatively spliced Cac isoforms enable important changes in Cav2 expression, localization, and function in synaptic transmission and plasticity at the Drosophila neuromuscular junction. How the isoforms affect synaptic calcium channel levels remains less clear. This study provides insights into the roles of voltage-gated calcium channel splice isoforms in synaptic transmission.

Reviewer #2 (Public review):

This study by Bell et al. focuses on understanding the roles of two alternatively spliced exons in the single Drosophila Cav2 gene cac. The authors generate a series of cac alleles in which one or the other mutually exclusive exons are deleted to determine the functional consequences at the neuromuscular junction. They find alternative splicing at one exon encoding part of the voltage sensor impacts the activation voltage as well as localization to the active zone. In contrast, splicing at the second exon pair does not impact Cav2 channel localization, but it appears to determine the abundance of the channel at active zones. Together, the authors propose that alternative splicing at the Cac locus enables diversity in Cav2 function generated through isoform diversity generated at the single Cav2 alpha subunit gene encoded in Drosophila.

Overall this is an excellent, rigorously validated study that defines unanticipated functions for alternative splicing in Cav2 channels. The authors have generated an important toolkit of mutually exclusive Cac splice isoforms that will be of broad utility for the field, and show convincing evidence for distinct consequences of alternative splicing of this single Cav2 channel at synapses. Importantly, the authors use electrophysiology and quantitative live sptPALM imaging to determine the impacts of Cac alternative splicing on synaptic function. There remain some questions regarding the mechanisms underlying the changes in Cac localization to somatodendritic compartments. Nonetheless, this is a compelling investigation of alternative splicing in Cav2 channels that should be of interest to many researchers.

Reviewer #3 (Public review):

Summary:

Bell and colleagues studied how different splice isoforms of voltage-gated CaV2 calcium channels affect channel expression, localization, function, synaptic transmission, and locomotor behavior at the larval Drosophila neuromuscular junction. They reveal that one mutually exclusive exon located in the fourth transmembrane domain encoding the voltage sensor is essential for calcium channel expression, function, active zone localization, and synaptic transmission. Furthermore, a second mutually exclusive exon residing in an intracellular loop containing the binding sites for Caβ and G-protein βγ subunits promotes the expression and synaptic localization of around ~50% of CaV2 channels, thereby contributing to ~50% of synaptic transmission. This isoform enhances release probability, as evident from increased short-term depression, is vital for homeostatic potentiation of neurotransmitter release induced by glutamate receptor impairment, and promotes locomotion. The roles of the two other tested isoforms remain less clear.

Strengths:

The study is based on solid data that was obtained with a diverse set of approaches. Moreover, it generated valuable transgenic flies that will facilitate future research on the role of calcium channel splice isoforms in neural function.

Weaknesses:

Comments on revisions:

The authors addressed most points. However, from my point of view, the new data (somatodendritic cac currents in adult motoneurons of IS4B mutants without the pre-pulse, and localization of IS4A channels in the larval brain) do not strongly support that the IS4B exon is required for cacophony localization. According to their definition of localization, IS4B is required for cacophony channels to enter motoneuron boutons and to localize to active zones. In case of a true localization defect (without degradation, as they claim), IS4A channels should mislocalize to the soma, axon, or dendrite. However, they do not find them in motoneurons of IS4B mutants. Furthermore, I find the interpretation of the voltage clamp data in flight motoneurons rather difficult. On the one hand, sustained HVA cac currents are strongly attenuated/absent in IS4B mutants. On the other hand, total cac currents (without the -50 mV pre-pulse, not shown in the original submission) are less affected in IS4B mutants. Based on these data, they conclude that IS4B is required for sustained HVA cac currents and that IS4A channel isoforms are expressed and functional. How does this relate to a localization defect at the NMJ? Finally, detecting IS4A channels in other cell types and regions is not a strong argument for a localization defect at the NMJ. I, therefore, suggest toning down the conclusions regarding a localization defect in IS4B mutants/a role for the IS4B exon in cac localization. It should be also discussed how a splice isoform in S4 may result in no detectable cac channels at the NMJ or regulate subcellular channel localization.

I have a few additional points, mainly related to the responses to my previous points:

(1) The authors state "active zones at the NMJ contain only cac isoforms with the IS4B exon. Nevertheless, the small representative EPSC remaining in IS4B mutants suggests that there is synchronous release in the absence of IS4B (Fig. 3B). Are the small EPSCs in dIS4B (Fig. 3B) indeed different from noise/indicative of evoked release? If yes, which cac channels may drive these EPSCs? IS4A channels?<br /> (2) (Related to previous point 4) The authors argue that EPSC amplitudes are not statistically different between Canton S and IS4A mutants (Fig. 2F). However, the Canton S group appears undersampled, thus precluding conclusions based on statistics. Moreover, the effect size Canton S vs. dIS4A looks similar to the one of Canton S vs. dIS4A/dIS4B.<br /> (3) (Related to previous point 11): Can they cite a paper relating calcium channel inactivation to EPSC half width/decay kinetics to support their speculation that "decreased EPSC half width could be caused by significantly faster channel inactivation kinetics" (p. 42, l.42). In addition, many papers have demonstrated that mini decay kinetics provide valuable insights into GluR subunit composition at the Drosophila NMJ (e.g., Schmid et al., 2008 https://doi.org/10.1038/nn.2122). Thus, the statement "Mini decay kinetic analysis because this depends strongly on the distance of the recording electrode to the actual site of transmission in these large muscle cells" is not valid and should be revised.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Bell et. al. describes an analysis of the effects of removing one of two mutually exclusive splice exons at two distinct sites in the Drosophila CaV2 calcium channel Cacophony (Cac). The authors perform imaging and electrophysiology, along with some behavioral analysis of larval locomotion, to determine whether these alternatively spliced variants have the potential to diversify Cac function in presynaptic output at larval neuromuscular junctions. The author provided valuable insights into how alternative splicing at two sites in the calcium channel alters its function.

Strengths:

The authors find that both of the second alternatively spliced exons (I-IIA and I-IIB) that are found in the intracellular loop between the 1st and second set of transmembrane domains can support Cac function. However, loss of the I-IIB isoform (predicted to alter potential beta subunit interactions) results in 50% fewer channels at active zones and a decrease in neurotransmitter release and the ability to support presynaptic homeostatic potentiation. Overall, the study provides new insights into Cac diversity at two alternatively spliced sites within the protein, adding to our understanding of how regulation of presynaptic calcium channel function can be regulated by splicing.

Weaknesses:

The authors find that one splice isoform (IS4B) in the first S4 voltage sensor is essential for the protein's function in promoting neurotransmitter release, while the other isoform (IS4A) is dispensable. The authors conclude that IS4B is required to localize Cac channels to active zones. However, I find it more likely that IS4B is required for channel stability and leads to the protein being degraded, rather than any effect on active zone localization. More analysis would be required to establish that as the mechanism for the unique requirement for IS4B.

(1) We thank the reviewer for this important point. In fact, all three reviewers raised the same question, and the reviewing editor pointed out that caution or additional experiments were required to distinguish between IS4 splicing being important for cac channel localization versus channel stability/degradation. We provide multiple sets of experiments as well as text and figure revisions to strengthen our claim that the IS4B exon is required for cacophony channels to enter motoneuron presynaptic boutons and localize to active zones.

a. If IS4B was indeed required for cac channel stability (and not for localization to active zones) IS4A channels should be instable wherever they are. This is not the case because we have recorded somatodendritic cacophony currents from IS4A expressing adult motoneurons that were devoid of cac channels with the IS4B exon. Therefore, IS4A cac channels are not instable but underlie somatodendritic voltage dependent calcium currents in these motoneurons. These new data are now shown in the revised figure 3C and referred to in the text on page 7, line 42 to page 8 line 9.

b. Similarly, if IS4B was required for channel stability, it should not be present anywhere in the nervous system. We tested this by immunohistochemistry for GFP tagged IS4A channels in the larval CNS. Although IS4A channels are sparsely expressed, which is consistent with low expression levels seen in the Western blots (Fig. 1E), there are always defined and reproducible patterns of IS4A label in the larval brain lobes as well as in the anterior part of the VNC. This again shows that the absence of IS4A from presynaptic active zones is not caused by channel instability, because the channel is expressed in other parts of the nervous system. These data are shown in the new supplementary figure 1 and referred to in the text on page 15, lines 3 to 8.

c. As suggested in a similar context by reviewers 1 and 2, we now show enlargements of the presence of IS4B channels in presynaptic active zones as well as enlargements of the absence of IS4A channels in presynaptic active zones in the revised figures 2A-C and 3A. In these images, no IS4A label is detectable in active zones or anywhere else throughout the axon terminals, thus indicating that IS4B is required for expressing cac channels in the axon terminal boutons and localizing it to active zones. Text and figure legends have been adjusted accordingly.

d. Related to this, reviewer 1 also recommended to quantify the IS4A and ISB4 channel intensity and co-localization with the active zone marker brp (recommendation for authors). After following the reviewers’ suggestion to adjust the background values in IS4A and IS4B immunolabels to identical (revised Figs. 2A-C), it becomes obvious that IS4A channel are not detectable above background in presynaptic terminals or active zones, thus intensity is close to zero. We still calculated the Pearsons co-localization coefficient for both IS4 variants with the active zone marker brp. For IS4B channels the Pearson’s correlation coefficient is control like, just above 0.6, whereas for IS4A channels we do not find colocalization with brp (Pearson’s below 0.25). These new analyses are now shown in the revised figure 2D and referred to on page 6, lines 33 to 38.

e. Consistent with our finding that IS4B is required for cac channel localization to presynaptic active zones, upon removal of IS4B we find no evoked synaptic transmission (Fig. 2 in initial submission, now Fig. 3B).

Together these data are in line with a unique requirement of IS4B at presynaptic active zones (not excluding additional functions of IS4B), whereas IS4A containing cac isoforms are not found in presynaptic active zones and mediate different functions.

Reviewer #2 (Public Review):

This study by Bell et al. focuses on understanding the roles of two alternatively spliced exons in the single Drosophila Cav2 gene cac. The authors generate a series of cac alleles in which one or the other mutually exclusive exons are deleted to determine the functional consequences at the neuromuscular junction. They find alternative splicing at one exon encoding part of the voltage sensor impacts the activation voltage as well as localization to the active zone. In contrast, splicing at the second exon pair does not impact Cav2 channel localization, but it appears to determine the abundance of the channel at active zones.

Together, the authors propose that alternative splicing at the Cac locus enables diversity in Cav2 function generated through isoform diversity generated at the single Cav2 alpha subunit gene encoded in Drosophila.

Overall this is an excellent, rigorously validated study that defines unanticipated functions for alternative splicing in Cav2 channels. The authors have generated an important toolkit of mutually exclusive Cac splice isoforms that will be of broad utility for the field, and show convincing evidence for distinct consequences of alternative splicing of this single Cav2 channel at synapses. Importantly, the authors use electrophysiology and quantitative live sptPALM imaging to determine the impacts of Cac alternative splicing on synaptic function. There are some outstanding questions regarding the mechanisms underlying the changes in Cac localization and function, and some additional suggestions are listed below for the authors to consider in strengthening this study. Nonetheless, this is a compelling investigation of alternative splicing in Cav2 channels that should be of interest to many researchers.

(2) We believe that the additional data on cac IS4A isoform localization and function as detailed above (response to public review 1) has strengthened the manuscript and answered some of the remaining questions the reviewer refers to. We are also grateful for the specific additional reviewer suggestions which we have addressed point-by-point and refer to below (section recommendations for authors).

Reviewer #3 (Public Review):

Summary:

Bell and colleagues studied how different splice isoforms of voltage-gated CaV2 calcium channels affect channel expression, localization, function, synaptic transmission, and locomotor behavior at the larval Drosophila neuromuscular junction. They reveal that one mutually exclusive exon located in the fourth transmembrane domain encoding the voltage sensor is essential for calcium channel expression, function, active zone localization, and synaptic transmission. Furthermore, a second mutually exclusive exon residing in an intracellular loop containing the binding sites for Caβ and G-protein βγ subunits promotes the expression and synaptic localization of around ~50% of CaV2 channels, thereby contributing to ~50% of synaptic transmission. This isoform enhances release probability, as evident from increased short-term depression, is vital for homeostatic potentiation of neurotransmitter release induced by glutamate receptor impairment, and promotes locomotion. The roles of the two other tested isoforms remain less clear.

Strengths:

The study is based on solid data that was obtained with a diverse set of approaches. Moreover, it generated valuable transgenic flies that will facilitate future research on the role of calcium channel splice isoforms in neural function.

Weaknesses:

(1) Based on the data shown in Figures 2A-C, and 2H, it is difficult to judge the localization of the cac isoforms. Could they analyze cac localization with regard to Brp localization (similar to Figure 3; the term "co-localization" should be avoided for confocal data), as well as cac and Brp fluorescence intensity in the different genotypes for the experiments shown in Figure 2 and 3 (Brp intensity appears lower in the dI-IIA example shown in Figure 3G)? Furthermore, heterozygous dIS4B imaging data (Figure 2C) should be quantified and compared to heterozygous cacsfGFP/+.

According to the reviewer’s suggestion, we have quantified cac localization relative to brp localization by computing the Pearson’s correlation coefficient for controls and IS4A as well as IS4B animals. These new data are shown in the revised Fig. 2D and referred to on page 6, lines 33-38. Furthermore, we now confirm control-like Pearson’s correlation coefficients for all exon out variants except ΔIS4B and show Pearson’s correlation coefficients for all genotypes side-by-side in the revised Fig. 4D (legend has been adjusted accordingly). In addition, in response to the recommendations to authors, we now provide selective enlargements for the co-labeling of Brp and each exon out variant in the revised figures 2-4. We have also adjusted the background in Fig. 2C (ΔIS4B) to match that in Figs. 2A and B (control and ΔIS4A). This allows a fair comparison of cac intensities following excision of IS4B versus excision of IS4A and control (see also Fig 3). Together, this demonstrates the absence of IS4A label in presynaptic active zones much clearer. As suggested, we have also quantified brp puncta intensity on m6/7 across homozygous exon excision mutants and found no differences (this is now stated for IS4A/IS4B in the results text on page 6, lines 37/38 and for I-IIA/I-IIB on page 8, lines 42-44.). We did not quantify the intensity of cacophony puncta upon excision of IS4B because the label revealed no significant difference from background (which can be seen much better in the images now), but the brp intensities remained control-like even upon excision of IS4B.

(2) They conclude that I-II splicing is not required for cac localization (p. 13). However, cac channel number is reduced in dI-IIB. Could the channels be mis-localized (e.g., in the soma/axon)? What is their definition of localization? Could cac be also mis-localized in dIS4B? Furthermore, the Western Blots indicate a prominent decrease in cac levels in dIS4B/+ and dI-IIB (Figure 1D). How do the decreased protein levels seen in both genotypes fit to a "localization" defect? Could decreased cac expression levels explain the phenotypes alone?

We have now precisely defined what we mean by cac localization, namely the selective label of cac channels in presynaptic active zones that are defined as brp puncta, but no cac label elsewhere in the presynaptic bouton (page 6, lines 18 to 20). On the level of CLSM microscopy this corresponds to overlapping cac puncta and brp puncta, but no cac label elsewhere in the bouton. Based on the additional analysis and data sets outlined in our response 1 (see above) we conclude that excision of IS4B does not cause channel mislocalization because we find reproducible expression patterns elsewhere in the nervous system as well as somatodendritic cac current in ΔIS4B (for detail see above). Therefore, the isoforms containing the mutually exclusive IS4A exon are expressed and mediate other functions, but cannot substitute IS4B containing isoforms at the presynaptic AZ. In fact, our Western blots are in line with reduced cac expression if all isoforms that mediate evoked release are missing, again indicating that the presynapse specific cac isoforms cannot be replaced by other cac isoforms. This is also in line with the sparse expression of IS4A throughout the CNS as seen in the new supplementary figure 1 (for detail see above).

(3) Cac-IS4B is required for Cav2 expression, active zone localization, and synaptic transmission. Similarly, loss of cac-I-IIB reduces calcium channel expression and number. Hence, the major phenotype of the tested splice isoforms is the loss of/a reduction in Cav2 channel number. What is the physiological role of these isoforms? Is the idea that channel numbers can be regulated by splicing? Is there any data from other systems relating channel number regulation to splicing (vs. transcription or post-transcriptional regulation)?

Our data are not consistent with the idea that splicing regulates channel numbers. Rather, splicing can be used to generate channels with specific properties that match the demand at the site of expression. For the IS4 exon pair we find differences in activation voltage between IS4A and IS4B channels (revised Fig. 3C), with IS4B being required for sustained HVA current. IS4A does not localize to presynaptic active zones at the NMJ and is only sparsely expressed elsewhere in the NS (new supplementary Fig. 1). By contrast, IS4B is abundantly expressed in many neuropils. Therefore, taking out IS4B takes out the more abundant IS4 isoform. This is consistent with different expression levels for IS4 isoforms that have different functions, but we do not find evidence for splicing regulating expression levels per se.

Similarly, the I-II mutually exclusive exon pair differs markedly in the presence or absence of G-protein βγ binding sites that play a role in acute channel regulation as well the conservation of the sequence for β-subunit binding (see page 5, lines 9-17). Channel number reduction in active zones occurs specifically if expression of the cac channels with the G_βγ-binding site as well as the more conserved β-subunit binding is prohibited by excision of the I-IIB exon (see Fig. 5F). Vice versa, excision of I-IIA does not result in reduced channel numbers. This scenario is consistent with the hypothesis that conserved β-subunit binding affects channel number in the active zone (see page 17, lines 3 to 6 and lines 33-36), but we have no evidence that I-II splicing per se affects channel number.

(4) Although not supported by statistics, and as appreciated by the authors (p. 14), there is a slight increase in PSC amplitude in dIS4A mutants (Figure 2). Similarly, PSC amplitudes appear slightly larger (Figure 3J), and cac fluorescence intensity is slightly higher (Figure 3H) in dI-IIA mutants. Furthermore, cac intensity and PSC amplitude distributions appear larger in dI-IIA mutants (Figures 3H, J), suggesting a correlation between cac levels and release. Can they exclude that IS4A and/or I-IIA negatively regulate release? I suggest increasing the sample size for Canton S to assess whether dIS4A mutant PSCs differ from controls (Figure 2E). Experiments at lower extracellular calcium may help reveal potential increases in PSC amplitude in the two genotypes (but are not required). A potential increase in PSC amplitude in either isoform would be very interesting because it would suggest that cac splicing could negatively regulate release.

There are several possibilities to explain this, but as none of the effects is statistically significant, we prefer to not investigate this in further depth. However, given that we cannot find IS4A in presynaptic active zones (revised figures 2C and 3A plus the new enlargements 2Ci and 3Ai, revised text page 6, lines 22 to 24 and 29 to 31, and page 7, second paragraph, same as public response 1D) IS4A channels cannot have a direct negative effect on release probability. Nonetheless, given that IS4A containing cac isoforms mediate functions in other neuronal compartments (see revised Fig. 3C) it may regulate release indirectly by affecting e.g. action potential shape. Moreover, in response to the more detailed suggestions to authors we provide new data that give additional insight.

(5) They provide compelling evidence that IS4A is required for the amplitude of somatic sustained HVA calcium currents. However, the evidence for effects on biophysical properties and activation voltage (p. 13) is less convincing. Is the phenotype confined to the sustained phase, or are other aspects of the current also affected (Figure 2J)? Could they also show the quantification of further parameters, such as CaV2 peak current density, charge density, as well as inactivation kinetics for the two genotypes? I also suggest plotting peaknormalized HVA current density and conductance (G/Gmax) as a function of Vm. Could a decrease in current density due to decreased channel expression be the only phenotype? How would changes in the sustained phase translate into altered synaptic transmission in response to AP stimulation?

Most importantly, sustained HVA current is abolished upon excision of IS4B (not IS4A, we think the reviewer accidentally mixed up the genotype) and presynaptic active zones at the NMJ contain only cac isoforms with the IS4B exon. This indicates that the cac isoforms that mediate evoked release encode HVA channels. The somatodendritic currents shown in the revised figure 3C (previously 2J) that remain upon excision of IS4B are mediated by IS4A containing cac isoforms. Please note that these never localize to the presynaptic active zone, and thus do not contribute to evoked release. Therefore, the interpretation is that specifically sustained HVA current encoded by IS4B cac isoforms is required for synaptic transmission. Reduced cac current density due to decreased channel expression is not the cause for impaired evoked release upon IS4B excision, but instead, the cause is the absence of any cac channels in active zones. IS4B-containing cac isoforms encode sustained HVA current, and we speculate that this might be a well suited current to minimize cacophony channel inactivation in the presynaptic active zone. Given that HVA current shows fast voltage dependent activation and fast inactivation upon repolarization, it is useful at large intraburst firing frequencies as observed during crawling (Kadas et al., 2017) without excessive cac inactivation (see page 15, Kadas, lines 16 to 20).

However, we agree with the reviewer that a deeper electrophysiological analysis of splice isoform specific cac currents will be instructive. We have now added traces of control and ΔIS4B from a holding potential of -90 mv (revised Fig. 3C, bottom traces and revised text on page 7, line 43 to page 8, lines 1 to 10), and these are also consistent with IS4B mediating sustained HVA cac current. However, further analysis of activation and inactivation voltages and kinetics suffers form space clamp issues in recordings from the somata of such complex neurons (DLM motoneurons of the adult fly contain roughly 6000 µm of dendrites with over 4000 branches, Ryglewski et al., 2017, Neuron 93(3):632-645). Therefore, we will analyze the currents in a heterologous expression system and present these data to the scientific community as a separate study at a later time point.

(6) Why was the STED data analysis confined to the same optical section, and not to max. intensity z-projections? How many and which optical sections were considered for each active zone? What were the criteria for choosing the optical sections? Was synapse orientation considered for the nearest neighbor Cac - Brp cluster distance analysis? How do the nearest-neighbor distances compare between "planar" and "side-view" Brp puncta?

Maximum intensity z-projections would be imprecise because they can artificially suggest close proximity of label that is close by in x and y but far away in z. Therefore, the analysis was executed in xy-direction of various planes of entire 3D image stacks. We considered active zones of different orientations (Figs. 5C, D) to account for all planes. In fact, we searched the entire z-stacks until we found active zones of all orientations within the same boutons, as shown in figures 5C1-C6. The same active zone orientations were analyzed for all exon-out mutants with cac localization in active zones. The distance between cac and brp did not change if viewed from the side or any other orientation. We now explain this in more clarity in the results text on page 9, lines 23/24.

(7) Cac clusters localize to the Brp center (e.g., Liu et al., 2011). They conclude that Cav2 localization within Brp is not affected in the cac variants (p. 8). However, their analysis is not informative regarding a potential offset between the central cac cluster and the Brp "ring". Did they/could they analyze cac localization with regard to Brp ring center localization of planar synapses, as well as Brp-ring dimensions?

In the top views (planar) we did not find any clear offset in cac orientation to brp between genotypes. In such planar synapses (top views, Fig. 5D, left row) we did not find any difference in Brp ring dimensions. We did not quantify brp ring dimensions rigorously, because this study focusses on cac splice isoform-specific localization and function. Possible effects of different cac isoforms on brp-ring dimensions or other aspects of scaffold structure are not central to our study, in particular given that brp puncta are clearly present even if cac is absent from the synapse (Fig. 3A), indicating that cac is not instructive for the formation of the brp scaffold.

(8) Given the accelerated PSC decay/ decreased half width in dI-IIA (Fig. 5Q), I recommend reporting PSC charge in Figure 3, and PPR charge in Figures 5A-D. The charge-based PPRs of dI-IIA mutants likely resemble WT more closely than the amplitude-based PPR. In addition, miniature PSC decay kinetics should be reported, as they may contribute to altered decay kinetics. How could faster cac inactivation kinetics in response to single AP stimulation result in a decreased PSC half-width? Is there any evidence for an effect of calcium current inactivation on PSC kinetics? On a similar note, is there any evidence that AP waveform changes accelerate PSC kinetics? PSC decay kinetics are mainly determined by GluR decay kinetics/desensitization. The arguments supporting the role of cac splice isoforms in PSC kinetics outlined in the discussion section are not convincing and should be revised.

We agree that reporting charge in figure 3 is informative and do so in the revised text. Since the result (no significant difference in the PSCs between between CS, cac^GFP, ^ΔI-IIA, and transheterozygous I-IIA/I-IIB, but significantly smaller values in ΔI-IIB) remained unchanged no matter whether charge or amplitude were analyzed, we decided to leave the figure as is and report the additional analysis in the text (page 8, lines 40 to 42). This way, both types of analysis are reported. Please note that EPSC amplitude is slightly but not significantly increased upon excision of I-IIA (Fig. 4J), whereas EPSC half amplitude width is significantly smaller (Fig. 5Q, now revised Fig 6R). Together, a tendency of increased EPSC amplitudes and smaller half amplitude width result in statistically insignificant changes in EPSC in ∆I-IIA (now discussed on page 15, lines 37 to 40). We also understand the reviewer’s concern attributing altered EPSC kinetics to presynaptic cac channel properties. We have toned down our interpretation in the discussion and list possible alterations in presynaptic AP shape or cac channel kinetics as alternative explanations (not conclusions; see revised discussion on page 15, line 40 to page 16, line 2). Moreover, we have quantified postsynaptic GluRIIA abundance to test whether altered PSC kinetics are caused by altered GluRIIA expression. In our opinion, the latter is more instructive than mini decay kinetic analysis because this depends strongly on the distance of the recording electrode to the actual site of transmission in these large muscle cells. Although we find no difference in GluRIIA expression levels we now clearly state that we cannot exclude other changes in GluR receptor fields, which of course, could also explain altered PSC kinetics. We have updated the discussion on page 16, lines 2/3 accordingly.

(9) Paired-pulse ratios (PPRs): On how many sweeps are the PPRs based? In which sequence were the intervals applied? Are PPR values based on the average of the second over the first PSC amplitudes of all sweeps, or on the PPRs of each sweep and then averaged? The latter calculation may result in spurious facilitation, and thus to the large PPRs seen in dI-IIB mutants (Kim & Alger, 2001; doi: 10.1523/JNEUROSCI.21-2409608.2001).

We agree that the PP protocol and analyses had to be described more precisely in the methods and have done so on page 23, lines 31 to 37 in the methods. Mean PPR values are based on the PPRs of each sweep and then averaged. We are aware of the study of Kim and Alger 2001 and have re-analyzed the PP data in both ways outlined by the reviewer. We get identical results with either analyses method. Spurious facilitation is thus not an issue in our data. We now explain this in the methods section along with the PPR protocol. The large spread seen in dI-IIB is indeed caused by reduced calcium influx into active zones with fewer channels, as anticipated by the reviewer (see next point).

(10) Could the dI-IIB phenotype be simply explained by a decrease in channel number/ release probability? To test this, I propose investigating PPRs and short-term dynamics during train stimulation at lower extracellular Ca2+ concentration in WT. The Ca2+ concentration could be titrated such that the first PSC amplitude is similar between WT and dI-IIB mutants. This experiment would test if the increased PPR/depression variability is a secondary consequence of a decrease in Ca2+ influx, or specific to the splice isoform.

In fact, the interpretation that decreased PSC amplitude upon I-IIB excision is caused mainly by reduced channel number is precisely our interpretation (see discussion page 14, last paragraph to page 15, first paragraph in the original submission, now page 16, second paragraph paragraph). In addition, we are grateful for the reviewer’s suggestion to triturate the external calcium such that the first PSC amplitude in matches in ∆I-IIB and control. This experiment tests whether altered short term plasticity is solely a function of altered channel number or whether additional causes, such as altered channel properties, also play into this. We triturated the first pulse amplitude in ∆I-IIB to match control and find that paired pulse ratio and the variance thereof are not different anymore. Therefore, the differences observed in identical external calcium can be fully explained by altered channel numbers. This additional dataset is shown in the revised figures 6D and E and referred to in the results section on page 10, lines 14 to 25 and the discussion on page16, lines 36 to 38.

(11) How were the depression kinetics analyzed? How many trains were used for each cell, and how do the tau values depend on the first PSC amplitude? Time constants in the range of a few (5-10) milliseconds are not informative for train stimulations with a frequency of 1 or 10 Hz (the unit is missing in Figure 5H). Also, the data shown in Figures 5E-K suggest slower time constants than 5-10 ms. Together, are the data indeed consistent with the idea that dIIIB does not only affect cac channel number, but also PPR/depression variability (p. 9)?

For each animal the amplitudes of all subsequent PSCs in each train were plotted over time and fitted with a single exponential. For depression at 1 and 10 Hz, we used one train per animal, and 5-6 animals per genotype (as reflected in the data points in Figs. 6I, M). This is now explained in more detail in the revised methods section (page 23, lines 39 to 41). The tau values are not affected by the amplitude of the first PSC. First, we carefully re-fitted new and previously presented depression data and find that the taus for depression at low stimulation frequencies (1 and 10Hz) are not affected by exon excisions at the I-II site. We thank the reviewer for detecting our error in units and tau values in the previous figure panels 5H and L (this has now been corrected in the revised figure panels 6I and M). Given that PSC amplitude upon I-IIB excision is significantly smaller than in controls and following I-IIA excision, we suspected that the time course of depression at low stimulation frequency is not significantly affected by the amount of calcium influx during the first PSC. To further test this, we followed the reviewer ’s suggestion and re-measured depression at 1 and 10 Hz for cac-GFP controls and for delta I-IIB in a higher external calcium concentration (1.8 mM), so that the first PSC was increased in amplitude in both genotypes (1.8 mM external calcium triturates the PSC amplitude in delta I-IIB to match that of controls measured in 0.5 mM external calcium, see revised Figs. 6H, L). Neither in control, nor in delta I-IIB did this affect the time course of synaptic depression (see revised Figs. 6I, M). This indicates that at low stimulation frequencies (1 and 10Hz) the time course of depression is not affected by mean quantal content. This is consistent with the paired pulse ratio at 100 ms interpulse interval shown in figures 6A-D. However, for synaptic depression at 1 Hz stimulation the variability of the data is higher for delta I-IIB (independent of external calcium concentration, see rev. Fig. 6I), which might also be due to reduced channel number in this genotype. Taken together, the data are in line with the idea that altered cac channel numbers in active zones are sufficient to explain all effects that we observe upon I-IIB excision on PPRs and synaptic depression at low stimulation frequencies. This is now clarified in the revised text on page 12, lines 3 to 7.

(12) The GFP-tagged I-IIA and mEOS4b-tagged I-IIB cac puncta shown in Figure 6N appear larger than the Brp puncta. Endogenously tagged cac puncta are typically smaller than Brp puncta (Gratz et al., 2019). Also, the I-IIA and I-IIB fluorescence sometimes appear to be partially non-overlapping. First, I suggest adding panels that show all three channels merged. Second, could they analyze the area and area overlap of I-IIA and I-IIB with regard to each other and to Brp, and compare it to cac-GFP? Any speculation as to how the different tags could affect localization? Finally, I recommend moving the dI-IIA and dI-IIB localization data shown in Figure 6N to an earlier figure (Figure 1 or Figure 3).

We now show panels with the two I-II cac isoforms merged in the revised figure 7H (previously 6N). We also tested merging all three labels as suggested, but found this not instructive for the reader. We thank the reviewer for pointing out that the Brp puncta appeared smaller than the cac puncta in some panels. We carefully went through the data and found that the Brp puncta are not systematically smaller than the cac puncta. Please note that punctum size can appear quite differently, depending on different staining qualities as well as different laser intensities and different point spread in different imaging channels. The purpose of this figure was not to analyze punctum size and labeling intensity, but instead, to demonstrate that I-IIA and I-IIB are both present in most active zones, but some active zones show only I-IIB labeling, as quantified in figure 7I. We did not follow the suggestion to conduct additional co-localization analyses and compare it with cac-GFP controls, because Pearson co-localization coefficients for cac-GFP and all exon-out variants analyzed, including delta I-IIA and delta I-IIB are presented in the revised figure 4D. Moreover, delta I-IIA and delta I-IIB show similar Manders 1 and 2 co-localization coefficients with Brp (see Figs. 4E, F). We do not want to speculate whether the different tags have any effect on localization precision. Artificial differences in localization precision can also be suggested by different antibodies, but we know from our STED analyses with identical tags and antibodies for all isoforms that I-IIA and I-IIB co-localize identically with Brp (see Figs. 5A-E). Finally, we prefer to not move the figure because we believe it is informative to show our finding that active zones usually contain both splice I-II variants together with the finding that only I-IIB is required for PHP.

Recommendations for the authors:

Reviewing Editor Comments:

We thank you for your submission. All three reviewers urge caution in interpreting the S4 splice variant playing a role specifically in Cac localization, as opposed to just leading to instability and degradation. There are other issues with the electrophysiological experiments, a need for improved imaging and analyses, and some areas of interpretation detailed in the reviews.

We agree that additional data was required to conclude that IS4 splicing plays a specific role in cac channel localization and is not just leading to channel instability and degradation. As outlined in detail in our response to reviewer 1, comment 1, we conducted several sets of experiments to support our interpretation. First, electrophysiological experiments show that upon removal of IS4B, which eliminates synaptic transmission at the larval NMJ and cac positive label in presynaptic active zones, somatodendritic cac current is reliably recorded (new data in revised figure 3C). This is not in line with a channel instability or degradation effect, but instead with IS4B containing isoforms being required and sufficient for evoked release from NMJ motor terminals, whereas IS4A isoforms are not sufficient for evoked release from axon terminals, but IS4A isoforms alone can mediate a distinct component of somatodendritic calcium current. Second, immunohostochemical analyses reveal that IS4A, which is not present in NMJ presynaptic active zones, is expressed sparsely, but in reproducible patterns in the larval brain lobes and in specific regions of the anterior VNC parts (new supplementary figure 1). Again, the absence of a IS4A-containing cac isoform from presynaptic active zones but their simultaneous presence in other parts of the nervous system is in accord with isoform specific localization, but not with general channel isoform instability. Third, enlargements of NMJ boutons with brp positive presynaptic active zones confirm the absence of IS4A and the presence of IS4B in active zones (these enlargements are now shown in the revised figures 2A-C, 3A, and 4A-C). Fourth, as suggested we have quantified the Pearson co-localization of IS4 isoforms with Brp in presynaptic active zones (revised Fig. 2D). This confirms quantitatively similar co-localization of IS4B and control with Brp, but no co-localization of IS4A with Brp. In fact, the labeling intensity of IS4A in presynaptic active zones is quantitatively not significantly different from background, no IS4A label is detected anywhere in the axon terminals at the NMJ, but we find IS4 label in the CNS. Together, these data strongly support our interpretation that the IS4 splice site plays a distinct role in cac channel localization. Figure legends as well as results and discussion section have been modified accordingly (the respective page and line numbers are listed in our-point-by-point responses).

In addition, we have carefully addressed all other public comments as well as all other recommendations for authors by providing multiple new data sets, new image analyses, and revising text. Addressing the insightful comments of all three reviewers and the reviewing editor has greatly helped to make the manuscript better.

Reviewer #1 (Recommendations For The Authors):

The conclusion that the IS4B exon controls Cac localization to active zones versus simply being required for channel abundance is not well supported. The authors need to either mention both possibilities or provide stronger support for the active zone localization model if they want to emphasize this point.

We agree and have included several additional data sets as outlined in our response to point 1 of reviewer 1 and to the reviewing editor (see above). These new data strongly support our interpretation that the IS4B exon controls Cac localization to active zones and is not simply required for channel abundance. The additions to the figures and accompanying text (including the respective figure panel, page, and line numbers) are listed in the point-bypoint responses to the reviewers’ public suggestions.

Figure 2C staining for Cac localization in the delta 4B line is difficult to compare to the others, as the background staining is so high (muscles are green for example). As such, it is hard to determine whether the arrows in C are just background.

We had over-emphasized the green label to show that there really is no cacophony label in active zones. However, we agree that this hampered image interpretation. Thus, we have adjusted brightness such that it matches the other genotypes (see new figure panel 2C, and figure 3A, bottom). Revising the figure as suggested by the reviewer shows much more clearly that IS4B puncta are detected exclusively in presynaptic active zones, whereas IS4A channels are not detectable in active zones or anywhere else in the axon terminal boutons. Quantification of IS4A label in brp positive active zones confirms that labeling intensity is not significantly above background (page 6, lines 29 to 31 and page 7, lines 19 to 21). Therefore, IS4A is not detectable in active zones at the NMJ.

It seems more likely that the removal of the 4B exon simply destabilizes the protein and causes it to be degraded (as suggested by the Western), rather than mislocalizing it away from active zones. It's hard to imagine how some residue changes in the S4 voltage sensor would control active zone localization to begin with. The authors should note that the alternative explanation is that the protein is just degraded when the 4B exon is removed.

Based on additional data and analyses, we disagree with the interpretation that removal of IS4B disrupts protein integrity and present multiple lines of evidence that support sparse expression of IS4A channels (ΔIS4B). As outlined in our response to reviewer 1 and to the reviewing editor, we show (1) in new immunohistochemical stainings (new supplementary figure 1) that upon removal of IS4B, sparse label is detectable in the VNC and the brain lobes (for detail see above). (2) In our new figure 3C, we show cacophony-mediated somatodendritic calcium currents recorded from adult flight motoneurons in a control situation and upon removal of IS4B that leaves only IS4A channels. This clearly demonstrates that IS4A underlies a substantial component of the HVA somatodendritic calcium current, although it is absence from axon terminals. This is in line with isoform specific functions at different locations, but not with IS4A instability/degradation. (3) We do not agree with the reviewer’s interpretation of the Western Blot data in figure 1E (formerly figure 1D). Together with our immunohistochemical data that show sparse cacophony IS4A expression, we think that the faint band upon removal of IS4B in a heterozygous background (that reduces labeled channels even further) reflects the sparseness of IS4A expression. This sparseness is not due to channel instability, but to IS4A functions that are less abundant than the ubiquitously expressed cac^IS4B channels at presynaptic active zones of fast chemical synapses (see page 15, lines 24 to 29).

If they really want to claim the 4B exon governs active zone localization, much higher quality imaging is required (with enlarged views of individual boutons and their AZs, rather than the low-quality full NMJ imaging provided). Similarly, higher resolution imaging of Cac localization at Muscle 12 (Figure 2H) boutons would be very useful, as the current images are blurry and hard to interpret. Figure 6N shows beautiful high-resolution Cac and Brp imaging in single boutons for the I-II exon manipulations - the authors should do the same for the 4B line. For all immuno in Figure 2, it is important to quantify Cac intensity as well. There is no quantification provided, just a sample image. The authors should provide quantification as they do for the delta I-II exons in Figure 3.

We did as suggested and added figure panels to figure 2A-C and to new figures 3A (formerly part of figure 2 and 4A-C (formerly figure 3) showing magnified label at the NMJ AZs to better judge on cacophony expression after exon excision. These data are now referred to in the results section on page 6, lines 22 to 24, page 7, lines 18 to 21 and page 8, lines 17/18.

As suggested, we now also provide quantification of co-localization with brp puncta as Pearson’s correlation coefficient for control, IS4B, and IS4A in the new figure panel 2D (text on page 6, lines 34 to 38). This further underscores control-like active zone localization of IS4B but no significant active zone localization of IS4A. As suggested, we quantified now also the intensity of IS4B label in active zones, and it was not different from control (see revised figure 4H and text on page 8, lines 38/39). We did not quantify the intensity of IS4A label, because it was not over background (text, page 6, lines 30/31).

Reviewer #2 (Recommendations For The Authors):

(1a) Questions about the engineered Cac splice isoform alleles:

The authors using CRISPR gene editing to selectively remove the entire alternatively spliced exons of interest. Do the authors know what happens to the cac transcript with the deleted exon? Is the deleted exon just skipped and spliced to the next exon? Or does the transcript instead undergo nonsense-mediated decay?

We do not believe that there is nonsense mediated mRNA decay, because for all exon excisions the respective mRNA and protein are made. Protein has been detected on the level of Western blotting and immunocytochemistry. Therefore, we are certain that the mRNA is viable for each exon excision (and we have confirmed this for low abundance cac protein isoforms by rt-PCR), but only subsets of cac isoforms can be made from mRNAs that are lacking specific exons. However, we can not make any statements as to whether the lack of specific protein isoforms exerts feedback on mRNA stability, the rate of transcription and translation, or other unknown effects.

(1b) While it is clear that the IS4 exons encode part of the voltage sensor in the first repeat, are there studies in Drosophila to support the putative Ca-beta and G-protein beta-gamma binding sites in the I-II loop? Or are these inferred from Mammalian studies?

To the best of our knowledge, there are no studies in Drosophila that unambiguously show Caβ and Gβγ binding sites in the I-II loop of cacophony. However, sequence analysis strongly suggests that I-IIB contains both, a Caβ as well as a Gβγ binding site (AID: α-interacting domain) because the binding motif QXXER is present. In mouse Cav2.1 and Ca_v2.2 channels the sequence is QQIER, while in Drosophila cacophony I-IIB it is QQLER. In the alternative IIIA, this motif is not present, strongly suggesting that G_βγ subunits cannot interact at the AID. However, as already suggested by Smith et al. (1998), based on sequence analysis, Ca_β should still be able to bind, although possibly with a lower affinity. We agree that this information should be given to the reader and have revised the text accordingly on page 5, lines 9 to 17.

(1c) The authors assert that splicing of Cav2/cac in flies is a means to encode diversity, as mammals obviously have 4 Cav2 genes vs 1 in flies. However, as the authors likely know, mammalian Cav2 channels also have various splice isoforms encoded in each of the 4 Cav2 genes. The authors should discuss in more detail what is known about the splicing of individual mammalian Cav2 channels and whether there are any homologous properties in mammalian channels controlled by alternative splicing.

We agree and now provide a more comprehensive discussion of vertebrate Ca_v2 splicing and its impact on channel function. In line to what we report in Drosophila, properties like G_βγ binding and activation voltage can also be affected by alternative splicing in vertebrate Ca_v2 channel, through the exon patterns are quite different from Drosophila. We integrated this part on page 14, first paragraph) in the revised discussion. The respective text is below for the reviewer’s convenience:

“However, alternative splicing increases functional diversity also in mammalian Ca_v2 channels. Although the mutually exclusive splice site in the S4 segment of the first homologous repeat (IS4) is not present in vertebrate Cav channels, alternative splicing in the extracellular linker region between S3 and S4 is at a position to potentially change voltage sensor properties (Bezanilla 2002). Alternative splice sites in rat Ca_v2.1 exon 24 (homologous repeat III) and in exon 31 (homologous repeat IV) within the S3-S4 loop modulate channel pharmacology, such as differences in the sensitivity of Ca_v2.1 to Agatoxin. Alternative splicing is thus a potential cause for the different pharmacological profiles of P- and Q-channels (both Ca_v2.1; Bourinet et al. 1999). Moreover, the intracellular loop connecting homologous repeats I and II is encoded by 3-5 exons and provides strong interaction with G_βγ-subunits (Herlitze et al. 1996). In Ca_v2.1 channels, binding to G_βγ subunits is potentially modulated by alternative splicing of exon 10 (Bourinet et al. 1999). Moreover, whole cell currents of splice forms α1A-a (no Valine at position 421) and α1A-b (with Valine) represent alternative variants for the I-II intracellular loop in rat Ca_v2.1 and Ca_v2.2 channels. While α1A-a exhibits fast inactivation and more negative activation, α1A-b has delayed inactivation and a positive shift in the IV-curve (Bourinet et al. 1999). This is phenotypically similar to what we find for the mutually exclusive exons at the IS4 site, in which IS4B mediates high voltage activated cacophony currents while IS4A channels activate at more negative potentials and show transient current (Fig. 3; see also Ryglewski et al. 2012). Furthermore, altered Ca_β interaction have been shown for splice isoforms in loop III (Bourinet et al. 1999), similar to what we suspect for the I-II site in cacophony. Finally, in mammalian VGCCs, the C-terminus presents a large splicing hub affecting channel function as well as coupling distance to other proteins. Taken together, Ca_v2  channel diversity is greatly enhanced by alternative splicing also in vertebrates, but the specific two mutually exclusive exon pairs investigated here are not present in vertebrate Ca_v2 genes.”

(1d) In Figure 1, it would be helpful to see the entire cac genomic locus with all introns/exons and the 4 specific exons targeted for deletion.

We agree and have changed figure 1 accordingly.

(2a) Cav2.IS4B deletion alleles:

More work is necessary to explain the localization of Cac controlled by the IS4B exon. First, can the authors determine whether actual Cac channels are present at NMJ boutons? The authors seem to indicate that in the IS4B deletion mutants, some Cac (GFP) signal remains in a diffuse pattern across NMJ boutons. However, from the imaging of wild-type Cac-GFP (and previous studies), there is no Cac signal outside of active zones defined by the BRP signal. It would benefit the study to a) take additional, higher resolution images of the remaining Cac signal at NMJs in IS4B deletion mutants, and b) comment on whether the apparent remaining signal in these mutants is only observed in the absence of IS4Bcontaining Cac channels, or if the IS4A-positive channels are normally observed (but perhaps mis-localized?).

We have conducted additional analyses to show convincingly that IS4A channels (that remain upon IS4B deletion) are absent from presynaptic active zone. Please see also responses to reviewers 1 and 3. By adjusting the background values in of CLSM images to identical values in control, delta IS4A, and delta IS4B, as well as by providing selective enlargements as suggested, the figure panels 2C, Ci and 3A now show much clearer, that upon deletion of IS4B no cac label remains in active zones or anywhere else in the axon terminal boutons (see text on page 6, lines 22 to 24). This is further confirmed by quantification showing the in IS4B mutants cac labeling intensity in active zones is not above background (see text on page 6, lines 27 to 31). We never intended to indicate that there was cac signal outside of active zones defined by the brp signal, and we now carefully went through the text to not indicate this possibility unintentionally anywhere in the manuscript.

(2b) Do the authors know whether any presynaptic Ca2+ influx is contributed by IS4Apositive Cac channels at boutons, given the potential diffuse localization? There are various approaches for doing presynaptic Ca2+ imaging that could provide insight into this question.

We agree that this is an interesting question. However, based on the revisions made, we now show with more clarity that IS4A channels are absent from the presynaptic terminal at the NMJ. IS4A labeling intensities within active zones and anywhere else in the axon terminals are not different from background (see text on page 6, lines 27 to 31 and revised Figs. 2C, Ci, and 3A with new selective enlargements in response to comments of both other reviewers). This is in line with our finding that evoked synaptic transmission from NMJ axon terminals to muscle cells is mostly absent upon excision of IS4B (see Fig. 3B). The very small amplitude EPSC (below 5 % of the normal amplitude of evoked EPSCs) that can still be recorded in the absence of IS4B is similar to what is observed in cac null mutant junctions and is mediated by calcium influx through another voltage gated calcium channels, a Ca_v1 homolog named Dmca1D, as we have previously published (Krick et al., 2021, PNAS 118(28):e2106621118. Gathering additional support for the absence of IS4A from presynaptic terminals by calcium imaging experiments would suffer significantly from the presence of additional types of VGCCs in presynaptic terminals (for sure Dmca1D (Krick et al., 2021) and potentially also the Ca_v3 homolog DmαG or Dm-α1T). Such experiments would require mosaic null mutants for cac and DmαG channels in a mosaic IS4B excision mutant, which, if feasible at all, would be very hard and time consuming to generate. In the light of the additional clarification that IS4A is not located in NMJ axon terminal boutons, as shown by additional labeling intensity analysis, revised figures with selective enlargement, and revised text, we feel confident to state that IS4A is not sufficient for evoked SV release.

(2c) Mechanistically, how are amino acid changes in one of the voltage sensing domains in Cac related to trafficking/stabilization/localization of Cac to AZs?

This is an exciting question that has occupied our discussions a lot. Some sorting mechanism must exist that recognizes the correct protein isoforms, just as sorting and transport mechanisms exist that transport other synaptic proteins to the synapse. We do not think that the few amino acid changes in the voltage sensor are directly involved in protein targeting. We rather believe that the cacophony variants that happen to contain this specific voltage sensor are selected for transport out to the synapse. There are possibilities to achieve this cell biological, but we have not further addressed potential mechanisms because we do not want enter the realms of speculation.

(3) How are auxiliary subunits impacted in the Cac isoform mutants?

Recent work by Kate O'Connor-Giles has shown that both Stj and Ca-Beta subunits localize to active zones along with Cac at the Drosophila NMJ. Endogenously tagged Stj and CaBeta alleles are now available, so it would be of interest to determine if Stj and particular Cabeta levels or localization change in the various Cac isoform alleles. This would be particularly interesting given the putative binding site for Ca-beta encoded in the I-II linker.

We agree that the synthesis of the work of Kate O'Connor-Giles group and our study open up new avenues to explore exciting hypotheses about differential coupling of specific cacophony splice isoforms with distinct accessory proteins such as Caβ and α₂δ subunits. However, this requires numerous full sets of additional experiments and is beyond the scope of this study.

(4a) Interpretation of short-term plasticity in the I-IIB exon deletion:

The changes in short-term plasticity presented in Figure 5 are interpreted as an additional phenotype due to the loss of the I-IIB exon, but it seems this might be entirely explained simply due to the reduced Cac levels. Reduced Cac levels at active zones will obviously reduce Ca2+ influx and neurotransmitter release. This may be really the only phenotype/function of the I-IIB exon. Hence, to determine whether loss of the I-IIB exon encodes any functions in short-term plasticity, separate from reduced Cac levels, the authors should compare short-term plasticity in I-IIB loss alleles compared to wild type with starting EPSC amplitudes are equal (for example by reducing extracellular Ca2+ levels in wild type to achieve the same levels at in Cac I-IIB exon deleted alleles). Reduced release probability, simply by reduced Ca2+ influx (either by reduced Cac abundance or extracellular Ca2+) should result in more variability in transmission, so I am not sure there is any particular function of the I-IIB exon in maintaining transmission variability beyond controlling Cac abundance at active zones.

For two reasons we are particularly grateful for this comment. First, it shows us that we needed to explain much clearer that our interpretation is that changes in paired pulse ratios (PPRs) and in depression at low stimulation frequencies are a causal consequence of lower channel numbers upon I-IIB exon deletion, precisely as pointed out by the reviewer. We have carefully revised the text accordingly on page 10, lines 14-25, page 11, lines 3-7 and 22-28; page 16, lines 36-38. Second, the experiment suggested by the reviewer is superb to provide additional evidence that the cause of altered PPRs is in fact reduced channel number, but not altered channel properties. Accordingly, we have conducted additional TEVC recordings in elevated external calcium (1.8 mM) so that the single PSC amplitudes in I-IIB excision animals match those of controls in 0.5 mM extracellular calcium. This makes the amplitudes and the variance of PPR for all interpulse intervals tested control-like (see revised Figs. 6D, E). This strongly indicates that differences observed in PPRs as well as the variance thereof were caused by the amount of calcium influx during the first EPSC, and thus by different channel numbers in active zones.

(4b) Another point about the data in Figure 5: If "behaviorally relevant" motor neuron stimulation and recordings are the goal, the authors should also record under physiological Ca2+ conditions (1.8 mM), rather than the highly reduced Ca2+ levels (0.5 mM) they are using in their protocols.

Although we doubt that the effective extracellular calcium concentration that determines the electromotoric force for calcium to enter the ensheathed motoneuron terminals in vivo during crawling is known, we followed the reviewer’s suggestion partly and have repeated the high frequency stimulation trains for ΔI-IIB in 1.8 mM calcium. As for short-term plasticity this brings the charge conducted to values as observed in control and in ΔI-IIA in 0.5 mM calcium. Therefore, all difference observed in previous figure 5 (now revised figure 6) can be accounted to different channel numbers in presynaptic active zones. This is now explained on page 11, lines 19-28. For controls recordings at high frequency stimulation in higher external calcium (e.g. 2 mM) have previously been published and show significant synaptic depression (e.g. Krick et al., 2021, PNAS). Given that in the exon out variants we do not expect any differences except from those caused by different channel numbers, we did not repeat these experiments for control and ΔI-IIA.

(5a) Mechanism of Cac's role in PHP :

As the authors likely know, mutations in Cac were previously reported to disrupt PHP expression (see Frank et al., 2006 Neuron). Inexplicably, this finding and publication were not cited anywhere in this manuscript (this paper should also be cited when introducing PhTx, as it was the first to characterize PhTx as a means of acutely inducing PHP). In the Frank et al. paper (and in several subsequent studies), PHP was shown to be blocked in mutations in Cac, namely the CacS allele. This allele, like the I-IIB excision allele, reduces baseline transmission presumably due to reduced Ca2+ influx through Cac. The authors should at a minimum discuss these previous findings and how they relate to what they find in Figure 6 regarding the block in PHP in the Cac I-IIB excision allele.

We thank the reviewer for pointing this out and apologize for this oversight. We agree that it is imperative to cite the 2006 paper by Frank et al. when introducing PhTx mediated PHP as well as when discussing cac the effects of cac mutants on PHP together with other published work. We have revised the text accordingly on page 12, lines 9-11 and 21-23 and on page 17, lines 29-33.

In terms of data presentation in Fig. 6, as is typical in the field, the authors should normalize their mEPSC/QC data as a percentage of baseline (+PhTx/-PhTx). This makes it easier to see the reduction in mEPSC values (the "homeostatic pressure" on the system) and then the homeostatic enhancement in QC. Similarly, in Fig. 6M, the authors should show both mEPSC and QC as a percentage of baseline (wild type or non-GluRIIA mutant background).

We agree and have changed figure presentation accordingly. Figure 7 (formerly figure 6) was updated as was the accompanying results text on page 12, lines 23-40.

(6) Cac I-IIA and I-IIB excision allele colocalization at AZs:

These are very nice and important experiments shown in Figures 6N and O, which I suggest the authors consider analyzing in further detail. Most significantly:

(6i) The authors nicely show that most AZs have a mix of both Cac IIA and IIB isoforms. Using simple intensity analysis, can the authors say anything about whether there is a consistent stoichiometric ratio of IIA vs IIB at single AZs? It is difficult to extract actual numbers of IIA vs IIB at individual AZs without having both isoforms labeled mEOS4b, but as a rough estimate can the authors say whether the immunofluorescence intensity of IIA:IIB is similar across each AZ? Or is there broad heterogeneity, with some AZs having low vs high ratios of each isoform (as the authors suggest across proximal to distal NMJ AZs)?

We agree and have conducted experiments and analyses to provide these data. We measured the cac puncta fluorescence intensities for heterozygous cac^sfGFP/cac, cacIIIA^sfGFP/cacI-IIB, and cacI-IIB^sfGFP/cacI-IIA animals. We preferred this strategy, because intensity was always measured from cac puncta with the same GFP tag. Next, we normalized all values to the intensities obtained in active zones from heterozygous cac^sfGFP/cac controls and then plotted the intensities of I-IIA versus I-IIB containing active zones side by side. Across junctions and animals, we find a consistent ratio 2:1 in the relative intensities of I-IIB and I-IIA, thus indicating on average roughly twice as many I-IIB as compared to I-IIA channels across active zones. This is consistent with the counts in our STED analysis (see Fig. 5F). These new data are shown in the new figure panel 7J and referred to on page 13, lines 10-16 in the revised text.

(6ii) Intensity analysis of Cac IIA vs IIB after PHP: Previous studies have shown Cac abundance increases at NMJ AZs after PHP. Can the authors determine whether both Cac IIA vs IIB isoforms increase after PHP or whether just one isoform is targeted for this enhancement?

We already show that PHP is not possible in the absence of I-IIB channels (see figure 7). However, we agree that it is an interesting question to test whether I-IIA channel are added in the presence of I-IIB channels during PHP, but we consider this a detail beyond the scope of this study.

Minor points:

(1) Including line numbers in the manuscript would help to make reviewing easier.

We agree and now provide line numbers.

(2) Several typos (abstract "The By contrast", etc).

We carefully double checked for typos.

(3) Throughout the manuscript, the authors refer to Cac alleles and channels as "Cav2", which is unconventional in the field. Unless there is a compelling reason to deviate, I suggest the authors stick to referring to "Cac" (i.e. cacdIS4B, etc) rather than Cav2. The authors make clear in the introduction that Cac is the sole fly Cav2 channel, so there shouldn't be a need to constantly reinforce that cac=Cav2.

We agree and have changed all fly Ca_v2 reference to cac.

(4) In some figures/text the authors use "PSC" to refer to "postsynaptic current", while in others (i.e. Figure 6) they switch to the more conventional terms of mEPSC or EPSC. I suggest the authors stick to a common convention (mEPSC and EPSC).

We have changed PSC to EPSC throughout.

Reviewer #3 (Recommendations For The Authors):

(1) The abstract could focus more on the results at the expense of the background.

We agree and have deleted the second introductory background sentence and added information on PPRs and depression during low frequency stimulation.

(2) What does "strict" active zone localization refer to? Could they please define the term strict?

Strict active zone localization means that cac puncta are detected in active zones but no cac label above background is found anywhere else throughout the presynaptic terminal, now defined on page 6, lines 27-29.

(3) Single boutons/zoomed versions of the confocal images shown in Figures 2A-C, 2H, and 3A-C would be very helpful.

We have provided these panels as suggested (see above and revised figures 2-4). Figure 3 is now figure 4.

(4) The authors cite Ghelani et al. (2023) for increased cac levels during homeostatic plasticity. I recommend citing earlier work making similar observations (Gratz et al., 2019; DOI: 10.1523/JNEUROSCI.3068-18.2019), and linking them to increased presynaptic calcium influx (Müller & Davis, 2012; DOI: 10.1016/j.cub.2012.04.018).

We agree and have added Gratz et al. 2019 and Davis and Müller 2012 to the results section on page 12, lines 17/18 and lines 21-23, in the discussion on page 17, lines 29-33.

(5) The data shown in Figure 3 does not directly support the conclusion of altered release probability in dI-IIB. I therefore suggest changing the legend's title.

We have reworded to “Excisions at the I-II exon do not affect active zone cacophony localization but can alter cacsfGFP label intensity in active zones and PSC amplitude” as this is reflecting the data shown in the figure panels more directly.

(6) It would be helpful to specify "adult flight muscle" in Figure 2J.

We agree that it is helpful to specify in the figure (now revised figure 3C) that the voltage clamp recordings of somatodendritic calcium current were conducted in adult flight motoneurons and have revised the headline of figure panel 3C and the legend accordingly. Please note, these are not muscle cells but central neurons.

(7) Do dIS4B/Cav2null MNs indeed show an inward or outward current at -90 to -70 mV/-40 and -50 mV, or is this an analysis artifact?

No, this is due to baseline fluctuations as typical for voltage clamp in central neurons with more than 6000 µm dendritic length and more than 4000 dendritic branches.

(8) Loss of several presynaptic proteins, including Brp (Kittel et al., 2006), and RBP (Liu et al., 2011), induce changes in GluR field size (without apparent changes in miniature amplitude). The statement regarding the Cav2 isoform and possible effects on GluR number (p. 8) should be revised accordingly.

We understand and have done two things. First, we measured the intensity of GluRIIA immunolabel in ΔI-IIA, ΔI-IIB, and controls and found no differences. Second, we reworded the statement. It now reads on page 9, lines 1-6: “It seems unlikely that presynaptic cac channel isoform type affects glutamate receptor types or numbers, because the amplitude of spontaneous miniature postsynaptic currents (mEPSCs, Fig. 4K) and the labeling intensity of postsynaptic GluRIIA receptors are not significantly different between controls, I-IIA, and I-IIB junctions (see suppl. Fig. 2, p = 0.48, ordinary one-way ANOVA, mean and SD intensity values are 61.0 ± 6.9 (control), 55.8 ± 8.5 (∆I-IIA), 61.1 ± 17.3 (∆I-IIB)). However, we cannot exclude altered GluRIIB numbers and have not quantified GluR receptor field sizes.”

(9) The statement relating miniature frequency to RRP size is unclear (p. 8). Is there any evidence for a correlation between miniature frequency to RRP size? Could the authors please clarify?

We agree that this statement requires caution. Although there is some published evidence for a correlation of RRP size and mini frequency (Neuron, 2009 61(3):412-24. doi: 10.1016/j.neuron.2008.12.029 and Journal of Neuroscience 44 (18) e1253232024; doi: 10.1523/JNEUROSCI.1253-23.2024), which we now refer to on page 9, it is not clear whether this is true for all synapses and how linear such a relationship may be. Therefore, we have revised the text on page 9, lines 6-9. It now reads: “Similarly, the frequency of miniature postsynaptic currents (mEPSCs) remains unaltered. Since mEPSCs frequency has been related to RRP size at some synapses (Pan et al., 2009; Ralowicz et al., 2024) this indicates unaltered RRP size upon I-IIB excision, but we have not directly measured RRP size.”

(10) Please define the "strict top view" of synapses (p. 8).

Top view is what this reviewer referred to as “planar view” in the public review points 6 and 7. In our responses to these public review points we now also define “strict top view”, see page 9, lines 17-19.

(11) Two papers are cited regarding a linear relationship between calcium channel number and release probability (p. 15). Many more papers could be cited to demonstrate a supralinear relationship (e.g., Dodge & Rahaminoff, 1967; Weyhersmüller et al., 2011 doi: 10.1523/JNEUROSCI.6698-10.2011). The data of the present study were collected at an extracellular calcium concentration of 0.5 mM, whereas Meideiros et al. (2023) used 1.5 mM. The relationship between calcium and release is supra-linear around 0.5 mM extracellular calcium (Weyhersmüller et al. 2011). This should be discussed/the statements be revised. Also, the reference to Meideiros et al. (2023) should be included in the reference list.

We have now updated the Medeiros reference (updated version of that paper appeared in eLife in 2024) in the text and reference list. We agree that the relationship of the calcium concentration and P_r can also be non-linear and refer to this on page 16, lines 26-32, but the point we want to make is to relate defined changes in calcium channel number (not calcium influx) as assessed by multiple methods (CLSM intensity measures and sptPALM channel counting) to release probability. We now also clearly state that we measured at 0.5 mM external calcium (page 16, lines 27/28) whereas Medeiros et al. 2024 measured at 1.5 mM calcium (page 16, lines 31/32).

(12) Figure 6: Quantal content does not have any units - please remove "n vesicles".

We have revised this figure in response to reviewer 2 (comment 5) and quantal content is now expressed as percent baseline, thus without units (see revised figure 7).

(13) Figure 6C should be auto-scaled from zero.

This has been fixed by revising that figure in response to reviewer 2 (comment 5)

(14) The data supporting the statement on impaired motor behavior and reduced vitality of adult IS4A should be either shown, or the statement should be removed (p. 13). Any hypotheses as to why IS4A is important for behavior and or viability?

As suggested, we have removed that statement.

(15) They do not provide any data supporting the statement that changes in PSC decay kinetics "counteract" the increase in PSC amplitude (p. 14). The sentence should be changed accordingly.

We agree and have down toned. It now reads on page 16, lines 7-9: “During repetitive firing, the median increase of PSC amplitude by ~10 % is potentially counteracted by the significant decrease in PSC half amplitude width by ~25 %...”.

(16) How do they explain the net locomotion speed increase in dI    -IIA larvae? Although the overall charge transfer is not affected during the stimulus protocols used, could the accelerated PSC decay affect PSP summation (I would actually expect a decrease in summation/slower speed)? Independent of the voltage-clamp data, is muscle input resistance changed in dI-IIA mutants?

Muscle input resistance is not altered in I-II mutants. We refer to potential causes of the locomotion effects of I-IIA excision in the discussion. On page 16, lines 12 to 21 it reads: “there is no difference in charge transfer from the motoneuron axon terminal to the postsynaptic muscle cell between ∆I-IIA and control. Surprisingly, crawling is significantly affected by the removal of I-IIA, in that the animals show a significantly increased mean crawling speed but no significant change in the number of stops. Given that the presynaptic function at the NMJ is not strongly altered upon I-IIA excision, and that I-IIA likely mediates also Ca_v2 functions outside presynaptic AZs (see above) and in other neuron types than motoneurons, and that the muscle calcium current is mediated by Ca_v1>/i> and Ca_v3, the effects of I-IIA excision of increasing crawling speed is unlikely caused by altered pre- or postsynaptic function at the NMJ. We judge it more likely that excision of I-IIA has multiple effects on sensory and pre-motor processing, but identification of these functions is beyond the scope of this study.”

eLife Assessment

This important study presents an evaluation of several tools used for detecting Identity-By-Descent (IBD) segments in highly recombining genomes, using simulated data to replicate the high recombination and low marker density of Plasmodium falciparum, the parasite responsible for malaria. Most of the evidence presented by the authors is solid demonstrating that users should be cautious calling IBD when SNP density is low and recombination rate is high. This study will be of interest to scientists working in the field of genome evolution and infectious diseases.

Reviewer #1 (Public review):

Summary:

Authors benchmarked 5 IBD detection methods (hmmIBD, isoRelate, hap-IBD, phasedIBD, and Refined IBD) in Plasmodium falciparum using simulated and empirical data. Plasmodium falciparum has a mutation rate similar to humans but a much higher recombination rate and lower SNP density. Thus, the authors evaluated how recombination rate and marker density affect IBD segment detection. Next, they performed parameter optimization for Plasmodium falciparum and benchmarked the robustness of downstream analyses (selection detection and NE inference) using IBD detected by each of the methods. They also tracked the computational efficiency of these methods. The authors work is valuable for the tested species and the analyses presented appear to support their claim that users should be cautious calling IBD when SNP density is low and recombination rate is high.

Strengths:

The study design was solid. The authors set up their reasoning for using P. falciparum very well. The high recombination rate and similar mutation rate to human is indeed an interesting case. Further, they chose methods that were developed explicitly for each species. This was a strength of the work, as well as incorporating both simulated and empirical data to support their goal that IBD detection should be benchmarked in P. falciparum.

Weaknesses:

The scope of the optimization and application of results from the work are narrow, in that everything is fine-tuned for Plasmodium. Some of the results were not entirely unexpected for users of any of the tested software that was developed for humans. For example, it is known that Refined IBD is not going to do well with the combination of short IBD segments and low SNP density. Lastly, it appears the authors only did one large-scale simulation (there are no reported SDs).

Reviewer #2 (Public review):

Summary:

Guo et al. benchmarked and optimized methods for detecting Identity-By-Descent (IBD) segments in Plasmodium falciparum (Pf) genomes, which are characterized by high recombination rates and low marker density. Their goal was to address the limitations of existing IBD detection tools, which were primarily developed for human genomes and do not perform well in the genomic context of highly recombinant genomes. They first analysed various existing IBD callers, such as hmmIBD, isoRelate, hap-IBD, phased-IBD, refinedIBD. They focused on the impact of recombination on the accuracy, which was calculated based on two metrics, the false negative rate and the false positive rate. The results suggest that high recombination rates significantly reduce marker density, leading to higher false negative rates for short IBD segments. This effect compromises the reliability of IBD-based downstream analyses, such as effective population size (Ne) estimation.<br /> They showed that the best tool for IBD detection in Pf is hmmIBD, because it has relatively low FN/FP error rates and is less biased for relatedness estimates. However, this method is the less computationally efficient.<br /> Their suggestion is to optimize human-oriented IBD methods and use hmmIBD only for the estimation of Ne.

Strengths:

Although I am not an expert on Plasmodium falciparum genetics, I believe the authors have developed a valuable benchmarking framework tailored to the unique genomic characteristics of this species. Their framework enables a thorough evaluation of various IBD detection tools for non-human data, such as high recombination rates and low marker density, addressing a key gap in the field.<br /> This study provides a comparison of multiple IBD detection methods, including probabilistic approaches (hmmIBD, isoRelate) and IBS-based methods (hap-IBD, Refined IBD, phased IBD). This comprehensive analysis offers researchers valuable guidance on the strengths and limitations of each tool, allowing them to make informed choices based on specific use cases. I think this is important beyond the study of Pf.<br /> The authors highlight how optimized IBD detection can help identify signals of positive selection, infer effective population size (Ne), and uncover population structure.<br /> They demonstrate the critical importance of tailoring analytical tools to suit the unique characteristics of a species. Moreover, the authors provide practical recommendations, such as employing hmmIBD for quality-sensitive analyses and fine-tuning parameters for tools originally designed for non-P. falciparum datasets before applying them to malaria research.

Overall, this study represents a meaningful contribution to both computational biology and malaria genomics, with its findings and recommendations likely to have an impact on the field.

Weaknesses:

One weakness of the study is the lack of emphasis on the broader importance of studying Plasmodium falciparum as a critical malaria-causing organism. Malaria remains a significant global health challenge, causing hundreds of thousands of deaths annually. The authors could have introduced better the topic, even though I understand this is a methodological paper. While the study provides a thorough technical evaluation of IBD detection methods and their application to Pf, it does not adequately connect these findings to the broader implications for malaria research and control efforts. Additionally, the discussion on malaria and its global impact could have framed the study in a more accessible and compelling way, making the importance of these technical advances clearer to a broader audience, including researchers and policymakers in the fight against malaria.

Author response:

Provisional Responses to Review #1's comments:

We thank the reviewer for the comments, which highlight both strengths and weaknesses.

We acknowledge that the optimized parameter values are somewhat specific to Plasmodium, as demographic and mutation/recombination rates can vary across species. However, we would like to emphasize that our simulation and benchmarking framework, along with associated tools like the efficient ibdutils, should be broadly applicable to many species, such as Apicomplexan parasites and other high-recombining eukaryotes, especially when their demographic and evolutionary parameters can be provided or estimated. We will update relevant paragraphs in the disucssion to highlight this point.

Results related to Refined IBD may not seem unexpected, but our work demonstrates that its direct application to malaria parasites without species-specific optimization can be suboptimal, as has previously occurred in malaria research with their validity not formally evaluated. We believe it is crucial for the research community focusing on non-standard model organisms to validate assumptions made in methods developed for standard models, such as humans, before they are applided to new species.

Although standard deviations (SDs) are not provided for many analyses, we argue that simulating 14 chromosomes independently serves as repeats (data were shown as means over chromosomes), particularly when assessing the accuracy of IBD segments or scanning for selection signals. For analyses that aggregate information across chromosomes, we are planning to conduct additional repeated simulations or analyses to quantify the uncertainty of estimates. In the upcoming revised version, we will provide SDs where appropriate and explanations when repeated simulation are not necessary given a large number of data points have well captured their empirical distributions.

Provisional response to review #2's comment:

Thank you to the reviewer for the suggestions. We agree with the comments, and addressing the mentioned weakness will improve the manuscript's clarity and impact. We plan to enhance the introduction by highlighting the significance of studying malaria and specifically focusing on P. falciparum in this work. We will also update the discussion to reinforce the connection between our findings and malaria research and control and further emphasize the broader implications for the field.

eLife Assessment

This useful observational study was conducted in Dar es Salaam, Tanzania, to investigate potential associations between genetic variation in Mycobacterium tuberculosis and human host vs. disease severity. The authors conclude that human genetic ancestry did not contribute to tuberculosis severity, but the evidence for this conclusion is currently incomplete, as the analysis did not fully leverage the genome-wide data available in a human-strain association study, and there was no comparison group from the general population (or household controls), to which the ancestry findings could be compared. The findings have significance for the understanding of the influence of host / bacillary genetics on tuberculosis disease.

Reviewer #1 (Public review):

Summary:

This Tanzanian study focused on the relationship between human genetic ancestry, Mycobacterium tuberculosis complex (MTBC) diversity, and tuberculosis (TB) disease severity. The authors analyzed the genetic ancestry of 1,444 TB patients and genotyped the corresponding MTBC strains isolated from the same individuals. They found that the study participants predominantly possess Bantu-speaking genetic ancestry, with minimal European and Asian ancestry. The MTBC strains identified were diverse and largely resulted from introductions from South or Central Asia. Unfortunately, no associations were identified between human genetic ancestry, the MTBC strains, or TB severity. The authors suggest that social and environmental factors are more likely to contribute to TB severity in this setting.

Strengths:

In comparison to other studies investigating the role of human genetics in TB phenotypes, this study is relatively large, with more than 1,400 participants.

The matched human-MTBC strain collection is valuable and offers the opportunity to address questions about human-bacterium co-evolution.

Weaknesses:

Although the authors had genome-wide genotyping and whole genome sequencing data, they only compared the associations between human ancestry and MTBC strains. Given the large sample size, they had the opportunity to conduct a genome-wide association study similar to that of Muller et al. (https://doi.org/10.1016/j.ygeno.2021.04.024).

The authors tested whether human genetic ancestry is associated with TB severity. However, the basis for this hypothesis is unclear. The studies cited as examples all focused on progression to active TB (from a latent infection state), which should not be conflated with disease severity. It is difficult to ascertain whether the role of genetic ancestry in disease severity would be detectable through this study design, as some participants might simply have been sicker for longer before being diagnosed (despite the inquiry about cough duration). This delay in diagnosis would not be influenced solely by human genetics, which is the conclusion of the study.

Additionally, the study only included participants who attended the TB clinic.

Including healthy controls from the general population would have provided an interesting comparison to see if ancestry proportions differ.

Although the authors suggest that social and environmental factors contribute to TB severity, only age, smoking, and HIV status were characterised in the study.

Reviewer #2 (Public review):

Summary:

This manuscript reports the results of an observational study conducted in Dar es Salaam, Tanzania, investigating potential associations between genetic variation in M. tuberculosis and human host vs. disease severity. The headline finding is that no such associations were found, either for host / bacillary genetics as main effects or for interactions between them.

Strengths:

Strengths of the study include its large size and rigorous approaches to classification of genetic diversity for host and bacillus.

Weaknesses:

(1) There are some limitations of the disease severity read-outs employed: X-ray scores and Xpert cycle thresholds from sputum analysis can only take account of pulmonary disease. CXR is an insensitive approach to assessing 'lung damage', especially when converted to a binary measure. What was the basis for selection of Ralph score of 71 to dichotomise patients? If outcome measures were analysed as continuous variables, would this have been more sensitive in capturing associations of interest?

(2) There is quite a lot of missing data, especially for TB scores - could this have introduced bias? This issue should be mentioned in the discussion.

(3) The analysis adjusted for age, sex, HIV status, age, smoking and cough duration - but not for socio-economic status. This will likely be a major determinant of disease severity. Was adjustment made for previous TB (i.e. new vs repeat episode) and drug-sensitivity of the isolate? Cough duration will effectively be a correlate/consequence of more severe disease - thus likely highly collinear with disease severity read-outs - not a true confounder. How does removal of this variable from the model affect results? Data on socioeconomic status should be added to models, or if not possible then lack of such data should be noted as a limitation.

(4) Recruitment at hospitals may have led to selection bias due to exclusion of less severe, community cases. The authors already acknowledge this limitation in the Discussion however.

(5) Introduction: References refer to disease susceptibility, but the authors should also consider the influences of host/pathogen genetics on host response - both in vitro (PMIDs 11237411, 15322056) and in vivo (PMID 23853590). The last of these studies encompassed a broader range of ethnic variation than the current study, and showed associations between host ancestry and immune response - null results from the current study may reflect the relative genetic homogeneity of the population studied.

eLife Assessment

This important study introduces a fully differentiable variant of the Gillespie algorithm as an approximate stochastic simulation scheme for complex chemical reaction networks, allowing kinetic parameters to be inferred from empirical measurements of network outputs using gradient descent. The concept and algorithm design are convincing and innovative. While the proofs of concept are promising, the determination of the range of applicability and of the errors is incomplete, leaving open some questions about implications for more complex systems that cannot be addressed by existing methods. This work has the potential to be of significant interest to a broad audience of quantitative and synthetic biologists.

Reviewer #1 (Public review):

Summary:

This work introduces the differentiable Gillespie algorithm, DGA, which is a differentiable variant of the celebrated (and exact) Gillespie algorithm commonly used to perform stochastic simulations across numerous fields, notably in the life sciences. The proposed DGA approximates the exact Gillespie algorithm using smooth functions yielding a suitable approximate differentiable stochastic system as a proxy for the underlying discrete stochastic system, where DGA stochastic reactions have continuous reaction index and the species abundances. To illustrate their methodology, the authors specifically consider in detail the case of a well-studied two-state promoter gene regulation system that they analyze using a machine learning approach, and by combining simulation data with analytical results. For the two-state promoter gene system, the DGA is benchmarked by accurately reproducing the results of the exact Gillespie algorithm. For this same simple system, the authors also show that how the DGA can be used for estimating kinetic parameters of both simulated and real noisy experimental data. This let them argue convincingly that the DGA can become a powerful computation tool for applications in quantitative and synthetic biology. In order to argue that the DGA can be employed to design circuits with ad-hoc input-output relations, these considerations are then extended to a more complex four-state promoter model of gene regulation.

Strengths:

The main strength of the paper is its clarity and its pedagogical presentation of the simulation methods.

Weaknesses:

It would have been useful to have a brief discussion, based on a concrete example, of what can be achieved with the DGA and is totally beyond the reach of the Gillespie algorithm and the numerous existing stochastic simulation methods. A more comprehensive and quantitative analysis of the limitations of the DGA, e.g. for rare events, would have also been helpful.

Reviewer #2 (Public review):

Summary:

In this work, the authors present a differentiable version of the widely-used Gillespie Algorithm. The Gillespie Algorithm has been used for decades to simulate the behavior of stochastic biochemical reaction networks. But while the Gillespie Algorithm is a powerful tool for the forward simulation of biochemical systems given some set of known reaction parameters, it cannot be used for reverse process, i.e. inferring reaction parameters given a set of measured system characteristics. The Differentiable Gillespie Algorithm ("DGA") overcomes this limitation by approximating two discontinuous steps in the Gillespie Algorithm with continuous functions. This makes it possible to calculate of gradients for each step in the simulation process which, in turn, allows the reaction parameters to be optimized via powerful backpropagation techniques. In addition to describing the theoretical underpinnings of DGA, the authors demonstrate different potential use-cases for the algorithm in the context of simple models of stochastic gene expression.

Overall, the DGA represents an important conceptual step forward for the field, and should lay the groundwork for exciting innovations in the analysis and design of stochastic reaction networks. At the same time, significantly more work is needed to establish when the approximations made by DGA are valid, and to demonstrate the viability of the algorithm in the context of complicated reaction networks.

Strengths:

This work makes an important conceptual leap by introducing a version of the Gillespie Algorithm that is end-to-end differentiable. This idea alone has the potential to drive a number of exciting innovations in the analysis, inference, and design of biochemical reaction networks. Beyond the theoretical adjustments, the authors also implement their algorithm in a Python-based codebase that combines DGA powerful optimization libraries like PyTorch. This codebase has the potential to be of interest to a wide range of researchers, even if the true scope of the method's applicability remains to be fully determined.

The authors also demonstrate how DGA can be used in practice both to infer reaction parameters from real experimental data (Figure 7) and to design networks with user-specified input-output characteristics (Figure 8). These illustrations should provide a nice roadmap for researchers interested in applying DGA to their own projects/systems.

Finally, although it does not stem directly from DGA, the exploration of pairwise parameter dependencies in different network architectures provides an interesting window into the design constraints (or lack thereof) that shape the architecture of biochemical reaction networks.

Weaknesses:

While it is clear that the DGA represents an important conceptual advancement, the authors do not do enough in the present manuscript to (i) validate the robustness of DGA inference and (ii) demonstrate that DGA inference works in the kinds of complex biochemical networks where it would actually be of legitimate use.

It is to the authors' credit that they are open and explicit about the potential limitations of DGA due to breakdowns in its continuous approximations. However they do not provide the reader with nearly enough empirical (i.e. simulation-based) or theoretical context to assess when, why, and to what extent DGA will fail in different situations. In Figure 2, they compare DGA to GA (i.e. ground-truth) in the context of a simple two state model of a stochastic transcription. Even in this minimal system, we see that DGA deviates notably from ground-truth both in the simulated mRNA distributions (Figure 2A) and in the ON/OFF state occupancy (Figure 2C). This begs the question of how DGA will scale to more complicated systems, or systems with non-steady state dynamics. Will the deviations become more severe? This is important because, in practice, there is really not much need for using DGA with a simple 2 state system-we have analytic solutions for this case. It is the more complex systems where DGA has the potential to move the needle.

A second concern is that the authors' present approach for parameter inference and error calculation does not seem to be reliable. For example, in Figure 5A, they show DGA inference results for the ON rate of a two-state system. We see substantial inference errors in this case, even though the inference problem should be non-degenerate in this case. One reason for this seems to be that the inference algorithm does not reliably find the global minimum of the loss function (Figure 2B). To turn DGA into a viable approach, it is paramount that the authors find some way to improve this behavior, perhaps by using multiple random initializations to better search the loss space.

Finally, the authors do a good job of illustrating how DGA might be used to infer biological parameters (Figure 7) and design reaction networks with desired input-output characteristics (Figure 8). However, analytic solutions exist for both of the systems they select for examples. This means that, in practice, there would be no need for DGA in these contexts, since one could directly optimize, e.g., the expressions for the mean and Fano Factor of the system in Figure 7A. I still believe that it is useful to have these examples, but it seems critical to add a use-case where DGA is the only option.

Reviewer #3 (Public review):

Summary:

This manuscript introduces a differentiable variant of the Gillespie algorithm (DGA) that allows gradient calculation using backpropagation. The most significant contribution of this work is the development of the DGA itself, a novel approach to making stochastic simulations differentiable. This is achieved by replacing discontinuous operations in the traditional Gillespie algorithm with smooth, differentiable approximations using sigmoid and Gaussian functions. This conceptual advance opens up new avenues for applying powerful gradient-based optimization techniques, prevalent in machine learning, to studying stochastic biological systems.

The method was tested on a simple two-state promoter model of gene expression. The authors found that the DGA accurately captured the moments of the steady-state distribution and other major qualitative features. However, it was less accurate at capturing information about the distribution's tails, potentially because rare events result from frequent low-probability reaction events where the approximations made by the DGA have a greater impact. The authors could further use the DGA to design a four-state promoter model of gene regulation that exhibited a desired input-output relationship. The DGA could learn parameters that produced a sharper response curve, which was achieved by consuming more energy.

The authors conclude that the DGA is a powerful tool for analyzing and designing stochastic systems.

Strengths:

The DGA allows gradient-based optimization techniques to estimate parameters and design networks with desired properties.

The DGA efficacy in estimating kinetic parameters from both synthetic and experimental data. This capability highlights the DGA's potential to extract meaningful biophysical parameters from noisy biological data.

The DGA's ability to design a four-state promoter architecture exhibiting a desired input-output relationship. This success indicates the potential of the DGA as a valuable tool for synthetic biology, enabling researchers to engineer biological circuits with predefined behaviours.

Weaknesses:

The study primarily focuses on analysing the steady-state properties of stochastic systems. It is unclear how and if this framework can be used beyond the steady-state data presented in the case studies, where it is already quite computationally heavy.<br /> A more in-depth exploration of the DGA's performance in analysing dynamic trajectories, which capture the system's evolution over time, would provide a more comprehensive view of the algorithm's capabilities.<br /> Gradient computations in the DGA can be susceptible to numerical instability, particularly when the sharpness parameters of the sigmoid and Gaussian approximations are set to high values. This issue could lead to challenges in convergence during the optimization process.

eLife Assessment

This study presents a platform to implement closed-loop experiments in mice based on auditory feedback. The authors provide solid evidence that their platform enables a variety of closed-loop experiments using neural or movement signals, indicating that it will be a valuable resource to the neuroscience community. However, the demonstration experiments could be strengthened by increasing the sample size for several groups in the neurofeedback experiments, as well as a more thorough description of the results in the text.

Reviewer #1 (Public review):

Summary:

The authors provide a resource to the systems neuroscience community, by offering their Python-based CLoPy platform for closed-loop feedback training. In addition to using neural feedback, as is common in these experiments, they include a capability to use real-time movement extracted from DeepLabCut as the control signal. The methods and repository are detailed for those who wish to use this resource. Furthermore, they demonstrate the efficacy of their system through a series of mesoscale calcium imaging experiments. These experiments use a large number of cortical regions for the control signal in the neural feedback setup, while the movement feedback experiments are analyzed more extensively.

Strengths:

The primary strength of the paper is the availability of their CLoPy platform. Currently, most closed-loop operant conditioning experiments are custom built by each lab and carry a relatively large startup cost to get running. This platform lowers the barrier to entry for closed-loop operant conditioning experiments, in addition to making the experiments more accessible to those with less technical expertise.

Another strength of the paper is the use of many different cortical regions as control signals for the neurofeedback experiments. Rodent operant conditioning experiments typically record from the motor cortex and maybe one other region. Here, the authors demonstrate that mice can volitionally control many different cortical regions not limited to those previously studied, recording across many regions in the same experiment. This demonstrates the relative flexibility of modulating neural dynamics, including in non-motor regions.

Finally, adapting the closed-loop platform to use real-time movement as a control signal is a nice addition. Incorporating movement kinematics into operant conditioning experiments has been a challenge due to the increased technical difficulties of extracting real-time kinematic data from video data at a latency where it can be used as a control signal for operant conditioning. In this paper they demonstrate that the mice can learn the task using their forelimb position, at a rate that is quicker than the neurofeedback experiments.

Weaknesses:

There are several weaknesses in the paper that diminish the impact of its strengths. First, the value of the CLoPy platform is not clearly articulated to the systems neuroscience community. Similarly, the resource could be better positioned within the context of the broader open-source neuroscience community. For an example of how to better frame this resource in these contexts, I recommend consulting the pyControl paper. Improving this framing will likely increase the accessibility and interest of this paper to a less technical neuroscience audience, for instance by highlighting the types of experimental questions CLoPy can enable.

While the dataset contains an impressive amount of animals and cortical regions for the neurofeedback experiment, and an analysis of the movement-feedback experiments, my excitement for these experiments is tempered by the relative incompleteness of the dataset, as well as its description and analysis in the text. For instance, in the neurofeedback experiment, many of these regions only have data from a single mouse, limiting the conclusions that can be drawn. Additionally, there is a lack of reporting of the quantitative results in the text of the document, which is needed to better understand the degree of the results. Finally, the writing of the results section could use some work, as it currently reads more like a methods section.

Suggestions for improved or additional experiments, data or analyses:

Not necessary for this paper, but it would be interesting to see if the CLNF group could learn without auditory feedback.

There are no quantitative results in the results section. I would add important results to help the reader better interpret the data. For example, in: "Our results indicated that both training paradigms were able to lead mice to obtain a significantly larger number of rewards over time," You could show a number, with an appropriate comparison or statistical test, to demonstrate that learning was observed.

For: "Performing this analysis indicated that the Raspberry Pi system could provide reliable graded feedback within ~63 {plus minus} 15 ms for CLNF experiments." The LED test shows the sending of the signal, but the actual delay for the audio generation might be longer. This is also longer than the 50 ms mentioned in the abstract.

It could be helpful to visualize an individual trial for each experiment type, for instance how the audio frequency changes as movement speed / calcium activity changes.

The sample sizes are small (n=1) for a few groups. I am excited by the variety of regions recorded, so it could be beneficial for the authors to collect a few more animals to beef up the sample sizes.

I am curious as to why 60 trials sessions were used. Was it mostly for the convenience of a 30 min session, or were the animals getting satiated? If the former, would learning have occurred more rapidly with longer sessions?

Figure 4 E is interesting, it seems like the changes in the distribution of deltaF was in both positive and negative directions, instead of just positive. I'd be curious as to the author's thoughts as to why this is the case. Relatedly, I don't see Figure 4E, and a few other subplots, mentioned in the text. As a general comment, I would address each subplot in the text.

For: "In general, all ROIs assessed that encompassed sensory, pre-motor, and motor areas were capable of supporting increased reward rates over time," I would provide a visual summary showing the learning curves for the different types of regions.

Relatedly, I would further explain the fast vs slow learners, and if they mapped onto certain regions.

Also I would make the labels for these plots (e.g. Supp Fig3) more intuitive, versus the acronyms currently used.

The CLMF animals showed a decrease in latency across learning, what about the CLNF animals? There is currently no mention in the text or figures.

Reviewer #2 (Public review):

Summary:

In this work, Gupta & Murphy present several parallel efforts. On one side, they present the hardware and software they use to build a head-fixed mouse experimental setup that they use to track in "real-time" the calcium activity in one or two spots at the surface of the cortex. On the other side, the present another setup that they use to take advantage of the "real-time" version of DeepLabCut with their mice. The hardware and software that they used/develop is described at length, both in the article and in a companion GitHub repository. Next, they present experimental work that they have done with these two setups, training mice to max out a virtual cursor to obtain a reward, by taking advantage of auditory tone feedback that is provided to the mice as they modulate either (1) their local cortical calcium activity, or (2) their limb position.

Strengths:

This work illustrates the fact that thanks to readily available experimental building blocks, body movement and calcium imaging can be carried using readily available components, including imaging the brain using an incredibly cheap consumer electronics RGB camera (RGB Raspberry Pi Camera). It is a useful source of information for researchers that may be interested in building a similar setup, given the highly detailed overview of the system. Finally, it further confirms previous findings regarding the operant conditioning of the calcium dynamics at the surface of the cortex (Clancy et al. 2020) and suggests an alternative based on deeplabcut to the motor tasks that aim to image the brain at the mesoscale during forelimb movements (Quarta et al. 2022).

Weaknesses:

This work covers 3 separate research endeavors: (1) The development of two separate setups, their corresponding software. (2) A study that is highly inspired from the Clancy et al. 2020 paper on the modulation of the local cortical activity measured through a mesoscale calcium imaging setup. (3) A study of the mesoscale dynamics of the cortex during forelimb movements learning. Sadly, the analyses of the physiological data appears uncomplete, and more generally the paper tends to offer overstatements regarding several points:<br /> - In contrast to the introductory statements of the article, closed-loop physiology in rodents is a well-established research topic. Beyond auditory feedback, this includes optogenetic feedback (O'Connor et al. 2013, Abbasi et al. 2018, 2023), electrical feedback in hippocampus (Girardeau et al. 2009), and much more.<br /> - The behavioral setups that are presented are representative of the state of the art in the field of mesoscale imaging/head fixed behavior community, rather than a highly innovative design. In particular, the closed-loop latency that they achieve (>60 ms) may be perceived by the mice. This is in contrast with other available closed-loop setups.<br /> - Through the paper, there are several statements that point out how important it is to carry out this work in a closed-loop setting with an auditory feedback, but sadly there is no "no feedback" control in cortical conditioning experiments, while there is a no-feedback condition in the forelimb movement study, which shows that learning of the task can be achieved in the absence of feedback.<br /> - The analysis of the closed-loop neuronal data behavior lacks controls. Increased performance can be achieved by modulating actively only one of the two ROIs, this is not clearly analyzed (for instance looking at the timing of the calcium signal modulation across the two ROIs. It seems that overall ROIs1 and 2 covariate, in contrast to Clancy et al. 2020. How can this be explained?

Reviewer #3 (Public review):

Summary:

The study demonstrates the effectiveness of a cost-effective closed-loop feedback system for modulating brain activity and behavior in head-fixed mice. Authors have tested real-time closed-loop feedback system in head-fixed mice two types of graded feedback: 1) Closed-loop neurofeedback (CLNF), where feedback is derived from neuronal activity (calcium imaging), and 2) Closed-loop movement feedback (CLMF), where feedback is based on observed body movement. It is a python based opensource system, and authors call it CLoPy. The authors also claim to provide all software, hardware schematics, and protocols to adapt it to various experimental scenarios. This system is capable and can be adapted for a wide use case scenario.

Authors have shown that their system can control both positive (water drop) and negative reinforcement (buzzer-vibrator). This study also shows that using the close loop system mice have shown better performance, learnt arbitrary task and can adapt to change in the rule as well. By integrating real-time feedback based on cortical GCaMP imaging and behavior tracking authors have provided strong evidence that such closed-loop systems can be instrumental in exploring the dynamic interplay between brain activity and behavior.

Strengths:

Simplicity of feedback systems designed. Simplicity of implementation and potential adoption.

Weaknesses:

Long latencies, due to slow Ca2+ dynamics and slow imaging (15 FPS), may limit the application of the system.

Major comments:

(1) Page 5 paragraph 1: "We tested our CLNF system on Raspberry Pi for its compactness, general-purpose input/output (GPIO) programmability, and wide community support, while the CLMF system was tested on an Nvidia Jetson GPU device." Can these programs and hardware be integrated with windows-based system and a microcontroller (Arduino/ Tency). As for the broad adaptability that's what a lot of labs would already have (please comment/discuss)?

(2) Hardware Constraints: The reliance on Raspberry Pi and Nvidia Jetson (is expensive) for real-time processing could introduce latency issues (~63 ms for CLNF and ~67 ms for CLMF). This latency might limit precision for faster or more complex behaviors, which authors should discuss in the discussion section.

(3) Neurofeedback Specificity: The task focuses on mesoscale imaging and ignores finer spatiotemporal details. Sub-second events might be significant in more nuanced behaviors. Can this be discussed in the discussion section?

(4) The activity over 6s is being averaged to determine if the threshold is being crossed before the reward is delivered. This is a rather long duration of time during which the mice may be exhibiting stereotyped behaviors that may result in the changes in DFF that are being observed. It would be interesting for the authors to compare (if data is available) the behavior of the mice in trials where they successfully crossed the threshold for reward delivery and in those trials where the threshold was not breached. How is this different from spontaneous behavior and behaviors exhibited when they are performing the test with CLNF?

eLife Assessment

This important study conducted experiments to quantify how changes in blood flow results in apparent fluorescence changes when imaging neural activity sensors using two-photon microscopy. While the study highlights the prevalence neural-activity independent artifacts in two-photon imaging, the evidence linking the observed signals to hemodynamic occlusion remains incomplete.

Reviewer #1 (Public review):

Summary:

Fluorescence imaging has become an increasingly popular technique for monitoring neuronal activity and neurotransmitter concentrations in the living brain. However, factors such as brain motion and changes in blood flow and oxygenation can introduce significant artifacts, particularly when activity-dependent signals are small. Yogesh et al. quantified these effects using GFP, an activity-independent marker, under two-photon and wide-field imaging conditions in awake behaving mice. They report significant GFP responses across various brain regions, layers, and behavioral contexts, with magnitudes comparable to those of commonly used activity sensors. These data highlight the need for robust control strategies and careful interpretation of fluorescence functional imaging data.

Strengths:

The effect of hemodynamic occlusion in two-photon imaging has been previously demonstrated in sparsely labeled neurons in V1 of anesthetized animals (see Shen and Kara et al., Nature Methods, 2012). The present study builds on these findings by imaging a substantially larger population of neurons in awake, behaving mice across multiple cortical regions, layers, and stimulus conditions. The experiments are extensive, the statistical analyses are rigorous, and the results convincingly demonstrate significant GFP responses that must be accounted for in functional imaging experiments. However, whether these GFP responses are driven by hemodynamic occlusion remains less clear, given the complexities associated with awake imaging and GFP's properties (see below).

Weaknesses:

(1) The authors primarily attribute the observed GFP responses to hemodynamic occlusion. While this explanation is plausible, other factors may also contribute to the observed signals. These include uncompensated brain movement (e.g., axial-direction movements), leakage of visual stimulation light into the microscope, and GFP's sensitivity to changes in intracellular pH (see e.g., Kneen and Verkman, 1998, Biophysical Journal). Although the correlation between GFP signals and blood vessel diameters supports a hemodynamic contribution, it does not rule out significant contributions from these (or other) factors. Consequently, whether GFP fluorescence can reliably quantify hemodynamic occlusion in two-photon microscopy remains uncertain.

(2) Regardless of the underlying mechanisms driving the GFP responses, these activity-independent signals must be accounted for in functional imaging experiments. However, the present manuscript does not explore potential strategies to mitigate these effects. Exploring and demonstrating even partial mitigation strategies could have significant implications for the field.

(3) Several methodology details are missing from the Methods section. These include: (a) signal extraction methods for two-photon imaging data (b) neuropil subtraction methods (whether they are performed and, if so, how) (c) methods used to prevent visual stimulation light from being detected by the two-photon imaging system (d) methods to measure blood vessel diameter/area in each frame. The authors should provide more details in their revision.

Reviewer #2 (Public review):

Approach

In this study, Yogesh et al. aimed at characterizing hemodynamic occlusion in two photon imaging, where its effects on signal fluctuations are underappreciated compared to that in wide field imaging and fiber photometry. The authors used activity-independent GFP fluorescence, GCaMP and GRAB sensors for various neuromodulators in two-photon and widefield imaging during a visuomotor context to evaluate the extent of hemodynamic occlusion in V1 and ACC. They found that the GFP responses were comparable in amplitude to smaller GCaMP responses, though exhibiting context-, cortical region-, and depth-specific effects. After quantifying blood vessel diameter change and surrounding GFP responses, they argued that GFP responses were highly correlated with changes in local blood vessel size. Furthermore, when imaging with GRAB sensors for different neuromodulators, they found that sensors with lower dynamic ranges such as GRAB-DA1m, GRAB-5HT1.0, and GRAB-NE1m exhibited responses most likely masked by the hemodynamic occlusion, while a sensor with larger SNR, GRAB-ACh3.0, showed much more distinguishable responses from blood vessel change.

Strengths

This work is of broad interest to two photon imaging users and GRAB developers and users. It thoroughly quantifies the hemodynamic driven GFP response and compares it to previously published GCaMP data in a similar context, and illustrates the contribution of hemodynamic occlusion to GFP and GRAB responses by characterizing the local blood vessel diameter and fluorescence change. These findings provide important considerations for the imaging community and a sobering look at the utility of these sensors for cortical imaging.

Importantly, they draw clear distinctions between the temporal dynamics and amplitude of hemodynamic artifacts across cortical regions and layers. Moreover, they show context dependent (Dark versus during visual stimuli) effects on locomotion and optogenetic light-triggered hemodynamic signals.

Most of the first generation neuromodulator GRAB sensors showed relatively small responses, comparable to blood vessel changes in two photon imaging, which emphasizes a need for improved the dynamic range and response magnitude for future sensors and encourages the sensor users to consider removing hemodynamic artifacts when analyzing GRAB imaging data.

Weaknesses

The largest weakness of the paper is that, while they convincingly quantify hemodynamic artifacts across a range of conditions, they do not quantify any methods of correcting for them. The utility of the paper could have been greatly enhanced had they tested hemodynamic correction methods (e.g. from Ocana-Santero et al., 2024) and applied them to their datasets. This would serve both to verify their findings-proving that hemodynamic correction removes the hemodynamic signal-and to act as a guide to the field for how to address the problem they highlight.

The paper attributes the source of 'hemodynamic occlusion' primarily to blood vessel dilation, but leaves unanswered how much may be due to shifts in blood oxygenation. Figure 4 directly addresses the question of how much of the signal can be attributed to occlusion by measuring the blood vessel dilation, but notably fails to reproduce any of the positive transients associated with locomotion in Figure 2. Thus, an investigation into or at least a discussion of what other factors (movement? Hb oxygenation?) may drive these distinct signals would be helpful.

Along these lines, the authors carefully quantified the correlation between local blood vessel diameter and GFP response (or neuropil fluorescence vs blood vessel fluorescence with GRAB sensors). To what extent does this effect depend on proximity to the vessels? Do GFP/ GRAB responses decorrelate from blood vessel activity in neurons further from vessels (refer to Figure 5A and B in Neyhart et al., Cell Reports 2024)?

Raw traces are shown in Figure 2 but we are never presented with the unaveraged data for locomotion of stimulus presentation times, which limits the reader's ability to independently assess variability in the data. Inclusion of heatmaps comparing event aligned GFP to GCaMP6f may be of value to the reader.

More detailed analysis of differences between the kinds of dynamics observed in GFP vs GCaMP6f expressing neurons could aid in identifying artifacts in otherwise clean data. The example neurons in Figure 2A hint at this as each display unique waveforms and the question of whether certain properties of their dynamics can reveal the hemodynamic rather than indicator driven nature of the signal is left open. Eg. do the decay rate and rise times differ significantly from GCaMP6f signals?

The authors suggest that signal to noise ratio of an indicator likely affects the ability to separate hemodynamic response from the underlying fluorescence signal. Does the degree of background fluorescence affect the size of the artifact? If there was variation in background and overall expression level in the data this could potentially be used to answer this question. Could lower (or higher!) expression levels increase the effects of hemodynamic occlusion?<br /> The choice of the phrase 'hemodynamic occlusion' may cause some confusion as the authors address both positive and negative responses in the GFP expressing neurons, and there may be additional contributions from changes in blood oxygenation state.

The choice of ACC as the frontal region provides a substantial contrast in location, brain movement, and vascular architecture as compared to V1. As the authors note, ACC is close to the superior sagittal sinus and thus is the region where the largest vascular effects are likely to occur. The reader is left to wonder how much of the ROI may or may not have included vasculature in the ACC vs V1 recordings as the only images of the recording sites provided are for V1. We are left unable to conclude whether the differences observed between these regions are due to the presence of visible vasculature, capillary blood flow or differences in neurovasculature coupling between regions. A less medial portion of M2 may have been a more appropriate comparison. At least, inclusion of more example imaging fields for ACC in the supplementary figures would be of value.

In Figure 3, How do the proportions of responsive GFP neurons compare to GCaMP6f neurons?

How is variance explained calculated in Figure 4? Is this from a linear model and R^2 value? Is this variance estimate for separate predictors by using single variable models? The methods should describe the construction of the model including the design matrix and how the model was fit and if and how cross validation was run.

Cortical depth is coarsely defined as L2/3 or L5, without numerical ranges in depth from pia.

Overall Assessment:

This paper is an important contribution to our understanding of how hemodynamic artifacts may corrupt GRAB and calcium imaging, even in two-photon imaging modes. Certain useful control experiments, such as intrinsic optical imaging in the same paradigms, were not reported, nor were any hemodynamic correction methods investigated. Thus, this limits both mechanistic conclusions and the overall utility with respect to immediate applications by end users. Nevertheless, the paper is of significant importance to anyone conducting two-photon or widefield imaging with calcium and GRAB sensors and deserves the attention of the broader neuroscience and in-vivo imaging community.

Reviewer #3 (Public review):

Summary:

In this study, the authors aimed to investigate if hemodynamic occlusion contributes to fluorescent signals measured with two-photon microscopy. For this, they image the activity-independent fluorophore GFP in 2 different cortical areas, at different cortical depths and in different behavioral conditions. They compare the evoked fluorescent signals with those obtained with calcium sensors and neuromodulator sensors and evaluate their relationship to vessel diameter as a readout of blood flow.<br /> They find that GFP fluorescence transients are comparable to GCaMP6f stimuli-evoked signals in amplitude, although they are generally smaller. Yet, they are significant even at the single neuronal level. They show that GFP fluorescence transients resemble those measured with the dopamine sensor GRAB-DA1m and the serotonin sensor GRAB-5HT1.0 in amplitude an nature, suggesting that signals with these sensors are dominated by hemodynamic occlusion. 
Moreover, the authors perform similar experiments with wide-field microscopy which reveals the similarity between the two methods in generating the hemodynamic signals. Together the evidence presented calls for the development and use of high dynamic range sensors to avoid measuring signals that have another origin from the one intended to measure. In the meantime, the evidence highlights the need to control for those artifacts such as with the parallel use of activity independent fluorophores.

Strengths:

- Comprehensive study comparing different cortical regions in diverse behavioral settings in controlled conditions.<br /> - Comparison to the state-of-the-art, i.e. what has been demonstrated with wide-field microscopy.<br /> - Comparison to diverse activity-dependent sensors, including the widely used GCaMP.

Weaknesses:

- The kinetics of GCaMP is stereotypic. An analysis/comment on if and how the kinetics of the signals could be used to distinguish the hemodynamic occlusion artefacts from calcium signals would be useful.<br /> - Is it possible that motion is affecting the signals in a certain degree? This issue is not made clear.<br /> - The causal relationship with blood flow remains open. Hemodynamic occlusion seems a good candidate causing changes in GFP fluorescence, but this remains to be well addressed in further research.

eLife Assessment

This study examined how multidimensional social relationships influence social attention in rhesus macaques, linking individual and group-level behaviors to attentional processes. The findings that oxytocin altered social attention and its relationship to both social tendencies and dyadic relationships are important, as recent technological advances allow for the exploration of neuronal activities and mechanisms in free-moving macaques. This work is convincing and will be of interest to those studying the interplay between social dynamics and information processing in primates.

Reviewer #1 (Public review):

Summary:

This study aims to investigate the links between social behaviors observed in free-moving situations and behavioral performances measured in well-controlled, laboratory settings. The authors assessed general social tendencies and dyadic relationships among four monkeys in a group by scoring agonistic (aggression) and affiliative (grooming and proximity) behaviors in each pair. By measuring the saccadic reaction time in a classic social interference task, the authors reported that the monkeys with higher SEIs (i.e., more social individuals) were less distracted by the faces of other monkeys. These effects were enhanced when the distractors were out-group monkey faces rather than in-group ones. Lastly, oxytocin administration increased the impact of the out-group monkey faces in the social interference task, while reducing the magnitude of general social tendencies measured with SEI.

Strengths:

(1) The combination of behavioral data obtained in a colony room and in a laboratory environment is rare and important.<br /> (2) The evaluation of social interactions were successfully performed based on an automated target detection algorithm. The resulting multi-dimensional, complicated social interactions were summarized into simple indices (SEI and IEI). These indices provide a good measure for the social tendencies of each monkey.<br /> (3) Well-designed and robust experiments in the laboratory environment that are linked nicely with the general social tendencies observed in spontaneous behaviors.

Weaknesses:

(1) While the overall results are interesting, I am somewhat left confused about how to interpret the difference in the scores derived from different conditions. For example, the authors stated "Comparing the weights for in-group and out-group distractors, the effect of proximity was larger than that of aggression and grooming" in p.8. Does this mean that the proximity is indeed the type of behavior most affected in the out-group condition compared to the in-group condition? The out-group effects are difficult to examine with actual behavioral data, but some in-group effects such as those involving OT can be tested, which possibly provides good insights into interpreting the differences of the weights observed across the experimental conditions.

(2) I think it is important to provide how variable spontaneous social interactions were across sessions and how impactful the variability of the interactions is on the SEI and IEI, as it helps to understand how meaningful the differences of weights are across the conditions, but such data are missing. In line with this point, although the conclusions still hold as those data were obtained during the same experimental periods, shouldn't the weights in Fig. 3f and Figs. 4g and 4h (saline) be expected to be similar, if not the same?

Reviewer #2 (Public review):

Summary:

The study presents significant findings that elucidate the relationship between multi-dimensional social relationships and social attention in rhesus macaques. By integrating advanced computational methods, behavioral analyses, and neuroendocrine manipulation, the authors provide strong evidence for how oxytocin modulates attention within social networks. The results are robust and address critical gaps in understanding the dynamics of social attention in primates.

Strengths:

(1) The use of YOLOv5 for automatic behavioral detection is an exceptional methodological advance. The combination of automated analyses with manual validation enhances confidence in the data.<br /> (2) The study's focus on three distinct dimensions of social interaction (aggression, grooming, and proximity) is comprehensive and provides nuanced insights into the complexity of primate social networks.<br /> (3) The investigation of oxytocin's role adds a compelling neuroendocrine dimension to the findings, providing a bridge between behavioral and neural mechanisms.

Weaknesses:

(1) The study's conclusions are based on observations of only four monkeys, which limits the generalizability of the findings. Larger sample sizes could strengthen the validity of the results.<br /> (2) The limited set of stimulus images (in-group and out-group faces) may introduce unintended biases. This could be addressed by increasing the diversity of stimuli or incorporating a broader range of out-group members.

eLife Assessment

This valuable study uses a novel method to record spine calcium responses without the confounds of backpropagating action potentials to study how the dendritic integration of large numbers of inputs generates the tuned output of cortical neurons. While the results are generally solid, the study would benefit from more details, characterizations, and quantifications, including better validation of the method to suppress backpropagating action potentials.

Reviewer #1 (Public review):

Summary:

In this manuscript, Kondo et al. developed a method to suppress somatic action potentials while recording spine calcium signals using two-photon imaging in the L2/3 visual cortex in response to visual stimuli. The authors identified different patterns of dendritic spine activation by visual stimuli and analyzed how the different patterns of spine responses may contribute to somatic visual responses. Their analysis results suggest that spines on dendrites with a clustered arrangement can potentially generate sharply tuned output.

Strengths:

This is an interesting study addressing a standing question of how previously reported pepper-and-salt-like distributed sensory inputs on individual spines may give rise to somatic sensory selectivity. The method of somatic inhibition to prevent bAPs appears new and effective. The measurements of spine activity are carefully done. The finding that a small number of spines located in the same branch with similar tuning properties would predict the somatic tuning is consistent with local dendritic nonlinear integration mechanisms.

Weaknesses:

(1) The demonstration of the effectiveness of soma-specific inhibition is inadequate. Figure 1 only provides a single example trace showing the inhibition of somatic visual responses. The authors should provide statistical analysis over grouped data. For the effect of soma-specific inhibition on spine activity, the authors provided mostly negative results, lacking effects on spine responses for both soma inhibition and bAP subtraction. This is confusing. One possible explanation is that bAPs normally have little influence on spine activity. However, this would conflict with the known fact that somatic APs can easily invade spines in L2/3 neurons (e.g., Chen et al., Nature 2011). Another possibility is that under the current experimental conditions, somatic APs were rarely evoked by the visual stimulus. The authors should also rule out the possibility that the spines they imaged are from different neurons than the ones with somatic inhibition. The authors may consider identifying those cases where somatic APs have a significant impact on spine activity or spine tuning and show how bAP inhibition influences the dendritic and spine responses.

(2) Figure 4 shows that the proportion of spines with a preferred orientation similar to the soma (ΔOri {less than or equal to} 30{degree sign}) was 60%, which is surprisingly high. It is intriguing that without somatic AP invasion, there could be such a high degree of similarity between spine activity and somatic tuning. What is the ratio without soma inhibition? One could reason that with bAP invasion, there should be even more spines showing visual responses similar to those of the soma. Moreover, with such a high proportion of spines showing similar sensory tuning to the soma, it is inevitable that many branches contain more spines with similar tuning as the soma, exhibiting an apparent branch-specific clustering. While such apparent clustering may well predict somatic tuning, it primarily reflects a correlational relationship rather than a causal synaptic integration mechanism.

(3) There has been extensive work studying how the integration of spine activity or sub-branch activity gives rise to somatic output. The proposed main contribution of this study is to use an improved method to inhibit somatic activity in order to more confidently measure spine-specific activity and examine the integration mechanisms. However, the results showed that the measured spine-specific activity under soma inhibition was not significantly different from that measured under normal conditions (see point 1). It becomes unclear how this new method contributes to obtaining new insights into the synaptic integration mechanism.

(4) Figure 6 shows how the tuning similarity between spines depends on the distance between them. It is unclear what new information was acquired regarding the functional clustering of spines. This result can be largely explained by the overall higher proportion of similarly tuned spines (60%) compared to the soma's preferred orientations. Moreover, the authors did not demonstrate how such clustering may contribute to nonlinear synaptic integration.

(5) The results shown in Figure 7 can again be largely explained by the static property of a higher proportion of spines tuned similarly to the soma. These results do not reveal any active dendritic integration mechanisms.

Reviewer #2 (Public review):

Summary:

The paper from Kondo et al., addresses how the functional organization of synaptic inputs in 2/3 pyramidal neurons contributes to their output firing. Expressing GCamp6s to monitor calcium activity and the bi-stable inhibitory opsin SwiChR++ to inhibit the somatic activity of the imaged neurons, the authors were able to image up to ~5700 spines in basal dendrites from 6 neurons. Mapping the functional responses of such a large number of dendritic spines and relating it to the output firing of the parent neuron is a remarkable feat. The authors studied the clustering of similarly tuned spines within individual dendrites and found that while some dendrites are similarly tuned to the same orientation of the parent neuron, other dendrites exhibit tuning to other orientations and moreover a significant proportion of dendrites exhibit no tuning. Modelling work suggests that the clustering of spines in a small proportion of dendrites should suffice to give rise to the tuning of the parent cell.

Strengths:

(1) Removal of the potential confound of somatic firing via optogenetic inhibition is convincing and validates a useful tool for the neuroscientific community. As discussed by the authors the tool would be most valuable for the study of excitatory inputs in inhibitory neurons.

(2) The comparison of optogenetic inhibition of somatic responses and isolation of spine-specific signals using the removal of backpropagating action potential by robust regression is an important control and constitutes an important affirmation of previously published work.

(3) The large dataset size provides enough statistical power to test for clustering of similarly tuned spines in basal dendrites.

(4) The study provides a useful replication of previously published results.

(5) Modelling work in the study shows that as in the ferret visual cortex (Wilson et al., 2016), a combination of dendritic nonlinearity and spike thresholding contribute to the sharpness of orientation tuning in the mouse visual cortex.

Weaknesses:

(1) One of the main conclusions of the study, the classification of dendrites according to the presence or absence of visual responses, lacks quantification.

(2) Some of the statistics employed in combination with shuffling controls are not adequate.

(3) All the neurons imaged are very highly tuned (with a very high orientation selectivity index (OSI)). The performance of the models is evaluated by the correlation coefficient between the predicted and the measured somatic tuning curve. The high OSI of the neurons reduces the sensitivity of the evaluation of the models, as it results in extremely high or low correlation coefficients (Figure 8a). It would be important to recapitulate the results from the model for neurons with lower OSI, given that not all L2/3 neurons are so highly tuned.

(4) It is very hard to understand how the modelling results relate to the experimental data, as the definitions of what constitutes a clustered dendrite in the model or in the experimental data are unclear.

eLife Assessment

This study presents a valuable finding on a new role of glia in activity-dependent synaptic remodeling using the Drosophila NMJ as a model system. The evidence supporting the claims of the authors is solid. However, the unaddressed cell-type specific mechanisms of Shv secretion and regulation on the extracellular glutamate levels and lack of details on the methods for statistical analysis have hindered further evaluation of the claims. The work will be of interest to neuroscientists working on glia-neuron interaction and synaptic remodeling.

Reviewer #1 (Public review):

In this manuscript, Chang et al. investigated the cell type-specific role of the integrin activator Shv in activity-dependent synaptic remodeling. Using the Drosophila larval neuromuscular junction as a model, they show that glial-secreted Shv modulates synaptic plasticity by maintaining the extracellular balance of neuronal Shv proteins and regulating ambient extracellular glutamate concentrations, which in turn affects postsynaptic glutamate receptor abundance. Furthermore, they report that genetic perturbation of glial morphogenesis phenocopies the defects observed with the loss of glial Shv. Altogether, their findings propose a role for glia in activity-induced synaptic remodeling through Shv secretion. While the conclusions are intriguing, several issues related to experimental design and data interpretation merit further discussion.

Reviewer #2 (Public review):

In this paper Chang et al follow up on their lab's previous findings about the secreted protein Shv and its role in activity-induced synaptic remodeling at the fly NMJ. Previously they reported that shv mutants have impaired synaptic plasticity. Normally a high stimulation paradigm should increase bouton size and GluR expression at synapses but this does not happen in shv mutants. The phenotypes relating to activity dependent plasticity were completely recapitulated when Shv was knocked down only in neurons and could be completely rescued by incubation in exogenously applied Shv protein. The authors also showed that Shv activation of integrin signaling on both the pre- and post- synapse was the molecular mechanism underlying its function. Here they extend their study to consider the role of Shv derived from glia in modulating synaptic features at baseline and remodeling conditions. This study is important to understand if and how glia contribute to these processes. Using cell-type specific knockdown of Shv only in glia causes abnormally high baseline GluR expression and prevents activity-dependent increases in bouton size or GluR expression post-stimulation. This does not appear to be a developmental defect as the authors show that knocking down Shv in glia after basic development has the same effects as life long knockdown, so Shv is acting in real time. Restoring Shv in ONLY glia in mutant animals is sufficient to completely rescue the plasticity phenotypes and baseline GluR expression, but glial-Shv does not appear to activate integrin signaling which was shown to be the mechanism for neuronally derived Shv to control plasticity. This led the authors to hypothesize that glial Shv works by controlling the levels of neuronal Shv and extracellular glutamate. They provide evidence that in the absence of glial Shv, synaptic levels of Shv go up overall, presumably indicating that neurons secrete more Shv. In this context which could then work via integrin signaling as described to control plasticity. They use a glutamate sensor and observe decreased signal (extracellular glutamate) from the sensor in glial Shv KD animals, however, this background has extremely high GluR levels at the synapse which may account for some or all of the decreases in sensor signal in this background. Additional controls to test if increased GluR density alone affects sensor readouts and/or independently modulating GluR levels in the glial KD background would help strengthen this data. In fact, glial-specific shv KD animals have baseline levels of GluR that are potentially high enough to have hit a ceiling of expression or detection that accounts for the inability for these levels to modulate any higher after strong stimulation and such a ceiling effect should be considered when interpreting the data and conclusions of this paper. Several outstanding questions remain-why can't glial derived Shv activate integrin pathways but exogenously applied recombinant Shv protein can? The effects of neuronal specific rescue of shv in a shv mutant are not provided vis-à-vis GluR levels and bouton size to compare to the glial only rescue. Inclusion of this data might provide more insight to outstanding questions of how and why the source of Shv seems to matter for some aspects of the phenotypes but not others despite the fact that exogenous Shv can rescue and in some experimental paradigms but not others.

Reviewer #3 (Public review):

Summary:

The manuscript by Chang and colleagues provides compelling evidence that glia-derived Shriveled (Shv) modulates activity-dependent synaptic plasticity at the Drosophila neuromuscular junction (NMJ). This mechanism differs from the previously reported function of neuronally released Shv, which activates integrin signaling. They further show that this requirement of Shv is acute and that glial Shv supports synaptic plasticity by modulating neuronal Shv release and the ambient glutamate levels. However, there are a number of conceptual and technical issues that need to be addressed.

Major comments

(1) From the images provided for Fig 2B +RU486, the bouton size appears to be bigger in shv RNAi + stimulation, especially judging from the outline of GluR clusters.<br /> (2) The shv result needs to be replicated with a separate RNAi.<br /> (3) The phenotype of shv mutant resembles that of neuronal shv RNAi - no increased GluR baseline. Any insights why that is the case?<br /> (4) In Fig 3B, SPG shv RNAi has elevated GluR baseline, while PG shv RNAi has a lower baseline. In both cases, there is no activity induced GluR increase. What could explain the different phenotypes?<br /> (5) In Fig 4C, the rescue of PTP is only partial. Does that suggest neuronal shv is also needed to fully rescue the deficit of PTP in shv mutants?<br /> (6) The observation in Fig 5D is interesting. While there is a reduction in Shv release from glia after stimulation, it is unclear what the mechanism could be. Is there a change in glial shv transcription, translation or the releasing machinery? It will be helpful to look at the full shv pool vs the released ones.<br /> (7) In Fig 5E, what will happen after stimulation? Will the elevated glial Shv after neuronal shv RNAi be retained in the glia?<br /> (8) It would be interesting to see if the localization of shv differs based on if it is released by neuron or glia, which might be able to explain the difference in GluR baseline. For example, by using glia-Gal4>UAS-shv-HA and neuronal-QF>QUAS-shv-FLAG. It seems important to determine if they mix together after release? It is unclear if the two shv pools are processed differently.<br /> (9) Alternatively, do neurons and glia express and release different Shv isoforms, which would bind different receptors?<br /> (10) It is claimed that Sup Fig 2 shows no observable change in gross glial morphology, further bolstering support that glial Shv does not activate integrin. This seems quite an overinterpretation. There is only one image for each condition without quantification. It is hard to judge if glia, which is labeled by GFP (presumably by UAS-eGFP?), is altered or not.<br /> (11) The hypothesis that glutamate regulates GluR level as a homeostatic mechanism makes sense. What is the explanation of the increased bouton size in the control after glutamate application in Fig 6?<br /> (12) What could be a mechanism that prevents elevated glial released Shv to activate integrin signaling after neuronal shv RNAi, as seen in Fig 5E?<br /> (13) Any speculation on how the released Shv pool is sensed?

eLife Assessment

In this important manuscript, Ryan et al perform a genome-wide CRISPR based screen to identify genes that modulate TDP-43 levels in neurons. They identify a number of genes and pathways and highlight the BORC complex, which is required for anterograde lysosome transport as one such regulator of TDP-43 protein levels. Overall, this is a convincing study, which opens the door for additional future investigations on the regulation of TDP-43.

Reviewer #1 (Public review):

Summary:

As TDP-43 mislocalization is a hallmark of multiple neurodegenerative diseases, the authors seek to identify pathways that modulate TDP-43 levels. To do this, they use a FACS based genome wide CRISPR KD screen in a Halo tagged TDP-43 KI iPSC line. Their screen identifies a number of genetic modulators of TDP-43 expression including BORC which plays a role in lysosome transport.

Strengths:

Genome wide CRISPR based screen identifies a number of modulators of TDP-43 expression to generate hypotheses regarding RNA BP regulation and perhaps insights into disease.

Weaknesses:

It is unclear how altering TDP-43 levels may relate to disease where TDP-43 is not altered in expression but mislocalized. This is a solid cell biology study, but the relation to disease is not clear without providing evidence of BORC alterations in disease or manipulation of BORC reversing TDP-43 pathology in disease.

The mechanisms by which BORC and lysosome transport modulate TDP-43 expression are unclear. Presumably, this may be through altered degradation of TDP protein but this is not addressed.

Previous studies have demonstrated that TDP-43 levels can be modulated by altering lysosomal degradation so the identification of lysosomal pathways is not particularly novel.

It is unclear whether this finding is specific to TDP-43 levels or whether lysosome localization may more broadly impact proteostasis in particular of other RNA BPs linked to disease.

Unclear whether BORC depletion alters lysosome function or simply localization.

Reviewer #2 (Public review):

Summary:

The authors employ a novel CRISPRi FACS screen and uncover the lysosomal transport complex BORC as a regulator of TDP-43 protein levels in iNeurons. They also find that BORC subunit knockouts impair lysosomal function, leading to slower protein turnover and implicating lysosomal activity in the regulation of TDP-43 levels. This is highly significant for the field given that a) other proteins could also be regulated in this way, b) understanding mechanisms that influence TDP-43 levels are significant given that its dysregulation is considered a major driver of several neurodegenerative diseases and c) the novelty of the proposed mechanism.

Strengths:

The novelty and information provided by the CRISPRi screen. The authors provide evidence indicating that BORC subunit knockouts impair lysosomal function, leading to slower protein turnover and implicating lysosomal activity in the regulation of TDP-43 levels and show a mechanistic link between lysosome mislocalization and TDP-43 dysregulation. The study highlights the importance of localized lysosome activity in axons and suggests that lysosomal dysfunction could drive TDP-43 pathologies associated with neurodegenerative diseases like FTD/ALS. Further, the methods and concepts will have an impact to the larger community as well. The work also sets up for further work to understand the somewhat paradoxical findings that even though the tagged TDP-43 protein is reduced in the screen, it does not alter cryptic exon splicing and there is a longer TDP-43 half-life with BORC KD.

Weaknesses:

While the data is very strong, the work requires some additional clarification.

Reviewer #3 (Public review):

Summary:

In this work, Ryan et al. have performed a state-of-the-art full genome CRISP-based screen of iNEurons expressing a teggd version of TDP-43 in order to determine expression modifiers of this protein. Unexpectedly, using this approach the authors have uncovered a previously undescribed role of the BORC complex in affecting the levels of TDP-43 protein, but not mRNA expression. Taken together, these findings represent a very solid piece of work that will certainly be important for the field.

Strengths:

- BORC is a novel TDP-43 expression modifier that has never been described before and it seemingly acts on regulating protein half life rather than transcriptome level. It has been long known that different labs have reported different half-lives for TDP-43 depending on the experimental system but no work has ever explained these discrepancies. Now, the work of Ryan et al. has for the time identified one of these factors which could account for these differences and play an important role in disease (although this is left to be determined in future studies).<br /> - The genome wide CRISPR screening has demonstrated to yield novel results with high reproducibility and could eventually be used to search for expression modifiers of many other proteins involved in neurodegeneration or other diseases

Weaknesses:

- The fact that TDP-43 mRNA does not change following BORCS6 KD is based on a single qRT-PCR that does not really cover all possibilities. For example, the mRNA total levels may not change but the polyA sites may have switched from the highly efficient pA1 to the less efficient and nuclear retained pA4. There are therefore a few other experiments that could have been performed to make this conclusion more compelling, maybe also performing RNAscope experiments to make sure that no change occurred in TDP-43 mRNA localisation in cells.<br /> - Even assuming that the mRNA does not change, no explanation for the change in TDP-43 protein half life has been proposed by the authors. This will presumably be addressed in future studies: for example, are mutants that lack different domains of TDP-43 equally affected in their half-lives by BORC KD?. Alternatively, can a mass-spec be attempted to see whether TDP-43 PTMs change following BORCS6 KD?

eLife Assessment

This valuable study by Cui et al. investigates mechanisms generating sighs, which are crucial for respiratory function and linked to emotional states. Utilizing advanced methods in mice, they provide solid evidence that increased excitability in specific preBötzinger complex neuronal subpopulations expressing Neuromedin B receptors, gastrin-releasing peptide receptors, or somatostatin can induce sigh-like large amplitude inspirations. With additional technical clarifications and further elaboration of the limitations in terms of how the results are interpreted in the revised manuscript, the study will interest neuroscientists studying respiratory neurobiology and rhythmic motor systems.

Reviewer #1 (Public review):

Summary of what is achieved: This manuscript validates and extends upon the sigh generating circuit between the NMB/GRP+ RTN/parafacial neurons and the NMBR/GRPR+ preBötC neurons established in Li et al., 2016. The authors generate multiple transgenic lines that enable selective targeting of these various sub-populations of cells and demonstrate the sufficiency of each type in generating a sigh breath. Additionally, they show that NMBR and GPRP preBötC neurons are glutamatergic, have overlapping and distinct expression, and do not express SST. Beyond this validation, the authors show that ectopic stimulation of SST neurons is sufficient to evoke sighs and that they are necessary for NMB/GRP induced sighing. This data is the first time that preBötC neurons downstream of NMBR/GRPR neurons have been identified that transform a eupneic breath into a sign breath. The five conclusions stated at the end of the introduction are supported by the data.

Summary of a primary weakness: A strong emphasis throughout the manuscript is the identification of an unsubstantiated slow sigh rhythm that is produced by NMBR/GRPR neurons. It is even suggested that this is an intrinsic property of these neurons. However, to make such a novel (and quite surprising) claim requires many more studies and the conclusion is dependent on how the authors have defined a sigh. Moreover, some data within the paper conflicts with this idea. The resubmitted manuscript does not contain any revisions and the rebuttal does not sufficiently address the critiques.

In summary, the optogenetic and chemogenetic characterization of the neuropeptide pathway transgenic lines nicely aligns with and provides important validation of the previous study by Li et. al., 2016 and the SST neuron studies provide a new mechanism for the transformation of NMBR/GRPR neuropeptide activation into a sigh. These are important findings, and they should be the points emphasized. The proposal of a slow sigh rhythm should be more rigorously established with new experiments and analysis or should be more carefully described and discussed.

Reviewer #2 (Public review):

Summary:

This study investigates in mice neural mechanisms generating sighs, which are periodic large-amplitude breaths occurring during normal breathing that subserve physiological pulmonary functions and are associated with emotional states such as relief, stress, and anxiety. Sighs are generated by a structure called the preBötzinger complex (preBötC) in the medulla oblongata that generates various forms of inspiratory activity including sighs. The authors have previously described a circuit involving neurons producing bombesin-related peptides Neuromedin B (NMB) and gastrin releasing peptide (GRP) that project to preBötC neurons expressing receptors for NMB (NMBRs) and GRP (GRPRs) and that activation of these preBötC neurons via these peptide receptors generates sighs. In this study the authors further investigated mechanisms of sigh generation by applying optogenetic and chemogenetic strategies to selectively activate the subpopulations of preBötC neurons expressing NMBRs and/or GRPRs, and a separate subpopulation of neurons expressing somatostatin (SST) but not NMBRs and GRPRs. The authors present convincing evidence that sigh-like inspirations can be evoked by photostimulation of the preBötC neurons expressing NMBRs or GRPRs. Photostimulation of SST neurons can independently evoke sighs, and chemogenetic inhibition of these neurons can abolish sighs. The results presented support the authors' conclusion that the preBötC neurons expressing NMBRs or GRPRs produce sighs via pathways to downstream SST neurons. Thus, these studies have identified some of the preBötC cellular elements likely involved in generating sighs.

Strengths:

(1) This study employs an effective combination of electrophysiological, transgenic, optogenetic, chemogenetic, pharmacological, and neuron activity imaging techniques to investigate sigh generation by distinct subpopulations of preBötC neurons in mice.

(2) The authors extend previous studies indicating that there is a peptidergic circuit consisting of NMB and GRP expressing neurons that project from the parafacial (pF) nucleus region to the preBötC and provides sufficient input to generate sighs, since photoactivation of either pF NMB or GRP neurons evoke ectopic sighs in this study.

(3) Solid evidence is presented that sighs can be evoked by direct photostimulation of preBötC neurons expressing NMBRs and/or GRPRs, and also a separate subpopulation of neurons expressing somatostatin (SST) but not NMBRs and GRPRs.

(4) The mRNA-expression data presented from in situ hybridization indicates that most preBötC neurons expressing NMBR, GRPR (or both) are glutamatergic and excitatory.

(5) Measurements in slices in vitro indicate that only the NMBR expressing neurons are normally rhythmically active during normal inspiratory activity and endogenous sigh activity.

(6) Evidence is presented that activation of preBötC NMBRs and/or GRPRs is not necessary for sigh production, suggesting that sighs are not the unique product of the preBötC bombesin-peptide signaling pathway.

(7) The novel conclusion is presented that the preBötC neurons expressing NMBRs and/or GRPRs produce sighs via the separate downstream population of preBötC SST neurons, which the authors demonstrate can independently generate sighs, whereas chemogenetic inhibition of preBötC SST neurons selectively abolishes sighs generated by activating NMBRs and GRPRs.

Weaknesses:

(1) While these studies have identified subpopulations of preBötC neurons capable of episodically evoking sigh-like inspiratory activity, mechanisms producing the normal slow sigh rhythm were not investigated and remain unknown.

(2) The authors have addressed some of the reviewers' main technical concerns and issues relating to interpretation of the results in their rebuttal letter, but have minimally revised the manuscript. Accordingly, there remain important technical and interpretation issues requiring resolution in the revised manuscript.

Comments on revisions:

The authors have clarified in their rebuttal letter the rationale for utilizing two different photostimulation paradigms but have not incorporated any of this explanation in Methods, which would be helpful for readers.

Reviewer #3 (Public review):

Summary:

This manuscript by Cui et al., studies the mechanisms for the generation of sighing, an essential breathing pattern. This is an important and interesting topic, as sighing maintains normal pulmonary function and is associated with various emotional conditions. However, the mechanisms of its generation remain not fully understood. The authors employed different approaches, including optogenetics, chemogenetics, intersectional genetic approach, and slice electrophysiology and calcium imaging, to address the question, and found several neuronal populations are sufficient to induce sighing when activated. Furthermore, ectopic sighs can be triggered without the involvement of neuromedin B (NMB) or gastrin releasing peptide (GRP) or their receptors in the preBötzinger Complex (preBötC) region of the brainstem. Additionally, activating SST neurons in the preBötC region induces sighing, even when other receptors are blocked. Based on these results, the authors concluded that increased excitability in certain neurons (NMBR or GRPR neurons) activates pathways leading to sigh generation, with SST neurons serving as a downstream component in converting regular breaths into sighs.

Strengths:

The authors employed a combination of various sophisticated approaches, including optogenetics, chemogenetics, intersectional genetic approach, and slice electrophysiology and calcium imaging, to precisely pinpoint the mechanism responsible for sigh generation. They utilized multiple genetically modified mouse lines, enabling them to selectively manipulate and observe specific neuronal populations involved in sighing.<br /> Using genetics and calcium imaging, the authors record the neuronal activity of NMBR and GRPR neurons, respectively, and identified their difference in activity pattern. Furthermore, by applying the intersectional approach, the authors were able to genetically target and manipulate several distinct neuronal populations, such as NMBR+, GRPR- neurons and GRPR+, NMBR- neurons, and conducted a detailed characterization of their functions in influencing sighing.

Weaknesses:

(1) The authors employed two conditions for optogenetic activation: long pulse photostimulation (LPP) and short pulse photostimulation (SPP), with durations ranging from 4-10s for LPP and 100-500 ms for SPP. These could generate huge variability in the experiments. The rationale behind the selection of these conditions in each experiment remains unclear in the manuscript. Additionally, it is not explained why these specific durations were chosen. Furthermore, the interpretation for the varied responses observed under these conditions is not provided. Clarification on the rationale and interpretation of these experimental parameters would enhance the understanding of the results. The description of the experiment conditions should be consistent throughout the manuscript.

(2) Regarding the fiber optics, my understanding is that they are placed outside of the brainstem from the ventral side. Given the locations of the pF and preBötC neurons, could the differences in responses be attributed to the varying distances of each population from the ventral surface? In fact, in Figure 8, NMBR is illustrated as being closer to the ventral surface. Does it represent the actual location of these neurons?

(3) The results of recording on NMBR neurons in Figure 4 were compelling. However, I'm curious why the recording of GRPR neurons and their response to the neuropeptide were not presented or examined. Additionally, considering the known cross-reaction between peptides and their receptors, it might be worthwhile to investigate how GRP modulates NMBR neurons and how NMB modulates GRPR neurons.

(4) The authors found that activation of several preBötC populations, including NMBR, GRPR, and SST neurons, despite pharmacological inhibition of NMBR and GRPR, can still induce sighing, and concluded that "activation of preBötC NMBRs and/or GRPRs is not necessary for sigh production". I disagree with this conclusion. Even when the receptors are silenced, artificial (optogenetic or chemogenetic) activation could still activate the same downstream pathways. This cannot be used as evidence to claim that the receptors are not required for sighing in vivo, because it is possible that the receptors are still necessary for the activation of these neurons under natural conditions. For instance, while diaphragm activation induces breathing, it does not negate the crucial role of the nervous system in regulating this process in physiological conditions.

(5) The authors noted varied responses upon activating specific subpopulations of the preBötC neurons, namely NMBR, GRPR, and SST neurons. Could these differences be attributed to variations in viral labeling efficiency among different mouse genetic lines? Are there discrepancies in the number of labeled neurons across the lines? Additionally, the authors did not thoroughly characterize the specificities of AAV targeting in their Cre and Flp lines. It's uncertain whether the AAV-labeled neurons are strictly restricted to the designated population without notable leakage into other populations. This is particularly crucial for the experiments manipulating SST neurons. If there's substantial labeling of NMBR or GRPR neurons, it could undermine the conclusions drawn. Further examination of the precision and selectivity of the labeling techniques is necessary to ensure the accurate interpretation of the experimental findings.

(6) The authors have addressed some of the reviewers' concerns in the revision; however, many important issues remain unaddressed.

Author response:

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

(1) Reviewer 3: Moreover, the conclusion that preBötC NMBR and GRPR activations are unnecessary for sighing is not fully supported by the current experimental design. While the study shows that sighing can still be induced despite pharmacological inhibition of NMBR and GRPR, this does not conclusively prove that these receptors are not required under natural conditions. 

We concluded that “NMBR and GRPR receptors are not necessary for sigh generation”. We acknowledge that under normal conditions these receptors almost certainly play a role; in fact, microinjection of saporin conjugated to bombesin, which presumably ablates NMBR⁺ and GRPR⁺ preBötC neurons, completely eliminated endogenous sighing activity in awake mice (Li et al., Nature, 2015). However, that study did not establish that the receptors per se are essential in this context, since the protocol ablated not just the receptors but also the preBötC neurons that happened to express these receptors. Here, we show that we could evoke sighs AFTER complete pharmacological blockade of NMBRs and GRPRs. Also, we show that sighs can be elicited by stimulation of a distinct subpopulation of preBötC neurons expressing the peptide somatostatin (SST⁺). These results demonstrate that sighs can be evoked in absence of activation of NMBRs and/or GRPRs, leading to the conclusion that NMBRs and/or GRPRs are not required for sighs but rather contribute to periodic sigh generation under normal conditions.

(2) Reviewer 1: To make such a novel (and quite surprising) claim requires many more studies and the conclusion is dependent on how the authors have defined a sigh. Moreover, some data within the paper conflicts with this idea.

Our definition of sighs was carefully chosen so that it applied across different experimental conditions, including in vitro slices, anesthetized or awake in vivo. We defined sighs as transient changes in minute ventilation on a time scale slower than eupneic breathing period, to avoid classifying breathing after vagotomy or under isoflurane anesthesia as “all-sigh breathing”. This is why induction of persistent large amplitude breaths (such as in Figures 5-6) were not counted as sighs.

(3) Reviewer 2: Several key technical aspects of the study require further clarification to aid in interpreting the experimental results, including issues relating to the validation of the transgenic mouse lines and virally transduced expressions of proteins utilized for optogenetic and chemogenetic experiments, as well as justifying the optogenetic photostimulation paradigms used to evoke sighs.

The rationale for using SPP and LPP stems from our published observations of the effects of optogenetic stimulation of various preBötC neuronal subpopulations. Thus, SPP and LPP evoke the same responses in GlyT2 (Sherman et al., 2015) and Dbx1 (Cui et al., 2016) neurons, while for other subpopulations, e.g., SST (Cui et al., 2015), the effects of SPP are markedly different from LPP. Hence, in this study we examined both. As effects of SPP and LPP of SST neurons were examined previously (Cui et al., 2016), these protocols were not repeated except for evoking sighs after blockade of NMBR/GRPRs. SPP of pF NMB or GRP did not evoke any respiratory responses and hence were not presented in any figures (see Results, section “Activation of Nmb- or Grp-expressing pF neurons induces sighs”).

(4) Reviewer 3: however, the rationale and experimental details require further explanation, and their impacts on the conclusion require clarification. For instance, how and why the variability in optogenetic activation conditions could impact the experimental outcomes. 

Refractory periods reported here for pF NMB, pF GRP, preBötC NMBR and preBötC GRPR were all obtained using the same intensity LPP. We acknowledge the possibility, even the likelihood that higher intensity LPP would shorten refractory periods. In line with this, we observed that ectopic sighs were evoked earlier during the LPP as the sigh phase progressed. As described in RESULTS, such effects were observed for pF NMB, pF GRP, preBötC NMBR and preBötC GRPR only and not for preBötC SST, which might suggest that timing of intrinsically generated sighs depends on the NMB-GRP signaling pathway, yet sigh production depends on the SST pathway.

eLife Assessment

In this revised manuscript, Dong et al. investigate the role of the small Ras-like GTPase Rab10 in the exocytosis of DCVs in mouse hippocampal neurons, showing that Rab10 depletion hinders DCV exocytosis independently of its effects on neurite outgrowth. Upon revising their work, these findings provide compelling evidence that Rab10 depletion leads to altered ER morphology, impaired ER-based calcium buffering, and decreased ribosomal protein expression, which collectively contributes to defective DCV secretion. The study comes to the fundamental conclusion that Rab10 is critical for DCV release by ensuring ER calcium homeostasis.

Reviewer #1 (Public review):

Summary:

Dong et al here have studied the impact of the small Ras-like GTPase Rab10 on the exocytosis of dense core vesicles (DVC), which are important mediators of neuropeptide signaling in brain. They use optical imaging to show that lentiviral depletion of Rab10 in mouse hippocampal neurons in culture independent of the established defects in neurite outgrowth hamper DCV exocytosis. They further demonstrate that such defects are paralleled by changes in ER morphology and defective ER-based calcium buffering as well as reduced ribosomal protein expression in Rab10-depleted neurons. Re-expression of Rab10 or supplementation of exogenous L-leucine to restore defective neuronal protein synthesis rescues impaired DCV secretion. Based on these results they propose that Rab10 regulates DCV release by maintaining ER calcium homeostasis and neuronal protein synthesis.

Strengths:

This work provides interesting and potentially important new insights into the connection between ER function and the regulated secretion of neuropeptides via DCVs. The authors combine advanced optical imaging with light and electron microscopy, biochemistry and proteomics approaches to thoroughly assess the effects of Rab10 knockdown at the cellular level in primary neurons. The proteomic dataset provided may be valuable in facilitating future studies regarding Rab10 function. This work will thus be of interest to neuroscientists and cell biologists.

Weaknesses:

Whether and how the phenotypes of Rab10 reported in this study are linked remains an open question. Likewise, a possible role of Rab10 in exocytosis cannot be excluded at this stage.

Comments on revisions:

My previous questions and concerns have been satisfactorily addressed by the authors.

Reviewer #2 (Public review):

Summary:

In this paper, the authors assess the function of Rab10 in dense core vesicle (DCV) exocytosis using RNAi and cultured neurons. The author provides evidence that their knockdown (KD) is effective and provides evidence that DCV is compromised. They also perform proteomic analysis to identify potential pathway that are affected upon KD of Rab10 that may be involved in DCV release. Upon focusing on ER morphology and protein synthesis, the authors conclude that defects in protein synthesis and ER Ca2+ homeostasis contributes to the DVC release defect upon Rab10 KD.

Strengths:

The data related to Rab10's role in DCV release seems to be strong and carried out with rigor. While the paper lacks in vivo evidence that this gene is indeed involved in DCV in a living mammalian organism, I feel the cellular studies have value. The identification of ER defect in Rab10 manipulation is not truly novel but it is a good conformation of studies performed in other systems. The finding that DCV release defect and protein synthesis defect seen upon Rab10 KD can be significantly suppressed by Leucine supplementation is also a strength of this work.

Weaknesses:

The weaknesses mentioned in my previous comments have been addressed through the revision process.

Reviewer #3 (Public review):

In this study, Dong and colleagues set to dissect the role of Rab10 small GTPase on the intracellular trafficking and exocytosis of dense core vesicles (DCVs). While the authors have already shown that Rab3 plays a central role in the exocytosis of DVC in mammalian neurons, the roles of several other Rab-members have been identified genetically, but their precise mechanism of action in mammalian neurons remains unclear. In this study, the authors use a carefully designed and thoroughly executed series of experiments, including live-cell imaging, functional calcium-imaging, proteomics, and electron microscopy, to identify that DCV secretion upon Rab10 depletion in adult neurons is primarily a result of dysregulated protein synthesis and, to a lesser extent, disrupted intracellular calcium buffering. Given that the full deletion of Rab10 has deleterious effect on neurons and that Rab10 has a major role in axonal development, the authors cautiously employed the knock-down strategy from 7 DIV, to focus on the functional impact of Rab10 in mature neurons. The experiments in this study were meticulously conducted, incorporating essential controls and thoughtful considerations, ensuring rigorous and comprehensive results that fully support the conclusions.

Comments on revisions:

The authors have addressed all the comments and suggestions raised by reviewers, making this an excellent and timely study.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Dong et al here have studied the impact of the small Ras-like GTPase Rab10 on the exocytosis of dense core vesicles (DVC), which are important mediators of neuropeptide signaling in the brain. They use optical imaging to show that lentiviral depletion of Rab10 in mouse hippocampal neurons in culture independent of the established defects in neurite outgrowth hamper DCV exocytosis. They further demonstrate that such defects are paralleled by changes in ER morphology and defective ER-based calcium buffering as well as reduced ribosomal protein expression in Rab10-depleted neurons. Re-expression of Rab10 or supplementation of exogenous L-leucine to restore defective neuronal protein synthesis rescues impaired DCV secretion. Based on these results they propose that Rab10 regulates DCV release by maintaining ER calcium homeostasis and neuronal protein synthesis.

Strengths:

This work provides interesting and potentially important new insights into the connection between ER function and the regulated secretion of neuropeptides via DCVs. The authors combine advanced optical imaging with light and electron microscopy, biochemistry, and proteomics approaches to thoroughly assess the effects of Rab10 knockdown at the cellular level in primary neurons. The proteomic dataset provided may be valuable in facilitating future studies regarding Rab10 function. This work will thus be of interest to neuroscientists and cell biologists.

We appreciate the positive evaluation of our manuscript.

Weaknesses:

While the main conclusions of this study are comparably well supported by the data, I see three major weaknesses:

(1) For some of the data the statistical basis for analysis remains unclear. I.e. is the statistical assessment based on N= number of experiments or n = number of synapses, images, fields of view etc.? As the latter cannot be considered independent biological replicates, they should not form the basis of statistical testing.

This is an important point and we agree that multiple samples from the same biological replicate are not independent observations. We reanalyzed all nested data using a linear mixed model and indicated this in the Methods section and the relevant figure legends (Brunner et al., 2022). In brief, biological replicates (individual neuronal cultures) were used as a linear predictor. Outliers were identified and excluded using the ROUT method in GraphPad. A fixed linear regression model was then fitted to the data using the lm() function in R. A one-way anova (analysis of variance) was used to assess whether including the experimental group as a second linear predictor (formula = y ~ Group + Culture) statistically improved the fit of a model without group information (formula = y ~ 1 + Culture). Post-hoc analysis was performed using the emmeans() function with Tukey’s adjustment when more than two experimental groups were present. Importantly, our conclusions remain unchanged.

(2) As it stands the paper reports on three partially independent phenotypic observations, the causal interrelationship of which remains unclear. Based on prior studies (e.g. Mercan et al 2013 Mol Cell Biol; Graves et al JBC 1997) it is conceivable that defective ER-based calcium signaling and the observed reduction in protein synthesis are causally related. For example, ER calcium release is known to promote pS6K1 phosphorylation, a major upstream regulator of protein synthesis and ribosome biogenesis. Conversely, L-leucine supplementation is known to trigger calcium release from ER stores via IP3Rs. Given the reported impact of Rab10 on axonal transport of autophagosomes and, possibly, lysosomes via JIP3/4 or other mediators (see e.g. Cason and Holzbaur JCB 2023) and the fact that mTORC1, the alleged target of leucine supplementation, is located on lysosomes, which in turn form membrane contacts with the ER, it seems worth analyzing whether the various phenotypes observed are linked at the level of mTORC1 signaling.

This is great suggestion that could indeed further clarify the potential interplay between ER-based Ca2+ signaling and protein synthesis. To address this, we assessed the phosphorylation level of pS6K1 in control and Rab10 knockdown (KD) neurons with or without leucine treatment. These data are included in the new Figure 8—figure supplement 1 in the revised manuscript. Our results indicate that pS6K1 phosphorylation was not upregulated in Rab10 KD neurons, suggesting that the level of mTORC1 signaling is not different between wild-type or KD neurons. Furthermore, leucine treatment increased the pS6K1 phosphorylation level, as expected, but this effect was similar in both groups. Hence, we conclude that differences in mTORC1 signaling induced by Rab10 loss is not a major factor in the observed impairment in protein synthesis.

Author response image 1.

Rab10 depletion does not upregulate mTORC1 pathway. (A)Typical immunoblot showing pS6K1 levels in each condition. (B) Quantification of relative pS6K1 levels in each condition. All Data are plotted as mean±s.e.m. (C) Control, Control + Leu: N = 2, n = 2, Rab10 KD, Rab10 KD + Leu: N = 2, n = 4.

(3) The claimed lack of effect of Rab10 depletion on SV exocytosis is solely based on very strong train stimulation with 200 Aps, a condition not very well suited to analyze defects in SV fusion. The conclusion that Rab10 loss does not impact SV fusion thus seems premature.

We agree that 200 APs stimulation might be too strong to detect specific effects on evoked synaptic vesicle release, although this stimulation pattern is an established pattern in hundreds of studies (Emperador-Melero et al., 2018; Granseth et al., 2006; Ivanova et al., 2021; Kwon and Chapman, 2011; Reshetniak et al., 2020). We have toned down our conclusions and clarified in the revised manuscript that Rab10 is dispensable for SV exocytosis evoked by intense stimulations. The corresponding statements in the text have been modified accordingly (p. 5, l. 98, 124) and in figure legend (p. 17, 490).

Reviewer #2 (Public Review):

Summary:<br /> In this paper, the authors assess the function of Rab10 in dense core vesicle (DCV) exocytosis using RNAi and cultured neurons. The author provides evidence that their knockdown (KD) is effective and provides evidence that DCV is compromised. They also perform proteomic analysis to identify potential pathways that are affected upon KD of Rab10 that may be involved in DCV release. Upon focusing on ER morphology and protein synthesis, the authors conclude that defects in protein synthesis and ER Ca2+ homeostasis contributes to the DVC release defect upon Rab10 KD. The authors claim that Rab10 is not involved in synaptic vesicle (SV) release and membrane homeostasis in mature neurons.

Strengths:

The data related to Rab10's role in DCV release seems to be strong and carried out with rigor. While the paper lacks in vivo evidence that this gene is indeed involved in DCV in a living mammalian organism, I feel the cellular studies have value. The identification of ER defect in Rab10 manipulation is not truly novel but it is a good conformation of studies performed in other systems. The finding that DCV release defect and protein synthesis defect seen upon Rab10 KD can be significantly suppressed by Leucine supplementation is also a strength of this work.

We appreciate the positive evaluation of our manuscript.

Weaknesses:

The data showing Rab10 is NOT involved in SV exocytosis seems a bit weak to me. Since the proteomic analysis revealed so many proteins that are involved in SV exo/encodytosis to be affected upon Rab10, it is a bit strange that they didn't see an obvious defect. Perhaps this could have been because of the protocol that the authors used to trigger SV release (I am not an E-phys expert but perhaps this could have been a 'sledge-hammer' manipulation that may mask any subtle defects)? Perhaps the authors can claim that DCV is more sensitive to Rab10 KD than SV, but I am not sure whether the authors should make a strong claim about Rab10 not being important for SV exocytosis.

We agree that 200 APs stimulation might be too strong to see specific effects on evoked synaptic vesicle release, although this stimulation pattern is an established pattern in hundreds of studies. We have toned down our conclusions and clarified in the revised manuscript that Rab10 is dispensable for SV exocytosis evoked by intense stimulations. The corresponding statements in the text have been modified accordingly (p. 5, l. 98, 124) and in figure legend (p. 17, 490).

Also, the authors mention "Rab10 does not regulate membrane homeostasis in mature neurons" but I feel this is an overstatement. Since the authors only performed KD experiments, not knock-out (KO) experiments, I believe they should not make any conclusion about it not being required, especially since there is some level of Rab10 present in their cells. If they want to make these claims, I believe the authors will need to perform conditional KO experiments, which are not performed in this study.

This is a valid point. We have changed the statement to “membrane homeostasis in mature neurons was unaffected by Rab10 knockdown” (p. 13, l.376-377).

Finally, the authors show that protein synthesis and ER Ca2+ defects seem to contribute to the defect but they do not discuss the relationship between the two defects. If the authors treat the Rab10 KD cells with both ionomycin and Leucine, do they get a full rescue? Or is one defect upstream of the other (e.g. can they see rescue of ER morphology upon Leucine treatment)? While this is not critical for the conclusions of the paper, several additional experiments could be performed to clarify their model, especially considering there is no clear model that explains how Rab10, protein synthesis, ER homeostasis, and Ca2+ are related to DCV (but not SV) exocytosis.

This is an important point and a great suggestion. We have now tested the rescue effects of leucine treatment on ER morphology, as suggested. These data are included in the new Figure 8—figure supplement 2 in the revised manuscript. Our results indicate that the same dose of leucine that rescues DCV fusion and protein translation failed to rescue ER morphology. Hence, the defects in ER morphology appear to be independent of the impaired protein translation.

Author response image 2.

Leucine supplementation does not rescue ER morphological deficiency in Rab10 KD neurons. (A) Typical examples showing the KDEL signals in each condition. (B) Quantification of RTN4 intensity in MAP2-positive dendrites. (C) The ratio of neuritic to somatic RTN4 intensity (N/S).

All Data are plotted as mean±s.e.m. (B, C) Control: N = 3, n = 10; Rab10 KD: N = 3, n = 11; Rab10 KD + Leu: N = 3; n = 11. A one-way ANOVA tested the significance of adding experimental group as a predictor. **** = p<0.0001, ns = not significant.

Reviewer #3 (Public Review):

In the submitted manuscript, Dong and colleagues set out to dissect the role of the Rab10 small GTPase on the intracellular trafficking and exocytosis of dense core vesicles (DCVs). While the authors have already shown that Rab3 plays a central role in the exocytosis of DVC in mammalian neurons, the roles of several other Rab-members have been identified genetically, but their precise mechanism of action in mammalian neurons remains unclear. In this study, the authors use a carefully designed and thoroughly executed series of experiments, including live-cell imaging, functional calcium-imaging, proteomics, and electron microscopy, to identify that DCV secretion upon Rab10 depletion in adult neurons is primarily a result of dysregulated protein synthesis and, to a lesser extent, disrupted intracellular calcium buffering. Given that the full deletion of Rab10 has a deleterious effect on neurons and that Rab10 has a major role in axonal development, the authors cautiously employed the knock-down strategy from 7 DIV, to focus on the functional impact of Rab10 in mature neurons. The experiments in this study were meticulously conducted, incorporating essential controls and thoughtful considerations, ensuring rigorous and comprehensive results.

We are grateful for the positive evaluation of our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The work by Dong et al provides interesting and potentially important new insights into the connection between ER function and the regulated secretion of neuropeptides via DCVs. I suggest that the authors address the following points experimentally to increase the impact of this potentially important study.

Major points:

(1) As alluded to above, for some of the data the statistical basis for analysis remains unclear (examples are Figures 1C-F, J,K; Figure 2 1B-D,I-K; Figure 2 - Supplement 1D-F; Figure 2 - Supplement 2J,K, etc). I.e. is the statistical assessment based on N = number of experiments or n = number of synapses, images, fields of view etc.? As the latter cannot be considered independent biological replicates, they should not form the basis of statistical testing. The Ms misses also misses a dedicated paragraph on statistics in the methods section.

See reply to reviewer 1 above. We fully agree and solved this point.

(2) A main weakness of the paper is the missing connection between neuronal protein synthesis, and the observed structural and signaling defects at the level of the ER. I suggest that the authors analyze mTORC1 signaling in Rab10 depleted neurons and under rescue conditions (+Leu or re-expression of Rab10) as ribosome biogenesis is a major downstream target of mTORC1 and mTORC1 activity is related to lysosome position, which may be affected upon rab10 loss -either directly or via effects on the ER that forms tight contacts with lysosomes.

See reply to reviewer 1 above. We agreed and followed up experimentally.

(3) Related to the above: Does overexpression of SERCA2 restore normal DCV exocytosis in Rab10-depleted neurons? This would help to distinguish whether calcium storage and release at the level of the ER indeed contribute to the exocytosis defect.

This is an important point and a great suggestion. We have now tested the rescue effects of overexpression of SERCA2 on DCV fusion. These data are included in the new Figure 8—figure supplement 3 in the revised manuscript. SERCA2 OE failed to rescue the DCV fusion defects in Rab10 KD neurons.

Author response image 3.

Overexpression of SERCA2 does not rescue DCV fusion deficits in Rab10 KD neurons. (A) Typical examples showing the SERCA2 signals in each condition. (B) Cumulative plot of DCV fusion events per cell. (C) Summary graph of DCV fusion events per cell. (A) Total number of DCVs (total pool) per neuron, measured as the number of NPY-pHluorin puncta upon NH4Cl perfusion. (B) Fraction of NPY-pHluorin-labeled DCVs fusing during stimulation.

All Data are plotted as mean±s.e.m. (C-E) Control: N = 2, n = 10; Rab10 KD: N = 2, n = 13; SERCA2 OE: N = 2; n = 15. A one-way ANOVA tested the significance of adding experimental group as a predictor. *** = p<0.001, ** = p<0.01, ns = not significant.

(4) The claimed lack of effect of Rab10 depletion on SV exocytosis is solely based on very strong train stimulation with 200 Aps, a condition not very well suited to analyze defects in SV fusion. The conclusion that Rab10 loss does not impact SV fusion thus seems premature. The authors should conduct additional experiments under conditions of single or few Aps (e.g. 4 or 10 Aps) to really assess whether or not Rab10 depletion alters SV exocytosis at the level of pHluorin analysis in cultured neurons.

See reply to reviewer 2 above. Agreed to and made textual adjustments to solve this

(5) Related to the above: I am puzzled by the data shown in Figure 1H-J: From the pHluorin traces shown I would estimate a tau value of about 20-30 s (e.g. decay to 1/e = 37% of the peak value). The bar graph in Figure 1K claims 3-4 s, clearly clashing with the data shown. Were these experiments conducted at RT (where expected tau values are in the range of 30s) or at 37{degree sign}C (one would expect taus of around 10 s in this case for Syp-pH)? I ask the authors to carefully check and possibly re-analyze their datasets.

This is indeed a mistake. We thank the reviewer for flagging this miscalculation. Our original Matlab script used for calculating the tau value contained an error and the datasets were normalized twice by mistake. We now reanalyzed the data and the corresponding figures and texts have been updated. Our conclusion that Rab10 KD does not affect SV endocytosis remains unchanged since the difference in tau between the control (28.5 s) and Rab10 KD (32.8 s) suffered from the same systematic error and were/are not significantly different.

(6) How many times was the proteomics experiment shown in Figure 3 conducted? I noticed that the data in panel H missed statistical analysis and error bars. Given the typical variation in these experiments, I suggest to only include data for proteins identified in at least 3 out of 4 experimental replicates.

We agree that this information has not been clear. We have now explained replication in the Methods section (p. 42, l. 879-885). In brief, the proteomics experiment presented in Fig 3 was conducted with two independent cultures (‘biological replicates’), hence, formally only two independent observations. For each biological replicate, we performed four technical replicates. For our analysis, we only included peptides that were consistently detected across all samples (not only three as this reviewer suggests). Proteins in Panel H are ER-related proteins that are significantly different from control neurons with an adjusted FDR ≤ 0.01 and Log2 fold change ≥ 0.56. The primary purpose of our proteomics experiments was to generate hypotheses and guide subsequent experiments and the main findings were corroborated by other experiments presented in the manuscript.

Minor:

(7) Figure 2 - supplement 3 and Figure 4 - supplement 3 are only mentioned in the discussion. The authors should consider referring to these data in the results section.

This is a valid point. We have now added a new statement “Moreover, only 10% of DCVs co-transport with Rab10” in the Results (p. 6-7, l. 162-164).

(8) Where is the pHluorin data shown in Figure 1 bleach-corrected? If so, this should be stated somewhere in the Ms. Moreover, the timing of the NH4Cl pulse should be indicated in the scheme in panel I.

We thank the reviewer for pointing these omissions out. We have now included information about the timing of NH4Cl pulse in panel I. We did not do bleach-correction for the pHluorin data shown in Figure 1. It has been shown that pHluorin is very stable with a bleaching rate in the alkaline state of 0.06% per second and 0.0024% per second in the quenched state (Balaji and Ryan, 2007). Indeed, we did not observe obvious photobleaching in the first 30s during our imaging as indicated by the average trace of pHluorin intensity in panel I.

(9) Page 3/ lines 59-60: "...strongest inhibition of neuropeptide accumulation...". What is probably meant is "...strongest inhibition of neuropeptide release".

We agree this statement is unclear. Sasidharan et al used a coelomocyte uptake assay as an indirect readout for DCV release. The ‘strongest inhibition of neuropeptide accumulation’ in coelomocytes in Rab10 mutant indicates DCV fusion deficits. We have now replaced the text with “Rab10 deficiency produces the strongest inhibition of neuropeptide release in C. elegans” to make it more clear.

Reviewer #3 (Recommendations For The Authors):

I strongly recommend the publishing of this study as a VOR with minor comments directed to the authors.

(1) In Figure 4, the authors should include examples of tubular ER at the synapse, especially as this is an interesting point discussed in ln 226-229. Are there noticeable changes in the ER-mitochondria contacts at the synaptic boutons?

We agree that examples of tubular ER at the synapse would improve the manuscript. We have now replaced the Figure 4A with such examples. We found it challenging to quantify ER-mitochondria contacts based on the electron microscopy (EM) images we currently have. The ER-mitochondria contact sites are quite rare in the cross-sections of our samples, making it difficult to perform a reliable quantitative analysis.

(2) The limited impairment of calcium-ion homeostasis in Rab10 KD neurons is very interesting. Would the overexpression of Rab10T23N mimic the effect of a KD scenario? Is there a separation of function for Rab10 in calcium homeostasis vs. the regulation of protein synthesis?

This is an interesting possibility. We tested this and expressed Rab10T23N in a new series of experiments. These data are presented as a new Figure 5 in the revised manuscript (p. 29). We observed that Ca2+ refilling after caffeine treatment was delayed to a similar extent in Rab10T23N-expressing and Rab10 KD neurons. While impaired Ca2+ homeostasis may affect protein synthesis through ER stress or mTORC1 activation, our findings indicate otherwise in Rab10 KD neurons. First, ATF4 levels, a marker of ER stress, were unaffected in Rab10 KD neurons. This indicates that any ER stress present is minimal or insufficient to significantly impact protein synthesis through this pathway. Second, we did not observe significant changes in mTORC1 activation in Rab10 KD neurons as indicated by a normal pS6K1 phosphorylation (see above). Based on these observations, we conclude that Rab10's roles in calcium homeostasis and protein synthesis are most likely separate.

(3) The authors indicate that the internal release of calcium ions from the ER has no effect on DCV trafficking and fusion without showing the data. It is important to include this data as the major impact of the study is the dissecting of the calcium effects in mammalian neurons from the previous studies in invertebrates.

We agree this is an important aspect in our reasoning. We are submitting the related manuscript on internal calcium stores to BioRVix. The link will be added to the consolidated version of our manuscript

(4) The distinction between Rab3 and Rab10 co-trafficking on DCVs should be reported in the Results (currently, Figure 2 - supplement 3 is only mentioned in the Discussion) as it helps to understand the effects on DCV fusion.

We agree. We now added a new statement “Moreover, only 10% of DCVs co-transport with Rab10” in the Results (p. 6, l. 162-163).

Reference:

Balaji, J., Ryan, T.A., 2007. Single-vesicle imaging reveals that synaptic vesicle exocytosis and endocytosis are coupled by a single stochastic mode. Proceedings of the National Academy of Sciences 104, 20576–20581. https://doi.org/10.1073/pnas.0707574105

Brunner, J.W., Lammertse, H.C.A., Berkel, A.A. van, Koopmans, F., Li, K.W., Smit, A.B., Toonen, R.F., Verhage, M., Sluis, S. van der, 2022. Power and optimal study design in iPSC-based brain disease modelling. Molecular Psychiatry 28, 1545. https://doi.org/10.1038/s41380-022-01866-3

Emperador-Melero, J., Huson, V., van Weering, J., Bollmann, C., Fischer von Mollard, G., Toonen, R.F., Verhage, M., 2018. Vti1a/b regulate synaptic vesicle and dense core vesicle secretion via protein sorting at the Golgi. Nat Commun 9, 3421. https://doi.org/10.1038/s41467-018-05699-z

Granseth, B., Odermatt, B., Royle, S.J., Lagnado, L., 2006. Clathrin-Mediated Endocytosis Is the Dominant Mechanism of Vesicle Retrieval at Hippocampal Synapses. Neuron 51, 773–786. https://doi.org/10.1016/j.neuron.2006.08.029

Ivanova, D., Dobson, K.L., Gajbhiye, A., Davenport, E.C., Hacker, D., Ultanir, S.K., Trost, M., Cousin, M.A., 2021. Control of synaptic vesicle release probability via VAMP4 targeting to endolysosomes. Science Advances 7, eabf3873. https://doi.org/10.1126/sciadv.abf3873

Kwon, S.E., Chapman, E.R., 2011. Synaptophysin Regulates the Kinetics of Synaptic Vesicle Endocytosis in Central Neurons. Neuron 70, 847–854. https://doi.org/10.1016/j.neuron.2011.04.001

Reshetniak, S., Fernández-Busnadiego, R., Müller, M., Rizzoli, S.O., Tetzlaff, C., 2020. Quantitative Synaptic Biology: A Perspective on Techniques, Numbers and Expectations. International Journal of Molecular Sciences 21, 7298. https://doi.org/10.3390/ijms21197298

eLife Assessment

This important study develops and exploits novel ideas in dendritic integration and implements these ideas in a neural network. Historically, dendritic plateau potentials were thought to exist primarily for maintaining neurons in a depolarized state for 100s of milliseconds, but this study presents a new perspective that dendritic plateau potentials are equally effective in much shorter integration windows. The computational evidence supporting the article's claims is compelling.

Reviewer #2 (Public review):

Summary.

Some forms of Artificial Intelligence (AI), particularly those based on artificial neural networks (ANNs), draw inspiration from biological brains and neurons. Understanding the functional repertoire and underlying logic of real neurons could, therefore, help improve ANNs. While the cell bodies and axons of neurons produce rapid, high-amplitude action potentials (~100 mV over ~2 ms), dendrites-constituting about 80% of neuronal membrane area-generate smaller but longer-lasting electrical signals, known as glutamate-mediated dendritic plateau potentials (~50 mV over >100 ms). The authors have designed artificial neurons capable of producing these dendritic plateau potentials and, through simulations, demonstrate that such prolonged dendritic signals reduce the negative effects of temporal jitter in real or artificial neural networks. Specifically, they show that in ANNs with neurons capable of dendritic plateau potentials, reliable sparse spiking computation can occur without the need for precise input synchronization. This means that despite fluctuations in network activity (such as delays in the brain circuit responses, for example), neurons can still link related network events. Thus, dendritic plateau potentials enable neurons to retain information longer, connecting events that are not exactly simultaneous. Interestingly, one of the indirect conclusions of the current study is that neurons equipped with dendritic plateau potentials may reduce the total number of cells (nodes, units) required to perform robust computations.

Strengths.

Most studies in neuroscience are descriptive, focusing on observations and measurements. Fewer tackle the more challenging task of explaining the rationale behind specific natural designs. This study does just that, addressing the fundamental problem of asynchrony in neural communication caused by conduction delays and noise. Given that neurons with short membrane time constants can integrate only nearly simultaneous inputs, the authors propose a solution: dendritic plateau potentials. These potentials, generated through glutamate-mediated depolarization within dendritic branches, effectively broaden the temporal integration window, allowing neurons to handle temporal jitter, variability, stochasticity, and maintain reliable computation. Thus, dendritic plateau potentials appear to be an adaptive feature evolved to support rapid, reliable CNS computations.

Weaknesses.

The authors have appropriately revised unsupported statements from previous versions, but the manuscript could benefit from examples of testable hypotheses derived from their findings. For example, what specific experimental questions could be investigated to validate these computational predictions? Providing concrete examples of potential experimental tests would make the work more accessible and actionable for experimentalists, assuming such experiments are feasible.

Additionally, many readers may lack a background in computational modeling or Artificial Neural Networks. To enhance accessibility, key terms and concepts should be explained at a level suitable for first-year graduate students, ensuring clarity for a broader audience.

Author response:

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

Reviewer #1 (Public Review):

This is an elegant didactic exposition showing how dendritic plateau potentials can enable neurons to perform reliable 'binary' computations in the face of realistic spike time jitter in cortical networks. The authors make many good arguments, and the general concept underlying the paper is sound. A strength is their systematic progression from biophiysical to simplified models of single neurons, and their parallel investigation of spiking and binary neural networks, with training happening in the binary neural network.

Reviewer #2 (Public Review):

Summary:

Artificial intelligence (AI) could be useful in some applications and could help humankind. Some forms of AI work on the platform of artificial neural networks (ANN). ANNs are inspired by real brains and real neurons. Therefore understanding the repertoire and logic of real neurons could potentially improve AANs. Cell bodies of real neurons, and axons of real neurons, fire nerve impulses (nerve impulses are very brief ~2 ms, and very tall ~100 mV). Dendrites, which comprise ~80% of the total neuronal membrane (80% of the total neuronal apparatus) typically generate smaller (~50 mV amplitude) but much longer (~100 ms duration) electrical transients, called glutamate-mediated dendritic plateau potentials. The authors have built artificial neurons capable of generating such dendritic plateau potentials, and through computer simulations the authors concluded that long-lasting dendritic signals

(plateau potentials) reduce negative impact of temporal jitter occurring in real brain, or in

AANs. The authors showed that in AANs equipped with neurons whose dendrites are capable of generating local dendritic plateau potentials, the sparse, yet reliable spiking computations may not require precisely synchronized inputs. That means, the real world can impose notable fluctuations in the network activity and yet neurons could still recognize and pair the related network events. In the AANs equipped with dendritic plateaus, the computations are very robust even when inputs are only partially synchronized. In summary, dendritic plateau potentials endow neurons with ability to hold information longer and connect two events which did not happen at the same moment of time. Dendritic plateaus circumvent the negative impact, which the short membrane time constants arduously inflict on the action potential generation (in both real neurons and model neurons). Interestingly, one of the indirect conclusions of the current study is that neurons equipped with dendritic plateau potentials may reduce the total number of cells (nodes, units) required to perform robust computations.

Strengths:

The majority of published studies are descriptive in nature. Researchers report what they see or measure. A smaller number of studies embark on a more difficult task, which is to explain the logic and rationale of a particular natural design. The current study falls into that second category. The authors first recognize that conduction delays and noise make asynchrony unavoidable in communication between circuits in the real brain. This poses a fundamental problem for the integration of related inputs in real (noisy) world. Neurons with short membrane time constants can only integrate coincident inputs that arrive simultaneously within 2-3 ms of one another. Then the authors considered the role for dendritic plateau potentials. Glutamate-mediated depolarization events within individual dendritic branches, can remedy the situation by widening the integration time window of neurons. In summary, the authors recognized that one important feature of neurons, their dendrites, are built-in to solve the major problems of rapid signal processing: [1] temporal jitter, [2] variation, [3] stochasticity, and [4] reliability of computation. In one word, the dendritic plateau potentials have evolved in the central nervous systems to make rapid CNS computations robust.

Weaknesses:

The authors made some unsupported statements, which should either be deleted, or thoroughly defended in the manuscript. But first of all, the authors failed to bring this study to the readers who are not experts in computational modeling or Artificial Neural Networks. Critical terms (syntax) and ideas have not been explained. For example: [1] binary feature space? [2] 13 dimensions binary vectors? [3] the binary network could still cope with the loss of information due to the binarization of the continuous coordinates? [4] accurate summation?

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

However, I have a number of specific points, listed below, that should be addressed. Most of them are relatively minor, but the authors should especially address point 10, which is a major point, by redoing the simulations affected by the erroneous value of the time constant, and by remaking the relevant figures based on the new simulations.

Specific comments:

(1) 7f "This feature is conspicuous because it is an order of magnitude longer than unitary synaptic inputs and axonal spikes.": — It is an order of magnitude longer than AMPA receptor-mediated synaptic currents (EPSCs), but more similar in time course to synaptic potentials (EPSPs) whose decay is governed by the passive membrane time constant (about 10 to 20 ms in pyramidal neurons in vivo) and which determines the lifetime of the 'memory' of the neuron for synaptic inputs under conditions of subthreshold, non-spiking dendritic integration. The quoted sentence should be rewritten accordingly.

Following this suggestion, we have rewritten the sentence (l. 7) to: "This timescale is conspicuous, being many times longer than the fastest signalling processes in the nervous systems, including Excitatory Post-Synaptic Potentials (EPSPs) and axonal spikes."

(2) 16ff "This is especially relevant to integration of inputs during high conductance states that are prevalent in-vivo. In these states the effective time constant of the neuronal membrane is extremely short and varies substantially depending on synaptic drive [13, 34, 49].": — The time-averaged synaptic conductance driven by sensory input in vivo is much less high than implied by this statement (e.g. see Fig. 4 of Haider et al. 2013 https://www.nature.com/articles/nature11665 ), and reduces the passive membrane time constant only by a small percentage. The energy cost of a high prevalence of highconductance states and extremely short membrane time constants would also exceed the energy budget of the brain (ref. 4). I would therefore suggest dropping this sentence.

We have clarified this sentence thanks to the reviewer's suggestion. We meant that the instantaneous, rather than the time-averaged, conductance can be very big. To clarify this we have rewritten this section (l. 15): This is especially relevant to integration of inputs during high conductance states that are prevalent in vivo, where a typical neuron receives significant synaptic drive. In these states, the effective membrane time constant can be extremely short, and varies substantially depending on synaptic input.

(3) l. 17f "As a consequence, computations that rely on passive summation of multiple inputs place punishing constraints on spike timing precision.": — Again, the passive membrane time constant is on the order of 10 ms and I would tone down this statement accordingly, removing the word 'punishing' for example.

Following the suggestion, we have rewritten the sentence to (l. 18): "As a consequence, computations that rely on passive summation of multiple inputs would place strong constraints on spike timing precision."

(4) l. 18ff "Dendritic action potentials, by contrast, have a consistently long duration that is ensured by the kinetic properties of voltage gated ion channels and NMDA receptors [54, 47, 10, 3]. These properties are largely determined by the amino acid sequence of receptor and channel proteins that are specifically expressed in dendrites [45, 44, 40]. This suggests dendritic properties are specifically tuned to produce localised, suprathreshold events that outlive rapid membrane fluctuations.": — Yes, but see also Attwell & Gibb 2005 ( https://www.nature.com/articles/nrn1784 ), especially the last two of their key points. The slow NMDA receptor decay kinetics (and therefore their high affinity for binding glutamate) may also be the consequence of a design goal to set the temporal coherence window for NMDA receptor-mediated synaptic plasticity such as STDP to be on the order of tens of milliseconds, somewhat longer than the membrane time constant.

The reviewer is correct; other functions (e.g. synaptic plasticity) are also part of the dendrite's repertoire. To acknowledge this, we added a section (l. 34) where we mention that our idea does not conflict with, for example, synaptic plasticity.

(5) l. 32f "Numerous studies point out that nonlinear summation in dendrites can make neurons computationally equivalent to entire networks of simplified point models, or 'units' in a traditional neural network [9, 21, 38, 40, 45, 48, 50, 51].": — See also Beniaguev et al. 2021 ( https://www.cell.com/neuron/pdf/S0896-6273(21)00501-8.pdf ), which also speaks to the next sentence.

We thank the reviewer for the suggestion; the citation has been added.

(6) Fig. 2E and F: the top of panel F corresponds to the top of panel E, but the bottom ofpanel F does not correspond to the bottom of panel E - it corresponds to a dendritic neuron with passive dendrites, not a point neuron. Panel E should be changed to reflect this fact.

We have followed the suggestion to change the figure.

(7) l. 49f "Despite these dendritic spikes being initiated at different times, they still sum in the soma, leading to a sodium spike there (Figure 2E).": — You probably mean Fig. 2D, and instead of a sodium spike (which could be misunderstood as local and dendritic) you triggered a sodium action potential. Likewise, Fig. 2B (right) shows the timescale of sodium action potentials at the soma (cf. l. 46).

The error in the referencing to the figure has been corrected. The phrasing has also been changed to "a sodium action potential" (l. 56), following the reviewer's suggestion.

(8) Please check the scale bars in Fig. 2D. Do they also apply to panel F below? If yes thatshould be stated.

The scale bars are indeed the same; I have repeated them in the figure to avoid any confusion.

(9) l. 68 "This time constant is consistent with the high-conductance state of pyramidalneurons in the cortex [6]":

You do not need to invoke a high-conductance state to justify this time constant, which is indeed typical for the membrane time constant of pyramidal neurons in vivo.

On a related note, Fig. 3B and its legend seem to assume that tau = 1 ms, and calls that one EPSP duration in the legend. An EPSC may have a decay time constant of 1 ms, but an EPSP will have a decay time constant of about 10 ms, similar to the membrane time constant. Fig. 3B (and therefore also the rest of Figure 3) seems to have been constructed with a value of tau that is too small by a factor of 10, and this should be corrected by remaking the figure. If tau = 1 ms was used also in Figure 4 then this figure also needs to be remade.

Section 3.3 and Table 1 also use tau = 1 ms. This is unrealistic and needs to be changed an appropriate value of tau = 10 ms is given by the authors themselves in line 67. The incorrect value of tau in Table 1 causes other entries of the Table to be terribly wrong; a leak conductance of 1 µS would imply an input resistance of the neuron of 1 MOhm, but somatic input resistances of pyramidal neurons in vivo are on the order of 20 to 50 MOhm. The total capacitance of 1 nF is slightly too large, and should be adjusted to yield a membrane time constant of 10 ms given an appropriate leak conductance leading to an input resistance of about 20 to 50 MOhm. These are key numbers to get right for both Figures 3 and 4, especially if you want to be able to say "We have been careful to respect the essence of basic physiological facts while trying to build an abstraction of how elementary spiking computations might occur." (l. 215f).

We thank the reviewer for catching this. We had actually already used tau = 10 ms, but had not yet updated the paper. Moreover, the somatic input resistance was indeed off. To rectify this, we have used the values: $Cm = 0.5 nF$, $\taum = 10 ms$, $Rm = 20 M \Ohm$, $gl = 0.05 \mu S$. Figure 3 was remade using these values, and Table 1 updated accordingly.

(10) l. 158ff "The assumption that each neuron connects to one dendrite of an upstream neuron is actually grounded in physiology, although it may appear like a strong assumption at first glance: related inputs arrive at local clusters of spines synchronously [60].": — You probably mean "each neuron connects to one dendrite of a downstream neuron." And I would add "But see Beniaguev et al. 2022 https://www.biorxiv.org/content/10.1101/2022.01.28.478132v2.abstract " - your restrictive arrangement of inputs is probably not really needed, especially if postsynaptic neurons have more dendrites.

The suggested wording was correct, and has been now incorporated (l. 166). I have also added the suggested citation.

(11) I note that the plateaus in Fig. 4D are much shorter than those in Fig. 2D and F, but thisis a good thing: The experimental and simulation results in Fig. 2 are based on ref. 18, which used microiontophoresis of glutamate, leading to much slower glutamate concentration time courses at the dendritic NMDA receptors than synaptic release of glutamate would. The time courses of plateaus in Fig. 4 are much more in line with the NMDA plateau durations shown in ref. 21, especially their Figure 2B. These faster NMDA plateaus (or NMDA spikes as they are called in ref. 21) are based on synaptic release of glutamate in vivo, and on the faster NMDA receptor kinetics at physiological temperature compared to the old models with room temperature kinetics used in ref. 18.

Here are two additional references that the authors might find interesting:

Fisek et al. 2023 https://www.nature.com/articles/s41586-023-06007-6 Dudai et al. 2022 https://www.jneurosci.org/content/42/7/1184.full

We thank the reviewer for the suggested references. The first has been added to the references in the introduction, on l. 28. The second has been added on l. 78.

Reviewer #2 (Recommendations For The Authors):

(1) In Fig. 3A, we observed some animal pictures, which were never explained in the figurecaption, or text of the manuscript. These pictures were probably explained at the lab meeting, so it is unnecessary to waste effort on these pictures in the manuscript draft.

We agree with the reviewer; the figures have been removed.

(2) Figure 1 has not been referenced anywhere in the manuscript text!

Indeed, this had to be corrected, figure is now references on l. 9.

(3) Line 45. "[18] triggered two NMDA spikes by glutamate uncaging at the indicated (red,blue) sites". [18] triggered one NMDA spike while recording at three locations simultaneously (two locations in dendrite and one location in the soma).

The reviewer is correct here. The sentence has now been rephrased to "(ref.) triggered an NMDA spike by glutamate microiontophoresis while recording at the soma and the indicated (red, blue) sites in the dendrite." (l. 49)

(4) Fig. 2B. The two labels, "Dendrite 2" and "Dendrite 1" incorrectly suggest that two traceswere recorded in two dendrites. These two traces were recorded in the same dendrite.

We agree with the reviewer; labels have now been changed to "Dendrite site".

(5) Line 45. "[18] triggered two NMDA spikes by glutamate uncaging at the indicated (red,blue) sites". - - One NMDA spike by "glutamate microiontophoresis".

This is correct, the phrasing on (l. 50) has been changed accordingly.

(6) Line 47. "... simulated glutamate releases 50 ms apart in the three dendritic sites indicatedin Figure 2C, thereby triggering three NMDA spikes at those sites. Despite these dendritic spikes being initiated at different times, they still sum in the soma, leading to a sodium spike there (Figure 2E)". A similar experiment has been performed in real cortical neurons (KD Oikonomu et al., 2012, PMID: 22934081), and could potentially be cited here. Briefly, Oikonomou et al. generated two dendritic plateau potentials in two dendritic branches and monitored the summation of these dendritic plateau potentials in the cell body.

The reference has been added, on l. 54

(7) Line 63. "We compared the behaviour of our simplified model with that of the full, detailedbiophysical model". Which detailed biophysical model? Please cite here the detailed biophysical model that you used for comparisons with your simplified abstract model.

The reference to the paper has been added.

(8) Line 65. "Figure 2F shows that spikes arriving at different times are summed in anintegrate and hold-like manner". In Fig. 2F, I am unable to see that spikes arriving at different times are summed in an integrate and hold-like manner. Which feature of Fig. 2F refers to the "hold-like manner"? Please explain in the manuscript.

To clarify we have added "Figure 2F, top" in the text (l. 71).

(9) Figure 2 caption. "(F) The voltage traces of the abstract model, with and without plateaus.Because of the extended time duration of the plateau potentials, they sum accurately to produce a somatic spike". I am unable to understand what an "accurate summation" in Fig. 2 is. Could the authors provide an illustrative example of a situation in which the neuronal potentials DID NOT sum accurately?

To address this confusion, we have changed the wording to "...they are summed to reach threshold."

(10) Line 75. "This is an important issue we intend to return to in future work". The authorspersonal plans should not be in the text discussing scientific results.

We believe it is entirely reasonable to discuss scientific plans that are part of ongoing work, and this is quite common throughout the literature. Nonetheless, we have now reworded this to "This is an important issue for future work." (l. 81)

(11) In Fig. 4F, the full-line and the dashed-line have not been identified! The readers are leftto guess.

This has now been addressed both with text inserts in the figure, and specification in the figure caption.

(12) Line 247. "would amount to scaling up the number of cells in a network to performcomputations that could, in principle, be performed by more robust single units". Did the authors mean to say: "would amount to scaling up the number of cells in a network to perform computations that could, in principle, be performed by a fewer (but more robust) single units"?

We have replaced the sentence with the reviewer's suggestion (l. 259)

(13) In the abstract, the authors repeat sentences: "the timescale of dendritic potentialsallows reliable integration of asynchronous inputs" and "nonlinear dendritic plateau potentials allow reliable integration of asynchronous spikes". Besides this being a bad writing style, the authors cannot decide if inputs to the model neuron are asynchronous, or spiking of the model neuron is asynchronous. Are these asynchronous spikes occurring in the neuron experiencing dendritic plateau potentials, or these asynchronous spikes occur in the neuronal network? This confusion of terms and ideas must be removed from the abstract.

We have rewritten the second sentence, which now reads: "Using this model, we show that long-lived, nonlinear dendritic plateau potentials allow neurons to spike reliably when confronted with asynchronous input spikes."

(14) In the abstract, the authors claim: "Our results provide empirically testable hypothesesfor the role of dendritic action potentials in cortical function". With great anticipation, I read throughout the manuscript, but I was unable to find one single experimental design that could support the authors' bald statement. In the text of the manuscript, the authors must carefully reveal the precise experimental outline that would test their specific hypothesis, or delete the untrue statement.

We respectfully challenge the rather critical tone of the reviewer. The central hypothesis that plateaus enable robust summation, and that circuit level computations rely on this is an experimentally testable hypothesis. The precise experimental design of how to test such a hypothesis is always best left to an experimentalist to determine, as there are many possible means of doing this and each will depend on the preparation and methodology at hand. At the same time, we understand that there is an increasing culture of expecting explicit "testable hypotheses" spelled out to the reader. To satisfy this expectation while avoiding overly prescriptive ideas for how future work should proceed, we have now added more explicit descriptions of possible experimental tests in l. 231 and onwards.

(15) Fig. 2F was submitted for review without a time scale, while at the same time the authorsheavily discuss specific numerical values for time intervals. Namely, the authors instruct readers to pay attention to a 10 ms time constant and 2-3 ms input decay (Fig. 2F), but they do not show the time scale in Fig. 2F.

"We compared this to a situation where all inputs arrive at a soma with standard LIF dynamics and a 10 ms membrane time constant. This time constant is consistent with the high-conductance state of pyramidal neurons in the cortex [6]: Inputs decay after 2-3 ms, and fail to sum to spike threshold (Figure 2F, lower)".

The time (and voltage) bars have now been added to Fig. 2F.

(16) Line 75. "In the scope of what remains here we want to ask if integrate-and-hold isminimally feasible". This reviewer is unable to understand the meaning of the syntaxes "integrate-and-hold" and "minimally feasible" in the context of dendritic integration. This reviewer is worried that the majority of the journal readers would feel exactly the same. To alleviate this problem, the authors should explain both terms right here, in line 77.

Integrate-and-hold is defined on line 57 (to be exact we write: "We refer to this behavior as “Leaky Integrate-and-Hold” (LIH)." To be more clear we could reuse the acronym LIH here, to emphasise that we are referring to the same thing. By 'minimally feasible' we mean biologically plausible given assumptions that are not strong. Can use another term, e.g. "biologically plausible under lenient assumptions".

To address this point, we have rephrased the sentence as "In the scope of what remains here we want to ask if Leaky-Integrate-and-Hold (LIH) can easily and plausibly facilitate network computations with spikes." (l. 81), repeating the LIH definition.

(17) Line 91. "Spikes arriving even slightly out of sync with each other introduces noise in themembrane potential ..." Introduce.

The sentence has been fixed using the reviewer's correction.

(18) The caption of the Fig. 3B was submitted for review without any explanation of thenormalization procedure used. Also, in the caption of the same figure, one cannot find explanation of the light-gray area surrounding the black curves. Also, the readers are left to wonder how the results of a simulation could possibly be greater than 1 in some simulation trials.

We have added a description of the normalization and the shaded area to the caption of Fig. 3B.

(19) Line 117. "We assumed that inputs to a network arrive at the dendrites within some timewindow, and their combined depolarisations are either sufficient to either elicit a dendritic spike or not, as shown in Figure 3". We could potentially compact the current text by deleting one instance of "either".

We agree this is better writing; one of the occurrences of 'either' has been removed.

(20) Line 127. "where incoming connections can be represented with a 1 (a spike arrives)..."Did you mean "a presynaptic spike arrives"?

The sentence has been rewritten following the suggestion.

(21) Line 134. "with each unit only having ..." Dendrite can be a unit. Dendritic spine can be aunit. Did you mean "with each unit (i.e. neuron) having ..."

We have incorporated the suggestion.

(22) Fig. 4, Caption. "Each point is a 2D input vector x, the colors represent the differentclasses". An effort was made to introduce 3 different classes. But then, no mention of "classes" thereafter. The three input vectors, mentioned in Line 170, perhaps represent the remnants of the class concept mentioned in the previous paragraph.

We have now rewritten the sentence beginning with "These three input vectors ..." on l. 182 to emphasise that a correct answer means a correct classification.

(23) Line 152. "The 2D input points were first projected onto a binary feature space, to obtain13D binary vectors". Did you mean to say: "The 2D input points (three classes, Fig. A) were first projected onto a binary feature space, to obtain three binary vectors; each 13D binary vector responding to a specific class".

The sentence has been replaced with the reviewer's suggestion (l. 159).

(24) Line 163. "Because our focus is to account for how transient signals can be summed andthresholded robustly, we are assuming that inhibition is implicitly accounted for in the lumped abstraction". Could you please explain your two ideas: [1] "inhibition is implicitly accounted for" and [2] "lumped abstraction", because this reviewer did not get neither idea.

The reviewer is right that as it stood, the sentence was unclear. To clarify the point we have decided to expand upon that sentence and break it out as an individual paragraph (starting l. 171).

eLife Assessment

This study aggregates across five fMRI datasets and reports that a network of brain areas previously associated with response inhibition processes, including several in the basal ganglia, are more active on failed stop than successful stop trials. This study is valuable as a well-powered investigation of fMRI measures of stopping, and following revisions provides solid evidence for its conclusions.

Reviewer #2 (Public review):

This work aggregates data across 5 openly available stopping studies (3 at 7 tesla and 2 at 3 tesla) to evaluate activity patterns across the common contrasts of Failed Stop (FS) > Go, FS > stop success (SS), and SS > Go. Previous work has implicated a set of regions that tend to be positively active in one or more of these contrasts, including the bilateral inferior frontal gyrus, preSMA, and multiple basal ganglia structures. However, the authors argue that upon closer examination, many previous papers have not found subcortical structures to be more active on SS than FS trials, bringing into question whether they play an essential role in (successful) inhibition. In order to evaluate this with more data and power, the authors aggregate across five datasets and find many areas that are *more* active for FS than SS, including bilateral preSMA, GPE, thalamus, and VTA. They argue that this brings into question the role of these areas in inhibition, based upon the assumption that areas involved in inhibition should be more active on successful stop than failed stop trials, not the opposite as they observed.

Comments on revisions:

The authors have been responsive to the feedback of both reviewers and they have significantly improved the manuscript. I now judge the work as valuable and solid. The authors have achieved their aims to characterize subcortical BOLD activation in the stop-signal paradigm.

Author response:

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

Reviewer 1:

This study is one in a series of excellent papers by the Forstmann group focusing on the ability of fMRI to reliably detect activity in small subcortical nuclei - in this case, specifically those purportedly involved in the hyper- and indirect inhibitory basal ganglia pathways. I have been very fond of this work for a long time, beginning with the demonstration of De Hollander, Forstmann et al. (HBM 2017) of the fact that 3T fMRI imaging (as well as many 7T imaging sequences) do not afford sufficient signal to noise ratio to reliably image these small subcortical nuclei. This work has done a lot to reshape my view of seminal past studies of subcortical activity during inhibitory control, including some that have several thousand citations.

Comments on revised version:

This is my second review of this article, now entitled "Multi-study fMRI outlooks on subcortical BOLD responses in the stop-signal paradigm" by Isherwood and colleagues.

The authors have been very responsive to the initial round of reviews.

I still think it would be helpful to see a combined investigation of the available 7T data, just to really drive the point home that even with the best parameters and a multi-study sample size, fMRI cannot detect any increases in BOLD activity on successful stop compared to go trials. However, I agree with the authors that these "sub samples still lack the temporal resolution seemingly required for looking at the processes in the SST." As such, I don't have any more feedback.

We thank the reviewer for their positive feedback, and for their thorough and constructive comments on our initial submission. 

Reviewer 2:

This work aggregates data across 5 openly available stopping studies (3 at 7 tesla and 2 at 3 tesla) to evaluate activity patterns across the common contrasts of Failed Stop (FS) > Go, FS > stop success (SS), and SS > Go. Previous work has implicated a set of regions that tend to be positively active in one or more of these contrasts, including the bilateral inferior frontal gyrus, preSMA, and multiple basal ganglia structures. However, the authors argue that upon closer examination, many previous papers have not found subcortical structures to be more active on SS than FS trials, bringing into question whether they play an essential role in (successful) inhibition. In order to evaluate this with more data and power, the authors aggregate across five datasets and find many areas that are *more* active for FS than SS, including bilateral preSMA, GPE, thalamus, and VTA. They argue that this brings into question the role of these areas in inhibition, based upon the assumption that areas involved in inhibition should be more active on successful stop than failed stop trials, not the opposite as they observed.

Since the initial submission, the authors have improved their theoretical synthesis and changed their SSRT calculation method to the more appropriate integration method with replacement for go omissions. They have also done a better job of explaining how these fMRI results situate within the broader response inhibition literature including work using other neuroscience methods.

They have also included a new Bayes Factor analysis. In the process of evaluating this new analysis, I recognized the following comments that I believe justify additional analyses and discussion:

First, if I understand the author's pipeline, for the ROI analyses it is not appropriate to run FSL's FILM method on the data that were generated by repeating the same time series across all voxels of an ROI. FSL's FILM uses neighboring voxels in parts of the estimation to stabilize temporal correlation and variance estimates and was intended and evaluated for use on voxelwise data. Instead, I believe it would be more appropriate to average the level 1 contrast estimates over the voxels of each ROI to serve as the dependent variables in the ROI analysis.

We agree with the reviewer’s assertion that this approach could create estimation problems. However, in this instance, we turned off the spatial smoothing procedure that FSL’s FILM normally uses for estimating the amount of autocorrelation – thus, the autocorrelation was estimated based on each voxel’s timeseries individually. We also confirmed that all voxels within each ROI had identical statistics, which would not be the case if the autocorrelation estimates differed per voxel. We have added the following text to the Methods section under fMRI analysis: ROI-wise:

Note that the standard implementation of FSL FILM uses a spatial smoothing procedure prior to estimating temporal autocorrelations which is suitable for use only on voxelwise data (Woolrich et al., 2001). We therefore turned this spatial smoothing procedure off and instead estimated autocorrelation using each voxel’s individual timeseries.

Second, for the group-level ROI analyses there seems to be inconsistencies when comparing the z-statistics (Figure 3) to the Bayes Factors (Figure 4) in that very similar zstatistics have very different Bayes Factors within the same contrast across different brain areas, which seemed surprising (e.g., a z of 6.64 has a BF of .858 while another with a z of 6.76 has a BF of 3.18). The authors do briefly discuss some instances in the frequentist and Bayesian results differ, but they do not ever explain by similar z-stats yield very different bayes factors for a given contrast across different brain areas. I believe a discussion of this would be useful.

We thank the reviewer for their keen observation, and agree that this is indeed a strange inconsistency. Upon reviewing this issue, we came across an error in our analysis pipeline, which led to inconsistent scaling of the parameter estimates between datasets. We corrected this error, and included new tables (Figures 3, 4, and Supplementary Figure 5) which now show improved correspondence between the frequentist results from FSL and the Bayesian results.

We have updated the text of the Results section accordingly. In this revision, we have also updated all BFs to be expressed in log₁₀ form, to ensure consistency for the reader. Updates to the manuscript are given below.

Results: Behavioural Analyses:

Consistent with the assumptions of the standard horse-race model (Logan & Cowan, 1984), the median failed stop RT is significantly faster within all datasets than the median go RT (Aron_3T: p < .001, BF_log10 = 2.77; Poldrack_3T: p < .001, BF_log10 = 23.49; deHollander_7T: p < .001, B BF_log10 = 8.88; Isherwood_7T: p < .001, BF_log10 = 2.95; Miletic_7T: p = .0019, BF_log10 = 1.35). Mean SSRTs were calculated using the integration method and are all within normal range across the datasets.

Results: ROI-wise GLMS: 

To further statistically compare the functional results between datasets, we then fit a set of GLMs using the canonical HRF with a temporal derivative to the timeseries extracted from each ROI. Below we show the results of the group-level ROI analyses over all datasets using z-scores (Fig. 3) and log-transformed Bayes Factors (BF; Fig. 4). Note that these values were time-locked to the onset of the go signal. See Supplementary Figure 5 for analyses where the FS and SS trials were time-locked to the onset of the stop signal. To account for multiple comparisons, threshold values were set using the FDR method for the frequentist analyses. 

For the FS > GO contrast, the frequentist analysis found significant positive z-scores in all regions bar left and right M1, and the left GPi. The right M1 showed a significant negative z-score; left M1 and GPi showed no significant effect in this contrast. The BFs showed moderate or greater evidence for the alternative hypothesis in bilateral IFG, preSMA, caudate, STN, Tha, and VTA, and right GPe. Bilateral M1 and left GPi showed moderate evidence for the null. Evidence for other ROIs was anecdotal (see Fig 4). 

For the FS > SS contrast, we found significant positive z-scores in in all regions except the left GPi. The BFs showed moderate or greater evidence for right IFG, right GPi, and bilateral M1, preSMA, Tha, and VTA, and moderate evidence for the null in left GPi. Evidence for other ROIs was anecdotal (see Fig 4). 

For the SS > GO contrast we found a significant positive z-scores in bilateral IFG, right Tha, and right VTA, and significant negative z-scores in bilateral M1, left GPe, right GPi, and bilateral putamen. The BFs showed moderate or greater evidence for the alternative hypothesis in bilateral M1 and right IFG, and moderate or greater evidence for the null in left preSMA, bilateral caudate, bilateral GPe, left GPi, bilateral putamen, and bilateral SN. Evidence for other ROIs was anecdotal (see Fig 4). 

Although the frequentist and Bayesian analyses are mostly in line with one another, there were also some differences, particularly in the contrasts with FS. In the FS > GO contrast, the interpretation of the GPi, GPe, putamen, and SN differ. The frequentist models suggests significantly increased activation for these regions (except left GPi) in FS trials. In the Bayesian model, this evidence was found to be anecdotal in the SN and right GPi, and moderate in the right GPe, while finding anecdotal or moderate evidence for the null hypothesis in the left GPe, left GPi, and putamen. For the FS > SS contrast, the frequentist analysis showed significant activation in all regions except for the left GPi, whereas the Bayesian analysis found this evidence to be only anecdotal, or in favour of the null for a large number of regions (see Fig 4 for details).  

Since the Bayes Factor analysis appears to be based on repeated measures ANOVA and the z-statistics are from Flame1+2, the BayesFactor analysis model does not pair with the frequentist analysis model very cleanly. To facilitate comparison, I would recommend that the same repeated measures ANOVA model should be used in both cases. My reading of the literature is that there is no need to be concerned about any benefits of using Flame being lost, since heteroscedasticity does not impact type I errors and will only potentially impact power.

We agree with the reviewer that there are differences between the two analyses. The advantage of the z-statistics from FSL’s flame 1+2 is that these are based on a multi-level model in which measurement error in the first level (i.e., subject level) is taken into account in the group-level analysis. This is an advantage especially in the current paper since the datasets differ strongly in the degree of measurement error, both due to the differences in field strength and in the number of trials (and volumes). Although multilevel Bayesian approaches exist, none (except by use of custom code) allow for convolution with the HRF of a design matrix like typical MRI analyses. Thus, we extracted the participant-level parameter estimates (converted to percent signal change), and only estimated the dataset and group level parameters with the BayesFactor package. As such, this approach effectively ignores measurement error. However, despite these differences in the analyses, the general conclusions from the Bayesian and frequentist analyses are very aligned after we corrected for the error described above. The Bayesian results are more conservative, which can be explained by the unfiltered participantlevel measurement error increasing the uncertainty of the group-level parameter estimates. At worst, the BFs represent the lower bounds of the true effect, and are thus safe to interpret. 

We have also included an additional figure (Supplementary Figure 7) that shows the correspondence between the BFs and the z scores. 

Though frequentist statistics suggest that many basal ganglia structures are significantly more active in the FS > SS contrast (see 2nd row of Figure 3), the Bayesian analyses are much more equivocal, with no basal ganglia areas showing Log10BF > 1 (which would be indicative of strong evidence). The authors suggest that "the frequentist and Bayesian analyses are monst in line with one another", but in my view, this frequentist vs. Bayesian analysis for the FS > SS contrast seems to suggest substantially different conclusions. More specifically, the frequentist analyses suggest greater activity in FS than SS in most basal ganglia ROIs (all but 2), but the Bayesian analysis did not find *any* basal ganglia ROIs with strong evidence for the alternative hypothesis (or a difference), and several with more evidence for the null than the alternative hypothesis. This difference between the frequentist and Bayesian analyses seems to warrant discussion, but unless I overlooked it, the Bayesian analyses are not mentioned in the Discussion at all. In my view, the frequentist analyses are treated as the results, and the Bayesian analyses were largely ignored.

The original manuscript only used frequentist statistics to assess the results, and then added Bayesian analyses later in response to a reviewer comment. We agree that the revised discussion did not consider the Bayesian results in enough detail, and have updated the manuscript throughout to more thoroughly incorporate the Bayesian analyses and improve overall readability. 

In the Methods section, we have updated the fMRI analysis – general linear models (GLMs): ROIwise GLMs section to more thoroughly incorporate the Bayesian analyses as follows: 

We compared the full model (H1) comprising trial type, dataset and subject as predictors to the null model (H0) comprising only the dataset and subject as predictor. Datasets and subjects were modeled as random factors in both cases. Since effect sizes in fMRI analyses are typically small, we set the scaling parameter on the effect size prior for fixed effects to 0.25, instead of the default of 0.5, which assumes medium effect sizes (note that the same qualitative conclusions would be reached with the default prior setting; Rouder et al., 2009). We divided the resultant BFs from the full model by the null model to provide evidence for or against a difference in beta weights for each trial type. To interpret the BFs, we used a modified version of Jeffreys’ scale (Andraszewicz et al., 2014; Jeffreys, 1939). To facilitate interpretation of the BFs, we converted them to the logarithmic scale. The approximate conversion between the interpretation of logarithmic BFs and standard interpretation on the adjusted Jeffreys’ scale can be found in Table 3.   

The Bayesian results are also more incorporated into the Discussion as follows: 

Evidence for the role of the basal ganglia in response inhibition comes from a multitude of studies citing significant activation of either the SN, STN or GPe during successful inhibition trials (Aron, 2007; Aron & Poldrack, 2006; Mallet et al., 2016; Nambu et al., 2002; Zhang & Iwaki, 2019). Here, we re-examined activation patterns in the subcortex across five different datasets, identifying differences in regional activation using both frequentist and Bayesian approaches. Broadly, the frequentist approach found significant differences between most ROIs in FS>GO and FS>SS contrasts, and limited differences in the SS>GO contrast. The Bayesian results were more conservative; while many of the ROIs showed moderate or strong evidence, some with small but significant z scores were considered only anecdotal by the Bayesian analysis. In our discussion, where the findings between analytical approaches differ, we focus mainly on the more conservative Bayesian analysis.

Here, our multi-study results found limited evidence that the canonical inhibition pathways (the indirect and hyperdirect pathways) are recruited during successful response inhibition in the SST. We expected to find increased activation in the nodes of the indirect pathway (e.g., the preSMA, GPe, STN, SN, GPi, and thalamus) during successful stop compared to go or failed stop trials. We found strong evidence for activation pattern differences in the preSMA, thalamus, and right GPi between the two stop types (failed and successful), and limited evidence, or evidence in favour of the null hypothesis, in the other regions, such as the GPe, STN, and SN. However, we did find recruitment of subcortical nodes (VTA, thalamus, STN, and caudate), as well as preSMA and IFG activation during failed stop trials. We suggest that these results indicate that failing to inhibit one’s action is a larger driver of the utilisation of these nodes than action cancellation itself. 

These results are in contention to many previous fMRI studies of the stop signal task as well as research using other measurement techniques such as local field potential recordings, direct subcortical stimulation, and animal studies, where activation of particularly the STN has consistently been observed (Alegre et al., 2013b; Aron & Poldrack, 2006; Benis et al., 2014; Fischer et al., 2017; Mancini et al., 2019; Wessel et al., 2016).

eLife Assessment

In this fundamental study, the authors describe ELF3 as a candidate driver of luminal progenitor transformation, such that its up-regulation during replicative stress conditions and in BRCA1 deficient cells may permit cell proliferation by suppressing genome instability. While the work is certainly of interest, the supporting data remain incomplete as luminal progenitor cells could not be isolated, which would be needed in order to definitively determine whether ELF3 is a driver of transformation in these cells. Overall this paper may offer insight into mechanisms by which BRCA1 deficiency fuels breast tumorigenesis.

Reviewer #1 (Public review):

The authors set out to define the molecular basis for LP as the origin of BRCA1-deficient breast cancers. They showed that LPs have the highest level of replicative stress, and hypothesise that this may account for their tendency to transform. They went on to identify ELF3 as a candidate driver of LP transformation and showed that ELF3 expression is up-regulated in response to replicative stress as well as BRCA1 deficiency. They went on to show that ELF3 inactivation led to a higher level of DNA damage, which may result from compromised replicative stress responses.

While the manuscript supports the interesting idea wherein ELF3 may fuel LP cell transformation, it remains obscure how ELF3 promotes cell tolerance to DNA damage. Interestingly the authors proposed that ELF3 suppresses excessive genomic instability, but in my opinion, I do not see any evidence that supports this claim. In fact, one might think that genomic instability is key to cell transformation.

Comments on revisions:

The authors have addressed most of my concerns.

This being said, the one major criticism raised by both Reviewers is the lack of evidence to support ELF3 as a driver of transformation of and in LP cells. The authors appear to have invested much resource and time but were not successful in isolating LP cells for experimentations. I would therefore suggest that the authors tone down their claims throughout the manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The authors set out to define the molecular basis for LP as the origin of BRCA1deficient breast cancers. They showed that LPs have the highest level of replicative stress, and hypothesise that this may account for their tendency to transform. They went on to identify ELF3 as a candidate driver of LP transformation and showed that ELF3 expression is up-regulated in response to replicative stress as well as BRCA1 deficiency. They went on to show that ELF3 inactivation led to a higher level of DNA damage, which may result from compromised replicative stress responses.

While the manuscript supports the interesting idea wherein ELF3 may fuel LP cell transformation, it remains obscure how ELF3 promotes cell tolerance to DNA damage. Interestingly the authors proposed that ELF3 suppresses excessive genomic instability, but in my opinion, I do not see any evidence that supports this claim. In fact, one might think that genomic instability is key to cell transformation.

We greatly appreciate your thorough review and insightful comments on our manuscript. We have taken your feedback seriously and have made several key revisions to address your concerns.

To your primary point about how ELF3 helps cells tolerate DNA damage, we have expanded our discussion to clarify the role of ELF3 in the context of BRCA1 deficiency and high replicative stress. We clarified that while ELF3 may not directly suppress excessive genomic instability, it plays a role in maintaining a balance that prevents catastrophic damage in BRCA1-deficient cells. Both BRCA1 deficiency and increased replication stress induce up-regulation of ELF3, which acts as a transcription factor, and it’s up-regulation leads to up-regulation of the expression of a variety of DNA replication-associated proteins that help to maintain homeostasis in the DNA replication process (Figure 5 E and F). Defects in ELF3 also do lead to disruption of the DNA replication process (Figure 5 G-I). While ELF3 cannot completely eliminate genomic instability, ELF3 essentially maintains genomic instability within a dangerous yet non-lethal range: higher than in normal cells, but not so high as to cause cell death.

This precarious balance can facilitate the transformation of LPs into a malignant state, as you pointed out.

In the revised manuscript, we emphasized that in cells with inherently low replicative stress, such as other non-LP mammary cells, the ELF3-associated mechanism might help cells endure the high replicative stress caused by BRCA1 deficiency without leading to cancerous changes. However, in LP cells, which naturally experience higher replicative stress, this ELF3-related mechanism may make them more susceptible to transformation into cancer cells. This supports our hypothesis that the combination of high replicative stress and BRCA1 deficiency specifically predisposes LP cells to tumorigenesis.

We have modified the working model to make it clearer.

Reviewer #2 (Public Review):

Summary:

The manuscript focuses on a persistent question of why germline mutations in BRCA1 which impair homology-directed repair of DNA double-strand breaks predispose to primarily breast and ovarian cancers but not other tissues. The authors propose that replication stress is elevated in the luminal progenitor (LP) cells and apply the gene signature from Dreyer et al as a measure of replication stress in populations of cells selected by FACS previously (published by Lim et al.) and suggest an enrichment of replication stress among the LP cells. This is followed by single-cell RNA seq data from a small number of breast tissues from a small number of BRCA1 mutation carriers but the pathogenic variants are not listed. The authors perform an elegant analysis of the effects of BRCA1 knockdown in MCF10A cells, but these cells are not considered a model of LP cells.

Overall, the manuscript suffers from significant gaps and leaps in logic among the datasets used. The connection to luminal progenitor cells is not adequately established because the models used are not representative of this population of cells. Therefore, the central hypothesis is not sufficiently justified.

Strengths:

The inducible knockdown of BRCA1 provided compelling data pointing to an upregulation of ELF3 in this setting as well as a small number of other genes. It would be useful to discuss the other genes for completeness and explain the logic for focusing on ELF3. Nonetheless, the connection with ELF 3 is reasonable. The authors provide significant data showing a role for ELF3 in breast epithelial cells and its role in cell survival.

Weaknesses:

The initial observations in primary breast cells have small sample sizes. The mutations in BRCA1 seem to be presumed to be all the same, but we know that pathogenic variants differ among individuals and range from missense mutations affecting interactions with one critical partner to large-scale truncations of the protein.

The figure legends are missing critical details that make it difficult for the reader to evaluate the data. The data support the notion that ELF3 may participate in relieving replication stress, but does not appear to be limited to LP cells as proposed in the hypothesis.

We would like to sincerely thank you for your thorough review and constructive feedback on our manuscript. Your insightful comments and suggestions have been invaluable in guiding our revisions.

(1) Acknowledgment of Data Set Limitations and Additional Analyses:    We fully acknowledge the importance of the concerns raised regarding the datasets used in our study. We have supplemented our manuscript with the missing information you pointed out and conducted additional analyses as suggested. These efforts have

(2) Challenges in LP Cell Experiments:

One of the most critical issues you raised was the lack of validation in LP cells, particularly concerning the role of ELF3 in these cells. We are acutely aware of the significance of this point. Following your review, we made extensive efforts to isolate and culture LP cells from both BRCA1-proficient and BRCA1-deficient patient samples. We tried various methods and invested substantial resources, including time, manpower, and materials, to establish a reliable protocol for isolating and cultivating LP cells in vitro. Unfortunately, despite our best efforts, we were unable to obtain a sufficient number of high-quality cells to generate solid and reproducible results.

The challenges we faced included the limited availability of patient tissues and the technical difficulties in consistently obtaining viable LP cells. Given the already extended timeline for the revision of this manuscript, we regretfully decided to forgo further attempts to perform these critical experiments with LP cells. In the revised manuscript, we have explicitly addressed the limitations of our cell models and provided a detailed discussion of the challenges faced in isolating LP cells. Despite these limitations, we believe that the consistency between our results and LP cell sequencing data provides valuable insights and a solid foundation for future studies.

(3) Data Presentation Improvements:

In response to your feedback, we have also made significant improvements to the data presentation in our manuscript. We updated and optimized figure legends and narrative sections to ensure that the data are clearly and accurately conveyed. These changes aim to enhance the readability and comprehensibility of our findings.

We greatly appreciate your valuable feedback, which has significantly contributed to the improvement of our manuscript. Your suggestions have helped us refine our arguments and present a more robust and nuanced interpretation of our data. 

Thank you once again for your critical and constructive review. We look forward to your feedback on our revised manuscript.

Recommendations for the authors:  

Reviewer #1 (Recommendations For The Authors):  

As such, in addition to consolidating the role of ELF3 in promoting cell tolerance to replicative stress (or in suppressing genomic instability), I have a few comments the authors should consider to improve their manuscript.  

(1) I am not sure how cells have gained a growth advantage if they were arrested (Line 105-106). Perhaps the authors can elaborate.

Thanks for pointing this out and we are sorry for the misleading statement. We have revised the manuscript and would like to clarify that “survival advantage” may be more accurate than “growth advantage”, and since long-term DOX treatment led to decreased cell survival indicated by decreased number of colonies in Supplemental Fig. S1D, thus many cells died during DOX treatment. Therefore, the cells able to survive throughout DOX treatment and being collected for sequencing may have gained survival advantage compared to their counterparts who fail to survive.  

(2) Figure 3D - From Western blotting of ELF3, forced expression of E2F6 does not appear to "block" HU-induced ELF3 up-regulation, but merely down-regulate basal level of ELF3, with the effect of HU still notable.

Thanks for the comment and we agree that E2F6 down-regulate ELF3 baseline expression levels and did not fully block ELF3 up-regulation. After calculating the foldchange after E2F6 overexpression, we did confirm that E2F6 overexpression still partially block HU-induced ELF3 up-regulation, with foldchange from 3.32 to 2.40, supporting our conclusion that HU-induced ELF3 upregulation is regulated by ATRChk1-E2F axis. It does, however, cannot be excluded that E2F6 also regulates ELF3 expression in other replication stress-independent ways, and we have revised the manuscript accordingly. 

(3) Figure 3J & K - In my opinion, if BRCA1 knockdown were more efficient it remains formally possible that co-depletion of BRCA1 and GATA3 may exhibit additive effects in up-regulating ELF3 mRNA level.

Thank you for the comment. Actually, the BRCA1 knockdown efficiency in Figure 3J was shown in Supplemental Fig. S3B, and notably both BRCA1 and GATA3 knockdown were numerically more efficient in the double-knockdown group than in the single-knockdown group, individually. Thus, the higher ELF3 up-regulation in double-knockdown group in Figure 3J could be cause by the superior knockdown efficiency of both BRCA1 and GATA3. Nonetheless, we agree that it might be possible that BRCA1 and GATA3 still have separate functions in this experimental setting and marginal additive effect may exist, and the manuscript was revised accordingly.

(4) Figure 4 - Perhaps the authors can change its title to better summarise the findings. Cell sensitivity assays and xenograph experimentations may not necessarily relate to genomic instability.

Thank you for the great suggestion. To summarize the results more accurately, we have revised the title as “ELF3 can help cells tolerate replication stress and sustain cell survival”.

(5) Figure 5B&C - It would be important to document the time-dependent resolution of HU-induced DNA lesions by including additional time-points before, during, and after HU treatment.

We appreciate the suggestion to include additional time points to document the timedependent resolution of HU-induced DNA lesions. In our experiments, we observed that ELF3 knockdown leads to genomic instability both in the presence and absence of HU treatment. Specifically, Figure 5A and Figure S5 demonstrate that ELF3 knockdown increases genomic instability without HU treatment, indicating its role in maintaining genomic stability under normal conditions. On the other hand, Figure 5B, 5C, and 5D show that ELF3 knockdown under HU-induced replication stress further exacerbates genomic instability. This observation aligns with our finding that ELF3 expression increases in response to replication stress, suggesting its critical role in maintaining replication homeostasis under such conditions. 

6) Figure 5F&I - Which ELF3 siRNA was used in these experimentations? Since the authors did not exclude off-target effects perhaps it may be worthwhile to include both ELF3 siRNAs for Panel F.

Thanks for your advice. The qPCR (Figure 5F) and DNA fiber assay (Figure 5I) were using siELF3-4 siRNA. And we repeat the qPCR experiments for Panel F using siELF3-5 siRNA (Supplement Fig. S5B).

We sincerely thank you for your thoughtful feedback and constructive suggestions. Addressing these points has strengthened our manuscript, and we are grateful for the opportunity to refine and clarify our work. We appreciate your critical evaluation and look forward to further constructive dialogue.

Reviewer #2 (Recommendations For The Authors):  

(1) The data driving the hypothesis uses gene expression signatures as an indirect measure of replication stress. This is a critical concern.

a. At this time, numerous gene expression signatures have been reported to be biomarkers of replication stress. Therefore, it would be valuable to apply additional gene expression signatures to examine the performance and the overlap in the results.

The recent work by Takahashi et al., 2022 (https://pubmed.ncbi.nlm.nih.gov/36381660/) provides a signature that was derived independently and offers one that can be used to assess the performance of the signatures and stability of the conclusions.

Thank you for the valuable suggestion. We have done the replication stress evaluation of mammary cell subgroups using the Repstress score developed in the work you mentioned. The result showed that LP cells have trends of higher replication stress compared with other subgroups, though no statistical significance. This result, consistent with our previous analysis, indicated that LP cells have higher trends of replication stress levels. And we have added this data as the last line of Figure 1A in revised vision.

Author response image 1.

Replication stress pathway scores of different human normal mammary cell  populations. The gene expression data were from Lim et al. (3).

b. A direct measure of replication stress in LP cells would be important to confirm the gene expression signature. Therefore, performing immunostaining for markers of replication stress (eg gamma-H2AX foci, DNA fiber assays) would provide more direct data to support the assertions.

Thank you for this suggestion and we totally agree that experiments revealing replication stress levels by investigating common markers, e.g., gamma-H2AX foci, DNA fiber assays, will provide vital evidence for our hypothesis. However, since our last response, we have been diligently trying to obtain LP cells for these experiments but encountered technical challenges while attempting to isolate and culture LP cells in vitro. 

In the discussion part, we have revised the manuscript to emphasize that the data obtained from MCF10A should be interpreted with caution and there are certain gaps between the cell models and LP cells.

(2) The depth of single-cell sequencing can often be limiting. Therefore, a supplementary table listing the genes used for the replication stress signature and the frequency that they are observed in the single-cell sequencing data. This is needed to ensure that the replication stress score does not reflect a small subset of the replication stress signature genes.

Thanks very much for this evaluable suggestion. We have provided an expression matrix of genes for the replication stress signature in the revised version (Supplementary Table S1), And we also calculated the average expression level of each gene in the cells. As shown in Author response image 2, these genes expressed relatively low at the single-cell level (with counts≤10), The expression differences among genes are relatively small. Thus, we excluded the possibility that several high-expressed genes significantly affect the replicative stress score.

Author response image 2.

Average counts of Top 50 genes for the replication stress signature

(3) As only 4 BRCA mutation carriers are analyzed, it is critical that the mutations be reported for these individuals because pathogenic variants differ in their effects and interactions with the DNA repair machinery in cells.

Thanks for the suggestion and the information of 4 BRCA1 mutant carriers were added in Supplemental Table S2.

(4) The figures throughout lack critical details making it difficult to evaluate. Figure 1A states that these are "replication stress pathway scores..." but there is no evaluation of levels of statistical differences. The heat map has what appears to be a log unit score between +2 and -2 but it is unclear whether it is log2 or log10 or some other unit. In 1B, the replication stress scores are visualized as relative values between 0 and 0.1, but there is no indication of what this means or whether there is a statistically significant difference in the levels among the populations. As tumors are composed of multiple cell types, it should be stated how the "tumor cells" are uniquely identified in the figure legend. The lack of critical information is common across many of the figures making review frustratingly difficult.

Thanks for the suggestion. We have added the statistical analysis and scale in Figure 1A legend. For Figure 1B, replication stress was calculated by sum of replication stress gene expression and presented as ln value. We have provided a quantitative figure and statistical tests (by Mann-Whitney) of replication stress scores for various cell types (Supplementary Figure 1A). 

In addition, we added details of identification of tumor cells in the method section in the revised manuscript. Briefly, the adjacent normal breast sample served as a control to filter various types of normal cells from tumor samples. the normal cells from the tumor sample were merged with the same types of normal cells from adjacent normal breast samples, leaving one cell cluster only generalized by tumor sample. These tumor specific clusters were considered as malignant cell populations. We further found that the malignant cell population showed higher UMI counts than the normal cell populations, consistent with active metabolism in the malignant cells. More importantly, ER, PR, and HER2 expression of the malignant cells in each case were exactly matched with the clinical records. Finally, we utilized InferCNV to validate malignant cells subset as higher copy number alterations (CNAs) detected in the malignant cells compared with normal cells.

(5) The hypothesis states that the LP cells are uniquely sensitive to deficiency in BRCA1 compared to other cells. However, the authors use knockdown of BRCA1 in MCF10A cells which are generally considered to be basal cells and not LP cells.

Thanks for the comment. We totally agree that MCF10A cannot reflect the LP features and was mainly used as a normal mammary cell line model. We have tried to obtain human LP to perform some experiments but have all failed due to the cell vulnerability and difficult to be passed on in vitro. The gap between MCF10A and LP cells was stressed in the discussion part.

(6) Figure 2, the number of samples being compared is not listed for most of the panels. It appears that ELF3 is enriched in subsets of breast cancers, but much of the data is not focused on BRCA1-deficient tumors. Therefore, the data appears to show that ELF3 expression is more of a generalized feature of TNBCs (which has been reported previously) and dilutes the support for the hypothesis. Therefore, panels C-G raise concerns regarding the overall hypothesis that LP cells are the cell type that is affected.

Thanks for the suggestion. We have added the number of samples in Figure 2 legends.

Our analysis focus on basal subtype because of the well-known relationship between BRCA1 deficiency and this subtype. Our results demonstrate the association between ELF3 expression and basal, TNBC, as well as HER2+ subtype, consistent with previous reports. Since TNBC also has high replication stress levels (NPJ Breast Cancer. 2020 Sep 7;6:40.), ELF3 upregulation in this subtype may not be solely due to BRCA1 deficiency, and we totally agree that this analysis may dilute the relationship between ELF3 and BRCA1. We have revised the discussion part to be more precise on this. 

(7) Figure 3 provides experimental support for the hypothesis. While panel A is of interest, the legend lacks any description beyond "normal mammary tissue" and that there are non-carriers and carriers of BRCA1 mutations. Is this from bulk RNAseq data or single-cell RNAseq data? How many carriers and how many noncarriers? Panel E is ENCODE data from MCF7 cells that are ER+ luminal subtype so it is unclear if this is relevant to the LP cells that are the focus of the hypothesis.

Thanks for the comments. Figure 3 panel A was from single-cell RNAseq data, including 3 BRCA1 WT patients and 4 BRCA1 mutant patients. All cells (normal cells and tumor cells) are involving, and ELF3 expression was normalized by reads in each cell. We have added this information in the figure legend. 

It has been difficult to obtain ENCODE data in LP cells. The effect of E2F1 on regulation of ELF3 was validated in MCF10A cells by experiment and consistent with MCF7 ENCODE data, thus we suggest this effect can be conserve in mammary cells, but further confirmation in LP cells is needed. We have revised the manuscript to note that.

(8) In Figure 4, the authors use BRCA1-deficient breast cancer cells to show the reliance on ELF3 and suggest that this is specific to this genetic lesion and not other subtypes. However, there is no data to show that this is not observed using ER+ cells or TNBC that are not BRCA1-deficient cell lines or models.

Thanks for pointing this out. As ELF3 knockdown in MCF10A resulted in increased genomic instability (Supplement Fig S5) and less capability to resolve replication stress (Figure 5B), we believe that ELF3 can help deal with replication stress not specifically in BRCA1-mutant cells, but also normal mammary cells, and also multiple cell lines with distinct backgrounds as suggested in Figure 4G, 4H and Supplement Fig S4G. The special link between ELF3 and BRCA1 is reflected by ELF3 significant upregulation upon BRCA1 deficiency, but not ELF3 downstream functions. 

(9) Figure 5 provides the first direct evaluation of biomarkers of replication stress (gamma H2AX, 53BP1). DNA fiber assays provide the most direct evaluation of replication fork kinetics, and therefore, replication stress. The knockdown of BRCA1 and ELF3 appear to phenocopy one another in the HCC1937, but there is no other cell type to show whether this is specific for BRCA1-deficient cells. For example, the MCF7 cells show E2F1 binding to ELF3 (Figure 3E) and may show replication stress upon knockdown of ELF3. Without testing this, the authors cannot suggest that the effect is linked to BRCA1 status. The authors do not identify the BRCA1 mutation in these cells and whether there is homozygous loss. Similarly, the mutational status in the SUM149PT cells should also be stated. These need to be added to aid interpretation of the results.

Thank you for the constructive advice. We have added information regarding BRCA1 status of HCC1937 and SUM149PT. As discussed before, the results from Figure 4G and 4H suggest that ELF3 expression is associated with sensitivity to replicationstress-inducing-drugs across many cell lines. Thus ELF3 can maintain the stability of DNA replication is not specific to BRCA1-deficient cells. The reliance of ELF3 in BRCA1-deficiency we proposed is mainly focus on the fact that ELF3 is upregulated in BRCA1 deficient conditions, plus ELF3 may help cells tolerate replication stress during the transformation, therefore the resulted tumor cells-that is BRCA1-deficient breast cancer cells-may be more sensitive when losing ELF3 expression.

(10) While the data in Figure 6 are valuable extensions of the gene signature derived from the MCF10A cells with BRCA1 knockdown, only 2 BRCA1 carriers are reported. As carriers bear heterozygous mutations in BRCA1, haplo-insufficiency would be necessary to generate the signature. The authors do note the publication by Panthania et al, but there are relatively few examples of haploinsufficiency. It should be noted that Sedic et al., 2015 also suggested haploinsufficiency in breast epithelial cell cultures from BRCA1 heterozygotes which appears to cause premature senescence, possibly via replication stress. However, this was observed in the basal epithelial cells. Therefore, this appears to be a feature of the breast epithelium more generally and is not enriched or limited to the LP cells.

Thanks very much for your valuable suggestion. We have revised the discussion part to involve this important work and we fully agree that BRCA1 deficiency can cause replication stress not limited to LP cells. While in fact, the point we would like to address in Figure 6 is that BRCA1 deficiency modules the transcription profile towards LP-like cells, but not other-subtype-like cells, in normal mammary cells. We observed surprisingly similar profile between BRCA1-deficient cells and LP cells, suggesting there might be an inherent function of BRCA1 to mediate LP genes transcription. Furthermore, the data indicate that ELF3 has a tighter association with LP genes than other recognized LP-specific transcription factors like ELF5 and EHF, which are of the same family of ELF3. This result is intriguing since ELF3 can be upregulated by BRCA1 deficiency and replication stress. We assume that ELF3 could be a transcription node downstream of BRCA1 deficiency and modulate LP genes expression, and this process might be limited to LP cells since ELF3 has the highest expression levels in LP. Nonetheless, this hypothesis is also needed to be validated in LP cells by experiments. 

We would like to express our deepest gratitude to the reviewers for their thorough and constructive feedback. Their insightful comments have been invaluable in guiding the revisions of our manuscript, helping us to clarify our hypotheses and strengthen the presentation of our findings. While we encountered some challenges, particularly with the isolation and culturing of LP cells, we made significant efforts to address the reviewers' concerns to the best of our ability. We have updated our manuscript accordingly, ensuring that all issues raised have been addressed comprehensively. We believe that these revisions have substantially improved the quality and clarity of our work, and we are excited to share our findings with the scientific community. Thank you once again for the opportunity to revise our manuscript, and we look forward to your feedback on the updated version.

eLife Assessment

This important work advances our understanding of factors influencing efficacy assessments and biomarker viability for complement-directed gene therapy against age-related macular degeneration. The data presented is convincing and offers insights and teachings for the design of gene therapy and complement-targeted therapeutics in the eye and more broadly for future ocular biomarker studies.

Reviewer #1 (Public review):

Summary:

This study analyzed biomarker data from 28 subjects with geographic atrophy (GA) in a Phase I/II clinical trial of PPY988, a subretinal AAV2 complement factor I (CFI) gene therapy, to evaluate pharmacokinetics and pharmacodynamics. Post-treatment, a 2-fold increase in vitreous humor (VH) FI was observed, correlating with a reduction in FB breakdown product Ba but minimal changes in other complement factors. The aqueous humor (AH) was found to be an unreliable proxy for VH in assessing complement activation. In vitro assays showed that the increase in FI had a minor effect on the complement amplification loop compared to the more potent C3 inhibitor pegcetacoplan. These findings suggest that PPY988 may not provide enough FI protein to effectively modulate complement activation and slow GA progression, highlighting the need for thorough biomarker review to determine optimal dosing in future studies.

Strengths:

This manuscript provides critical data on the efficacy of gene therapy for the eye, specifically introducing complement FI expression. It presents the results from a halted clinical trial, making the publication of this data essential for understanding the outcomes of this gene therapy approach. The findings offer valuable insights and lessons for future gene therapy attempts in similar contexts.

Weaknesses:

No particular weaknesses. The study was carefully performed and limitations are discussed.

I have just some concerns about the methodology used. The authors use the MILLIPLEX assays, which allow for multiplexed detection of complement proteins and they mention extensive validation. How are the measurements with this assay correlating with gold standard methods? Is the specificity and the expected normal ranges preserved with this assay? This also stands for the Olink assay. Some of the proteins are measured by both assay and/or by standard ELISA. How do these measurements correlate?

Comments on revisions:

The authors answered part of my comments. Only one remained - please provide a comparison between ELISA/Multiplex and Olink data to judge the robustness of the Olinkl assay for complement.

Reviewer #2 (Public review):

Summary:

The results presented demonstrate AAV2-CFI gene therapy delivers long-term and marginally higher FI protein in vitreous humor that results in a concomitant reduction in the FB activation product Ba. However, the lack of clinical efficacy in the phase I/II study, possibly due to lower in vitro potency when compared to currently approved pegcetacoplan, raise important considerations for the utility of this therapeutic approach. Despite the early termination of the PPY988 clinical development program, the study achieved significant milestones, including the implementation of subretinal gene therapy delivery in older adults, complement biomarker comparison between serial vitreous humor and aqueous humor samples and vitreous humor proteomic assessment via Olink.

Strengths:

Long-term augmentation of FI protein in vitreous humor over 96-weeks and reduction of FB breakdown product Ba in vitreous humor suggests modulation of the complement system. Developed a novel in vitro assay suggesting FI's ability to reduce C3 convertase activity is weaker than pegcetacoplan and FH and may suggest a higher dose of FI will be required for clinical efficacy. Warn of the poor correlation between vitreous humor and aqueous humor biomarkers and suggest aqueous humor may not be a reliable proxy for vitreous humor with regard to complement activation/inhibition studies.

Weaknesses:

The vitrectomy required for subretinal route of administration causes long-term loss of total protein and may influence interpretation of complement biomarker results even with normalization. The modified in vitro assay of complement activation suggests a several hundred-fold increase in FI protein is required to significantly affect C3a levels. Interestingly, the in vitro assay demonstrates 100% inhibition of C3a with pegcetacoplan and FH therapeutics, but only a 50% reduction with FI even at the highest concentrations tested. This observation suggests FI may not be rate-limiting for negative complement regulation under the in vitro conditions tested and potentially in the eye. It is unclear if pharmacokinetic and pharmacodynamic properties in aqueous humor and vitreous humor compartments are a reliable predictor of FI level/activity after subretinal delivery AAV2-CFI gene therapy.

Reviewer #3 (Public review):

Summary:

The manuscript by Hallam et al describes the analysis of various biomarkers in patients undergoing complement factor I supplementation treatment (PPY988 gene therapy) as part of the FOCUS Phase I/II clinical trial. The authors used validated methods (multiplexed assays and OLINK proteomics) for measuring multiple soluble complement proteins in the aqueous humour (AH) and vitreous humour (VH) of 28 patients over a series of timepoints, up to and including 96 weeks. Based on biomarker comparisons, the levels of FI synthesised by PPY988 were believed to be insufficient to achieve the desired level of complement inhibition. Subsequent comparative experiments showed that PPY988-delievred FI was much less efficacious than Pegceptacoplan (FDA approved complement inhibitor under the name SYFORVE) when tested in an artificial VH matrix.

Strengths:

The manuscript is well written with data clearly presented and appropriate statistics used for the analysis itself. It's great to see data from real clinical samples that can help support future studies and therapeutic design. The identification that complement biomarker levels present in the AH do not represent the levels found in the VH is an important finding for the field, given the number of complement-targeting therapies in development and the desperate need for good biomarkers for target engagement. This study also provides a wealth of baseline complement protein measurements in both human AH and VH (and companion measurements in plasma) that will prove useful for future studies.

Weaknesses:

No real weaknesses in the manuscript itself. It is only a shame that it would appear that FI supplementation is not a viable way forward for treating GA secondary to AMD.

Comments on revisions:

I think the authors have done all that they can to present this study in the most robust manner possible.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study analyzed biomarker data from 28 subjects with geographic atrophy (GA) in a Phase I/II clinical trial of PPY988, a subretinal AAV2 complement factor I (CFI) gene therapy, to evaluate pharmacokinetics and pharmacodynamics. Post-treatment, a 2-fold increase in the vitreous humor (VH) FI was observed, correlating with a reduction in FB breakdown product Ba but minimal changes in other complement factors. The aqueous humor (AH) was found to be an unreliable proxy for VH in assessing complement activation. In vitro assays showed that the increase in FI had a minor effect on the complement amplification loop compared to the more potent C3 inhibitor pegcetacoplan. These findings suggest that PPY988 may not provide enough FI protein to effectively modulate complement activation and slow GA progression, highlighting the need for a thorough biomarker review to determine optimal dosing in future studies.

Strengths:

This manuscript provides critical data on the efficacy of gene therapy for the eye, specifically introducing complement FI expression. It presents the results from a halted clinical trial, making sharing this data essential for understanding the outcomes of this gene therapy approach. The findings offer valuable insights and lessons for future gene therapy attempts in similar contexts.

Weaknesses:

No particular weaknesses. The study was carefully performed and limitations are discussed.

I have just some concerns about the methodology used. The authors use the MILLIPLEX assays, which allow for multiplexed detection of complement proteins and they mention extensive validation. How are the measurements with this assay correlating with gold standard methods? Is the specificity and the expected normal ranges preserved with this assay? This also stands for the Olink assay. Some of the proteins are measured by both assay and/or by standard ELISA. How do these measurements correlate?

The authors thank the reviewer for the positive response. Regarding the ELISA assays used to measure the array of complement proteins described, these were extensively validated for the following parameters: specificity, intra-assay and inter-assay precision, accuracy, stability, reference range, and parallelism. All assays were validated in plasma, vitreous and aqueous humour. Due to the limited volume and availability of ocular fluids from individuals in the study, validation in vitreous and aqueous matrices was performed using a pool of several samples from post-mortem donors. At the time this study was initiated, the Millipore Luminex complement panels and the Quidel C3a and Ba EIA were the most sensitive assays and the only commercially available options capable of measuring the proteins of interest in the context of limited vitreous and aqueous humor sample. The concentrations measured were observed at similar ranges as those published in the literature using assays in distinct patient populations e.g. in (Mandava et al, Invest Ophthalmol Vis Sci, 2020).

Measurements from vitreous and aqueous from subject samples were deemed reportable if they were within the quantifiable ranges defined for these sample types during the validation (coefficient of variation of 20%, or 30% when results were below the lower limit of quantification but above limit of detection). Notably, given the limited amount of biomarker data due to small sample size, we share results from outlier biomarker measurements, to illustrate the heterogeneity in sample quality. We further publish plasma sample biomarker results in supplemental table 5 wherein complement protein concentrations can be observed and compared to normal ranges in the literature.

Adding confidence to the robustness of our assays was the observation that some of the complement proteins quantified by standard assay (e.g. plate and bead-based ELISAs) were also measured by the OLINK assay, and there was a general trend observed for positive correlation between results from both assays for FI levels post-treatment. However, we did not provide detailed correlative statistical analyses for further complement proteins as OLINK findings were deemed highly exploratory and hypothesis generating, and because the OLINK assay produced normalised results which are challenging to directly compare to ELISA results that were absolute.

Reviewer #2 (Public Review):

Summary:

The results presented demonstrate that AAV2-CFI gene therapy delivers long-term and marginally higher FI protein in vitreous humor that results in a concomitant reduction in the FB activation product Ba. However, the lack of clinical efficacy in the phase I/II study, possibly due to lower in vitro potency when compared to currently approved pegcetacoplan, raises important considerations for the utility of this therapeutic approach. Despite the early termination of the PPY988 clinical development program, the study achieved significant milestones, including the implementation of subretinal gene therapy delivery in older adults, complement biomarker comparison between serial vitreous humor and aqueous humor samples and vitreous humor proteomic assessment via Olink.

Strengths:

Long-term augmentation of FI protein in vitreous humor over 96 weeks and reduction of FB breakdown product Ba in vitreous humor suggests modulation of the complement system. Developed a novel in vitro assay suggesting FI's ability to reduce C3 convertase activity is weaker than pegcetacoplan and FH and may suggest a higher dose of FI will be required for clinical efficacy. Warn of the poor correlation between vitreous humor and aqueous humor biomarkers and suggest aqueous humor may not be a reliable proxy for vitreous humor with regard to complement activation/inhibition studies.

Weaknesses:

The vitrectomy required for the subretinal route of administration causes a long-term loss of total protein and may influence the interpretation of complement biomarker results even with normalization. The modified in vitro assay of complement activation suggests a several hundred-fold increase in FI protein is required to significantly affect C3a levels. Interestingly, the in vitro assay demonstrates 100% inhibition of C3a with pegcetacoplan and FH therapeutics, but only a 50% reduction with FI even at the highest concentrations tested. This observation suggests FI may not be rate-limiting for negative complement regulation under the in vitro conditions tested and potentially in the eye. It is unclear if pharmacokinetic and pharmacodynamic properties in aqueous humor and vitreous humor compartments are reliable predictors of FI level/activity after subretinal delivery AAV2-CFI gene therapy.

The authors thank the reviewer for the positive response and we agree that a limitation of the biomarker strategy for ocular gene therapy delivered to the retinal tissues is inferring PK/PD from vitreous and aqueous samples, which are the fluid sample compartments accessible from subjects available to measure molecular treatment response. We agree that these compartments may not accurately represent sub-retinal and tissue level complement turnover. In the discussion, line 508, we state: ‘Overall, the data suggests that fully functional FI is being secreted into the VH, but the regulatory effects on the level of Ba may be representative of convertase formation in the VH and not the macula retina/RPE nor the choroid. To validate this hypothesis, one approach would be to conduct vitreal sampling using an effective drug targeting C3 for GA in a larger cohort’.

However, the observation of elevation of FI in VH (and AH) post treatment, and changes in levels of downstream complement proteins that align with prior knowledge of control of alternative pathway activation, is compelling evidence that these measurements reflect modest but direct consequences of an FI-gene therapy that was delivered to the subretinal space. We add to the discussion, line 479: ‘the findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment.’

Furthermore, the observation of moderately raised FI levels in modelled VH post treatment being insufficient to control CS activation in vitro accords with the lack of clinical response observed at phase II. We note that measuring FI and complement biomarkers in retinal tissues from treated eyes at post-mortem would be one way to explore the PK/PD effects from AAV2-FI gene therapy.

Reviewer #3 (Public Review):

Summary:

The manuscript by Hallam et al describes the analysis of various biomarkers in patients undergoing complement factor I supplementation treatment (PPY988 gene therapy) as part of the FOCUS Phase I/II clinical trial. The authors used validated methods (multiplexed assays and OLINK proteomics) for measuring multiple soluble complement proteins in the aqueous humour (AH) and vitreous humour (VH) of 28 patients over a series of time points, up to and including 96 weeks. Based on biomarker comparisons, the levels of FI synthesised by PPY988 were believed to be insufficient to achieve the desired level of complement inhibition. Subsequent comparative experiments showed that PPY988-delivered FI was much less efficacious than Pegceptacoplan (FDA-approved complement inhibitor under the name SYFORVE) when tested in an artificial VH matrix.

Strengths:

The manuscript is well written with data clearly presented and appropriate statistics used for the analysis itself. It's great to see data from real clinical samples that can help support future studies and therapeutic design. The identification that complement biomarker levels present in the AH do not represent the levels found in the VH is an important finding for the field, given the number of complement-targeting therapies in development and the desperate need for good biomarkers for target engagement. This study also provides a wealth of baseline complement protein measurements in both human AH and VH (and companion measurements in plasma) that will prove useful for future studies.

Weaknesses:

Perhaps the conclusions drawn regarding the lack of observed efficacy are not fully justified. The authors focus on the hypothesis that not enough FI was synthesised in these patients receiving the PPY988 gene therapy, suggesting a delivery/transduction/expression issue. But beyond rare CFI genetic variants, most genetic associations with AMD imply that it is a FI-cofactor disease. A hypothesis supported by the authors' own experiments when they supplement their artificial VH matrix with FH and achieve a significantly greater breakdown of C3b than achieved with PPY988 treatment alone. Justification around doubling FI levels driving complement turnover refers to studies conducted in blood, which has an entirely different complement protein profile than VH. In Supplemental Table 5 we see there is approx. 10-fold more FH than FI (533ug/ml vs 50ug/ml respectively) so increasing FI levels will have a direct effect. Yet in Supplemental Table 3 we see there is more FI than FH in VH (608ng/ml vs 466ng/ml respectively). Therefore, adding more FI without more co-factors would have a very limited effect. Surely this demonstrates that the study was delivering the wrong payload, i.e. FI, which hit a natural ceiling of endogenous co-factors within the eye?

See response to reviewer 3’s review after reviewer 3 recommendations section below.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

The authors present strong evidence using validated complement biomarker assays and comprehensive proteomic profiling that support their findings. The presentation of complement biomarker data in vitreous humor and aqueous humor after FI augmentation is presented in a clear and concise format. The direct comparison of complement biomarkers in vitreous humor and aqueous humor from the same patients and demonstrating similarities and differences is important for the nascent complement gene therapy field. Developing a novel in vitro complement model and comparing pegcetacoplan, FH, and FI inhibitors provides the field with a valuable assay to benchmark other complement therapeutics. As currently designed, the in vitro assay supports why FI augmentation did not contribute to clinical success. It also suggests that non-physiological concentrations of FI protein (over 100 µg/mL) maximally inhibit C3a signal by ~50%, whereas both pegcetacoplan and FH reduce the signal by 100%. Does this suggest that CFI is not an appropriate therapeutic target to control complement overactivation in the eye?

We agree with the reviewer that the new data from the novel in vitro assay coupled with the clinical findings from the phase II gene therapy trial does now suggest FI is less attractive as a therapeutic target for controlling complement activation in the retinal tissues of subjects with Geographic Atrophy.

Reviewer #3 (Recommendations For The Authors):

I think the authors have done a great job collecting and analysing these clinical samples and elucidating the baseline complement protein profile in both the AH and VH. I only have minimal suggested changes.

Perhaps a more direct discussion around the limitations of adding more FI into environments where there is no excess of FI-cofactors present? And a discussion around the limitations of VH (and VA for that matter) biomarker sampling for a disease that primarily affects the neurosensory retina and outer blood/retinal barrier: perhaps the landscape of complement proteins is different yet again (although, admittedly, impossible to sample in a patient)? Finally, would it not have been better to perform complement activation experiments using the VH of treated patients directly rather than creating an artificial VH matrix (there may, or may not, be a couple of things in human VH that directly affect complement turnover...)?

We thank the reviewer for the supportive comments. This study is the first to describe FI and FH levels and respective ratios in vitreous humour (plus aqueous and plasma) from GA subjects, before and after sub-retinal gene therapy. It is compelling to observe that in the VH the levels of FI are greater than FH, the primary fluid phase co-factor for FI enzymatic activity. This new information does indeed argue against further FI supplementation (using gene therapy) being of added benefit to controlling the complement system in the broader population in individuals with Geographic Atrophy. We note that at the start of the clinical development of GT005/PPY988 AAV2-FI gene therapy, there was limited information on FI and FH levels in AMD in ocular fluids to inform the pharmacodynamics of complement activation. Now, by running the FOCUS phase I clinical trial and measuring the complement biomarker data using validated assays we have added to our understanding on the levels and ratio of FI to FH and other complement proteins in a larger number of GA subjects’ ocular samples.  We report the levels of complement proteins measured in ocular and systemic samples, to show the ranges and also the differences in ratios between the different matrices.   

Regarding the statement that FI supplementation could likely be ineffective due to limited FH cofactor; FH is not the only co-factor that FI may partner with at cell surfaces to become enzymatically active (others include MCP (CD46) and CR1 (CD35), although the latter is known to be of limited expression in the eye), as such, it is certainly true that other proteins may be present in the tissue altering the kinetics of FI’s activity after sub-retinal gene-therapy. In addition, the ratio between FI and FH detected in the VH may not be the same as in retinal tissue. As such, we agree that drawing insights from biomarkers in the VH may not fully reflect the disease processes and treatment response at the retinal cell layers, but it is the closest fluid sample available to sample tissue released soluble proteins. We acknowledge that VH biomarkers will not fully capture retinal disease processes and treatment responses, but due to their proximity, will reflect retina-released soluble proteins. The findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment. We agree modelling different inhibitor effects on complement activation directly using subject’s vitreous would be informative, but this was not possible due to the limitations of very small sample volume.

We add several sentences to the discussion regarding the points above. Line 473: ‘Notably, that FI does not reduce C3a breakdown to baseline even at supermolecular concentrations suggests cofactor limitation that might be more pronounced in VH given FH is not in excess of FI as is the case in blood 27. Moreover, there are additional cell-bound cofactors for FI that may be present in retinal tissue that are not present in the VH and could further alter the kinetics of the assay, such as MCP (CD46) albeit with disease related changes observed 37. However, the findings of elevated FI in the VH after sub-retinally delivered CFI gene therapy and changes in complement pathway proteins post-treatment build confidence that VH matrix is at least partially reflecting the complement system at the retinal layers and treatment site, and is a valid biomarker for PK/PD insights in response to treatment.’

Minor comments:

Line 237: Missing parenthesis at the end of the sentence

Manuscript updated.

Line 435: Missing secondary parenthesis after .....Figure 3A)......

Manuscript updated.

Line 536: I don't think suggesting the addition of FHR proteins into the neurosensory retina/VH is such a good idea

The reference to FHRs has been clarified in the manuscript, line 558. The authors note that FHR dimerization domains have been engineered to dimerize Factor H constructs increasing half-life and potency for drugs currently in development.

eLife Assessment

In this valuable study, the authors propose a model wherein the bacterial redox state plays a crucial role in the differentiation of Chlamydia trachomatis into elementary and reticulate bodies. They provide solid evidence to argue that a highly oxidising environment favours the formation of elementary bodies while a reducing condition slows down development. Overall, the study convincingly demonstrates that Chlamydial redox states play a role in differentiation, an observation that may have implications for the study of other bacterial systems.

Reviewer #1 (Public review):

Summary:

Chlamydia spp. has a biphasic developmental cycle consisting of an extracellular, infectious form called an elementary body (EB) and an intracellular, replicative form known as a reticular body (RB). The structural stability of EBs is maintained by extensive cross linking of outer membrane proteins while the outer membrane proteins of RBs are in a reduced state. The overall redox state of EBs is more oxidized than RBs. The authors propose that redox state may be a controlling factor in the developmental cycle. To test this, alkyl hydroperoxide reductase subunit C (ahpC) was overexpressed or knocked down to examine effects on developmental gene expression. KD of ahpC induced increased expression of EB-specific genes and accelerated EB production. Conversely, overexpression of phpC delayed differentiation to EBs. The results suggest that chlamydial redox state may play a role in differentiation.

Strengths:

Uses modern genetic tools to explore the difficult area of temporal gene expression throughout the chlamydial developmental cycle.

Weaknesses:

The environmental signals triggering ahpC expression/activity are not determined.

Comments on revisions:

I am satisfied with the modifications made to the manuscript.

Reviewer #2 (Public review):

The factors that influence the differentiation of EBs and RBs during Chlamydial development are not clearly understood. A previous study had shown a redox oscillation during the Chlamydial developmental cycle. Based on this observation, the authors hypothesize that the bacterial redox state may play a role in regulating the differentiation in Chlamydia. To test their hypothesis, they make knock-down and overexpression strains of the major ROS regulator, ahpC. They show that the knock-down of ahpC leads to a significant increase in ROS levels leading to an increase in the production of elementary bodies and overexpression leads to a decrease in EB production likely caused by a decrease in oxidation. From their observations, they present an interesting model wherein an increase in oxidation favors the production of EBs.

Comments on revisions:

Major concerns have been satisfactorily addressed.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Chlamydia spp. has a biphasic developmental cycle consisting of an extracellular, infectious form called an elementary body (EB) and an intracellular, replicative form known as a reticular body (RB). The structural stability of EBs is maintained by extensive cross-linking of outer membrane proteins while the outer membrane proteins of RBs are in a reduced state. The overall redox state of EBs is more oxidized than RBs. The authors propose that the redox state may be a controlling factor in the developmental cycle. To test this, alkyl hydroperoxide reductase subunit C (ahpC) was overexpressed or knocked down to examine effects on developmental gene expression. KD of ahpC induced increased expression of EB-specific genes and accelerated EB production. Conversely, overexpression of ahpC delayed differentiation to EBs. The results suggest that chlamydial redox state may play a role in differentiation.

Strengths:

Uses modern genetic tools to explore the difficult area of temporal gene expression throughout the chlamydial developmental cycle.

Weaknesses:

The environmental signals triggering ahpC expression/activity are not determined.

Thank you for your comments. Our data and those of others have shown that ahpC is expressed as a mid-developmental cycle gene (i.e., when RBs predominate in the population). This is true of most chlamydial genes, and the factors that determine developmental expression are not fully understood. As we noted in the Discussion, Chlamydia lacks AhpF/D orthologs, so it is not clear how AhpC activity is regulated. Related to determining environmental signals that trigger activity of AhpC, then this is a non-trivial issue in an obligate intracellular bacterium. Our assumption is that AhpC is constitutively active and that the increasing metabolic production of ROS eventually overcomes the innate (and stochastic) activity of AhpC to handle it, hence the threshold hypothesis. Importantly, the stochasticity is consistent with what we know about secondary differentiation in Chlamydia. We have tried to clarify these points in the Discussion.

Reviewer #2 (Public Review):

The factors that influence the differentiation of EBs and RBs during Chlamydial development are not clearly understood. A previous study had shown a redox oscillation during the Chlamydial developmental cycle. Based on this observation, the authors hypothesize that the bacterial redox state may play a role in regulating the differentiation in Chlamydia. To test their hypothesis, they make knock-down and overexpression strains of the major ROS regulator, ahpC. They show that the knock-down of ahpC leads to a significant increase in ROS levels leading to an increase in the production of elementary bodies and overexpression leads to a decrease in EB production likely caused by a decrease in oxidation. From their observations, they present an interesting model wherein an increase in oxidation favors the production of EBs.

Major concern:

In the absence of proper redox potential measurements, it is not clear if what they observe is a general oxidative stress response, especially when the knock-down of ahpC leads to a significant increase in ROS levels. Direct redox potential measurement in the ahpC overexpression and knock-down cells is required to support the model. This can be done using the roGFP-based measurements mentioned in the Wang et al. 2014 study cited by the authors.

Thank you for this suggestion. It is definitely something that we are looking to implement. However, our current vectors don’t allow for roGFP2 in combination with inducible expression of a gene of interest. We will need to completely redesign our vectors, and, in Chlamydia, the validation of such new vectors together with ahpC OE or KD may literally take a year or longer.

In lieu of this, we used the CellRox redox reactive dye to image live chlamydiae during normal growth or ahpC KD. During ahpC KD, these organisms are clearly much brighter than the control, uninduced conditions. These data are included as new Figure 5 to go along with the data we previously reported from the plate reader measurements. These data also clearly indicate that the readings we observed are from Chlamydia and not the host cell.

As far as a general oxidative stress response, Chlamydia lacks any transcriptional regulators akin to OxyR. The response we’ve measured, earlier expression of genes associated with secondary differentiation, would be an odd stress response not consistent with a focused program to respond to oxidative stress. We added new RNAseq data further showing this effect of a global earlier increase in late gene transcripts.

Reviewer #3 (Public Review):

Summary:

The study reports clearly on the role of the AhpC protein as an antioxidant factor in Chlamydia trachomatis and speculates on the role of AhpC as an indirect regulator of developmental transcription induced by redox stress in this differentiating obligate intracellular bacterium.

Strengths:

The question posed and the concluding model about redox-dependent differentiation in chlamydia is interesting and highly relevant. This work fits with other propositions in which redox changes have been reported during bacterial developmental cycles, potentially as triggers, but have not been cited (examples PMID: 2865432, PMID: 32090198, PMID: 26063575). Here, AhpC over-expression is shown to protect Chlamydia towards redox stress imposed by H2O2, CHP, TBHP, and PN, while CRISPRi-mediated depletion of AhpC curbed intracellular replication and resulted in increased ROS levels and sensitivity to oxidizing agents. Importantly, the addition of ROS scavengers mitigated the growth defect caused by AhpC depletion. These results clearly establish the role of AhpC affects the redox state and growth in Ct (with the complicated KO genetics and complementation that are very nicely done).

Weaknesses:

However, with respect to the most important implication and claims of this work, the role of redox in controlling the chlamydial developmental cycle rather than simply being a correlation/passenger effect, I am less convinced about the impact of this work. First, the study is largely observational and does not resolve how this redox control of the cell cycle could be achieved, whereas in the case of _Caulobacte_r, a clear molecular link between DNA replication and redox has been proposed. How would progressive oxidation in RBs eventually trigger the secondary developmental genes to induce EB differentiation? Is there an OxyR homolog that could elicit this change and why would the oxidation stress in RBs gradually accumulate during growth despite the presence of AhpC? In other words, the role of AhpC is simply to delay or dampen the redox stress response until the trigger kicks in, again, what is the trigger? Is this caused by increasing oxidative respiration of RBs in the inclusion? But what determines the redox threshold?

Thank you for your comments. As the reviewer notes, our work clearly demonstrates that AhpC acts as an antioxidant in Chlamydia trachomatis. Further, we have shown that transcription of the late cycle genes is altered upon altered activity of AhpC, which acts as a proof of concept that redox is (one of) the key factor(s) controlling developmental cycle progression in Chlamydia. Our new RNAseq data indicate that a broad swath of well characterized late genes is activated, which contradicts the argument that what we’ve measured is a stress response (unless activation of late genes in Chlamydia is generally a stress response (not the case based on other models of stress) – in which case we would not be able to differentiate between these effects). We hypothesize that ROS production from the metabolic activities of RBs serves as a signal to trigger secondary differentiation from RBs to EBs. How this exact threshold is determined is currently unknown as Chlamydia does not have any annotated homolog for OxyR. It is beyond the scope of the present manuscript to identify and then characterize what specific factor(s) control(s) this response. We fully anticipate that multiple factors are likely impacted by increasing oxidation, so dissecting the exact contributions of any one factor will represent (a) potential separate manuscript(s). Nonetheless, this remains an overarching goal of the lab yet remains challenging given the obligate intracellular nature of Chlamydia. Strategies that would work in a model system, like Caulobacter, that can be grown in axenic media are not easily implemented in Chlamydia.

As we noted above in another response, ahpC is transcribed as a mid-cycle gene with a peak of transcription corresponding to the RB phase of growth. We hypothesize that the gradual accumulation of ROS from metabolic activity will eventually supercede the ability of AhpC to detoxify it. This would result in any given RB asynchronously and stochastically passing this threshold (and triggering EB formation), which is consistent with what we know about secondary differentiation in Chlamydia.

I also find the experiment with Pen treatment to have little predictive power. The fact that transcription just proceeds when division is blocked is not unprecedented. This also happens during the Caulobacter cell cycle when FtsZ is depleted for most developmental genes, except for those that are activated upon completion of the asymmetric cell division and that is dependent on the completion of compartmentalization. This is a smaller subset of developmental genes in caulobacter, but if there is a similar subset that depends on division on chlamydia and if these are affected by redox as well, then the argument about the interplay between developmental transcription and redox becomes much stronger and the link more intriguing. Another possibility to strengthen the study is to show that redox-regulated genes are under the direct control of chlamydial developmental regulators such as Euo, HctA, or others and at least show dual regulation by these inputs -perhaps the feed occurs through the same path.

Comparisons to other model systems are generally of limited value with Chlamydia. All chlamydial cell division genes are mid-cycle (RB-specific) genes, just like ahpC. There is no evidence of a redox-responsive transcription factor (whether EUO, HctA, or another) that activates or represses a subset of genes in Chlamydia. Similarly, there is no evidence that redox directly and specifically impacts transcription of cell division genes based on our new RNAseq data. The types of experiments suggested are not easily implemented in Chlamydia, but we would certainly like to be able to do them.

As it pertains to penicillin specifically, we and others have shown that treating chlamydiae with Pen blocks secondary differentiation (meaning late genes are not transcribed). Effectively, Pen treatment freezes the organism in an RB state with continued transcription of RB genes. What we have shown is that, even during Pen treatment (which blocks late gene transcription), ahpC KD can overcome this block, which shows that elevated oxidation is able to trigger late gene expression even when the organisms are phenotypically blocked from progressing to EBs. The comparison from our perspective to Caulobacter is of limited value.

This redox-transcription shortcoming is also reflected in the discussion where most are about the effects and molecular mitigation of redox stress in various systems, but there is little discussion on its link with developmental transcription in bacteria in general and chlamydia.

We have edited the Discussion to include a broader description of the results and included additional citations as suggested by the reviewer (PMID: 32090198, PMID: 26063575). However, we found one suggested article (PMID: 2865432) is not relevant to our study, so we didn’t cite it in our present manuscript. There may have been a typo, so feel free to provide us the correct PMID that can be cited.

Reviewer #1 (Recommendations For The Authors):

(1) Line 146. A minor point, but inclusion-forming units directly measure infectious EBs. In some cases, the particle-to-infectivity ratio approaches unity. I don't believe IFUs are a "proxy".

Following reviewers comment we have modified the statement.

(2) Figure 2E. Results are normalized to uninduced. The actual number of IFUs in the uninduced should be provided.

In the revised version of the manuscript, we have provided actual number of IFUs at 24 and 48 hpi in the uninduced condition of both ahpC OE and EV.

(3) Figures 3B&D. The shades of gray are not possible to distinguish. I'd suggest color or direct labeling.

Following reviewer’s suggestion, in the latest version of the manuscript we have replaced gray shaded graphs with RGB colored graphs for better visualization and understanding.

(4) Lines 217-224, Figure 4. Is it possible to get micrographs of the reporter retention in chlamydiae to demonstrate that it is chlamydial ROS levels that are being measured and not cellular?

Following reviewer’s comment, we performed live-cell microscopy using uninfected HeLa cells and ahpC KD in the uninduced and induced conditions at 24 and 40 hpi. We have created new Fig. 5A with the quantitative ROS measurement graph done by the plate reader (old figure 4 E) and these new 24 hpi/40 hpi microscopy images (Fig 5B and S4).

(5) The Discussion is overly long and redundant. Large portions of the discussion are simply a rehash of the Results listing by figure number the relevant conclusions.

Following reviewer’s suggestion, the discussion is modified.

Reviewer #2 (Recommendations For The Authors):

(1) In Figure 2, ahpC is significantly overexpressed at 14 hpi. An IFA as in 2B for 14hpi will be useful. This will help to understand how quick the effect of ahpC overexpression is on development.

We have added 14 hpi IFA of ahpC and EV as part of Fig 2B.

(2) In Figure 2E, is there a reason that there is no increase in recoverable IFUs between 24h and 48h for the EV?

The graph in 2E is % of uninduced. For more clarity, we have mentioned absolute IFUs of uninduced samples in the revised manuscript and IFU level at 48 hpi IFU is higher than the 24 hpi.

(3) In Figure 3, Can relative levels of RB vs EB measured? This will provide a convincing case for the production of more EBs even when only less/more RBs are present. The same stands for Figure 4.

We assumed that the comment is for Fig. 2 not the Fig. 3 and following reviewer’s constructive suggestion, we have attempted to resolve the issue. We normalized log10 IFUs/ml with log10 gDNA for 24 hpi and added as figure 2F and 4E. This may resolve the reviewer’s concern about the levels of RBs and EBs.

(4) A colour-coded Figure 3B and D, instead of various shades of grey, will be easy for the reader to interpret.

Agreed with the reviewer. For better visualization and understanding of the data, we have replaced gray shaded graphs with RGB colored graphs in the latest version of the manuscript.

Reviewer #3 (Recommendations For The Authors):

Other comments:

(1) The first paragraph of the discussion should be deleted. It's not very useful or revealing and just delivers self-citations.

Following reviewer’s suggestion, we rewrote the discussion.

(2) The first paragraph of the results section does not present results. It's an intro.

We incorporated this information into the Intro as suggested.

(3) Has the redox difference between RBs and EBs been experimentally verified by these authors as depicted and claimed in Figure 1A with the cell-permeable, fluorogenic dye CellROX Deep Red for example? It is important to confirm this for EBs and RBs in this setup.

The difference between redox status of RBs and EBs is studied and established before by previous studies such as Wang et al., 2014.

(4) l77. Obligate intracellular alpha-proteobacteria also differentiate ... not only chlamydiae.

We have modified the sentence.

(5) l127. Is the redox state altered upon ahpC overexpression?

The ahpC overexpression strain showed hyper resistance for the tested oxidizing agents (including the highest concentration tested) indicating highly reduced conditions as a result of higher activity of AhpC.

eLife Assessment

This is a valuable study on the efficacy of a live attenuated vaccine that was tested in different animal models and the evidence is convincing. The study has been strengthened after revisions.

Reviewer #2 (Public review):

Summary:

In this manuscript the authors evaluate the attenuation, immunogenicity, and protection efficacy of a live-attenuated SARS-CoV-2 vaccine candidate (BK2102) against SARS-CoV-2.

Strengths:

The authors demonstrate that intranasal inoculation of BK2102 is safe and able to induce humoral and cellular immune responses in hamsters, without apparent signs of damage in the lungs, that protects against homologous SARS-CoV-2 and Omicron BA.5 challenge. Safety of BK2102 was further confirmed in a new hACE2 transgenic mouse model generated by the authors.

Weaknesses:

The authors have addressed my previous comments on the first submission of the document.

Reviewer #3 (Public review):

Summary:

Suzuki-Okutani and collogues reported a new live-attenuated SARS-CoV-2 vaccine (BK2102) containing multiple deletion/substitution mutations. They show that the vaccine candidate is highly attenuated and demonstrates great safety profile in multiple animal models (hamsters and Tg-Mice). Of importance, their data show that singe intranasal immunization with BK2102 leads to strong protection of hamsters against D614G and BA.5 challenge in both lungs and URT (nasal wash). Both humoral and cellular responses were induced, and neutralization activity remained for >360 after single inoculation.

Strengths:

The manuscript describes a comprehensive study that evaluates safety, immunogenicity, and efficacy of a new live-attenuated vaccine. Strengths of the study include: 1) strong protection against immune evasive variant BA.5 in both lungs and NW; 2) durability of immunity for >360 days; 3) confirmation of URT protection through a transmission experiment.<br /> While first-generation COVID-19 vaccines have achieved much success, new vaccines that provide mucosal and durable protection remain needed. Thus, the study is significant.

Weaknesses:

Lack of a more detailed discussion of this new vaccine approach in the context of reported live-attenuated SARS-CoV-2 vaccines in terms of its advantages and/or weakness<br /> Antibody endpoint titers could be presented.<br /> Lack of elaboration on immune mechanisms of protection at the upper respiratory tract (URT) against an immune evasive variant in the absence of detectable neutralizing antibodies

Comments on revisions:

In the revised submission, the authors have added new data and have modified the manuscript accordingly. They have reasonably addressed my comments raised in the previous round of review. The quality and clarity of the manuscript are improved.

Author response:

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

We sincerely thank the Editor and the Reviewers for their time and effort in thoroughly reviewing our manuscript and providing valuable feedback. We hope we have addressed their comments effectively and improved the clarity of our manuscript as a result.

The major revisions in the updated manuscript are as follows:

(1) Immunization experiments using mRNA in Syrian hamsters were performed (Supplementary figures 2A, B and C).

(2) An ELISPOT assay to evaluate cellular immunity in Syrian hamsters inoculated with BK2102 was conducted (Figure 2F).

(3) IgA titers in BK2102-inoculated Syrian hamsters were successfully measured (Supplementary figure 2B).

(4) New immunogenicity data for BK2102 in monkeys was additionally included (Supplementary figure 3B).

(5) The discussion section has been thoroughly revised to integrate the new data.

These results have been incorporated into the manuscript, and additional text has been added accordingly.

Below, we provide point-by-point responses to the reviewers’ comments and concerns.

Public Reviews:

Reviewer #1:

(1) A comparative safety assessment of the available m-RNA and live attenuated vaccines will be necessary. The comparison should include details of the doses, neutralizing antibody titers with duration of protection, tissue damage in the various organs, and other risks, including virulence reversal.

We agree with the Reviewer’s comment regarding the lack of data to compare BK2102 with an mRNA vaccine. Unfortunately, we were unable to obtain commercially available mRNA vaccines for research purposes and could not produce mRNA vaccines of equivalent quality. As a result, a direct comparison of the safety profiles of BK2102 and mRNA vaccines was not possible. To address this, we conducted a GLP study with an additional twelve monkeys to evaluate the safety of BK2102. Following three intranasal inoculations of BK2102 at two-week intervals, no toxic effects were observed in any of the parameters assessed, including tissue damage, respiratory rate, functional observational battery (FOB), hematology, or fever. These results are detailed in lines 115-117.

Furthermore, we compared the immunogenicity of BK2102 with that of an in-house prepared mRNA vaccine. The mRNA vaccine was designed to target the spike protein of SARS-CoV-2, and its immunogenicity was evaluated in hamsters. When serum neutralizing antibody titers were found to be comparable between the two, intranasal inoculation of BK2102 induced higher IgA levels in nasal wash samples compared to those from hamsters injected intramuscularly with the self-made mRNA vaccine (Supplementary figures. 2A and B, respectively). Additionally, while the mRNA vaccine induced Th1 and Th2 immune responses, as indicated by the detection of IgG1 and IgG2/3 (Supplementary figure. 2C), BK2102 mainly induced a Th1 response in hamsters. These explanatory sentences have been added to the manuscript (lines 140-150).

(2) The vaccine's effect on primates is doubtful. The study fails to explain why only two of four monkeys developed neutralizing antibodies. Information about the vaccine's testing in monkeys is also missing: What was the level of protection and duration of the persistence of neutralizing antibodies in monkeys? Were the tissue damages and other risks assessed?

We believe that the reason neutralizing antibody titers were observed in only 2 out of 4 monkeys in the immunogenicity study reported in the original manuscript is that only a single-dose was administered. We measured the neutralizing antibody titers in sera collected from monkeys used in the GLP study and confirmed the induction of neutralizing antibody in all 6 monkeys that received three inoculations of BK2102. This data has been included in a new figure (Supplementary figure 3B). While we would have liked to evaluate the persistence of immunity and conduct a protection study in monkeys, limitations related to facility availability and cost prevented us from doing so. As noted in (1), tissue injury and other risk assessments were evaluated in the GLP study, which showed no evidence of tissue injury or other toxic effects. These results are described in lines 113-117.

(3) The vaccine's safety in immunosuppressed individuals or individuals with chronic diseases should be assessed. Authors should make specific comments on this aspect.

In general, live-attenuated vaccines are contraindicated for immunosuppressed individuals or those with chronic conditions, and therefore BK2102 is also not intended for use in these patients.

This information has been added to the Discussion section (lines 309-311).

(4) The candidate vaccine has been tested with a limited number of SARS-CoV-2 strains. Of note, the latest Omicron variants have lesser virulence than many early variants, such as the alfa, beta, and delta strains.

We have added the results of a protection study against the SARS-CoV-2 gamma strain to Supplementary figures 5A and B. No weight loss was observed in BK2102-inoculated hamsters following infection with the gamma strain. These results are described in lines 109-111, 158-162.

(5) Limitations of the study have not been discussed.

We apologize for the ambiguity in the description of the Limitations of this paper. One major limitation of this study is that, despite observing high immunogenicity in hamsters, it remains uncertain whether the same positive results would be achieved in humans. Differences in susceptibility exist between species, which are not solely attributed to weight differences. For instance, while a single dose of 10³ PFU of BK2102 was sufficient to induce neutralizing antibodies in hamsters, a higher dose of 10⁷ PFU in monkeys was required to induce antibodies in only about 50% of the monkeys. Additionally, two more challenges in development of BK2102 were added to the discussion. The first was the limited availability of analytical reagents for hamster models, which restricted the detailed immunological characterization of the response. Second, it took time to gather preclinical data due to the space-related restrictions of BSL3 facilities, which delayed the clinical trials for BK2102 until many individuals had already acquired immunity against SARS-CoV-2. It remains to be seen whether our candidate will be optimal for human use, as the immunogenicity of live-attenuated vaccines is generally influenced by pre-existing immunity.

We added these considerations to the discussion section (lines 300-309).

Reviewer #2:

No major weaknesses were identified, however, this reviewer notes the following:

The authors missed the opportunity to include a mRNA vaccine to demonstrate that the immunity and protection efficacy of their live attenuated vaccine BK2102 is better than a mRNA vaccine.

One of the potential advantages of live-attenuated vaccines is their ability to induce mucosal

immunity. It would be great if the authors included experiments to assess the mucosal immunity of their live-attenuated vaccine BK2102.

We agree with the Reviewer’s suggestion regarding the importance of comparing BK2102 with the mRNA vaccine modality and evaluating the mucosal immunity induced by BK2102. In hamsters, under conditions where serum neutralizing antibody titers were equivalent, intranasal inoculation of BK2102 induced higher levels of antigen-specific IgA in nasal wash compared to intramuscular injection of the conventional mRNA vaccine. This new data has been added in Supplementary figures 2A and B, and corresponding sentences have been included in the Results and Discussion sections (lines 140-145, 292-299).

Reviewer #3:

Lack of a more detailed discussion of this new vaccine approach in the context of reported live-attenuated SARS-CoV-2 vaccines in terms of its advantages and/or weaknesses.

sCPD9 and CoviLiv^TM, two previously reported live-attenuated vaccines, achieve attenuation through codon deoptimization or a combination of codon deoptimization and FCS deletion. These two strategies affect viral proliferation but do not directly impact virulence. In contrast, the temperature sensitivity-related substitutions in NSP14 included in BK2102 selectively restrict the infection site, reducing the likelihood of lung infection and providing a safety advantage over the other live-attenuated vaccines. As mentioned in the response to comment (5) of Reviewer #1, a limitation of BK2102 is that its development began later than that of the previously reported live-attenuated vaccines. Consequently, we must consider the impact of pre-existing immunity in future human trials. Based on these points, we have added sentences discussing the advantages and disadvantages to the Discussion section (lines 302-305, 312-319).

Antibody endpoint titers could be presented.

Thank you for your suggestion. We calculated the antibody endpoint titers for Figure 2A and included the results in lines 105-107 of the revised manuscript.

Lack of elaboration on immune mechanisms of protection at the upper respiratory tract (URT) against an immune evasive variant in the absence of detectable neutralizing antibodies.

We appreciate the comment. The potential role of cellular and mucosal immunity in protection has been discussed in more detail in the revised manuscript, specifically in lines 283-295. According to the reference we initially cited, Hasanpourghadi et al. evaluated their adenovirus vector vaccine candidates and reported that the protection was enhanced by co-expression of the nucleocapsid protein rather than relying solely on the spike protein (Hasanpourghadi et al., Microbes Infect, 2023). Therefore, cellular immunity against the nucleocapsid and/or other viral proteins induced by BK2102 may also contribute to protection, as evidenced by more pronounced cellular immunity to the nucleocapsid detected through ELISPOT assay. Moreover, antigen-specific mucosal immunity was successfully detected in additional studies. The involvement of mucosal immunity in protection against mutant strains has been documented in the previously cited reference (Thwaites et al., Nat Commun, 2023). We have included these new data in Figure 2F and Supplementary figure 2B. Additionally, the results and discussion regarding the mechanisms of protection in the upper respiratory tract, in the absence of detectable neutralizing antibodies, have been incorporated into the revised lines 136-139, 143-145 and 283-295, respectively.

Recommendations for the authors:

Reviewer #2:

Figure 1: Please include the LOD and statistical analysis in both panels. Please consider passaging the virus in Vero cell s, approved for human vaccine production, to assess the stability of BK2102 after serial passage in vitro, which is important for its implementation as a live-attenuated vaccine. The authors should consider evaluating viral replication in different cell lines, and also assessing the plaque phenotype.

Thank you for your valuable comments. First, we have added the statistical analysis and the limit of detection (LOD) to Figure 1. In response to the comments regarding the stability of BK2102 after serial passage in Vero cells, as well as its replication and plaque phenotype in different cell lines, we manufactured test substances for GLP studies and clinical trials by passaging BK2102 in Vero cells, which are approved for human vaccine production. We confirmed that BK2102 is stable (data not shown). Additionally, we verified that BK2102 replicates in BHK, Vero E6, and Vero E6/TMPRSS2 cells, in addition to Vero cells. Among these options, we selected Vero cells due to their high proliferative capacity and ability to produce clear plaques.

Figure 2: Please, include statistical analysis in panels A, B, and D. Please, include the LOD in panels A and D. Please, include viral titers from these experiments in hamsters and NHPs.

First, we would like to note that Figure 2D has been replaced by Figure 2C in the revised manuscript, and the data on neutralizing antibody titers in non-human primates (NHPs), originally presented as Figure 2C, have been moved to the Supplementary figure 3A.

We have added the statistical analysis to Figure 2B and C, as well as the LOD to Figure 2C. Figure 2A (Spike-specific IgG ELISA) was intended for qualitative evaluation based on OD values, so the LOD was not defined. We have also added a detailed description of virus titer in the Methods section under the headings “Evaluation of Immunogenicity in Hamsters” and “Evaluation of Immunogenicity in Monkeys”, and updated the information in the Figure legends of the revised manuscript (lines 451, 459, 468-474, 566-567, 576-578, 582-584, 661-662).

Figure 3: Please, include the viral titers of the challenge virus in the NT and lungs.

We have added the virus titers for the challenge experiments to the Results section under the heading “BK2102 induced protective immunity against SARS-CoV-2 infection” (lines 168-174).

Figure 4: Please, include statistical analysis in panels B and C and evaluate viral titers.

We have added the statistical analysis to Figure 4B and C. Unfortunately, all samples in Figure 4 were fixed in formalin for histopathological examination, so virus titers could not be measured. However, in past experiments, we measured viral titers in the nasal wash samples and lungs of hamsters three days post-infection with D614G and BK2102. We confirmed that infectious virus was detected in both the nasal wash and lungs of the hamsters infected with D614G strain (2.9 log10 PFU/mL and 5.3 log10 PFU/g, respectively), but not in the lungs of the hamsters with BK2102. The viral titers in the nasal wash of BK2102-infected hamsters were equivalent to those of the hamsters infected with the D614G wild-type strain (3.0 log10 PFU/mL). However, we did not include this data to the revised manuscript.

Figure 5: Please, include viral titers in different tissues with the different vaccines (panels A and B). Please, include the body weight changes.  Finally, please, consider the possibility of challenging the vaccinated mice with the same SARS-CoV-2 strains used in the manuscript to demonstrate similar protection efficacy in this new ACE2 transgenic mice.

The different tissues of Tg mice were not sampled, as no gross abnormalities were observed in organs other than lungs and brains during necropsy. We have added new data on the body weight of Tg mice after infection to Supplementary figures 9B and 9C in the revised manuscript, along with additional lines in the Results section (lines 228-230 and 247-248). Although we do not know the reason, we have observed that immunization of this animal model does not lead to an increase in antibody titers. Therefore, we do not consider this animal model suitable for the protection study as you suggested. However, it could be useful in passive immunization experiments.

Supplementary Figure 1: Since most of the manuscript focuses on BK2102, the authors should consider removing the other live-attenuated vaccines (Supplementary Figure 1A).

We agree with the Reviewer’s suggestion and have simplified the description for Supplementary Figure 1A (lines 93-97).

Supplementary Figure 3: Please, include statistical analysis.

In the revised manuscript, Supplementary Figure 3 from the original manuscript has been moved to Supplementary Figure 2D. The IgG subclass ELISA was intended for a qualitative evaluation based on OD values, and therefore the results were included in the Supplementary figure. However, we realized the description was not clear, so we added further clarification in the Results section (lines 145-147).

Supplementary Figure 4: Please, include the viral titers in both infected and contact hamsters from this experiment.

In the revised manuscript, Supplementary Figure 4 in the original manuscript has been moved to Supplementary Figure 6. Unfortunately, due to limited breeding space for the hamsters, we were unable to prepare groups for the evaluation of viral titer, and instead prioritized evaluation by body weight.

Reviewer #3:

(1) It would be helpful to discuss this new vaccine in the context of other reported live-attenuated vaccines in terms of its advantages and/or disadvantages.

Please refer to our response to the Reviewer’s “first comment” above, as well as to the response in Public comment (5) of Reviewer #1. The modifications made in the manuscript are described in lines 302-305 and 312-319.

(2) Figure 2A: end-point titers could be presented, other than OD values.

This comment is addressed in the reviewer’s second public comment. The endpoint titer has been included in lines 105-107 of the revised manuscript.

(3) Figure 2C: it is unclear why only 2 out of 4 NHPs show neutralization titers. This could be moved to a supplementary figure.

As suggested by the Reviewer, Figure 2C of the original manuscript has been moved to Supplementary Figure 3A in the revised manuscript. In response Public comment (2) from Reviewer #1, we have also added new data on neutralizing antibodies in the monkeys as Supplementary figure 3B.

(4) Figures 2E-F: bulk measurement of cytokine production in supernatants is not an optimal way to measure vaccine-induced Ag-specific T cells. ELISPOT or ICS are better. T-cell ELSIPOT for hamsters is available. This should at least be discussed.

Please refer to our response to this Reviewer’s third public comment. We have added the new results in Figure 2F of the revised manuscript.

(5) It is quite interesting that no N-specific cellular response was observed, given that it is a live-attenuated vaccine. What about N-specific binding Abs?

We conducted the ELISPOT assay as suggested by the Reviewer and detected cellular immunity against both spike and nucleocapsid proteins (Figure 2F). We did not examine nucleocapsid-specific antibodies, as they do not contribute to the neutralizing activity; however, nucleocapsid-specific cellular immunity was confirmed.

(6) Figure 3: limit of detection for virological assays could be labeled.

We have added the LOD in Figures 3C, D, F and G.

(7) Figures 3E-F: it is interesting to see that the vaccine elicits almost complete protection at URT against BA.5, despite no BA.5 neutralizing titers being detected at all. What mechanism of URT protection by BK2102 would the authors speculate? T cells or other Ab effector functions?

Please refer to the response to this Reviewer’s third public comment. We have added new results regarding cellular and mucosal immunity (Figure 2F and Supplementary figure 2B) and discussed the mechanisms of protection in the upper respiratory tract in the absence of detectable neutralizing antibodies (lines 136-139, 143-145 and 283-295, respectively).

(8) Figure 3I: the durability of protection is a strength of the study. Other than body weight changes, what about viral loads in the animals after the challenge?

We primarily assessed the effect of the vaccine by monitoring changes in body weight, as the differences compared to the naïve group were clear. Unfortunately, we did not collect samples at different time points throughout the study, which prevented us from evaluating the viral titers.

In addition, we made corrections to several other sections identified during the revision process. The revised parts are as follows:

- In the Methods section under the title “Evaluation of BK2102 pathogenicity in hamsters”, the infectious virus titer of D614G strain has been corrected (line 478).

- In the Methods section under the title “In vivo passage of BK2102 in hamsters”, infectious virus titer of BK2102 and A50-18 strain has been corrected (line 487).

- The collection time of splenocytes after inoculation has been corrected in the figure legend of Figure 2D, (line 583).

- There was an error in Figure 2D. The figure has been replaced with the appropriate version.

- A new reference on NSP1 deletion (Ueno et al., Virology, 2024) has been added to the references.

- Several methods have been described more clearly.

eLife Assessment

In this important study, the authors investigate the biogenesis of extracellular vesicles in mycobacteria and provide several observations to link VirR with vesiculogenesis, peptidoglycan metabolism, lipid metabolism, and cell wall permeability. The authors have done a commendable job of comprehensively examining the phenotypes associated with the VirR mutant using various techniques. The evidence presented in the revised manuscript is convincing and creates several avenues for further research.

Reviewer #1 (Public Review):

Summary:

The present study's main aim is to investigate the mechanism of how VirR controls the magnitude of MEV release in Mtb. The authors used various techniques, including genetics, transcriptomics, proteomics, and ultrastructural and biochemical methods. Several observations were made to link VirR-mediated vesiculogenesis with PG metabolism, lipid metabolism, and cell wall permeability. Finally, the authors presented evidence of a direct physical interaction of VirR with the LCP proteins involved in linking PG with AG, providing clues that VirR might act as a scaffold for LCP proteins and remodel the cell wall of Mtb. Since the Mtb cell wall provides a formidable anatomical barrier for the entry of antibiotics, targeting VirR might weaken the permeability of the pathogen along with the stimulation of the immune system due to enhanced vesiculogenesis. Therefore, VirR could be an excellent drug target. Overall, the study is an essential area of TB biology.

Strengths:

The authors have done a commendable job of comprehensively examining the phenotypes associated with the VirR mutant using various techniques. Application of Cryo-EM technology confirmed increased thickness and altered arrangement of CM-L1 layer. The authors also confirmed that increased vesicle release in the mutant was not due to cell lysis, which contrasts with studies in other bacterial species.

Another strength of the manuscript is that biochemical experiments show altered permeability and PG turnover in the mutant, which fits with later experiments where authors provide evidence of a direct physical interaction of VirR with LCP proteins.

Transcriptomics and proteomics data were helpful in making connections with lipid metabolism, which the authors confirmed by analyzing the lipids and metabolites of the mutant.

Lastly, using three approaches, the authors confirm that VirR interacts with LCP proteins in Mtb via the LytR_C terminal domain.

Altogether, the work is comprehensive, experiments are designed well, and conclusions were made based on the data generated after verification using multiple complementary approaches.

Weaknesses:

The major weakness is that the mechanism of VirR-mediated EV release remains enigmatic. Most of the findings are observational and only associate enhanced vesiculogenesis observed in the VirR mutant with cell wall permeability and PG metabolism. Authors suggest that EV release occurs during cell division when PG is most fragile. However, this has yet to be tested in the manuscript-the AFM of the VirR mutant, which produces thicker PG with more pore density, displays enhanced vesiculogenesis. No evidence was presented to show that the PG of the mutant is fragile, and there are differences in cell division to explain increased vesiculogenesis. These observations, counterintuitive to the authors' hypothesis, need detailed experimental verification.

Transcriptomic data only adds a little substantial. Transcriptomic data do not correlate with the proteomics data. It remains unclear how VirR deregulates transcription. TLCs of lipids are not quantitative. For example, the TLC image of PDIM is poor; quantitative estimation needs metabolic labeling of lipids with radioactive precursors. Further, change in PDIMs is likely to affect other lipids (SL-1, PAT/DAT) that share a common precursor (propionyl- CoA).

The connection of cholesterol with cell wall permeability is tenuous. Cholesterol will serve as a carbon source and contribute to the biosynthesis of methyl-branched lipids such as PDIM, SL-1, and PAD/DAT. Carbon sources also affect other aspects of physiology (redox, respiration, ATP), which can directly affect permeability and import/export of drugs. Authors should investigate whether restoration of the normal level of permeability and EV release is not due to the maintenance of cell wall lipid balance upon cholesterol exposure of the VirR mutant.

Finally, protein interaction data is based on experiments done once without statistical analysis. If the interaction between VirR and LCP protein is expected on the mycobacterial membrane, how SPLIT_GFP system expressed in the cytoplasm is physiologically relevant. No explanation was provided as to why VirR interacts with the truncated version of LCP proteins and not with the full-length proteins.

Comments on revisions:

The authors have addressed my comments. I have no further issues.

Reviewer #2 (Public Review):

Summary:

In this work, Vivian Salgueiro et al. have comprehensively investigated the role of VirR in the vesicle production process in Mtb using state-of-the-art omics, imaging, and several biochemical assays. From the present study, authors have drawn a positive correlation between cell membrane permeability and vasculogenesis and implicated VirR in affecting membrane permeability, thereby impacting vasculogenesis.

Strengths:

The authors have discovered a critical factor (i.e. membrane permeability) that affects vesicle production and release in Mycobacteria, which can broadly be applied to other bacteria and may be of significant interest to other scientists in the field. Through omics and multiple targeted assays such as targeted metabolomics, PG isolation, analysis of Diaminopimelic acid and glycosyl composition of the cell wall, and, importantly, molecular interactions with PG-AG ligating canonical LCP proteins, the authors have established that VirR is a central scaffold at the cell envelope remodelling process which is critical for MEV production.

Comments on the revision.

Authors have addressed the concerns, specifically regarding the expression of downstream genes. It appears that they are not altered significantly.

Data in Fig 6C shows significantly higher expresssion of VirR compared to control or knock down. In the absence of using a regulatable expression such as nitrile, this is expected from a constitutive promoter.

I have no further questions for the author.

Author response:

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

Comments on the revised version:

Concerns flagged about using CRISPR -guide RNA mediated knockdown of viral has yet to be addressed entirely. I understand that the authors could not get knock out despite attempts and hence they have guide RNA mediated knockdown strategy. However, I wondered if the authors looked at the levels of the downstream genes in this knockdown.

We thank the reviewer for bringing this up since it is known that certain artifacts derived from this approach may be related with changes in expression of downstream genes. We run a qPCR of Rv0432 and Rv0433 and confirmed that no significant differences in expression of virR downstream genes were detected in the virR mutant or the complemented strains relative to WT. This is now indicated in the method section on Generation of the CRISPR mutants. The data is now presented as Supplementary Figure 13.

Authors have used the virmut-Comp strain for some of the experiments. However, the materials and methods must describe how this strain was generated. Given the mutant is a CRISPR-guide RNA mediated knockdown. The CRISPR construct may have taken up the L5 loci. Did authors use episomal construct for complementation? If so, what is the expression level of virR in the complementation construct? What are the expression levels of downstream genes in mutant and complementation strains? This is important because the transcriptome analysis was redone by considering complementation strain. The complemented strain is written as virmut-C or virmut-Comp. This has to be consistent.

We apologize for not having included the information about the generation of the complemented strain in our last version of the manuscript. We took the complementing vector from a previous paper on VirR (Rath et al., (2013) PNAS 110(49):E4790). This vector was constructed as follows: Complementation plasmids were cloned using Gateway® Cloning Technology (Invitrogen). E. coli strains expressing the following Gateway vectors were kindly provided by Dirk Schnappinger and Sabine Ehrt: pDO221A, pDO23A, pEN23A-linker1, pEN41A-TO2, pEN21A-Hsp60, pDE43-MEH. PCR was used to amplify the following target sequences from H37Rvgenomic DNA: coding sequence of Rv0431, coding sequence of Rv0431 with a FLAG tag either in its C-terminus or its N-terminus, and the predicted cytosolic sequence of Rv0431 with a FLAG tag in its new C-terminus. The primers used for PCR were designed such that the amplicons would be flanked with Gateway® cloning- specific attachment (att) sites. These PCR products were recombined into Gateway® donor vectors using bacteriophage-derived integrase and integration host factor, resulting in entry vectors. The recombination events are specific to the attB sites on the PCR products and to the attP sequences on the donor vectors, such that the orientation of the target sequence is maintained during the recombination reaction, also known as the BP reaction, for attB-attP recombination. Using the MultiSite Gateway® system, three DNA fragments, derived from each of three distinct entry vectors, can be simultaneously inserted into a final complementation vector called the destination vector in a specific order and orientation. Multisite recombination events are mediated by Integrase and Integrase Host Factor, in a process called the LR reaction (for the attL and attR sites in the entry and destination vectors). The Gateway® entry vectors thus generated were recombined with another entry vector containing either the Hsp60 promoter, an empty entry vector, and a complementation vector (episomal) to give rise to the final destination vector. The destination vector (episomal) was engineered to contain a hygromycin resistance cassette. These vectors were used to transform competent Rv0431-deficient Mtb. The transformation mixture was plated on 7H11 plates containing OADC and hygromycin (50 μg/ml). Colonies, typically observed 3-5 weeks later, were isolated and grown in 7H9 media and characterized.

For simplicity, we have just referenced our previous paper to indicate that the complementing plasmid is the same used in that study.

Regarding the virR expression levels in the WT, virR^mut and complemented virR strains please see previous Figure 6 C.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have revised the manuscript in light of previous reviews. The authors have addressed some of my concerns appropriately. However, the specific dataset remains unchanged and unclear.

Fig 8G and H: In response to a comment on the mechanism of how VirR mediates EV release, the authors have added new data showing an increase in the abundance of deacetylated muropeptides in the mutant. This observation is linked to altered lysozyme activity or PG fragility. In my opinion, this is another indirect observation. More concerning is the complemented strain, which also showed a comparable increase in deacetylated muropeptides, indicating that the altered muropeptides could be unrelated to VirR.

We must disagree here with the reviewer assessment about the fact that the abundance of deacetylated muropeptides is an indirect indication of PG fragility. We consider that this observation and quantitative fact is another additional evidence that indicate a more fragile PG. We believe that considering each of the supporting facts individually may be seen as indirect, but we would like that the reviewer take all the evidence together: (i) sensitivity to lysozyme; (ii) enlargement and altered physicochemical morphological characteristics including porosity or thickness; (iii) altered penetrance of FDAAs; and (iv) increased released of muropeptides. In this later fact, the complemented strain may not display the WT features, but this may be due to some artifacts derived from the complementation.

Taking all together, we believe that the PG of virR^mut is more fragile than that of the WT and the complemented strains based on a series of evidence. We hope the reviewer may consider this perspective when analyzing such a complex feature like PG fragility. So far, there is not a direct method to assess this condition.

Lipid analyses are not comprehensive. The issue related to the need for more clarity of DIMA and DIMB still needs to be addressed. I understand that the authors do not have facilities to perform radioactive assays. However, they could have repeated the experiment to generate a better-quality image. Similarly, the newly generated SL-1, PAT, and DAT TLC could be of better quality. Bands still need to be resolved. The solvent front is irregular. The same is true for PIMs and DPG TLCs. With the evidence provided, the deregulation of cell wall lipids is incomplete.

We agree with the reviewer that the quality of the TLC is not appropriate. We have no repeated the PDIM TLC (new Fig 7D). In addition, we have repeated the TLCs resolving sulfolipids in a 2D mode. For simplicity we just run the glycerol condition including the three strains. This is now part of a new Supplementary figure 8 B. For PIMs, we have a 1D and a 2D analysis that, after checking previous papers using similar approaches with no radioactivity, we consider that it has the desired quality to identify the indicated lipids.

We hope this new data and repeated experiments satisfy the reviewer concerns.

Thank you very much for your assessment and time to review this paper.