Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This foundational study builds on prior work from this group to reveal the complexities underlying ligand-dependent RXRγ-Nur77 heterodimer formation, offering a compelling re-evaluation of their earlier conclusions. The authors examine how a library of RXR ligands influences the biophysical, structural, and functional properties of Nur77. They find that although the Nur77-RXRγ heterodimer shares notable functional similarities with the Nurr1-RXRα complex, it also exhibits unique features, notably, both dimer dissociation and classical agonist-driven activities. This work advances our understanding of the nuanced behaviors of nuclear receptor heterodimers, which have important implications for health and disease.

Strengths:

(1) Builds on previous work by providing a comprehensive analysis that examines whether Nur77-RXRγ heterodimer formation parallels that of the Nurr1-RXRα complex.

(2) Systematic evaluation of a library of RXR ligands provides a broad survey of functional outputs.

(3) Careful reanalysis of previous work sheds new light on how NR4A heterodimers function.

We thank the reviewer for recognizing our work as foundational. In the nuclear receptor field, current understanding of ligand-regulated nuclear receptor activity is based largely on ligand-dependent coregulator recruitment preferences; for example, agonists enhance coactivator recruitment to activate transcription. Building on our recent study of Nurr1-RXRα, the present work suggests that activation of the evolutionarily related NR4A-RXR heterodimer Nur77-RXRγ by RXR ligands is also consistent with a non-classical activation mechanism involving heterodimer dissociation.

Weaknesses:

(1) Some conclusions appear overstated or are not well substantiated by the work presented. It's unclear how the data support a non-classical mode of agonism, for example, based on the data shown.

We thank the reviewer for this important point. We did not intend to claim that Nur77-RXRγ activation is explained exclusively by a non-classical mode of agonism. Rather, our interpretation was that the data are consistent with two possible, non-mutually exclusive mechanisms: (1) a classical pharmacological mechanism involving ligand-dependent coregulator recruitment; and (2) a non-classical mechanism involving ligand-binding domain (LBD) heterodimer dissociation, as we previously described for Nurr1-RXRα. This differs from our prior eLife study of Nurr1-RXRα, in which the data supported the LBD heterodimer dissociation model but not the classical pharmacological model.

In our revised manuscript, we clarify two points that are important for interpreting the Nur77-RXRγ data. First, several experimental limitations of the Nur77-RXRγ studies reduced the extent to which the mechanism could be resolved as rigorously as in our earlier Nurr1-RXRα study. Second, and more importantly, the currently available ligand set lacks Nur77-RXRγ-selective agonists. This limits our ability to determine whether LBD heterodimer dissociation is the sole or principal mechanism of activation, or instead one of several contributing mechanisms.

Taken together, these results support LBD heterodimer dissociation as a plausible and experimentally observable component of Nur77-RXRγ activation and, therefore, as a candidate shared activation mechanism for NR4A-RXR heterodimers. At the same time, because the quantitative evidence is less definitive than in the Nurr1-RXRα system, we agree that conclusions regarding Nur77-RXRγ should be stated more cautiously. This caution is reflected in both the title of our manuscript (“Towards a unified mechanism…”) and the language used throughout the text.

(2) Some assays have relatively few replicates, with only two in some cases.

We thank the reviewer for their attention to experimental rigor. For some assays, the findings were reproduced in two independent experiments, which we considered sufficient to confirm the presence and reproducibility of the effects observed in those particular assay formats. In the original manuscript, we used a general statement in the figure legends (“representative of two or more independent experiments”) across all assay data. In the revised manuscript, we now specify the number of independent experimental replicates for each assay in the corresponding figure legends to improve transparency.

Reviewer #2 (Public review):

Summary:

This study explores the mechanisms by which binding of the nuclear receptor RXRg regulates its heterodimeric partner Nur77. Previously, this group made the interesting discovery that ligand-dependent activation of RXRg bound to a related partner, Nurr1, does not occur through a classical pharmacological mechanism but through agonist-dependent dissociation of the complex through disruption of their ligand binding domain (LBD) interactions. Here, they revisit this paradigm with Nur77. In contrast to Nurr1, the authors do not have the reagents to clearly support a role for LBD dissociation. Following the model of partial ligand-dependent dissociation of the LBD heterodimer, the experimental data (NMR, ITC, SEC) are interesting and quite complex.

Strengths:

The authors do a rigorous job of describing the data and providing possible interpretations and caveats. Revisiting the analysis of Nurr1, they identify the crucial role that selective Nurr1-RXRg agonists played in supporting the LBD dissociation model; without analogous compounds for the Nur77-RXRg complex, it is difficult to invoke this mechanism. Interestingly, treatment with the Nurr1-RXRg selective agonist HX600 suggests it can induce some LBD dissociation. Therefore, there may be some similarities between the regulation of Nurr1 and Nur77 by RXRg.

We thank the reviewer for this thoughtful and balanced summary of our work. We appreciate the reviewer’s recognition of both our prior findings in the Nurr1-RXRα system and the interesting, but more complex, experimental behavior observed here for Nur77-RXRγ. We agree that the absence of Nur77-RXRγ-selective agonists currently limits how definitively the contribution of LBD dissociation can be resolved, and we have revised the manuscript to make this point more explicit and to further temper our conclusions accordingly.

Weaknesses:

Despite evidence supporting a partial role for RXRg LBD dissociation as a mechanism to activate Nur77, other data demonstrate that a fundamentally different regulatory mechanism likely exists in the Nur77-RXRg complex that involves the RXRg disordered NTD. The decision to describe further study of this as outside the scope of this work is unfortunate, as it closed off an avenue that could have provided fruitful data informing the apparently distinct regulatory mechanisms of the Nur77-RXRg complex. Given the uncertainty in the importance of the partial roles of the pharmacological mechanism, LBD dissociation, and the RXRg NTD, this study may have limited impact on the field.

We thank the reviewer for this thoughtful point. We agree that the RXRγ NTD likely contributes to regulation of Nur77-RXRγ transcription, and that our truncation data suggest that regions outside the LBD can influence transcriptional output. At present, however, the effect of RXRγ NTD truncation is not sufficiently mechanistically resolved to distinguish among several plausible explanations.

For example, the RXRγ NTD has been implicated in phase separation and biomolecular condensate formation in cells (PubMed ID 40392852, 40420113, 33971237, 31881311), and perturbing these properties (via RXRγ NTD truncation) could indirectly affect Nur77-RXRγ transcriptional activity. In addition, NTDs of nuclear receptors can participate in coactivator or corepressor interactions (PubMed ID 24284822), raising the possibility that removal of the RXRγ NTD alters transcription by changing recruitment of regulatory factors rather than by directly informing the LBD-centered mechanism examined here. We will clarify in the revised manuscript that these possibilities remain unresolved and represent important directions for future study.

We also agree that defining how multiple RXRγ domains contribute to Nur77-RXRγ regulation would be valuable for the field. However, the focus of the present study is narrower: to test whether, as in our previous eLife study of Nurr1-RXRα, RXR ligands can influence heterodimer function through effects on LBD-LBD interactions. Because the available data do not yet allow a mechanistic dissection of the RXRγ NTD contribution, we believe that a definitive analysis of this question would require a separate set of experiments beyond the scope of the present work. We have revised the manuscript to better acknowledge this limitation and to frame the conclusions accordingly.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Overall, this is a compelling body of work. Additional summary statements and clearer transitions would be helpful throughout.

Here are some points that should be addressed or at least discussed by the authors:

(1) It is unclear in the luciferase assays whether the truncated proteins are functional or not. Were there Western blots or other assays run to confirm protein concentrations?

We thank the reviewer for this point. We did not perform Western blotting or other assays to confirm equivalent expression levels of the truncated RXRγ constructs, and we agree that this is a limitation of the luciferase assay data. As a result, the transcriptional effects observed with the truncation constructs should be interpreted cautiously.

With that said, the increased transcriptional activity observed upon deletion of the RXRγ NTD/AF-1 region suggests that this region may exert a repressive effect on Nur77-RXRγ transcription. This effect could reflect multiple, non-mutually exclusive mechanisms, including altered phase separation or condensate-related properties of RXRγ, or altered recruitment of transcriptional coregulators through the NTD. Because our truncation strategy does not distinguish among these possibilities, we do not believe these data allow a definitive mechanistic interpretation of the NTD contribution.

We have revised the manuscript to clarify this limitation. We also note that the primary focus of the present study is the role of ligands in modulating Nur77-RXRγ function through LBD-mediated interactions, in direct comparison with our previous Nurr1-RXRα study. A more complete mechanistic dissection of how RXRγ domain architecture influences Nur77-RXRγ transcription will require future work.

(2) Why does the Nur77 construct lacking the NTD show increased luciferase activity?

Please see our response above to Reviewer 2’s Public Review, which also addresses this point.

(3) A case is made for the Nur77 LBD driving the activity, but it also could be inferred that the DBD is driving based on the data shown in Figure 1.

We thank the reviewer for this point. We agree that the Nur77 DBD is required for binding to NBRE response elements, and we did not intend to suggest otherwise. The experimental approach in Figure 1 was not designed to dissect the relative contributions of Nur77 domains, since Nur77 was tested only in its full-length form. Instead, the purpose of this experiment was to examine how truncation of RXRγ domains affects Nur77-RXRγ transcriptional activity, in direct comparison with our prior eLife study of Nurr1-RXRα, where RXRα domain truncations helped define the importance of RXR-LBD-mediated regulation. We will revise the text to clarify that Figure 1 does not distinguish whether Nur77 DBD-dependent DNA binding is necessary, but instead addresses whether the pattern of RXRγ domain dependence is consistent with an LBD-centered mechanism of ligand-regulated heterodimer function.

(4) It is stated that the HX600 coactivator recruitment requires further study. Why wasn't it studied here?

We thank the reviewer for this point. The primary focus of this study was to determine how RXR ligands influence Nur77-RXRγ heterodimer activity, particularly in relation to ligand-dependent effects on heterodimer function. A more detailed analysis of HX600-dependent coactivator recruitment would require a broader mechanistic investigation of RXRα and RXRγ homodimer pharmacology and RXR-specific coregulator interactions, which extends beyond the central scope of the present manuscript. We agree that this is an important question and view it as a valuable direction for future work.

(5) Figure 3B, the shifts in monomer populations, error bars aren't shown, the biggest shift is from 0.2 to 0.6, is that statistically meaningful?

We thank the reviewer for this point. The reviewer is correct that error bars were not shown for Figure 3B. These NMR measurements were performed once (n=1), and therefore the shifts in monomer populations shown in Figure 3B cannot be assessed statistically. Because these studies required substantial NMR instrument time and isotopically labeled protein at high concentration, we were not able to perform experimental replicates for this dataset. We have revised the figure legend to explicitly state that these data were collected from a single experiment and have tempered the corresponding language in the manuscript accordingly.

(6) Some ligands are shown in the figures but don't appear to be discussed in the text (at least that I can find), such as SR11237.

We thank the reviewer for pointing this out. We used a panel of 14 commercially available RXR ligands with different pharmacological properties to probe Nur77-RXRγ function, as in our previous Nurr1-RXRα study. In the text, we emphasized ligands that were most informative for the mechanistic conclusions, rather than discussing every compound individually. SR11237, for example, behaved similarly to the broader group of RXR agonists and was therefore shown as part of the full ligand panel but not specifically highlighted in the text. We will clarify this in the revised manuscript.

(7) There is a sentence in the discussion that says "these observations implicate that although RXRg LBD provides the protein-protein interaction interface to bind Nur77...." the authors did not show enough data to support this claim. It should be bolstered.

We thank the reviewer for this point. We agree that this statement was stronger than was warranted by the data presented. Our intent was not to claim that the present study definitively establishes the RXRγ LBD as the sole or fully defined protein-protein interaction interface for Nur77 binding. Rather, based on the domain truncation data together with our prior Nurr1-RXRα study, we intended this statement as a working interpretation consistent with an LBD-centered mechanism. In our revised manuscript, we have softened this language to avoid overstating the conclusion and clarified that the current data support, but do not definitively prove, a role for the RXRγ LBD in mediating functionally relevant interaction with Nur77.

Reviewer #2 (Recommendations for the authors):

Even though this study is not able to make definitive claims about the mechanism(s) of activation of Nur77 in the Nur77-RXRg complex, the work presented here is rigorous and solidly interpreted. Identifying differences between Nurr1 and Nur77 regulation is important, and the work here shows that selective agonists are essential for supporting the non-canonical mechanism they identified before. Although they address potential implications of NTD regulation in the discussion, it feels like a lot of insight into Nur77 regulation is being missed. However, it is clear that addressing this experimentally would require substantially more work. I don't have any specific recommendations. Given current limitations on funding, I think it's fine to focus on the work completed with the acceptance that it likely limits the impact of the work on the field.

We thank the reviewer for this thoughtful and balanced assessment of our work. The goal of this manuscript was to test whether the LBD heterodimer dissociation mechanism that we previously reported for Nurr1-RXRα may represent a conserved feature of NR4A-RXR heterodimers by extending these studies to Nur77-RXRγ. We agree that understanding the role of the RXRγ NTD in Nur77-RXRγ regulation is important and potentially highly informative. At the same time, resolving that question experimentally would require a distinct and more extensive set of studies beyond the scope of the present work. We have therefore chosen to focus this manuscript on the completed LBD-centered studies, while acknowledging that this narrower scope may limit the broader impact of the work.

Minor points:

(1) Without page and line numbers, it is not easy to point out specific text. On the bottom of page 6 of the document, there are two references to Figure 3a, and the arrows that help illustrate RXRg LBD-dependent CSPs; the second figure callout should describe the blue arrow, I believe.

Thank you, we made this change.

(2) Bottom of page 8, "...revealed two compounds [that] standout..."

Thank you, we made this change.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

We truly appreciate all the effort that the reviewer put into reading and understanding our work. With a total of 37 excellent questions, this is one of the most thorough reviews that we have received in a long time.

R1.0: Summary:

In this study, the authors propose a "unifying method to evaluate inter-areal interactions in different types of neuronal recordings, timescales, and species". The method consists of computing the variance explained by a linear decoder that attempts to predict individual neural responses (firing rates) in one area based on neural responses in another area.

The authors apply the method to previously published calcium imaging data from layer 4 and layers 2/3 of 4 mice over 7 days, and simultaneously recorded Utah array spiking data from areas V1 and V4 of 1 monkey over 5 days of recording. They report distributions over "variance explained" numbers for several combinations: from mouse V1 L4 to mouse V1 L2/3, from L2/3 to L4, from monkey V1 to monkey V4, and from V4 to V1. For their monkey data, they also report the corresponding results for different temporal shifts. Overall, they find the expected results: responses in each of the two neural populations are predictive of responses in the other, more so when the stimulus is not controlled than when it is, and with sometimes different results for different stimulus classes (e.g., gratings vs. natural images).

Strengths:

(1) Use of existing data.

(2) Addresses an interesting question.

R1.1: Unfortunately, the method falls short of the state of the art: both generalized linear models (GLMs), which have been used in similar contexts for at least 20 years (see the many papers, both theoretical and applied to neural population data, by e.g. Simoncelli, Paninsky, Pillow, Schwartz, and many colleagues dating back to 2004), and the extension of Granger causality to point processes (e.g. Kim et al. PLoS CB 2011). Both approaches are substantially superior to what is proposed in the manuscript, since they enforce non-negativity for spike rates (the importance of which can be seen in Figure 2AB), and do not require unnecessary coarse-graining of the data by binning spikes (the 200 ms time bins are very long compared to the time scale on which communication between closely connected neuronal populations within an area, or between related areas, takes place).

First, a few points of clarification.

(i) We worked with two-photon calcium imaging data (mice), and with the envelope of multi-unit activity (monkeys). While both of these types of signals are strongly correlated with spikes, neither of them can be truly considered to be a point process.

(ii)The reviewer points to Figure 2AB. The signals that we worked with can be negative. The black traces are the actual signals and show clear negative bouts, especially noticeable in the middle panel in Figure 2B. Of course, this does not mean that there are negative spike rates. This has to do with the way the data are normalized and not with the specific prediction method. However, the reviewer is correct in stating that the method that we used could also yield negative values even for non-negative spike rates.

(iii) We did not bin the macaque data into 200-ms time bins, but rather 25-ms time bins (line 548, Figure 1B legend). Additionally, we have now performed additional analyses with different window sizes, showing that the conclusions still hold (see Supplemental Figure 4 and lines 139-143).

To further address the reviewer’s question, we implemented a Poisson GLM enforcing non-negativity on macaque MUAe data (without spontaneous activity subtraction, ensuring strictly positive values; lines 135-139, Supplemental Figure 1M). The model did not improve predictions over ridge regression, confirming our methodological choice. This method is not directly applicable to mouse calcium data, since the activity after baseline subtraction can be negative.

We did not use Granger or any other causality methods. The question of causality is certainly important, and there are multiple methods developed to assess causality in neural signals. We do not make any claims about causality in our study. A rigorous evaluation of causality is an interesting line of research for future work.

R1.2: In terms of analysis results, the work in the manuscript presents some expected and some less expected results. However, because the monkey data are based on only one monkey (misleadingly, the manuscript consistently uses the plural ‘monkeys’), none of the results specific to that monkey, nor the comparison of that one monkey to mice, are supported by robust data.

We have now added data from 2 additional monkeys, including:

(i) A second monkey (monkey “A”) from the same dataset (Chen et al., 2020), which includes all activity types except the lights off condition (lines 90-96, 120-132, 159, 161, 171, 183-185, 188-194, 200-203, 228-237, 254-258, 292-296, 334-342, 351-353, 358-364, 374-378, 387-393, 400-408, 414, 417-421, 539-540, 544-545, 680-681, 696-698; Supplemental figures 1-6, 8, 11, 12, and 13; Table 2).

(i) We collected new neural activity from one additional monkey (monkey “D”) in collaboration with the Ponce lab (lines 90-96, 120-130, 132-134, 163-164, 228-235, 237-243, 292-296, 351-353, 374-378, 387-389, 539-540, 553-560, 696-698; Supplemental figures 1-2, 4, 6, 9, 11, and 12; Table 2). The new data include responses to the same checkerboard and gray screen images as the original dataset, along with responses during lights-off conditions.

R1.3: One of the main results for mice (bimodality of explained variance values, mentioned in the abstract) does not appear to be quantified or supported by a statistical test.

We have now formally quantified the bimodality of the relationship between one-vs-rest correlation and inter-laminar explained variance (EV) in mice using Hartigan’s dip test, applied to neurons with EV>0.4. The test confirmed significant bimodality in two of the three mice (MP031 and MP032: p<0.001; MP033: p=0.687). These results are now included in the Results section (lines 307-311) and shown in Supplemental Figure 7A,D. In datasets that did not show bimodality by visual inspection (macaque recordings), the same test yielded non-significant results (e.g., p=0.994), confirming that the statistical analysis distinguishes between bimodal and unimodal cases.

R1.4: Moreover, the two data sets differ in too many aspects to allow for any conclusions about whether the comparisons reflect differences in species (mouse vs. monkey), anatomy (L2/3-L4 vs. V1-V4), or recording technique (calcium imaging vs. extracellular spiking).

We also agree with this comment. Our goal is not to provide any direct quantitative comparison between the two species. We emphasize (lines 494-497) that the experiments in the two species differ along multiple dimensions, including: (i) differences in recording modalities (calcium vs. electrophysiology), (ii) associated differences in temporal resolution, neuronal types, and SNR, (iii) cortical targets (layers vs. areas), (iii) sample size, (iv) stimuli, (v) task conditions. In the revised manuscript, we also emphasized that the aim of this work is to investigate inter-areal interactions within each species rather than to draw quantitative comparisons between species (lines 497-499).

Reviewer #1 (Recommendations for the authors):

R1.5 In the analysis of directionality, you stated that subsampling was done randomly. Presumably, there could be multiple subsamples that fulfill the control of split-trial r. Are you only showing results from one subsample or multiple subsamples?

We show the median from 10 subsample permutations. This is now clarified in line 621.

R1.6 About the measurement 1-vs-rest r2. Understanding the definition is important for interpreting the results, but the definition was not clearly written. In lines 195-196, could you be more clear about whether the correlation is between the predicted neuron and other neurons in the predicted population or between the predicted neuron and the mean activity of the predictor population? Also, in line 212, why do you call this self-consistency? Isn't this a correlation between a neuron and the others?

The 1-vs-rest r² value, or self-consistency, is the correlation calculated for each neuron i and does not involve other neurons. Let indicate the response 𝑟 of neuron i during trial t (t=1,..., T where T is the total number of trials). For a given trial t, we compute the average activity of the neuron excluding this trial:

Throughout, the superscript (rest)means “all repetitions excluding repeat 𝑡”. The one-vs-rest correlation for the held-out repetition 𝑡 is:

We then average these correlations across all held-out repetitions:

We now clarify this in the text (lines 304-306 and lines 642-647).

R1.7 In Figure 6 G and I. The "all" condition contains more neurons than either of the other two. In this case, is this comparison fair or meaningful?

The reviewer is also correct here. The comparisons between the <10% and >80% groups contain the same number of predictor neurons, and those are fair comparisons. The “all” condition contains more predictor neurons, and, therefore, those comparisons are not fair. We clarified this point in lines 360-364.

We included the “all” condition here because we think that it is an instructive sanity check in terms of reporting how EV changes with more neurons, and also in terms of understanding why the EV values in the other two conditions are lower. Expanding on this point with a little bit of philosophy, ultimately, when considering a neuron in area B (e.g., V4) and the contributions from neurons in another area A (e.g., V1), one would like to have access to all the inputs (e.g., all the neurons in V1 that are monosynaptically connected to the target neuron in area V4). We do not have access to this type of information, and we do not make any claims about monosynaptic connectivity, let alone exhaustive sampling of inputs to a given neuron. The “all” condition merely provides a quantitative illustration of the fact that EV increases with the number of predictor neurons. This observation may be considered to be somewhat trivial, but it should be pointed out that the conclusion relies on the input neurons sharing information with the target neurons (e.g., perhaps one may not be able to predict V4 activity very well from the responses of millions of neurons in the cerebellum).

R1.8 I believe the results section can be improved by adding some interpretation after each finding.

We thank the reviewer for the suggestion. We generally like to separate results from interpretation. However, to honor the suggestion, we added brief interpretations throughout the results section (lines 142-143, 171-173, 272-273, 279-281, 331-333, and 361-364) and expanded on the interpretations in the Discussion section.

R1.9 Line 52 - 74: It would be better to be more specific about what kind of neuronal interactions, e.g., noise correlation, synchrony, etc.

We added a clarification on the types of interactions we study in lines 68-73.

R1.10 Line 81. Something seems to be missing after "5500". 5500 trials? Neurons?

We thank the reviewer for pointing this out. The number refers to neurons (fixed in line 87).

R1.11 Line 94. The readers would appreciate more explanation of the method.

We have expanded on the explanation, as suggested (lines 106-107).

R1.12 Line 104. The fraction of visually responsive neurons seems to be small. Is this typically for mouse V1? Would this fraction be higher if you also used the peak, as you did for macaque data in your SNR calculation (line 412)? And what is this number for the recorded L4?

The reviewer correctly points out the small number of visually responsive neurons.

We note that we now refer to the subset of neurons used for prediction analyses as visually reliable (VR) neurons (lines 115-116, 125-126, 178-179, 183-184, 211-212, 214-216, 217-226, 283-286), defined conservatively as neurons with SNR > 2 computed from the mean across all stimuli (not the peak to any one stimulus) and split-half reliability >0.8 (Methods, lines 569–590). This choice emphasizes neurons that are consistently informative over the full stimulus set.

Regarding the question of how typical the number of responsive neurons in mice is, the fraction of “responsive” neurons in mouse V1 varies widely depending on the definition and stimulus set but the fractions are substantially lower than those reported in monkeys (with different methods). For those of us more used to the macaque neurophysiology literature, this has been one of the biggest surprises coming from work in rodents. Many studies report a sizable group of non-responsive neurons in mouse V1 (e.g., as little as 37% percent of V1 neurons being responsive in at least 25% of the trials according to de Vries et al., Nat Neur, 2020). Our fraction of visually responsive neurons is small because it couples a conservative SNR metric with a high trial-reliability threshold.

As the reviewer notes, a peak-based metric based on any stimulus would be a less conservative criterion that would increase the fraction of neurons labeled responsive.

R1.13 Line 113. Why not also give an exact percentage number?

We have given the exact percentage number (lines 125-126).

R1.14 Line 128. Is this just because L2/3 has more neurons? If so, then isn't this trivial?

Our intention was to illustrate the best prediction performance we could get in either direction, which means including all L2/3 neurons. We have reworded our text to clarify (lines 149-151).

R1.15 Line 134. Isn't this expected? Since V1 have more units than V4?

The reviewer is correct. As discussed in R1.7 in mice, we sought to report the best prediction performances in either direction. We have edited our text for clarity (lines 149-151).

R1.16 Line 165-168. What's the logical connection between these two sentences? If the former is true, we should expect to see differences. Also, why the same population? Shouldn't you include non-visual neurons?

The two sentences in question are: “The difference in predictability in the absence of a stimulus could in principle change according to the directionality in inter-laminar interactions.” and, “There was no statistically significant difference in the EV fraction between laminar directions (L4→L2/3 vs. L2/3→L4) using the same control population as in Figure 3B (Figure 5A-C and Figure Supplement 2H).”. The key point here was to control for similar reliability values in order to make fair comparisons. We have added an additional comparison between directionalities focusing on nonvisual neurons (SNR<2 & r<0.8), and have also found no statistically significant difference between direction of predictability (Supplemental Figure 3A, right, lines 221-224).

R1.17 Table 2. The information of which session corresponds to which experiment can be put in the table, which would be easier to read.

We have added which sessions correspond to which experiments in Table 2.

R1.18 Figure 1, Captions for panel c and d. I don't see any colored arrows in the figure.

We removed the color descriptions (Figure 1C-D).

R1.19 Figures 3, 4, and others. The annotations of "n.s." are very hard to see.

We changed the color so that it is easier to see now (Figures 3, 4, 6, and Supplementary Figures 1-4, 6, and 8-10).

R1.20 Figure 5, panel A. The legend is too small.

We increased the legend size (Figure 5A).

R1.21 Figure S5, panel D. Why are some of the data points connected?

The paired connections are illustrated specifically in the highly predictable neurons to highlight the two separate distributions of neurons. One group, the highly predictable and highly reliable group, maintains its inter-laminar predictability after projecting out the “non-visual” activity (lines 327-330), whereas the highly predictable yet unreliable group shows a sharp decrease in inter-areal predictability, which corroborates the idea of non-visual components influencing neurons in mouse V1, as shown by Stringer et al. 2019b and consistent with our results.

R1.22 l.91 "Ope" -> open?

We fixed the typo (line 100).

R1.23 Fig. 3C+D: Why is only one session used for this?

One session was used to illustrate the distribution of split-half reliability values per area. Figure 3D contains information about all 5 stimulus sessions (see legend to Figure 3D).

R1.24 "Even without controlling for the number of predictors or their respective split-half correlation values (627-688 sites in V1, 86-115 sites in V4), we found better predictability in the V1 to V4 direction than the reverse ( 𝑝 < 0.001, Figure Supplement 2I)." -> What does "even" mean here? Isn't this simply the null result if there is no true difference and the real reason the authors controlled for size?

The reviewer’s understanding is correct. We have edited our text for clarity (lines 157-160)

R1.25 "We could predict V1 and V4 activity across all stimulus types ( 𝑝 < 0.001, paired permutation test of prediction vs. shuffled frames prediction)." -> better than chance? For all neurons on average? What does this mean? Isn't it trivial and 100% expected that neural activity in the visual cortex is above chance related to the visual input?

We stated that sites in V1 and V4 could predict each other across all stimulus types before describing the differences between them. We agree that this observation is to be expected and indicated so now in the text (lines 185-186).

R1.26 "The predictability was the highest in both directions for neuronal activity in response to a full field checkerboard images (Figure 4D). In the V1 → V4 direction, the EV fraction was higher when predicting a slow-moving small thin bar compared to a fast-moving large thick bar (Figure 4D, left), whereas the opposite was true for the V4 → V1 direction (Figure 4D, right)." -> What does this mean? Is this expected or not? Under what theories of cortical processing?

The differences between EV prediction directions (V1→V4: slow thin bars > fast thick bars; V4→V1: fast thick bars > slow thin bars) could be because V4 responses are more reliable for the slow thin bars whereas V1 responses are more reliable for the fast thick bars (Supplemental Figure 5H–I). To account for this possibility, we controlled for differences in target-related properties by regressing out covariates like SNR, split-half correlation, and variance. In monkey L, regressing out reliability/drive within direction using these covariates, the V4→V1 bar difference between slow thin bars and fast thick bars was not significant and the difference in the V1→V4 difference direction was reduced (Supplemental Figure 5K, lines 198-203). This suggests that the asymmetry primarily reflects stimulus‑dependent reliability of the target population rather than a strong directional selectivity.

To the best of our knowledge, there are no clear predictions that match these observations from existing theories of visual cortical processing, especially given the paucity of computational models that include stimulus velocity when describing the responses in area V4. There has been extensive work on theories of surround suppression, but it seems unlikely that the thick bars would elicit surround suppression given the size of the V4 receptive fields. Many current computational models that aim to fit the responses of neurons in the visual cortex use neural networks that take an image as visual input and yield activations. Most of these models do not incorporate stimulus movement, and even those that do incorporate stimulus dynamics, only indirectly map onto interlaminar stimulus transformations or even between-area stimulus transformations. We hope that the results in this manuscript will help inspire and constrain better models of visual cortical processing.

R1.27 Shouldn't all the predictability analysis be done conditioned on the stimulus in order to tell us more than the trivial "both V1 and V3, or L2/3 and L4, are driven by visual inputs"? (The spontaneous activity analyses are essentially that, for a small subset of the stimuli.)

The key goal of this study is to quantify inter-areal interactions both under visual input and without visual input. This type of analysis is important because inter-areal interactions may depend both on visual inputs but also on neuronal inputs that are not triggered by visual signals. For example, extensive work in mice has now shown that neuronal responses in V1 depend on an animal’s running speed, independently of any visual input. Even within the visual input conditions, we present analyses where we shuffle trial order (e.g., Figure 7, Supplementary Figure 11) to estimate the contribution of trial-by-trial variations that are independent of visual inputs and other analyses where we project out non-visual activity (e.g., Supplementary Figure 7).

R1.28 "In visually responsive neurons, there was a significant reduction in EV during gray screen compared to visual stimulus presentation" -> perfectly expected. But the report-worthy result here is how much is left, not whether EV is decreased!

We have changed the wording on the results to highlight the sustained predictability (lines 211-212). It is important to note that, although the reduction in EV during gray screen may be expected, this observation does not hold for all neurons. In fact, there are some neurons for which the EV during visual presentation is comparable to that during gray screen (Figure 5B,C,E: neurons that lie on the diagonal line).

R1.29 "Similar to the conclusions drawn from the mouse data, the predictability of neuronal activity was higher in response to stimulus presentation than to gray screen presentations" -> Really? Conditioned on stimulus, or explainable by the well-known fact that both V1 and V4 are visually driven?

As discussed in R1.28, in mice, there are many neurons where the EV during gray screen is comparable to that during stimulus presentation. In monkeys, most sites were visually driven. As the reviewer points out, we expected that EV during stimulus presentation would be higher than during gray screen; this observation is a reasonable sanity check. The difference between unshuffled trials and shuffled trials (Figure 7, Supplementary Figure 11) provides an estimate of the interactions that are not purely explained by visual inputs alone in monkeys.

R1.30 "Unlike the mouse, macaque correlation of visual predictability between stimulus presentation and spontaneous activity was high across all types of spontaneous conditions" -> Why? Is this simply explainable by a lower mean response in the spontaneous condition in the mouse? Are these mouse and monkey experiments truly comparable? Isn't it surprising that spontaneous activity in the monkey visual cortex compared to evoked activity is higher than in the mouse?

With respect to the question of whether spontaneous activity (or stimulus-evoked activity) in monkeys is higher than in the mouse, it is difficult to make these comparisons. We emphasize in the text the multiple differences between the experiments in both species. Our goal is not to perform any quantitative comparison across species (see R1.4). We changed the wording to remove any inference of comparison between species (lines 248-250).

R1.31 Occasionally imprecise presentation. Ex "To further examine the non-stimulus driven component, we reasoned that if the shared information between areas were strictly driven by the visual stimulus, then using the activity of a stimulus presentation repeat to one specific image could be used to predict the responses to any other stimulus repeat of the same image. On the other hand, if the shared activity does not have any stimulus-response information, then the prediction model would not work when considering responses across repeated presentations of identical stimuli in different trials. To test these two opposing ideas, we compared the inter-areal prediction EV fractions using unshuffled versus shuffled trials." -> Sets up two extreme strawmen (100% driven by stimulus vs 0% driven by stimulus). What does "model would not work" mean? EV=0? Hypotheses not ideas.

Our intent was to set up two extreme hypotheses, not to claim that neurons must fall exclusively into one or the other. The two extremes help better interpret the results.

The reviewer indicates that these are straw-man hypotheses. This may well be the case. But note the responses to R1.12, R1.27, R1.28, and R1.29. The reviewer seems to assume that all or most neurons in the visual cortex should be mostly or exclusively driven by visual stimuli.

We also replaced “ideas” with “hypotheses”, as suggested. We have expanded the discussion of these points in the manuscript (lines 480-493). Many neurons occupy intermediate positions between these two extreme hypotheses. We clarified that “model would not work” refers to prediction accuracy approaching chance (EV ≈ 0).

R1.32 "In both species and in both directions, inter-areal prediction EV fraction persisted (𝑝 < 0.001," Doesn't persist mean EV is unchanged? But the test is EV>0 or not in both cases.

We meant that EV values remained significantly above chance, not that they were unchanged. The statistical test was indeed whether EV > 0 as the reviewer indicated. We have revised the text accordingly (lines 375-380).

R1.33 "In mice, neurons showed a bimodal distribution in terms of their response predictability in shuffled and unshuffled trials" -> I don't see any bimodality in the figure, nor is there a statistical test provided for bimodality.

In Figure 7C, a group of neurons lay essentially along the horizontal axis, whereas the other group is dispersed closer to the diagonal line. Specifically, the neurons that lay on the horizontal axis are also the ones whose responses are best predicted during gray screen activity. We have changed the text to clarify this point (lines 380-382).

R1.34 "In the macaque V4 → V1 direction, there was a large proportion of neurons with peak EV when considering 25 ms to 50 ms offsets in the positive direction (i.e., V4 after V1, Figure 7I, right)." -> So what does this mean? Is this compatible with anything we know? This is the anti-causal direction so some kind of explanation would be warranted.

In the V4→V1 panel, a positive offset means we use V4 at t+Δt to predict V1 at t (and conversely in the V1→V4 panel). Therefore, the fact that the peak EV occurs at +10–20 ms indicates that V1 leads V4 by ~10–20 ms: in other words, V1’s earlier response best predicts V4’s slightly later response. This observation is not anti-causal, but rather it is consistent with the canonical largely feed-forward V1→V4 latency (e.g., Schmolesky et al., 1998 among many others). We clarified this in text (lines 400-404).

R1.35 L. 307: "In monkeys," plural!?

While this was not correct in the original version, we have now added data from two more monkeys.

R1.36 L. 313: "we observed an approximately bimodal distribution of neuronal responses, with a large subset of neurons that do not show reliable responses to visual stimuli both in L4 and L2/3" -> where?

The bimodal distribution can be appreciated in Figure 6B (1-vs-rest r2, third panel, note neurons along the y-axis, see also R1.33) and Supplementary Figure 7B (lines 307-312). Additionally, as stated in R1.3, we have now formally quantified the bimodality of the relationship between one-vs-rest correlation and inter-laminar explained variance (EV) in mice using Hartigan’s dip test (lines 310-313); see also Supplementary Figure 7A,D. In datasets that did not show bimodality by visual inspection (macaque recordings) the same test yielded non-significant results, confirming that the statistical analysis distinguishes between bimodal and unimodal cases.

R1.37 Random subsampling to control for population size done with how many subsamples? How are they combined? Variability across subsamples interpreted how?

We performed 10 permutations and used the median distributions across permutations (line 621).

Reviewer #2 (Public Review):

R2.0: “Summary:

In this work, the authors investigated the extent of shared variability in cortical population activity in the visual cortex in mice and macaques under conditions of spontaneous activity and visual stimulation. They argue that by studying the average response to repeated presentations of sensory stimuli, investigators are discounting the contribution of variable population responses that can have a significant impact at the single trial level. They hypothesized that, because these fluctuations are to some degree shared across cortical populations depending on the sources of these fluctuations and the relative connectivity between cortical populations within a network, one should be able to predict the response in one cortical population given the response of another cortical population on a single trial, and the degree of predictability should vary with factors such as retinotopic overlap, visual stimulation, and the directionality of canonical cortical circuits.”

R2.1: To test this, the authors analyzed previously collected and publicly available datasets. These include calcium imaging of the primary visual cortex in mice and electrophysiology recordings in V1 and V4 of macaques under different conditions of visual stimulation. The strength of this data is that it includes simultaneous recordings of hundreds of neurons across cortical layers or areas. However, the weaknesses of calcium dynamics (which has lower temporal resolution and misses some non-linear dynamics in cortical activity) and multi-unit envelope activity (which reflects fluctuations in population activity rather than the variance in individual unit spike trains), underestimate the variability of individual neurons. The authors deploy a regression model that is appropriate for addressing their hypothesis, and their analytic approach appears rigorous and well-controlled.

We agree with these points, and we discuss these specific limitations in capturing the variability of individual neurons in the Discussion section (lines 500-504). We have now also added analyses based on local field potentials (LFP). LFPs do not directly reflect the activity of individual neurons either.

R2.2: From their analysis, they found that there was significant predictability of activity between layer II/III and layer IV responses in mice and V1 and V4 activity in macaques, although the specific degree of predictability varied somewhat with the condition of the comparison with some minor differences between the datasets. The authors deployed a variety of analytic controls and explored a variety of comparisons that are both appropriate and convincing that there is a significant degree of predictability in population responses at the single trial level consistent with their hypothesis. This demonstrates that a significant fraction of cortical responses to stimuli is not due solely to the feedforward response to sensory input, and if we are to understand the computations that take place in the cortex, we must also understand how sensory responses interact with other sources of activity in cortical networks. However, the source of these predictive signals and their impact on function is only explored in a limited fashion, largely due to limitations in the datasets. Overall, this work highlights that, beyond the traditionally studied average evoked responses considered in systems neuroscience, there is a significant contribution of shared variability in cortical populations that may contextualize sensory representations depending on a host of factors that may be independent of the sensory signals being studied.

We agree that these datasets do not lend themselves well to directly separating and quantifying all the different sources of the predictive signals. We expand on this point in the Discussion section (lines 509-511).

R2.3: The different recording modalities and comparisons (within vs. across cortical areas) limit the interpretability of the inter-species comparisons.

We also agree with this comment. We emphasize that our goal is not to attempt a direct quantitative comparison across species (lines 497-499).

R2.4: Strengths:

This work considers a variety of conditions that may influence the relative predictability between cortical populations, including receptive field overlap, latency that may reflect feed-forward or feedback delays, and stimulus type and sensory condition. Their analytic approach is well-designed and statistically rigorous. They acknowledge the limitations of the data and do not over-interpret their findings.

Weaknesses:

The different recording modalities and comparisons (within vs. across cortical areas) limit the interpretability of the inter-species comparisons.The mechanistic contribution of known sources or correlates of shared variability (eye movements, pupil fluctuations, locomotion, whisking behaviors) were not considered, and these could be driving or a reflection of much of the predictability observed and explain differences in spontaneous and visual activity predictions.

We have expanded on the Discussion section to explicitly state the points raised by the reviewer (lines 494-509).

In mice, we have now also analyzed a separate dataset in which behavioral measurements were available, including running speed and facial motion (FaceMap SVDs). We used these to build behavioral-only and combined models to predict neural activity. We found that behavioral variables explained a modest but consistent portion of the variance across both spontaneous and stimulus conditions (Supplementary Figure 10A,C, lines 268-273).

For the macaque data, we analyzed pupil size as the only available behavioral measure in the macaque dataset. We focused specifically on the “resting state, eyes open” condition, where both neural activity and pupil measurements were available. Using ridge regression, we assessed the extent to which pupil size predicted neural activity in V1 and V4. Pupil size alone explained only a small fraction of the variance (Supplementary Figure 10E, lines 274-276).

R2.5: Previous work has explored correlations in activity between areas on various timescales, but this work only considered a narrow scope of timescales.

Without going into specifics about the numbers, it is hard to fully address this question. As the reviewer noted in R2.1, the mouse data analyzed here do not lend themselves to evaluating predictability on scales of tens of milliseconds. In the macaque data, we have now conducted additional analyses where we binned the activity across a range of bin sizes (10 ms to 200 ms). The new analyses are shown in Supplementary Figure 4, and described in lines 140-143, 160-163.

R2.6: The observation that there is some degree of predictability is not surprising, and it is unclear whether changes in observed predictability with analysis conditions are informative of a particular mechanism or just due to differences in the variance of activity under those conditions. Some of these issues could be addressed with further analysis, but some may be due to limitations in the experimental scope of the datasets and would require new experiments to resolve.

First, we note that several of the analyses and comparisons are within conditions and not across conditions, where by “condition” we mean the presence or absence of a stimulus or different stimuli (e.g., Figures 3, 5, 6, 7, Supplementary Figures 3-4, 7–13).

Second, we note that our mouse preprocessing standardized responses by spontaneous mean and SD per neuron, controlling baseline scale across conditions (lines 535-538). Because of this standardization, spontaneous traces have unit scale (mean = 0, SD = 1).

To test whether differences in variance underlie our findings, we calculated the variance for both species. For mice, we computed variance across repeats (visual) and across timepoints (lines 286-291). For the macaque moving-bar sessions, we computed variance across the concatenated held-out samples pooling timepoints, repeats, and bar identities (lines 291-292).

The V4 population showed a higher overall variance distribution compared to the V1 population (Supplementary Figure 2I-J), and L2/3 variance was also overall higher than L4 (Supplementary Figure 2D-E). We also see a modest monotonic relationship between EV fraction and this variance (mouse visual: Spearman ρ = 0.43–0.52, p < 0.001; macaque stimulus responses: ρ = 0.50–0.56, p < 0.001; macaque gray-screen responses: ρ = 0.38, p < 0.001, Figure 6A,D), indicating variance contributes to (but is not the primary driver of) EV prediction fraction. We then adjusted for variance by fitting, within each stimulus condition, a linear regression of EV on variance (excluding shuffled-control rows) and conducted all comparisons on the resulting residual EV values, thereby isolating effects not attributable to variance (see Supplementary Figure 3E-G, lines 165-171).

Reviewer #2 (Recommendations for the authors):

R2.7 Overall I found this manuscript to be very clearly written and the results compelling, although I found myself wanting a little more. I believe these datasets also include information about eye movements, pupil diameter, and maybe locomotion and whisking in the rodent work. I think it could be informative to ask the degree to which the predictability, particularly during the spontaneous activity, is attributable to these other known sources of variance in trial-by-trial measures. My concern is that during visual stimulation, the space of cortical responses is limited to a very narrow scope (observing a visual stimulus during fixation) whereas spontaneous activity includes a broader range of possibilities (different states of arousal, eye movement).

We analyzed the role of behavioral variables that could explain the neural activity in mouse V1 (including the variables suggested by the reviewer, running speed, facemap SVDs). The open dataset authors warned not to use pupil size since in the dark, the measurements were not accurate. In terms of the contribution to the predictability of mouse V1 activity, these behavioral variables showed a weak yet significant contribution (Supplementary Figure 10A,C, lines 260-270).

R2.8 By controlling for eye movements or pupil diameter during spontaneous measurements, would you improve your measure of predictability?

When predicting neural activity in the lights-off eyes open condition, combining neural data of the predictor population with information of pupil size did not result in a statistically significant increase in EV fraction when predicting the target population (Supplementary Figure 10E, lines 276-278).

R2.9 Also, there is work that shows feed-forward correlations between V1 and higher visual areas are observed in higher frequency activity, whereas feedback is associated with lower frequency activity. If you compared your predictability measure over bandpasses with different timescales, would you find the direction of V1-V4 interactions changes consistent with this previous work?

To address this question, we extended our analyses to the local field potential signals (LFPs) in monkeys, using band-limited LFP power (2–12, 12–30, 30–45, 55–95 Hz). We reran the lag sweep analyses (10-ms steps; 200-ms windows slid every 10 ms) in both directions. The Gamma band showed a feed-forward signature in the early evoked period: the V1→V4 predictability peaked at negative offsets (∼10–30ms; V1 leads), and the V4→V1 predictability peaked at positive offsets, consistent with previous findings. The results for low and beta frequency bands are also presented in the text (Supplemental Figure 13, lines 412-423).

Reviewer #3 (Public review):

R3.0: Neural activity in the visual cortex has primarily been studied in terms of responses to external visual stimuli. While the noisiness of inputs to a visual area is known to also influence visual responses, the contribution of this noisy component to overall visual responses has not been well characterized.

In this study, the authors reanalyze two previously published datasets - a Ca++ imaging study from mouse V1 and a large-scale electrophysiological study from monkey V1-V4. Using regression models, they examine how neural activity in one layer (in mice) or one cortical area (in monkeys) predicts activity in another layer or area. Their main finding is that significant predictions are possible even in the absence of visual input, highlighting the influence of non-stimulus-related downstream activity on neural responses. These findings can inform future modeling work of neural responses in the visual cortex to account for such non-visual influences.

R3.1: "A major weakness of the study is that the analysis includes data from only a single monkey. This makes it hard to interpret the data as the results could be due to experimental conditions specific to this monkey, such as the relative placement of electrode arrays in V1 and V4."

We have now added the second monkey (monkey “A”) from the same dataset (Chen et al., 2020), which includes all activity types except the lights-off condition. In addition, we collected new neural activity from one additional monkey (monkey “D”) in collaboration with the Carlos Ponce lab (monkey A: seelines 90-96, 120-132, 159, 161, 171, 183-185, 188-194, 200-203, 228-237, 254-258, 292-296, 334-342, 351-353, 358-364, 374-378, 387-393, 400-408, 414, 417-421, 539-540, 544-545, 680-681, 696-698; Supplemental Figures 1-6, 8, 11, 12, and 13; monkey D: see lines 90-96, 120-130, 132-134, 163-164, 228-235, 237-243, 292-296, 351-353, 374-378, 387-389, 539-540, 553-560, 696-698; Supplemental Figures 1-2, 4, 6, 9, 11, and 12. The conclusions for the new monkeys are qualitatively similar to the ones reported previously. The main quantitative differences are due to the very large difference in the number of predictor sites (Table 2, lines 127-134).

R3.2: The authors perform a thorough analysis comparing regression-based predictions for a wide variety of combinations of stimulus conditions and directions of influence. However, the comparison of stimulus types (Figure 4) raises a potential concern. It is not clear if the differences reported reflect an actual change in predictive influence across the two conditions or if they stem from fundamental differences in the responses of the predictor population, which could in turn affect the ability to measure predictive relationships. The authors do control for some potential confounds such as the number of neurons and self-consistency of the predictor population. However, the predictability seems to closely track the responsiveness of neurons to a particular stimulus. For instance, in the monkey data, the V1 neuronal population will likely be more responsive to checkerboards than to single bars. Moreover, neurons that don't have the bars in their RFs may remain largely silent. Could the difference in predictability be just due to this? Controlling for overall neuronal responsiveness across the two conditions would make this comparison more interpretable.

First, we note that several of the analyses and comparisons are within conditions and not across conditions, where by “condition” we mean the presence or absence of a stimulus or different stimuli (e.g., Figures 3, 5, 6, 7, Supplementary Figures 3-4, 7-13).

In Figure 4, differences in target-population responsiveness could influence predictability across stimulus types, as the reviewer points out. We therefore controlled for this by modeling EV as a function of the following neuron properties: split-half r, SNR, one-vs-rest r^2, and response variance. Regression was performed within each direction, where we then used residuals for inference_._ When comparing residuals, the predictability of checkerboard responses remained statistically higher than the predictability of the responses to moving bars (p<0.001, permutation test, Supplementary Figure 5K, lines 196-203), suggesting that the differences in predictability cannot be exclusively attributed to differences in the target population neuronal properties.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This important study provides the first direct neuroimaging evidence for the integration segregation theory of exogenous attention underlying inhibition of return, using an optimized IOR-Stroop fMRI paradigm to dissociate integration and segregation processes and to demonstrate that attentional orienting modulates semantic- and response-level conflict processing. Although the empirical evidence is compelling, clearer justification of the experimental logic, more cautious framing of behavioral and regional interpretations, and greater transparency in reporting and presentation are needed to strengthen the conclusions. The work will be of broad interest to researchers investigating visual attention, perception, cognitive control, and conflict processing.

We appreciate the positive reception to our manuscript. In the revised manuscript, we have further clarified the logic underlying the task design, adopted a more cautious tone in interpreting the behavioral and neuroimaging results, and enhanced the transparency of reporting and presentation.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study makes a significant and timely contribution to the field of attention research. By providing the first direct neuroimaging evidence for the integration-segregation theory of exogenous attention, it fills a critical gap in our understanding of the neural mechanisms underlying inhibition of return (IOR). The authors employ a carefully optimized cue-target paradigm combined with fMRI to elegantly dissociate the neural substrates of cue-target integration from those of segregation, thereby offering compelling support for the integration-segregation account. Beyond validating a key theoretical hypothesis, the study also uncovers an interaction between spatial orienting and cognitive conflict processing, suggesting that exogenous attention modulates conflict processing at both semantic and response levels. This finding shed new light on the neural mechanisms that connect exogenous attentional orienting with cognitive control.

Strengths:

The experimental design is rigorous, the analyses are thorough, and the interpretation is well grounded in the literature. The manuscript is clearly written, logically structured, and addresses a theoretically important question. Overall, this is an excellent, high-impact study that advances both theoretical and neural models of attention.

Weaknesses:

While this study addresses an important theoretical question and presents compelling neuroimaging findings, a few additional details would help improve clarity and interpretation. Specifically, more information could be provided regarding the experimental conditions (SI and RI), the justification for the criteria used for excluding behavioral trials, and how the null condition was incorporated into the analyses. In addition, given the non-significant interaction effect in the behavioral results, the claim that the behavioral data "clearly isolated" distinct semantic and response conflict effects should be phrased more cautiously.

We thank the reviewer for these helpful comments. In the revised manuscript, we have provided additional clarification regarding the SI and RI conditions (page 29), expanded the justification for the behavioral trial exclusion criteria (page 32), and clarified how the null condition was modeled and incorporated into the analyses (page 29). In addition, we have revised the description of the behavioral results to adopt more cautious wording, particularly given the absence of a significant interaction effect. For detailed responses to these specific points, please refer to the "Recommendations for the Authors" section below.

Reviewer #2 (Public review):

Summary:

This study provides evidence for the integration-segregation theory of an attentional effect, widely cited as inhibition of return (IOR), from a neuroimaging perspective, and explores neural interactions between IOR and cognitive conflict, showing that conflict processing is potentially modulated by attentional orienting.

Strengths:

The integration-segregation theory was examined in a sophisticated experimental task that also accounted for cognitive conflict processing, which is phenomenologically related to IOR but "non-spatial" by nature. This study was carefully designed and executed. The behavioral and neuroimaging data were carefully analyzed and largely well presented.

Weaknesses:

The rationale for the experimental design was not clearly explained in the manuscript; more specifically, why the current ER-fMRI study would disentangle integration and segregation processes was not explained. The introduction of "cognitive conflict" into the present study was not well reasoned for a non-expert reader to follow.

We thank the reviewer for raising these important points. In the revised manuscript, we have further clarified the rationale of the experimental design and the motivation for introducing cognitive conflict.

First, we clarified that previous neuroimaging studies relied primarily on SOA-based contrasts, which capture the temporal dynamics of attentional orienting but do not directly distinguish the functional processes of integration and segregation. We therefore established the direct comparison between cued and uncued targets in the long SOA as the critical test required by the theory, as these conditions are hypothesized to engage integration and segregation processes, respectively (pages 6-7, “The Challenge of Neural Verification”). Crucially, to successfully implement this comparison, we highlighted the specific methodological advantage of our study: the use of a Genetic Algorithm (GA) to optimize the stimulus sequence. We explained how this design maximizes statistical power specifically for contrast detection (i.e., cued vs. uncued) while maintaining high estimation efficiency, thereby directly overcoming the power constraints that had likely obscured these subtle neural signatures in prior ER-fMRI work (pages 7-8).

Second, we clarified that the manipulation of cognitive conflict was introduced with the additional aim of examining IOR expression mechanisms, specifically investigating how spatial attention modulates ongoing cognitive processing after target onset, rather than the generation of IOR itself. We have now provided a clearer rationale for embedding a modified Stroop task within the cue-target paradigm, and explained how this design allows us to dissociate semantic and response conflicts while avoiding methodological confounds present in previous studies (page 8).

The presentation of the results can be further improved, especially the neuroimaging results. For instance, Figure 4 is challenging to interpret. If "deactivation" (or a reduction in activation) is regarded as a neural signature of IOR, this should be clearly stated in the manuscript.

We thank the reviewer for pointing out the interpretational challenges in Figure 4. To address this, we have revised Figure 4 and provided a clearer and more precise interpretation of these interaction effects in the manuscript.

First, we have added explicit panel titles to Figure 4 (page 17). Panel A is now clearly labeled as the “Effect of IOR on Semantic Conflict”, while Panel B is labeled as the “Effect of IOR on Response Conflict”. We hope this visual labeling helps readers clearly identify the IOR modulation effects specific to each conflict type.

Second, we have revised the figure caption to explicitly define the interaction contrasts used to quantify these modulations, providing specific formulas (e.g., [UncuedRI – Uncued-SI] > [Cued-RI – Cued-SI] for response conflict) to ensure transparency.

Finally, regarding the reviewer’s comment on “deactivation”, we realized that our original figure terminology (e.g., “IOR effect under...”) might have caused confusion by mixing the interaction effect with the IOR effect itself. We have clarified that Figure 4 specifically illustrates the “Effect of IOR on the Semantic Conflict and the Response Conflict” (i.e., interaction effect between IOR and cognitive conflict). To interpret this interaction, we further examined the simple effects of conflict under each cueing condition. Specifically, we analyzed the neural signatures of semantic conflict (SI minus NE) and response conflict (RI minus SI) separately for the cued and uncued targets. Importantly, regarding the nature of the IOR effect itself (as displayed in Figure 3, page 14), it is not simply a uniform deactivation. Instead, by directly comparing the cued and uncued conditions for the neutral words, we observed neural changes in two directions: some specific regions exhibited an increased activation (Cued > Uncued), while others showed a reduced activation (Uncued > Cued). These differential patterns involved distinct brain networks and corresponded to the distinct integration and segregation mechanisms, respectively, rather than a global loss of activation (pages 20-21).

Reviewer #3 (Public review):

Summary:

This study aims to provide the first direct neuroimaging evidence relevant to the integration-segregation theory of exogenous attention - a framework that has shaped behavioral research for more than two decades but has lacked clear neural validation. By combining an inhibition-of-return (IOR) paradigm with a modified Stroop task in an optimized event-related fMRI design, the authors examine how attentional integration and segregation processes are implemented at the neural level and how these processes interact with semantic and response conflicts. The central goal is to map the distinct neural substrates associated with integration and segregation and to clarify how IOR influences conflict processing in the brain.

Strengths:

The study is well-motivated, addressing a theoretically important gap in the attention literature by directly testing a long-standing behavioral framework with neuroimaging methods. The experimental approach is creative: integrating IOR with a Stroop manipulation expands the theoretical relevance of the paradigm, and the use of a genetic algorithm-optimized fMRI design ensures high efficiency. Methodologically, the study is sound, with rigorous preprocessing, appropriate modeling, and analyses that converge across multiple contrasts. The results are theoretically coherent, demonstrating plausible dissociations between integration-related activity in the fronto-parietal attention network (FEF, IPS, TPJ, dACC) and segregation-related activity in medial temporal regions (PHG, STG). The findings advance the field by supplying much-needed neural evidence for the integration-segregation framework and by clarifying how IOR modulates conflict processing.

Weaknesses:

Some interpretive aspects would benefit from clarification, particularly regarding the dual roles ascribed to dACC activation and the circumstances under which PHG and STG are treated as a single versus separate functional clusters. Reporting conventions are occasionally inconsistent (e.g., statistical formatting, abbreviation definitions), which may hinder readability. More detailed reporting of sample characteristics, exclusion criteria, and data-quality metrics-especially regarding the global-variance threshold-would improve transparency and reproducibility. Finally, some limitations of the study, including potential constraints on generalization, are not explicitly acknowledged and should be articulated to provide a more balanced interpretation.

We thank the reviewer for the positive and constructive assessment of our study. In response to the concerns raised, we have carefully revised the manuscript and addressed all points in detail below. In brief, we have clarified key interpretation issues in the Discussion section, including the complementary roles of dACC activation and the distinction between statistical clustering and functional interpretation of PHG and STG activations (pages 20-21). We have also improved transparency and reporting throughout the manuscript by providing more detailed sample characteristics, clarifying exclusion criteria and global variance computation, adding illustrative supplementary figures, and standardizing statistical reporting and abbreviations (pages 28, 33). Finally, we have added a concise paragraph on limitations of the study to provide a more balanced interpretation of the findings (pages 26-27). Detailed, point-by-point responses to all specific comments are provided below (see the “Recommendations for the authors” Section).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Specific comments:

(1) The figure caption contains an unclear sentence (lines 195-196): "The target was a 450-ms colored Chinese character presented 600 ms after the fixation cue onset at the two target locations with equal probabilities." This description is ambiguous and should be revised for clarity.

Thanks for pointing this out. In the revised manuscript, we have rephrased the figure caption to improve clarity as follows (pages 9-10):

“Each trial started with a 150-ms non-informative cue presented at one of the two peripheral boxes. After a 150-ms interstimulus interval (ISI), a 150-ms fixation cue was presented at the central fixation box. Following a further 450-ms ISI, the target, a colored Chinese character, appeared at one of the two target locations with equal probabilities and remained on the screen for 450 ms. The trial ended with a variable intertrial interval (ITI) of 850, 1050, 1250, or 1450 ms (with equal probabilities).”

(2) Please provide a more detailed and clearer description of the SI and RI experimental conditions in the Methods section.

Thanks for this helpful suggestion. We have revised the Methods section to provide a more detailed description of the SI and RI conditions. Specifically, we have further described the stimulus-response mapping and clarified how the SI and RI conditions are defined based on whether the ink color and the character meaning fell into the same or different response categories under this mapping. In addition, we have added a clarification in the Methods section to make it clearer that the SI trials involved semantic conflict without response conflict, whereas RI trials involve both semantic and response conflicts (page 29).

(3) As the data were collected across two research centers, please clarify the number of participants enrolled at each site.

Thanks for this suggestion. We have now explicitly stated in the Apparatus and Data Acquisition section that 16 participants were enrolled at each site. The revised text reads (page 31)：

“The imaging data were acquired at two research sites following comparable protocols, with equal numbers of participants scanned at each site (n = 16 per site).”

(4) In the behavioral data analysis, please provide the rationale or justification for the criteria used to exclude trials.

Thanks for this comment. In the revised manuscript (page 32), we have clarified that reaction times (RTs) shorter than 150 ms were excluded as anticipatory responses, and RTs longer than 1,300 ms were excluded to limit the influence of unusually slow responses. These exclusion criteria are commonly adopted in RT research and were applied consistently across all conditions (Ratcliff, 1993; Whelan, 2008).

(5) Given that the behavioral interaction effect was not statistically significant, the conclusion on lines 236-237, "These data clearly isolated the two distinct conflict effects in the Stroop effect, namely the semantic conflict (SI-NE difference) and the response conflict (RI-SI difference)" appears overstated and should be softened accordingly.

We thank the reviewer for this important comment. We have clarified that our original statement was intended to highlight the successful isolation of conflict types based on the significant main effects of congruency (validating the task design), rather than implying a significant interaction effect. However, we agree that the original phrasing appeared unclear in this context. We have therefore revised the sentence to adopt a more cautious tone in the revised manuscript (page 12):

“These data demonstrated typical Stroop interference effects (Veen & Carter, 2005) in both the semantic (SI-NE difference) and response conflicts (RI-SI difference).”

(6) The statement on lines 281-282, "Although the IOR effect showed no effect on either the semantic conflict difference (SI-NE) or the response conflict difference (RI-SI) in the behavioral performance" lacks supporting statistical evidence. Please report the relevant test statistics.

We appreciate the reviewer’s careful reading and note that the relevant statistical evidence was missing from the original manuscript. This has now been added in the revised version. Specifically, we examined the interactions between cue validity and semantic conflict (SI vs. NE) as well as between cue validity and response conflict (RI vs. SI). Neither interaction was significant (see revised Results for full statistics on page 12), supporting our original statement that cue validity did not modulate either conflict component in behavioral performance.

(7) The manuscript mentions that a null condition (with no Chinese character presented) was included to increase statistical power for detecting differences across conditions. However, it is unclear how this null condition was actually used in the data analyses. Please clarify the role of the null condition in both the behavioral and neuroimaging analyses.

Thanks for this comment. We regret that this was not sufficiently clear in the original manuscript. The null condition was included for neuroimaging purposes and was not used in the behavioral analyses, as no response was required in these trials. In the fMRI analyses, null trials served as the implicit baseline and were not modeled as regressors of interest. Task-related activities for all experimental conditions were therefore estimated relative to this null baseline, facilitating estimations of task-related responses in randomized event-related designs (Burock et al., 1998; Friston et al., 1999; Liu, 2004). We have clarified this point in the revised manuscript (page 29).

References

Burock, M. A., Buckner, R. L., Woldorff, M. G., Rosen, B. R., & Dale, A. M. (1998). Randomized event-related experimental designs allow for extremely rapid presentation rates using functional MRI. NeuroReport, 9(16), 3735-3739. https://doi.org/10.1097/00001756-199811160-00030

Friston, K. J., Zarahn, E., Josephs, O., Henson, R. N. A., & Dale, A. M. (1999). Stochastic designs in event-related fMRI. NeuroImage, 10(5), 607-619. https://doi.org/10.1006/nimg.1999.0498

Liu, T. T. (2004). Efficiency, power, and entropy in event-related fMRI with multiple trial types: Part II: design of experiments. NeuroImage, 21(1), 401-413. https://doi.org/10.1016/j.neuroimage.2003.09.031

Ratcliff, R. (1993). Methods for dealing with reaction time outliers. Psychological Bulletin, 114(3), 510-532. https://doi.org/10.1037/0033-2909.114.3.510

Whelan, R. (2008). Effective analysis of reaction time data. The Psychological Record, 58(3), 475-482. https://doi.org/10.1007/BF03395630

Reviewer #2 (Recommendations for the authors):

(1) The paper is a bit too lengthy, with a lot of information that is hard for non-experts to grasp.

We thank the reviewer for this comment. We realized that the Introduction was the most challenging section for general readers. In the revision, we refined the text in the Introduction for a better structure and more reader-friendly wording to improve readability. In addition, following the reviewer’s suggestion (Recommendation 4 below), we have added short subsection titles to the Introduction, Results, and Discussion sections to better organize the content and highlight the main ideas. We hope these revisions make the manuscript more accessible and easier for a broader audience to follow.

(2) Please double-check the stats, as some of the results presented in the main text do not align well with the figures. Take Figure 2 as an example.

We appreciate the reviewer’s concern and have double-checked all statistics. All the results are consistent between the figures and the main text. Take Figure 2 as an example (page 12), the perceived discrepancy probably was caused by the fact that the descriptive values reported in the main text are marginal means for the main effects (i.e., the overall average of one factor, collapsed over the other factor), whereas Figure 2 shows the mean for each Congruency × Cue Validity condition (i.e., simple effect).

(3) The reasoning that the neuroimaging findings support the dissociation between integration and segregation needs to be improved.

We thank the reviewer for this important comment. In the revised Discussion (pages 1921), we have strengthened the reasoning linking our neuroimaging findings to the dissociation between the integration and segregation processes. Specifically, we make it clear how the distinct activation patterns observed for the cued and uncued targets map onto the different functional demands proposed by the integration-segregation theory. The cued targets were theorized to recruit the frontoparietal attentional control networks, consistent with the re-engagement of an existing object file (integration). On the other hand, the uncued targets should engage the medial temporal and temporal association regions responsible for novelty detection and episodic encoding, consistent with the creation of a new object file (segregation). We hope the reviewer finds that the revision offers a clearer explanation of how the observed neural patterns are consistent with a dissociation between the integration and segregation processes.

(4) Please use short section titles to organize the introduction, results, and discussion sections. For instance, the discussion section is a long chunk of text (almost 9 pages) and is pretty dense, making it hard to quickly grasp the ideas the authors want to convey.

Thanks for this helpful suggestion. Following the reviewer’s recommendation, we have now added short subsection titles to the Introduction and Discussion sections to improve structure and readability. For the Results section, we have maintained and further refined the existing subheadings to ensure consistent organization.

Reviewer #3 (Recommendations for the authors):

I found this manuscript to be a timely and substantive contribution to the study of attention and cognitive neuroscience. To my knowledge, it provides the first direct neuroimaging evidence relevant to the integration-segregation theory of exogenous attention, a framework that has been influential in behavioral work for more than two decades but has lacked clear neural support. The study is conceptually well motivated, methodologically solid, and generally clearly reported. The findings differentiate neural substrates associated with integration and segregation processes and further show how inhibition of return (IOR) interacts with semantic and response conflicts at the neural level.

The manuscript is well organized, the writing is mostly clear, and the progression from theory to hypotheses and methods is easy to follow. The combination of IOR with a modified Stroop paradigm is a clever choice that extends the theoretical scope of exogenous attention research. The use of an optimized event-related fMRI design based on a genetic algorithm is also a strength and reflects careful attention to design efficiency.

The main results are internally consistent and theoretically meaningful. Integration related activity in the fronto-parietal attention network (including FEF, IPS, TPJ, and dACC) and segregation-related activity in medial temporal areas (PHG and STG) it well with the proposed framework, and the pattern of activations is coherent across analyses.

Overall, I think this is a carefully executed study that offers much-needed neural evidence bearing on the integration-segregation theory of exogenous attention. I would recommend the following revisions.

Suggestions:

(1) In the Discussion (pp. ~17-18), dACC activation is described both in terms of general cognitive control demands and as reflecting a possible inhibitory bias toward the cued direction. It would help the reader if you could briefly indicate whether you see these as complementary (e.g., dual roles within the same region) or as more competing interpretations.

We thank the reviewer for this helpful comment. We have clarified in the revised manuscript that dACC exerts general cognitive control demands and biasing against the cued direction are complementary rather than competing interpretations. Specifically, we described how the dACC is involved in both the cognitive control required for target integration and the inhibitory bias toward the cued location, thereby highlighting its dual roles within the same region. The revised section reads as follows (page 20):

“Furthermore, the observed increase in the left dACC activity under the cued relative to the uncued condition likely reflected the engagement of cognitive control mechanisms (Botvinick et al., 2004; Chung et al., 2024; Mayer et al., 2012; Veen & Carter, 2005), particularly in resolving the conflict between the task-driven requirement of target integration and the reduced accessibility of the cue-initiated representation. In this context, the heightened activation of dACC may also reflect its role in fulfilling the inhibitory bias toward the cued location (Mayer et al., 2004) and discouraging inefficient integration attempts at a location marked as less relevant.”

(2) In the Discussion, you could consider adding a short paragraph explicitly acknowledging a few limitations and how they might constrain generalization of the findings. A concise reflection of this kind would give a more balanced picture without undermining the main conclusions.

We appreciate this helpful suggestion. In the revised manuscript, we have added a concise paragraph explicitly addressing a key limitation of the present study (pages 26-27). Specifically, we acknowledge that the absence of behavioral interactions alongside clear neural effects requires cautious interpretation. We discussed how this dissociation may reflect differences in measurement sensitivity between behavioral and neural indices, consistent with prior findings (Chen et al., 2006; Wilkinson & Halligan, 2004). We also note that the use of a GA-optimized sequence, while improving statistical efficiency, may have introduced unintended regularities in event order that could influence behavioral strategies.

(3) Since the dataset is hosted on GitHub, adding a short note in the Data Availability section about whether the repository will also include analysis scripts or future replication data would further enhance transparency and long-term usefulness.

Thanks for this helpful suggestion. We have revised the Data Availability section (page 35) to clarify that the GitHub repository contains the processed data used in the final analyses. Analysis scripts and additional materials for replication are available from the authors upon reasonable request.

(4) In the Results section, the formatting of statistics is not fully consistent. For example, some reports use spaces around symbols (e.g., "η² = 0.301") whereas others do not (e.g., "p< .001"). It would be good to standardize this (e.g., "p < .001", "η² = .30") across the manuscript.

Done as suggested.

(5) A few abbreviations appear before they are defined-for instance, SPC (superior parietal cortex) shows up in the Results (response conflict section) before the full name is given. Ensuring that each abbreviation is defined at first mention would help readers who may be less familiar with all of the regional acronyms.

Thanks for this comment. We have conducted a thorough check of the manuscript and ensured that all abbreviations are defined upon their first occurrence.

(6) The text sometimes refers to "PHG/STG" as a combined cluster, while at other points, PHG and STG are described separately. It would be useful to clarify under what circumstances they are treated as a single functional cluster versus distinct regions of interest, and to keep the nomenclature as consistent as possible between the main text and the tables.

Thanks for raising this point. In the revised manuscript, we have clarified this issue by distinguishing between statistical clustering and functional interpretation. In the whole brain analysis, activations in the left hemisphere formed a single continuous cluster spanning the PHG and STG; therefore, this cluster is labeled as “PHG/STG” in Table 1. We have explicitly noted the continuous nature of this cluster in the Results section (page 15) to ensure clarity:

“Notably, in the left hemisphere, these activations formed a continuous cluster spanning both regions (labeled as PHG/STG in Table 1).”

(7) It would be helpful to provide a bit more detail about the sample characteristics (e.g., age range, handedness, and inclusion/exclusion criteria) and to state explicitly how many participants, if any, were excluded from the analyses and for what reasons. This would help readers better evaluate data quality and generalizability.

Thanks for this helpful suggestion. We have revised the Participants section (page 28) to provide the full details regarding our sample:

“32 healthy participants with normal or corrected-to-normal vision and normal color vision were recruited. All participants were right-handed and reported no history of neurological or psychiatric disorders. Data from three participants were excluded due to excessive head movements and high global variances (see fMRI Data Analysis), leaving 29 participants for analysis (18 female, 11 male; aged 18-30 years, M = 22.69, SD = 2.58).”

Furthermore, we have provided a clearer description of the exclusion criteria in the Data Analysis section (pages 33-34) as follows:

“Runs with motions exceeding one voxel length in any direction were excluded (resulting in the exclusion of two runs) …Runs with global variance equal to or over 0.1% were excluded, resulting in the exclusion of eight runs (see Supplementary Information for details). Ultimately, three participants were excluded because neither run met the quality criteria. All remaining participants retained both runs, except for three individuals who each contributed only one valid run.”

(8) Given that participants were excluded based on global variance exceeding 0.1%, it would be very informative to include, in the Supplementary Materials, an illustrative figure showing the signal time series (or global signal variance over time) for excluded participants.

We appreciate this valuable suggestion. In the revised Supplementary Materials, we have included a new figure (Figure S2) that plots the global signal time series for the excluded runs to illustrate the signal patterns that led to their exclusion based on global variance.

(9) Relatedly, it may help to more explicitly describe how global variance was computed (e.g., over which time window, after which preprocessing steps, and whether it was calculated on whole-brain signal or within specific masks). A concise clarification would make the exclusion criterion easier to interpret.

Thanks for this helpful suggestion. We have now clarified in the manuscript how global variance was computed (page 33) and have also provided a more detailed description of the computation procedure in the Supplementary Materials (page 4). Specifically, after the standard preprocessing (slice timing correction, 3D motion correction, spatial smoothing, linear trend removal, and high-pass temporal filtering), the global signal was computed for each run as the mean signal across voxels with intensity values greater than 100 in each volume. Global variance was then quantified as the temporal variance of this run-wise global-signal time course across all volumes, providing a quality-control index of signal stability.

(10) Rather than only reporting a single overall exclusion rate (e.g., 5.52% of total trials), it would be informative to break this down by source, reporting separately the proportion of trials excluded as RT outliers and the proportion excluded due to response errors. This would further improve transparency regarding the behavioral preprocessing pipeline.

Thanks for this helpful suggestion. We have now broken down the overall exclusion rate by source in the revised manuscript. Specifically, we reported that 4.29% of trials were excluded due to incorrect responses, and 1.24% of trials were excluded as RT outliers (page 32).

References

Botvinick, M. M., Cohen, J. D., & Carter, C. S. (2004). Conflict monitoring and anterior cingulate cortex: an update. Trends in Cognitive Sciences, 8(12), 539-546. https://doi.org/10.1016/j.tics.2004.10.003

Chen, Q., Wei, P., & Zhou, X. (2006). Distinct neural correlates for resolving stroop conflict at inhibited and noninhibited locations in inhibition of return. Journal Of Cognitive Neuroscience, 18(11), 1937-1946. https://doi.org/10.1162/jocn.2006.18.11.1937

Chung, R. S., Cavaleri, J., Sundaram, S., Gilbert, Z. D., Del Campo-Vera, R. M., Leonor, A., Tang, A. M., Chen, K.-H., Sebastian, R., Shao, A., Kammen, A., Tabarsi, E., Gogia, A. S., Mason, X., Heck, C., Liu, C. Y., Kellis, S. S., & Lee, B. (2024). Understanding the human conflict processing network: A review of the literature on direct neural recordings during performance of a modified stroop task. Neuroscience Research, 206, 1-19. https://doi.org/10.1016/j.neures.2024.03.006

Mayer, A. R., Seidenberg, M., Dorflinger, J. M., & Rao, S. M. (2004). An event-related fMRI study of exogenous orienting: supporting evidence for the cortical basis of inhibition of return? Journal Of Cognitive Neuroscience, 16(7), 1262-1271. https://doi.org/10.1162/0898929041920531

Mayer, A. R., Teshiba, T. M., Franco, A. R., Ling, J., Shane, M. S., Stephen, J. M., & Jung, R. E. (2012). Modeling conflict and error in the medial frontal cortex. Human Brain Mapping, 33(12), 2843-2855. https://doi.org/10.1002/hbm.21405

Veen, V. V., & Carter, C. S. (2005). Separating semantic conflict and response conflict in the Stroop task: A functional MRI study. Neuro Image, 27(3), 497-504. https://doi.org/10.1016/j.neuroimage.2005.04.042

Wilkinson, D., & Halligan, P. (2004). The relevance of behavioural measures for functional imaging studies of cognition. Nature Reviews Neuroscience, 5(1), 67-73. https://doi.org/10.1038/nrn1302

Author response:

The following is the authors’ response to the original reviews

Thank you very much for the positive and constructive feedback on our manuscript. We have revised the manuscript accordingly and have added a substantial number of additional experiments and have extended the data.

Questions of the reviewers were focused mostly on mechanical insight into organoid formation, touching following aspects of lens organoid formation presented in the manuscript:

- Cellular arrangements/re-arrangements during the process of lens formation including potential contribution of differential adhesion-mediated cell sorting to the cellular arrangement in the organoid and characterization of individual contributions of lens- and retina- committed progenitors to this process.

- Activity of BMP and FGF signaling pathways during organoid formation, namely identification of tissue responding to the signaling withing forming organoids.

- Contribution of externally supplemented Matrigel to the differentiation process and cellular arrangements in ocular organoids. 

To address those points in detail we included additional experiments that are now presented in revised version of the manuscript, namely in revised Figure 2-figure supplement 1 (addressing contribution of Matrigel); new Figure 4-supplement 1/Video S5 (addressing contribution of differential adhesion-mediated cell sorting); revised Figure 4/Video S6/Video S7 (addressing contribution of lens-committed progenitors); revised Figure 6 (addressing BMP and FGF signaling pathway activities).

Reviewer #1 (Evidence, reproducibility and clarity):

Summary

The authors focused on medaka retinal organoids to investigate the mechanism underlying the eye cup morphogenesis. The authors succeeded to induce lens formation in fish retinal organoids using 3D suspension culture with minimal growth factor-containing media containing the Hepes. At day 1, Rx3:H2B-GFP＋ cells appear in the surface region of organoids. At day 1.5, Prox1+cells appear in the interface area between the organoid surface and the core of central cell mass, which develops a spherical-shaped lens later. So, Prox1+ cells covers the surface of the internal lens cell core. At day 2, foxe3:GFP+ cells appear in the Prox1+ area, where early lens fiber marker, LFC, starts to be expressed. In addition, foxe3:GFP+ cells show EdU+ incorporation, indicating that foxe3:GFP+ cells have lens epithelial cell-characters. At day 4, cry:EGFP+ cells differentiate inside the spherical lens core, whose the surface area consists of LFC+ and Prox1+ cells. Furthermore, at day 4, the lens core moves towards the surface of retinal organoids to form an eye-cup like structure, although this morphogenesis "inside out" mechanism is different from in vivo cellular "outside -in" mechanism of eye cup formation. From these data, the authors conclude that optic cup formation, especially the positioning of the lens, is established in retinal organoids though the different mechanism of in vivo morphogenesis.

Overall, manuscript presentation is nice. However, there are still obscure points to understand background mechanism. My comments are shown below.

Major comments

(1) At the initial stage of retinal organoid morphogenesis, a spherical lens is centrally positioned inside the retinal organoids, by covering a central lens core by the outer cell sheet of retinal precursor cells. I wonder if the formation of this structure may be understood by differential cell adhesive activity or mechanical tension between lens core cells and retinal cell sheet, just like the previous study done by Heisenberg lab on the spatial patterning of endoderm, mesoderm and ectoderm (Nat. Cell Biol. 10, 429 - 436 (2008)). Lens core cells may be integrated inside retinal cell mass by cell sorting through the direct interaction between retinal cells and lens cells, or between lens cells and the culture media. After day 1, it is also possible to understand that lens core moves towards the surface of retinal organoids, if adhesive/tensile force states of lens core cells may be change by secretion of extracellular matrix. I wonder if the authors measure physical property, adhesive activity and solidness, of retinal precursor cells and lens core cells. If retinal organoids at day 1 are dissociated and cultured again, do they show the same patterning of internal lens core covering by the outer retinal cell sheet?

The question, whether different adhesive activity is involved in cell sorting and lens formation is indeed very intriguing.

To address this point, we included additional experiments in the revised manuscript. As proposed by the reviewer, we performed dissociation and re-aggregation experiments of day one organoids at the timepoint, when retinal cell fate is already established and first cells with early lens fate (Foxe3::GFP positive) start appearing (see new Figure 4-figure supplement 1).

After dissociation we followed Foxe3::GFP cells over time and observed that initially equally dispersed GFP⁺ lens-committed cells gradually sort and establish contact with other GFP⁺ cells, ultimately resulting in the formation of a central GFP⁺ sphere within a retinal neuroepithelium (AcTub⁺) localized on the surface of the organoid (see new Figure 4-figure supplement 1e and new Video S5). This data show that differential adhesive properties of lens/retinal precursor cells can enable the formation of a spherical lens in the center of the organoid. This is now clearly stated in the revised version of the manuscript. 

(2) Optic cup is evaginated from the lateral wall of neuroepithelium of the diencephalon. In zebrafish, cell movement occurs from the pigment epithelium to the neural retina during eye morphogenesis in an FGF-dependent manner. How the medaka optic cup morphogenesis is coordinated? I also wonder if the authors conduct the tracking of cell migration during optic cup morphogenesis to reveal how cell migration and cell division are regulated in lens of the Medaka retinal organoids. It is also interesting to examine how retinal cell movement is coordinated during Medaka retinal organoids.

Looking into the detail of how optic cup-looking tissue arrangement of ocular organoids is achieved on cellular level is of course interesting. Our previous study showed that optic vesicles of medaka retinal organoids do not form optic cups (for details please see Zilova et al., 2021, eLife). We provide evidence that the formation of cup-looking structure of the ocular organoids presented here is mediated by the following processes: establishment of retina and lens domains at specific regions of the organoid – retina on the surface and lens in the center (see Figure 3-figure supplement 1d and Figure 3e, and Figure 4). Further, the dislocation of the centrally formed lens towards the organoid periphery results in the opening of the retina layer, moving the lens to the periphery while retinal cells stay static. We propose that the “cup-like” shape is acquired by an extrusion-like process of the lens from the center of the organoid.

To address the cellular mechanisms involved in this process, we included additional experiments and followed the movements of retinal and lens cells (see new Figure 4c and 4d, new Videos S6, S7 and S8). Retinal cells (tracked as nuclei of the Rx3::H2B-GFP transgenic line) established in the periphery display repeated short distance movements restricted to the retinal epithelium. These movements are characteristic for interkinetic nuclear migration as found in the developing retina. In contrast, Foxe3::GFP lens progenitor cells performed long distance movements from the center to the periphery of the organoid. This movement was accompanied by profound cell shape changes of lens progenitor cells, suggesting an active movement of lens cells to the organoid periphery. These movements are shown in new/extended figures and in new supplementary videos (new Figure 4c and 4d, new Videos S6, S7 and S8) in the revised version of the manuscript.

(3) The authors showed that blockade of FGF signaling affects lens fiber differentiation in day 1-2, whereas lens formation seems to be intact in the presence of FGF receptor inhibitor in day 0-1. I suggest the authors to examine which tissue is a target of FGF signaling in retinal organoids, using markers such as pea3, which is a downstream target of ERK branch of FGF signaling. Since FGF signaling promotes cell proliferation, is the lens core size normal in SU5402-treated organoids from day 0 to day 1?

Assessing the activity of FGF signaling (cross-reference to Reviewer #3) in the organoids is an important point that we have taken care of and included in the revised manuscript.

To address this point, we assessed which tissue/part of the organoid is responding to FGF signaling. To do so we analyzed the presence of phosphorylated ERK (pERK1/2) as FGF signaling target in ocular organoids from day 1 to day 2. At day 1, only low levels of FGF signaling activity were detectable in presumptive retinal or/and lens tissue (see revised Figure 6b). Only half a day later, a significant increase in FGF activity was observed specifically in the central region of the organoids (lens progenitor domain) (at day 1.5), prior to the onset of differentiation of lens fiber cells. This, together with inability of lens progenitor cells to differentiate to lens fiber cells in the presence of FGF inhibitor SU5402 provided during this critical period (day 1 to day 2) demonstrates that FGF signaling activity localized in the lens progenitor cells is required for lens fiber differentiation.

By day 2, FGF activity was detected in both lens and retinal tissue of the organoid. Similar patterns of FGF activity were observed in embryos at 2 days post fertilization (see revised Figure 6b).

The treatment with the FGF signaling inhibitor SU5402 from day 0 to day 1 did have no impact on the core size of organoid the dimension of which were fully comparable to the control (please see Figure 6d).

(4) Fig. 3f and 3g indicate that there is some cell population located between foxe3:GFP+ cells and rx2:H2B-RFP+ cells. What kind of cell-type is occupied in the interface area between foxe3:GFP+ cells and rx2:H2B-RFP+ cells?

That is for sure an interesting question. We are aware of this population of cells. We currently do not have data that clarify the fate of those cells with the required certainty. Rather than speculating, we are currently following up on that question by scRNA sequencing, however we see that beyond the scope of the current manuscript.

(5) Fig. 5e indicates the depth of Rx3 expression at day 1. Is the depth the thickness of Rx3 expressing cell sheet, which covers the central lens core in the organoids? If so, I wonder if total cell number of Rx3 expressing cell sheet may be different in each seeded-cell number, because thickness is the same across each seeded-cell number, but the surface area size may be different depending on underneath the lens core size. Please clarify this point.

The referee is right, figure 5e indicates the thickness of the cell sheet expressing Rx3 positioned at the surface of the organoid. Indeed, the number of Rx3-expressing cells (and lens cells) scales with the size of the organoid as stated in the submitted manuscript. We have taken care to remove ambiguities related to that point in the revised version of the manuscript.

(6) Noggin application inhibits lens formation at day 0-1. BMP signaling regulates formation of lens placode and olfactory placode at the early stage of development. It is interesting to examine whether Noggin-treated organoid expands olfactory placode area. Please check forebrain territory markers.

What tissue differentiates at the expense of the lens in BMP inhibitor-treated organoids is of course an intriguing question.

To address this point, we labeled Noggin treated organoids at day 2 and day 3 with forebrain and olfactory placode markers. We could identify an increase in the domains expressing Lhx2, HuC/D and Otx2 in Noggin-treated organoids, showing a shift of the preferential differentiation of the neurons of anterior forebrain identity (see attached figure for reviewer). However, the available markers Lhx2, HuC/D and Otx2 found in the olfactory placode are in addition also co-expressed in further neuronal cell types of the anterior forebrain. While the speculation is tempting, the shift in expression does not allow to conclusively state the expansion of the olfactory placode.

Author response image 1.

Expression of forebrain and olfactory placode markers.

I have no minor comments

Referees cross-commenting

I agree that all reviewers have similar suggestions, which are reasonable and provided the same estimated time for revision.

Reviewer #1 (Significance):

Strength:

This study is unique. The authors examined eye cup morphogenesis using fish retinal organoids. Eye cup normally consists of the lens, the neural retina, pigment epithelium and optic stalk. However, retinal organoids seem to be simple and consists of two cell types, lens and retina. Interestingly, a similar optic cup-like structure is achieved in both cases; however, underlying mechanism is different. It is interesting to investigate how eye morphogenesis is regulated in retinal organoids,under the unconstrained embryo-free environment.

Limitation:

Description is OK, but analysis is not much profound. It is necessary to apply a bit more molecular and cellular level analysis, such as tracking of cell movement and visualization of FGF signaling in organoid tissues.

Advancement:

The current study is descriptive. Need some conceptual advance, which impact cell biology field or medical science.

Audience:

The target audience of current study are still within ophthalmology and neuroscience community people, maybe translational/clinical rather than basic biology. To beyond specific fields, need to formulate a general principle for cell and developmental biology.

Reviewer #2 (Evidence, reproducibility and clarity):

In this study from Stahl et al., the authors demonstrate that medaka pluripotent embryonic cells can self-organise into eye organoids containing both retina and lens tissues. While these organoids can self-organize into an eye structure that resembles the vertebrate eye, they are built from a fundamentally different morphogenetic process - an "inside-out" mechanism where the lens forms centrally and moves outward, rather than the normal "outside-in" embryonic process. This is a very interesting discovery, both for our understanding of developmental biology and the potential for tissue engineering applications. The study would benefit from some additional experiments and a few clarifications.

The authors suggest that the lens cells are the ones that move from the central to a more superficial position. Is this an active movement of lens cells or just the passive consequence of the retina cells acquiring a cup shape? Are the retina cells migrating behind the lens or the lens cells pushing outwards? High-resolution imaging of organoid cup formation, tracking retina cells in combination with membrane labeling of all cells would help elucidate the morphogenetic processes occurring in the organoids. Membrane labeling would also be useful as Prox1 positive lens cells appear elongated in embryos while in the organoids, cell shapes seem less organised, less compact and not elongated (for example as shown in Fig 3f,g).

Looking into the detail of how the optic cup-like arrangement of ocular organoids is achieved on the cellular level is indeed highly interesting. In the revised manuscript we now provide evidence that the formation of cup-like structure of the ocular organoids presented here is mediated by the following processes: establishment of retina and lens domains at distinct regions of the organoid – retina on the surface and lens in the center (see Figure 3-figure supplement 1d and Figure 3e, and Figure 4). Further, the dislocation of the centrally formed lens towards the organoid periphery results in the opening of the retina layer, moving the lens to the periphery while retinal cells stay static. We propose that the cup-like shape is acquired by an extrusion process of the lens from the center of the organoid.

To address cellular mechanisms involved in this process, we included additional experiments and followed the movements of retinal and lens cells (see new Figure 4c and 4e, new Videos S6, S7 and S8).

Retinal cells (tracked as nuclei of the Rx3::H2B-GFP transgenic line) display repeated short distance movements within the retinal epithelium. These movements are characteristic for interkinetic nuclear migration as found in the developing retina.

In contrast, Foxe3::GFP lens progenitor cells performed long distance movements from the center to the periphery of the organoid. This movement was accompanied by profound cell shape changes of lens progenitor cells, suggesting an active movement of lens cells to the organoid periphery.

These movements are shown in new/extended figures and in new supplementary videos (new Figure 4c and 4e, new Videos S6, S7 and S8) in the revised version of the manuscript.

The organoids could be a useful tool to address how cell fate is linked to cell shape acquisition. In the forming organoids, retinal tissue initially forms on the outside, while non-retinal tissue is located in the centre; this central tissue later expresses lens markers. Do the authors have any insights into why fate acquisition occurs in this pattern? Is there a difference in proliferation rates between the centrally located cells and the external ones? Could it be that highly proliferative cells give rise to neural retina (NR), while lower proliferating cells become lens?

We agree with the reviewer that this is a highly interesting question and in the revised manuscript we followed the advice and dedicated a part of the discussion to this topic. We believe that the arrangement is due to the induction of central lens fates by signal emanating from the retinal epithelium and discuss the role of the diffusion limit and the potential contribution of BMB and FGF signaling to this arrangement. Additional experiments addressing the target tissues of FGF and BMP signaling in the organoid have been provided in response to Reviewer #1. Interfering with FGF signaling that is essential for lens fiber cell differentiation interestingly did not impact on the lens size arguing against an immediate proliferative effect. Although the analysis of the respective proliferation rates at the surface or in the central region of the organoid might show some differences, we do not have any indications, that the proliferation rate itself would be instructive or superior to the cell fate decisions.

What happens in organoids that do not form lenses? Do these organoids still generate foxe3 positive cells that fail to develop into a proper lens structure? And in the absence of lens formation, does the retina still acquire a cup shape?

Lens formation is primarily dependent on the acquisition/specification of Foxe3-expressing lens placode progenitors. In the absence of Foxe3-expression, a lens does not develop. Once Foxe3-expressing progenitors are established, a lens is formed in unperturbed conditions (measured by the presence of expression of crystallin proteins). Organoids that do not have a lens, do not contain Foxe3-expressing cells.

In the absence of a lens, the organoid is composed of retinal neuroepithelium, that does not form an optic cup like shape (for details of such phenotypes please see Zilova et al., 2021, eLIFE). We took care to state that clearly in the revised manuscript.

The author suggest that lens formation occurs even in the absence of Matrigel. Is the process slower in these conditions? Are the resulting organoids smaller? While there are indeed some LFC expressing cells by day2, these cells are not very well organised and the pattern of expression seems dotty. Moreover, LFC staining seems to localise posterior to the LFC negative, lens-like structure (e.g. Fig.S1 3o'clock). How do these organoids develop beyond day 4? Do they maintain their structural integrity at later stages?

The role of HEPES in promoting organoid formation is intriguing. Do the authors have any insights into why it is important in this context? Have the authors tried other culture conditions and does culture condition influence the morphogenetic pathways occurring within the organoids?

We thank the reviewer for pointing this out. In the revised manuscript we made sure to be sufficiently clear in the wording and description of our observation. Indeed, Matrigel is not required for the acquisition of lens fate, which can be demonstrated by the expression of lensspecific markers. However, the presence of Matrigel has a profound impact on structural aspects of organoid formation. Matrigel is essential for organization of retinal-committed cells to form a retinal epithelium (Zilova et al., 2021, eLife). The absence of the structure of the retinal epithelium indeed negatively impacts on the cellular organization and the overall lens structure.

To clarify the contribution of the Matrigel to the organoid organization, we performed additional experiments (see revised Figure 2-figure supplement 1c-f). As mentioned above, the absence of Matrigel impacts on the organization and thickness of retinal neuroepithelium (Rx2⁺, Figure 2-figure supplement 1c). However, measurement of the lens in organoids at day 2 and day 5 showed that size of the lens is not impacted upon in the absence of Matrigel (Figure 3-figure supplement 1d-e). Additionally, taking advantage of the Foxe3::GFP lens reporter line, we measured the onset of lens-specific gene expression in organoids with and without Matrigel. In both conditions, with and without Matrigel supplementation, Foxe3::GFP expression was initiated at 25 hours post aggregation (see revised Figure 4b).

The role of the HEPES in lens formation is indeed very intriguing and currently under investigation. HEPES is mainly used to regulate the pH of the culture media which on its own might have an impact on multiple cellular processes. It will require a significant time investment to address the potential HEPES triggered molecular mechanisms impacting on lens formation (cross reference with Reviewer #3), which goes beyond the scope of the current manuscript.

Referees cross-commenting

Pleased to see that all the other reviewers are positive about the study and raise similar concerns and comments

Reviewer #2 (Significance):

This is a very interesting paper, and it will be important to determine whether this alternative morphogenetic process is specific to medaka or if similar developmental routes can be recapitulated in organoid cultures from other vertebrate species.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

The manuscript by Stahl and colleagues reports an approach to generate ocular organoids composed of retinal and lens structures, derived from Medaka blastula cells. The authors present a comprehensive characterisation of the timeline followed by lens and retinal progenitors, showing these have distinct origins, and that they recapitulate the expression of differentiation markers found in vivo. Despite this molecular recapitulation, morphogenesis is strikingly different, with lens progenitors arising at the centre of the organoid, and subsequently translocating to the outside.

Comments:

The manuscript presents a beautiful set of high quality images showing expression of lens differentiation markers over time in the organoids. The set of experiments is very robust, with high numbers of organoids analysed and reproducible data. The mechanism by which lens specification is promoted in these organoids is, however, poorly analysed, and the reader does not get a clear understanding of what is different in these experiments, as compared to previous attempts, to support lens differentiation. There is a mention to HEPES supplementation, but no further analysis is provided, and the fact that the process is independent of ECM contradicts, as the authors point out, previous reports. The manuscript would benefit from a more detailed analysis of the mechanisms that lead to lens differentiation in this setting.

We followed the reviewer’s advice and have included a systematic analysis of the contribution of ECM (Matrigel) to the process of lens formation. In the revised manuscript we made sure to be sufficiently clear in the wording and description of our observation. Indeed, Matrigel is not required for the acquisition of lens fate, which can be demonstrated by the expression of lensspecific markers. However, the presence of Matrigel has a profound impact on structural aspects of organoid formation. Matrigel is essential for organization of retinal-committed cells to form a retinal epithelium (Zilova et al., 2021, eLIFE). The absence of the structure of the retinal epithelium in turn indeed negatively impacts on the cellular organization and the overall lens structure.

To clarify the contribution of the Matrigel to the organoid organization, we performed additional experiments (see revised Figure 2-figure supplement 1c-f). As mentioned above, the absence of Matrigel impacts on the organization and thickness of retinal neuroepithelium (Rx2⁺, Figure 2-figure supplement 1c). However, measurement of the lens in organoids at day 2 and day 5 showed that size of the lens is not impacted upon by the absence of Matrigel (Figure 3-figure supplement 1d-e).

Additionally, taking advantage of the Foxe3::GFP lens reporter line, we measured the onset of lens-specific gene expression in organoids with and without Matrigel. In both conditions (with and without Matrigel supplementation), Foxe3::GFP expression was initiated at 25 hours post aggregation (see revised Figure 4b).

The role of the HEPES in lens formation is indeed intriguing and currently under investigation. HEPES is mainly used to adjust the pH of the culture media, which, on its own might have an impact on multiple cellular processes. It will require a significant time investment to address the potential HEPES triggered molecular mechanisms impacting on lens formation (cross reference with Reviewer #3), which clearly goes beyond the scope of the current manuscript.

The markers analysed to show onset of lens differentiation in the organoids seem to start being expressed, in vivo, when the lens placode starts invaginating. An analysis of earlier stages is not presented. This would be very informative, allowing to determine whether progenitors differentiate as placode and neuroepithelium first, to subsequently continue differentiating into lens and retina, respectively. Could early placodal and anterior neural plate markers be analysed in the organoids? This would provide a more complete sequence of lens vs retina differentiation in this model.

We have taken care to show according stages in embryo and organoid side by side. We provide additional data to highlight the expression of Rx3::H2B-GFP (retina) and Foxe3::GFP (lens and lens placode) markers in earlier developmental stages. For the presumptive eye field within the region of the anterior neural plate (S16, late gastrula) Rx3 represents one of the earliest markers (see revised Figure 3-figure supplement 1). Already before an apparent lens placode is formed (see revised Figure 3d) Foxe3::GFP expression is detected within the presumptive lens ectoderm, demonstrating that Foxe3 is ideally suited as an early marker for placodal progenitors in medaka. The onset of Rx3 and Foxe3-driven reporters is clearly early enough to support the claim about the separate origin of the lens (placodal) and retinal (anterior neuroectoderm) tissues within the ocular organoids now represented in the revised figures.

The analysis of BMP and Fgf requirement for lens formation and differentiation is suggestive, but the source of these signals is not resolved or mentioned in the manuscript. Are BMP4 and Fgf8 expressed by the organoids? Where are they coming from?

Assessing the activity of BMP and FGF signaling (cross-reference to Reviewer #1) in the organoids is an important point that we have taken care of and included in the revised manuscript.

To address this point, we assessed which tissue/part of the organoid is responding to BMP and FGF signaling. To do so we analyzed the presence of phosphorylated SMAD1/5/8 (pSMAD1/5/8) and phosphorylated ERK (pERK1/2) as BMP and FGF signaling target in ocular organoids from day 1 to day 2. BMP signaling activity was detected in the center (region of establishment of lens-committed progenitors (Figure 3e)) of the organoid at day 1 (see revised Figure 6a). At day 1, only low levels of FGF signaling activity were detectable in presumptive retinal or/and lens tissue (see revised Figure S6b). Only half a day later, a significant increase in FGF activity was observed specifically in the central region of the organoids (lens progenitor domain, at day 1.5), prior to the onset of differentiation of lens fiber cells. This, together with inability of lens progenitor cells to differentiate to lens fiber cells in the presence of FGF inhibitor SU5402 provided during this critical period (day 1 to day 2) demonstrates that FGF signaling activity localized in the lens progenitor cells is required for lens fiber differentiation.

By day 2, FGF activity was detected in both lens and retinal tissue of the organoid. Similar patterns of FGF activity were observed in embryos at 2 days post fertilization (see revised Figure S6b).

The treatment with the FGF signaling inhibitor SU5402 from day 0 to day 1 did have no impact on the core size of organoid the dimension of which were fully comparable to the control (please see Figure 6b).

Related to the presence of the corresponding ligands we can state that they are indeed expressed in the organoids at the matching stages based on RNA seq and RT-PCR analyses, however we could not find them specifically localized. This may be due to a widespread, ubiquitous expression or may simply relate to technical problems.

While we can state with confidence that the ligands are present at the relevant time points and trigger the downstream pathways in a localized manner, the question whether the response is due to a localized signal or localized competence remains to be addressed.

The fact that the lens becomes specified in the centre of the organoid is striking, but it is for me difficult to visualise how it ends up being extruded from the organoid. Did the authors try to follow this process in movies? I understand that this may be technically challenging, but it would certainly help to understand the process that leads to the final organisation of retinal and lens tissues in the organoid. There is no discussion of why the morphogenetic mechanism is so different from the in vivo situation. The manuscript would benefit from explicitly discussing this.

Following the shift of the lens in vivo is indeed very relevant suggestion and we have taken care to address this in the revised manuscript.

To clarify this process, we included additional experiments and followed the movements of lens cells (see new Figures 4c, 4d and 4e, new Videos S6 and S7). Foxe3::GFP lens progenitor cells were found to actively move over long distances from center to the organoid periphery. This movement was accompanied by profound cell shape changes of lens progenitor cells with the active extension of lamellipodia and filopodia strongly arguing for an active movement of lens cells to the organoid periphery (cross-reference with Reviewer #1 and Reviewer #2).

Referees cross-commenting

We all seem to have similar comments and concerns. I think overall the suggestions are feasible and realistic for the timeframe provided.

Reviewer #3 (Significance):

This study describes a reproducible approach to differentiate ocular organoids composed of lens and retinal tissues. The characterisation of lens differentiation in this model is very detailed, and despite the morphogenetic differences, the molecular mechanisms show many similarities to the in vivo situation. The manuscript however does not highlight, in my opinion, why this model may be relevant. Clearly articulating this relevance, particularly in the discussion, will enhance the study and provide more clarity to the readers regarding the significance of the study for the field of organoid research, ocular research and regenerative studies.

This passage really challenged my understanding of the Anthropocene and stuck with me as I continued navigating your Scalar project. I had previously not concretely thought about the relationship with an everyday object, like the phone, and the environmental impacts in places so far from me, that I may never go to. More than that I had not been able to visualize the impacts of data on 'the cloud' until I read this page and thought about the amount of electricity that is being consumed for one photo. I think this is a really interesting way of reaching the local dimensions of the Anthropocene from something as global as phones. It makes you think about your personal impact and how far removed you are from it as we spoke about in class.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Joint Public Review:

Summary:

The authors investigate how stochastic and deterministic factors are integrated in cell fate decisions, using Dictyostelium discoideum as a model system. They show that cells in different cell cycle phases (a deterministic factor) are predisposed to different fates, albeit with deviations, when exposed to the same environmental stimulus. However, gene expression variability (a stochastic factor) enhances the robustness of cellular responses to environmental cues that disrupt the cell cycle.

Using a simple, tractable mathematical model, the authors demonstrate that cell fate decisions in D. discoideum depend on a combination of deterministic and stochastic factors, i.e., cell cycle phase and gene expression variability, respectively. They then identify Set1 - a key regulator of gene expression variability - indicate the mechanism through which it modulates this variability, and link it to a phenotype in D. discoideum development. Finally, they confirm that gene expression variability contributes to the robustness of the cell's response to environmental disruptions that interfere with the cell cycle.

Strengths:

The authors are careful in the choice of their experiments and in measuring gene expression variability, using methods that account for expected trends with average gene expression.

Weaknesses:

However, in terms of mathematical modelling, it would be important to rule out sources of stochasticity (other than gene expression variability), and also to consider cases where stochastic factors are not necessarily completely independent of the deterministic ones.

We thank you and the reviewers for the insightful comments that have helped clarify the findings presented. We have addressed all comments and feel that the revised manuscript is much improved.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Minor typographical mistakes:

(a) in the title: Linage -> lineage

Corrected as suggested

(b) on page 19: use a full stop in "...are biased towards the stalk fate, Use of the cell cycle position..."

Corrected as suggested

(c) on page 20: become -> becoming in "...(and end up biased towards become stalk)..."

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(d) on page 16: "mu = G p k". Perhaps it should be x instead of k?

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(2) Regarding the abstract:

(a) This work tries to outline general principles (coordination/integration of deterministic and stochastic factors) in cell fate choice, especially when cells are faced with (near) identical environmental conditions. Perhaps the abstract, especially the first line, could be rephrased to reflect the generality of symmetry breaking and differentiation that is studied in this article/work. e.g., as was done in the first paragraph of the discussion.

Corrected as suggested

(b) It might be worthwhile clarifying what "this" is in the sentence "We suggest this represents an adaptive mechanism that increases developmental robustness against perturbations that affect deterministic signals." in the abstract.

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(3) Regarding the model:

(a) The model tries to combine the stochastic and deterministic parts to explain the propensity for stalk fates. It is assumed that the cell cycle-associated factors (CCAF) provide the deterministic part while the cell cycle-independent factors (CCIF) provide the stochastic part. The net result is an addition of the two, which is then compared against a threshold to decide the propensity for stalk fates. However, another simple way to introduce stochasticity would be to make the CCAF decay stochastic. Reasons to consider this scenario would be: (i) the decay process (especially in the biological context) is generally stochastic, (ii) it would not be inconsistent with the fact that cell cycle dependent genes are also variable, and (iii) this way of introducing stochasticity would also provide expression level characteristics/plots similar to the ones outlined in Figure 1C, i.e. with a probability distribution of CCAF values for a given amount of time after mitosis. Would there be arguments or experimental evidence to rule this possibility out? For instance, would the results shown in Figure 7 contradict this model?

We agree that there could be stochasticity the CCAF decay process. In this scenario, the expected value of CCAF (which would reflect the mean of a noisy distribution) would show a deterministic pattern of decay through time, representing the average value of CCAF across cells that are in the same phase of the cell-cycle. The noisiness around such a pattern of deterministic decay in the mean value of CCAF (i.e., the residual variation) would then represent CCIF since it would be, by definition, cell-cycle independent. Hence, the present model is fully consistent with this possibility since it would still lead to some variation being cell-cycle associated and some variation being cell-cycle independent. Therefore, this scenario could be viewed as a different functional/biological process leading to the same ultimate distribution we model. To clarify this, we have added text justifying the hypothesis that the noisy distribution is due to gene expression differences, rather than decay itself:

“Protein levels can vary widely between cells because it is regulated at multiple levels, including transcription, translation and stability. The position of the noisiest step in a pathway affects the overall noise dramatically, because each step usually amplifies noise in the previous steps (Alon 2007). Consistent with this idea, theory and single-cell experiments have shown that a major contributor to cell-cell variation is the bursty expression of low-copy mRNAs. We therefore hypothesized that this noisiness across cells arises from stochastic expression of a set of genes contributing to CCIF levels.”

(b) On page 7, the formula for total CCIF variance assumes independence of the genes g_i. Is this a reasonable assumption?

This concerns the argument that a set of stochastically expressed genes will yield an approximately Gaussian distribution of CCIF. Our results do not depend on the solution for the mean and the variance, only that noisy genes will generally yield such a Gaussian distribution.This is because independence is not strictly required for the central limit theorem to yield a Gaussian distribution. The distribution will still be Gaussian under a broad range of conditions (especially since gene expression is bounded, so there is no chance of the total ending up generating an infinite variance). The primary requirement is that the expression of any given gene is independent from that of most other genes. As a result, most of the variation in expression across genes is independent (even if any given gene is not independent from all other genes).

The most likely pattern of non-independence will be the case in which gene expression is ‘modular’, where there are co-expressed blocks, meaning that non-independence is limited in scale so that genes within a co-regulated block show correlated expression, but their expression is uncorrelated to genes in other blocks. This pattern is functionally analogous to what is known as m-dependence in sequences of random variables (e.g., time series), where variables close together in sequence are correlated (but otherwise uncorrelated). Derivations of the central limit theorem have shown that the means (and hence the sum) of these sorts of variables still follow an approximately Gaussian distribution over a broad range of scenarios. In the case of non-independent gene expression, this means that we can view the independent random variable as being the expression value of a group of co-expressed genes (instead of individual genes). Hence, the means (or sums) of these values will still conform to the central limit theorem.

This problem is addressed in:

Diananda, P. H. 1955. The central limit theorem for m-dependent variables. Proc. Combin. Philos. Soc. 51:92-95

Hoeffding, W. & H. Robbins. 1948. The central limit theorem for dependent random variables. Duke Math. J. 15:773-780

Orey, S. A. 1958. Central limit theorems for m-dependent random variables. Duke Math. J. 25:543-546

Rosén, B. 1967. On the central limit theorem for sums of dependent random variables, Z. Wahrscheinlichkeitstheorie und Verw. Gebiete, 7:48-82

To clarify this, we have added the following text and references:

Although this derivation implicitly assumes that stochastically expressed genes are independent, this assumption is not strictly required for the distribution of CCIF to be approximately normal. If stochastically expressed genes show clustered co-expression owing to shared regulation, then the sum across these co-expressed blocks is still expected to be approximately normally distributed (as long as there are a reasonably large number of co-expressed clusters) (Diananda 1955; Hoeffding and Robbins 1994; Rosén 1967).

(4) In section "Cell cycle independent stochastic gene expression variation is extensive in growing cells":

Regarding the statement: "We first determined the coefficient of variation (CV2) of expression for all genes. As expected, this tends to decrease as average expression level increases (Supplementary Figure 2).":

It would be good to specify how the "expected variation" was calculated exactly. For instance, it was hard to discern from Supplementary Figure 2 how CV^2 decreasing with average expression levels was used in the calculation of expected variation.

This is described in the methods on page 38

“A trend line was fitted to the data using non-linear least squares regression (Scran v1.15.9). Genes were defined as variable (2073 genes) based on a one-sided test assuming a normal distribution around the trend but one where deviation changed depending on the mean expression of a given gene (Scran v1.15.9 - modelGeneCV2) with a FDR of < 0.05.”

(5) In section "Stochastically expressed genes are associated with cell fate determination"

(a) For readers unfamiliar with the organism ‘Dictyostelium discoideum’, a short description of its life cycle with growth and development/differentiation phases would be useful to provide the right context.

Corrected as suggested

(b) In section "Cell cycle independent stochastic gene expression variation is extensive in growing cells", it was shown that cell cycle dependent genes are also highly variable (in other words, ‘stochastic’). It would, therefore, be useful to elaborate on the definitions of "stochastically expressed genes, cell cycle-associated genes, and non-variable genes", as used in this section. Admittedly, the distinction does get clearer towards the last section of Results, but some elaboration here would make the reading smoother.

Corrected as suggested

(c) If the "cell cycle associated genes" are the same as "cell cycle dependent genes", it would be good to use one term consistently.

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(d) The developmental index is divided into 10 bins from 0 to 1. Is there a rationale for the choice of a number of bins? Would this choice affect significance tests for "stochastic" vs others? <br /> (The same question may apply to the "Cell type index")

Significance is robust to the number of bins chosen (e.g. 5-25). Of course, if there are too many bins (low number of genes) or too few bins (addition of noisy data) significance falls. In the case of developmental index, our choice of bins is also based on previous analyses (de Oliveira, et al 2019), which developed the index we used, and showed that a threshold of >0.9 can be used to identify ‘developmentally expressed genes’.

(6) In Figure 5:

(a) Does the statement "*** binomial test, p<0.01." (as seen in caption for part C) actually refer to part D?

Corrected as suggested

(b) Could the authors please specify what "mis-expressed" means in Figure 5D? Are these genes that are upregulated, downregulated, or both? From what set of genes was the random sampling done?

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(c) In Figure 5F, is the decrease in CV^2 explained entirely by the increase in mean (as shown in Figure 5E)?

We appreciate the point made by the reviewer and recognise that disentangling changes in gene expression variation from changes in expression levels is extremely difficult (any changes in burst frequency will necessarily affect expression level). However, we do not think this affects our conclusions, which are supported by results with representative Set1 dependent reporter genes (Figure 5G and H) which suggest that the number of cells expressing (rather than the expression in each cell is affected) in these cases at least.

(7) In Figure 6A: Could the authors please elaborate on the difference between the rows labelled "WT" and "set1-"? Are they two different types of chimera?

Corrected as suggested

(8) In Section "Cell cycle position and gene expression variation interact to control cell type proportioning":

Is there a graph corresponding to the statement "However, the level of GFP expression in each responding cell did not significantly change."?

Corrected as suggested

(9) In section "Influence of stochastic variation on sensitivity to cell cycle perturbations" of the Supplementary text:

(a) The model for cell cycle bias is not entirely clear. For instance, is the quantity N(t) = U(t) + Q_t U(t) also a probability distribution, like U(t) is? If so, there must be a normalization factor. It was difficult to understand the procedure behind this calculation. Perhaps some more elaboration (with words or a small schematic) on this model/method would help.

The value of U(t) was originally being used to denote the uniform probability density function (for the uniform distribution), but for clarity this has been changed to follow the convention that U[a,b] denotes the uniform distribution over the interval from a to b (which, in this case would be U[0, 1]), while f(t) is now being used to make it clear that this is the probability density, where f(t) = 1 across the interval. Because the uniform distribution necessarily integrates to 1 over the defined range, it does not need to be normalised. The confusion here is perhaps due to the expression f(t) = 1 being interpreted as defining the probability of sampling a value of t (but in a continuous distribution we can only define the probabilities of sampling over an interval), instead of defining the probability density over the interval from a to b, where f(x) would be 1/(b – a), and hence over the interval of 0 to 1, f(x) would equal 1.

To help clarify this issue, this section has been rewritten and a new figure (which appears as Supplementary Figure 12) has been added that illustrates the resulting probability density functions for biased sampling from the cell cycle.

(b) References to Figure 8A, B seem to be indicating Supplementary Figure 12 instead. 

Corrected as suggested

Reviewer #2 (Recommendations for the authors):

This manuscript seems quite interesting, but many sections are so unclear that I cannot follow what has been done. I would suggest slowly going through the manuscript and carefully explaining things. This will probably considerably increase the size of the manuscript, but many sections are too terse to follow even after many, many readings of the Results and figure legend.

Corrected as suggested

Some specific comments (this is not at all comprehensive, but rather illustrative)

Page 2 - 'genes strongly associated with fate choice' - can you explain this a bit more - genes associated with one cell type or another, or genes that somehow regulate the choice?

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Page 2 - this abstract is quite vague, I would suggest being more specific to reflect what is in the manuscript.

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Page 3 - 'exhibit bivalent H3K4me3..' please explain 'bivalent' a bit more.

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Page 7 - 'Bernoulli process with probability that (meaning that is scaled to the size of the temporal interval)' (non-copying symbols deleted) could be simplified.

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Page 7 - please define all variables/ equation components. What is N? What is x bar? What is s2? The middle paragraph is very difficult to follow.

This paragraph has been rewritten and a definition of the distribution added for clarity.

Page 7 - 'genes might logically vary in the value of pi, such variability does not impact our results. Trying to decipher this paragraph, it seems that pi is a function of time, so this could affect the results.

pi is the probability that a stochastically expressed gene is actually expressed in whatever interval is being considered for all genes. pi will necessarily increase if the time interval considered is increased. The key point is we are considering the probability that any given gene is expressed in the same time interval. In this case, genes could vary in pi, and thus some burst more often and others less often.

Page 9 - '(it is 98.35 times more likely' there may be too many significant figures here.

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Page 10 - for the Area Under the Receiver Operating Characteristic Curve (AUROC), what are you classifying? AUROC is typically used for diagnostic tests to determine how well the test can discriminate between two completely different outcomes. What is the input, and what are the outcomes?

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Figures:

What are the dashed lines in Figure S2A?

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What are the X-axes in Figure S3?

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I do not understand what you are showing in Figure S3.

Corrected as suggested in results

In Figure 2B, I cannot find in the text or figure legend any description or explanation of 'Group 1', 'Group 2', or 'Group 3'.

Corrected as suggested

Figure 3D needs a lot more explanation; I cannot understand this based on the text and the figure legend.

Corrected as suggested

The Set1 work should discuss the work in PMID: 39242621

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Figure 8 D needs a size bar

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Author response:

Many thanks to the three reviewers and the editors for their comments and review. These are fair, consistent (across positives and negatives), and largely expected comments. On behalf of my coauthors, I use this letter as a provisional response to indicate what we can and intend to change in a revised manuscript.

(1) A major comment from all three referees is that our single-nucleus RNA-seq data should be validated. The reviewers differ in the detail of exactly what they think should be validated, but they refer, individually, to (1) the discovery of ‘cell types’ themselves, (2) pathways inferred from trajectory analysis, (3) differentially expressed genes in plucked vs control condition at four time points and/or (4) inferred ligand-receptor pairs from cell-cell communication analysis, across the same time course. 

I think we’re actually on pretty good footing for 1-3, because of work we’ve published in the cichlid fish model.

I tally that in references cited in the manuscript, and highlighted below (References 1, 10, 11, 29, 30, 31), we present 29 figures with 273 individual figure panels of histology, in situ hybridization and immunohistochemistry featuring genes expressed across stages of tooth development and replacement. These genes are markers of dental competency and regenerative potential.

In addition, in multiple of these papers, we use pharmacology to manipulate the role of key pathways (Hh, BMP, Wnt, Notch) in cichlid tooth development and replacement. Identification and validation of cell types make use of these published data in cichlids (for markers matched to mouse), as well as an unbiased computational approach (SAMap) that draws homology between cichlid and mouse dental cell types, based on shared global patterns of gene expression.

In short, experiments to validate cell types, gene expression and pathways active in cichlid teeth are published and referenced herein. I noticed that these references (some of which include Gareth Fraser as an author, when he was a postdoc in my group; for Reviewer 2) were cited in the Introduction and not the Rationale/Methods or Results section (such that reviewers may have missed them). We will be clearer about this in the revision. 

We have not validated nor analyzed functionally the ligand-receptor pairs inferred from cell-cell communication analysis, across four times points of accelerated replacement. This work is beyond the scope of the current paper, and we will include a statement that these computational inferences represent hypotheses to be tested (although many of these ligand-receptor pairs have been noted in other ‘tooth’ publications that we cite).

(2) The biggest weakness of our manuscript, noted by referees, is that we do not provide serial histology to accompany our snRNA-seq time course after plucking. We describe this as a limitation in the “Study limitations and future direction” section of the Discussion, but we can and will be stronger about why this is a weakness (e.g., we do not explicitly know for instance, the degree of damage done to tissue in the plucking paradigm). We do know that the jaw recovers quickly, but we do not know how different the plucked side is from the control side (which is also undergoing active replacement and remodeling). Uniting reviewer comments 1 and 2 here, the best future approach is a spatial transcriptomics reference at distinct stages of the plucking<>recovery paradigm, as we framed in the Discussion section, because this addresses simultaneously the state of dental/jaw tissue and the in situ expression of thousands of genes.

(3) Reviewers asked about the presence of stromal cells in our snRNA-seq data. Because of this and another comment on the posted preprint version of our manuscript, we will take another look at the mesenchymal compartment of the snRNA-seq data and trajectories built from it.

(4) Multiple (minor) suggestions for clarification in text and figures will be adopted. 

Generally, I don’t think we’ll require reviewer re-engagement on the revision; editor review should be sufficient.

References cited in the manuscript, highlighted here:

(1) Fraser, G. J. et al. An Ancient Gene Network Is Co-opted for Teeth on Old and New Jaws. PLoS Biol. 7, e1000031 (2009).

(10) Fraser, G. J., Bloomquist, R. F. & Streelman, J. T. Common developmental pathways link tooth shape to regeneration. Dev. Biol. 377, 399–414 (2013).

(11) Bloomquist, R. F. et al. Developmental plasticity of epithelial stem cells in tooth and taste bud renewal. Proc. Natl. Acad. Sci. 116, 17858–17866 (2019).

(29) Streelman, J. T., Webb, J. F., Albertson, R. C. & Kocher, T. D. The cusp of evolution and development: a model of cichlid tooth shape diversity. Evol. Dev. 5, 600–608 (2003).

(30) Fraser, G. J., Bloomquist, R. F. & Streelman, J. T. A periodic pattern generator for dental diversity. BMC Biol. 6, 32 (2008).

(31) Bloomquist, R. F. et al. Coevolutionary patterning of teeth and taste buds. Proc. Natl. Acad. Sci. 112, (2015).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study examines how different parts of the brain's reward system regulate eating behavior. The authors focus on the medial shell of the nucleus accumbens, a region known to influence pleasure and motivation. They find that nerve cells in the front (rostral) portion of this region are inhibited during eating, and when artificially activated, they reduce food intake. In contrast, similar cells at the back (caudal) are excited during eating but do not suppress feeding. The team also identifies a molecular marker, Stard5, that selectively labels the rostral hotspot and enables new genetic tools to study it. These findings clarify how specific circuits in the brain control hedonic feeding, providing new entry points to understand and potentially treat conditions such as overeating and obesity.

We thank Reviewer 1 for the positive feedback, summary of our findings and for the thorough reading and constructive comments on the manuscript, which allowed us to improve the quality of the revised version.

Strengths:

(1) Conceptual advance: The work convincingly establishes a rostro-caudal gradient within the medNAcSh, clarifying earlier pharmacological studies with modern circuit-level and genetic approaches.

(2) Methodological rigor: The combination of fiber photometry, optogenetics, CRISPR-Cas9 genetic engineering, histology, FISH, scRNA-seq, and novel mouse genetics adds robustness, with complementary approaches converging on the central claim.

(3) Innovation: The generation of a Stard5-Flp line is a valuable resource that will enable precise interrogation of the rostral hotspot in future studies.

(4) Specificity of findings: The dissociation between appetitive and aversive conditions strengthens the interpretation that the observed gradient is restricted to feeding.

We thank Reviewer #1 for their supportive feedback.

Weaknesses and points for clarification

(1) Role of D2-SPNs: Since D1 and D2 pathways often show opposing roles in feeding, testing, or discussing D2-SPN contributions would provide an important control and context. Since the claim is that Stard5 is expressed in both D1- and D2MSNs, it seems to contradict the exclusive role of D1R MSNs in authorizing food intake.

We agree that D2-SPNs represent an important and relevant cell population in the context of our study. The Stard5-Flp line labels a mixed population of D1- and D2-SPNs, and we agree that dissecting the distinct contributions of Stard5⁺ D1-SPNs and Stard5⁺ D2-SPNs to feeding behavior would be both interesting and informative.

Although we understand the point raised by the Reviewer, we do not entirely agree that the expression of Stard5 in both D1- and D2-SPNs contradicts the established role of D1-SPNs in authorizing food intake. In the medNAcSh, D1- and D2-SPNs do not exert opposing functions. D2-SPNs project densely to the ventral pallidum and more sparsely to the lateral hypothalamus and, like D1-SPNs, are predominantly rewardinhibited at the population level (Domingues et al. 2025; Pedersen et al. 2022).

We added the following in the discussion: “Additionally, a new study showed that manipulation of D2-SPN cell bodies in the medNAcSh modulates reward preference, self-stimulation, and palatable food intake in a frequency- and context-dependent manner (Requejo-Mendoza et al., 2025). Together, these findings suggest that D1- and D2-SPNs within the medNAcSh play complementary rather than opposing roles in reward processing. Hence, the potential role of rostral and caudal medNAcSh D1- and D2-SPNs in foodrelated behaviors beyond the act of consumption could be addressed in future work.” We also acknowledge that not investigating rostro-caudal gradients of D2-SPN in reward and aversion processing “represents a limitation of this work”.

We fully agree that disentangling the specific contributions of Stard5⁺ D1- and Stard5⁺ D2-SPNs is an important next step. We have now crossed the Stard5-Flp line with Drd1-Cre and A2a-Cre lines. In a pilot experiment (not shown), we injected Flp+,Cre+, Flp+,Cre- and Flp-,Cre+ mice with 4 different FlpOn-CreOn AAVs to determine if any of these AAVs demonstrate specific expression. However, all AAVs exhibited moderate to strong leaky expression of the Cre, preventing reliable cell-type-specific targeting. This was not seen with Flp-only or Cre-only AAVs. The leakiness mentioned is a known challenge of FlpOn-CreOn AAVs and requires additional troubleshooting (e.g. reduce the titer). As this proved to be more challenging than anticipated, this work is ongoing and will be addressed in a future study rather than in the present revisions.

(2) Behavioral analyses:

(a) In Figure 2, group differences in consumption appear uneven; additional analyses (e.g., lick counts across blocks and session totals) would strengthen interpretation.

The group differences in consumption that appear uneven likely reflect an overall lower total lick counts per session in the Control group. We have now added analyses on average lick counts per block and session totals in the newly included Supplementary Figure S7, which support the results shown in Figure 2.

Although we observe a difference in total lick count across the entire session between Control and Rostral ChrimsonR mice (Supplementary Figure S7d), we deem the comparison in total session lick counts not that informative here. Instead, we would argue that the laser-on epoch is the most meaningful comparison. During this period, optogenetic activation had no effect on licking behavior in control mice, showed a nonsignificant trend toward reduced consumption in caudal ChrimsonR mice, and produced a significant reduction in lick counts when rostral medNAcSh D1-SPNs were activated (Figure 2g-i and Supplementary Figure S7c).

We added in the discussion the following explanation:

“In addition, comparison of licking behavior during the laser-off blocks revealed an interesting effect: following cessation of opto-stimulation, Rostral ChrimsonR mice licked more than Caudal ChrimsonR and Control mice, suggesting a possible compensatory overconsumption. One possible interpretation is that the optogenetic parameters used suppressed consummatory behavior without reducing the motivation to obtain the reward. Furthermore, consistent with the RTPPA results, activation of rostral D1-SPNs may be experienced as aversive and termination of the optogenetic stimulation could produce relief, which in turn reinforces the licking behavior. Further investigations are required to test these possibilities.”

(b) The design and contribution of aversive assays to the main conclusions remain somewhat unclear and could be better justified.

We appreciate the Reviewer’s comment regarding the design and contribution of the aversive assays. The rationale for including these experiments was to determine whether the rostro–caudal functional segregation observed for reward-related feeding also applies to aversive processing.

First, using foot shock, we tested whether D1-SPNs in the rostral versus caudal medNAcSh respond differently to an aversive stimulus. In contrast to reward-related responses, both populations responded similarly, exhibiting excitation. Second, to ensure that this effect was not specific to a single stressor, we tested a second aversive stimulus (tail lift) and again observed comparable excitatory responses in rostral and caudal D1-SPNs. Third, we assessed whether optogenetic activation of these neurons is perceived as rewarding or aversive. Using a real-time place preference/aversion assay, we found that optogenetic stimulation of D1-SPNs in both subregions induced place aversion.

Together, these experiments show that while D1-SPNs display region-specific effects on reward-related feeding behavior, their activity responses to aversive stimuli and the avoidance response to optogenetic activation are similar across rostral and caudal medNAcSh. This contrast strengthens our conclusion that the D1-SPN rostro-caudal gradient is specific to appetitive contexts.

We added the following in the discussion:

“Here, we further tested the existence of rostro-caudal gradients for aversion, asking whether D1-SPNs in the rostral vs. caudal medNAcSh respond differently to aversive stimuli. To ensure that any observed effects were not specific to a single stressor, we tested two distinct aversive stimuli (foot shock and tail lift). In both cases, we found no rostro-caudal differences, as D1-SPNs in both subregions responded with excitation. We also asked whether optogenetic activation of these neurons is perceived as aversive. Stimulation of D1- SPNs in both rostral and caudal medNAcSh promoted aversive behavioral responses in the RTPPA experiment. Hence, in contrast to the pharmacological inhibitions mentioned above, we did not detect differences in aversive behaviors according to the rostro-caudal medNAcSh site.”

(c) The scope of behavior is mainly limited to consumption; testing related domains (motivation, reward valuation, and extinction) could broaden the significance.

We thank the Reviewer for the suggestion to examine additional behavioral domains such as motivation, reward valuation, and extinction. We focused our efforts on consumption given the large body of literature demonstrating a very important role of the medNAcSh in reward consumption. However, we fully agree that feeding encompasses multiple phases, from appetitive and goal-directed behaviors to consummatory behavior, and that the NAc in general, and to some extent the NAcSh is involved in behaviors across this spectrum. For instance, prior work has shown that the medNAcSh is involved in reward preference and that this follows a rostro-caudal gradient (e.g. Pedersen et al. 2022).

While it would be informative to directly test motivational processes using operant paradigms (e.g., nosepoke or lever-press tasks), our current experimental setup did not allow for these assays. Instead, we performed exploratory experiments manipulating the animals’ internal state with food deprivation. As expected, under food deprivation, total licking increased robustly in control mCherry and Rostral ChrimsonR medNAcSh mice as compared to ad libitum feeding (25 min session with 5 alternating on-off blocks: ad libitum Control = 692 and Rostral ChrimsonR= 1280 average total licks per session, see Figure 2g-h and Supplementary Figure S7d; food deprived Control =2428 and Rostral ChrimsonR =2390 total licks averaged for N=9 Control, N= 12 Rostral). Moreover, similar to ad libitum feeding, optogenetic activation of rostral D1-SPNs suppressed licking in food-deprived mice , albeit to a lesser extent than under ad libitum feeding conditions (Figure 2).

These preliminary observations suggest that internal state modulates the role of rostral D1-SPNs in reward consumption, potentially reflecting an interaction between homeostatic and hedonic feeding circuits. However, as this line of investigation was exploratory and not pursued further in the present study, these data are not included in the main manuscript.

Author response image 1.

In vivo optogenetic stimulation of rostral medNAcSh inhibits reward consumption to a lesser extent after overnight food deprivation. a. Quantification of the average lick count per 5 min block in mCherry control mice vs. ChrimsonR (rostral) mice, showing a lower lick count in rostral medNAcSh ChrimsonR mice during the opto-stimulation epoch. Blocks of 5 min with or without opto-stimulation were alternated (on/off/on/off/on) for a total of 5 blocks. b. Quantification of mean lick counts in the opto-stimulation vs. non-opto-stimulation epochs shows a significant decrease in lick counts following stimulation of rostral medNAcSh D1-SPNs and no significant difference in the control mice. 2-way RM-ANOVA (group x epoch). Main effects: epoch F (1, 28) = 6.027, p=0.0206; group F (2, 28) = 1.448, p=0.2520; group x epoch F (2, 28) = 8.123, p=0.0017. Sidak post-hoc opto-stimulation vs. non opto-stimulation: Control on vs. off t(28) = 1.856, p=0.2061; Rostral medNAcSh on vs. off t(28) = 3.054, p= 0.0147. N=9 for Control mCherry; N=12 for Rostral medNAcSh ChrimsonR. c. Pie charts showing % of mice showing food intake inhibition (mean Δlick counts non-opto/opto>0) in each group: 42% of ChrimsonR rostral medNAcSh mice, 20% of controls. Data is mean ± SEM. *p<0.05; **p<0.01; ***p<0.001.

(3) Molecular profiling:

(a) Stard5 expression is present in both D1- and D2-SPNs; comparisons to bulk calcium signals and quantification of percentages across rostral and caudal cells would be helpful. The authors should establish whether these cells also express SerpinB2, an established marker of LH projecting neurons.

We thank the Reviewer for this relevant point. In the photometry experiments (Figure 7) using Stard5-Flp mice, we acknowledge that the recorded signals reflect a mixed population of D1- and D2-SPNs. Based on quantification in a separate set of brains, we estimate that Stard5 is expressed in a variety of cell types, of which 35% are D1-SPNs and 30% are D2-SPNs (Supplementary Figure S3). While Liu et al. 2024 reported no overlap between Stard5 and Drd2, canonical marker for D2-SPNs, available transcriptomic data (Chen et al. 2021) and our own histological and RNA-based analyses (Figure 6 and Supplementary Figure S3) found Stard5 to be expressed in both D1-SPNs and D2-SPNs. Hence, indeed, Stard5 is a mixed population.

We provide here the quantification of percentages of Stard5 expression across rostral and caudal cells: for instance, in the dorsal rostral medNAcSh, 79% of D1-SPNs and 76% of D2-SPNs express Stard5; in the ventral rostral medNAcSh the percentages are 47% and 55%, whereas the same percentages drop to 39 and 31% in the dorsal caudal medNAcSh and 15% and 20% in the ventral caudal medNAcSh.

As suggested by the Reviewer, we also performed further analysis of the publicly available scRNA-seq dataset from Chen et al. 2021, which shows that 4.4% of all Stard5-expressing cells are also Serpinb2+, while 1.8% of all sequenced NAc cells are Stard5+/Drd1+/Serpinb2+ and 0.21% are Stard5+/Drd2+/Serpinb2+.

(b) Verification of the Stard5-2A-Flp line (specificity, overlap with immunomarkers) should be documented more thoroughly.

We agree with the Reviewer that a more detailed characterization of the Stard5-2A-Flp mouse line would be relevant for the validation of the line.

In our study, we identified Stard5 as a marker gene that enables selective targeting of the rostral medNAcSh, as it is strongly enriched in the rostral medNAcSh (Figure 5-7). Stard5-Flp mice injected with Flp-dependent AAV in rostral medNAcSh, NAc core and dorsal striatum show specific AAV expression only in the rostral medNAcSh (Figure 7).

Moreover, we show that the line is specific as injection of a Flp-dependent AAV in a Stard5-Flp negative line does not lead to expression (Figure 7c).

However, re-analysis of the published scRNA-seq dataset (Chen et al. 2021) indicates that Stard5⁺ cells comprise a heterogeneous population, including D1-SPNs (~35%), D2-SPNs (~30%), local interneurons (~18%), glial cells (~12%), and other cell types (Suppl. Fig. S3).

Together, these data validate the Stard5-2A-Flp line as a spatially specific genetic entry point for the rostral medNAcSh, while highlighting the cellular heterogeneity of Stard5-expressing cells. Given the limited brain material left, we were not able to add additional colocalization analyses with immunomarkers, but agree this would be important to include in future studies.

(c) The molecular analysis is restricted to a small set of genes; broader spatial transcriptomics could uncover additional candidate markers. See also above.

We thank the Reviewer for this suggestion. Broader spatial transcriptomic analyses would indeed be highly valuable for identifying additional candidate markers. Our aim for the present study was to identify molecular landmarks to selectively target the rostral medNAcSh, but in a future study, we would be highly interested in building on our initial findings and providing an exhaustive molecular characterization of the region using spatial transcriptomics. We would be particularly motivated to do so, given the important functional specificity of the rostral NAcSh identified in the present publication.

Reviewer #2 (Public review):

Summary:

Marinescu et al. combine in vivo imaging with circuit-specific optogenetic manipulation to characterize the anatomic heterogeneity of the medial nucleus accumbens shell in the control of food intake. They demonstrate that the inhibitory influence of dopamine D1 receptor-expressing neurons of the medial shell on food intake decreases along a rostro-caudal gradient, while both rostral and caudal subpopulations similarly control aversion. They then identify Stard5 and Peg10 as molecular markers of the rostral and caudal subregions, respectively. Through the development of a new mouse line expressing the flippase under the promoter of Stard5, they demonstrate that Stard5-positive neurons recapitulate the activity of D1positive neurons of the rostral shell in response to food consumption and aversive stimuli.

We thank Reviewer 2 for the positive feedback, summary of our findings and for the thorough reading and constructive comments on the manuscript, which allowed us to improve the quality of the revised version.

Strengths:

This study brings important findings for the anatomical and functional characterization of the brain reward system and its implications in physiological and pathological feeding behavior. It is a well-designed study, technically sound, with clear and reliable effects. The generation of the new Stard5-Flp line will be a valuable tool for further investigations. The paper is very well written, the discussion is very interesting, addresses limitations of the findings, and proposes relevant future directions

We thank Reviewer #2 for their supportive feedback.

Weaknesses:

At this stage, identification and characterization of the activity of Stard5-positive neurons is a bit disconnected from the rest of the paper, as this population encompasses both D1- and D2-positive neurons as well as interneurons. While they display a similar response pattern as D1-neurons, it remains to be determined whether their manipulation would result in comparable behavioral outcomes.

We agree that this represents an important limitation of the current study. In our search for molecular markers of the rostral feeding hotspot, we identified Stard5 as a marker enriched in the rostral medNAcSh; however, Stard5 labels a heterogeneous population that includes D1- and D2-SPNs as well as other cell types. While Stard5⁺ neurons display activity patterns similar to D1-SPNs, we acknowledge that whether their direct manipulation would produce comparable behavioral effects to D1-SPNs remains to be determined. Moreover, it remains to be determined how the activity and function of Stard5⁺ neurons compares to D2-SPNs.

To specifically isolate Stard5⁺ D1-SPNs, we generated a Stard5-Flp;Drd1-Cre mouse line via breeding. However, the 4 CreON/FlpON AAVs which we tested exhibited leaky expression, including ectopic expression in Cre-positive but Flp-negative cells. This prevented reliable, cell-type-specific manipulation. We are actively working to overcome this common technical limitation of Flp/Cre AAVs, and these experiments will be addressed in a future study.

Recommendations for the authors:

Editor's note:

Readers would also benefit from coding individual data points by sex and noting N/sex in the figure legends.

We thank the editor for the note, we have noted in each figure legend the N and sex of the mice.

Reviewer #1 (Recommendations for the authors):

(1) Integration of results: The manuscript reads as two partly disconnected halves (functional gradient vs. molecular profiling). A more precise articulation of how the molecular findings (Stard5, Peg10) directly relate to the functional data would improve coherence.

We thank the Reviewer for raising this important point. We agree that clearer integration between the functional gradient and the molecular findings would strengthen the manuscript. In the present study, Stard5 and Peg10 are not introduced as mechanistic drivers of behavior, but as molecular landmarks that map onto the functional rostro-caudal organization of the medNAcSh.

Stard5 expression is enriched in the rostral medNAcSh, where we identify a functional hotspot for rewardrelated feeding, whereas Peg10 marks more caudal territories. Thus, the molecular profiling provides an independent axis that aligns with and supports the functional gradient revealed by photometry and optogenetic experiments. Whether these genes themselves contribute causally to feeding or aversive behaviors remains an open and interesting question for future studies.

To improve clarity, we have explicitly articulated this link in the Discussion:

“Importantly, our results indicate that spatial organization also defines functional specialization in the medNAcSh, and that molecular markers such as Stard5 provide access to these spatially defined subterritories rather than labeling a single, homogenous neuronal subtype.“

“Having established a robust functional dichotomy of D1-SPNs along the rostro-caudal axis in reward consumption, we next asked whether this functional organization is mirrored by differences in molecular composition across the medNAcSh. Using multiple anatomical techniques, we find strong differences in the molecular composition of the rostral vs. caudal medNAcSh, which in turn could explain behavioral differences between these brain subregions.”

“This makes Stard5 a spatial molecular landmark that captures the cellular ensemble of the rostral feeding hotspot, rather than a marker defining a single functional cell class. It is interesting that Stard5, a STARTdomain protein implicated in cholesterol metabolism and cellular stress responses (Alpy and Tomasetto, 2005; Rodriguez-Agudo et al., 2012; Calderon-Dominguez et al., 2014), and Peg10, an imprinted gene with roles in embryonic development and cancer (Mou et al. 2025), mark distinct rostro-caudal domains of the medNAcSh. Whether these genes themselves causally contribute to appetitive and consummatory behaviors, or aversive processing in this region remains an important question for future studies.”

(2) Injection site specificity: Given prior work on NAc manipulations, it is essential to ensure precise targeting. Representative images from both rostral and caudal placements, including verification of fiber/injection confinement, would increase confidence.

We thank the Reviewer for this important point regarding injection site specificity. Optic fiber placement was validated by identifying the coronal section in which the fiber tip was centered and aligning it to the mouse brain atlas (Franklin and Paxinos, The Mouse Brain in Stereotaxic Coordinates). We validated currently a total of 14 brains, shown in the newly added Supplementary Figure S10.

The primary source of variability across animals could be the extent of the viral spread and the size of the optic implants, which were 400 for photometry experiments and 200 μm for the optogenetic studies. We acknowledge that this limits the spatial precision with which the individual subregions can be isolated. This limitation is explicitly discussed in the manuscript.

Importantly, despite this limitation, we detected robust and reproducible differences between rostral and caudal medNAcSh in reward-consumption photometry and optogenetic assays. This argues against injection site proximity or fiber misplacement being a major confounding factor for the main conclusions. Nonetheless this comment is a valid point, and in future studies we plan to establish targeting methods with reduced viral volumes and/or tapered optic fibers (Pisanello et al. 2017). This will allow finer spatial restriction and more precise dissection of medNAcSh subregions.

(3) Minor clarifications:

(a) Provide explicit definitions of "rostral" and "caudal" coordinates.

We adjusted Figure 1 and added the coordinates.

(b) Consider alternative wording to "gradient" since only two rostro-caudal positions are tested.

RNA-seq and MERFISH data indicate that molecular markers in the NAcSh are organized along a continuous rostro–caudal gradient rather than discrete boundaries (Chen et al. 2021; Stanley et al. 2020). Our use of the term ‘gradient’ therefore reflects this established molecular organization, even though our functional experiments sampled two representative positions along this continuum.

We added the following sentence in the discussion for clarification:

“Of note, in this paper we decided to use the term “rostro-caudal gradient”, motivated by converging evidence from prior pharmacological studies (see below) and scRNA sequencing data (Chen et al., 2021; Stanley et al., 2020), which show continuous molecular and functional changes along the rostro-caudal axis of the medNAcSh rather than sharply defined boundaries. Our use of the term ‘gradient’ therefore reflects this established molecular organization, even though our functional experiments sampled only two representative positions along this continuum.”

(c) Enhance representative images (e.g., stronger DAPI, zoom-ins, bregma coordinates).

To improve clarity, we have adjusted Figure 1 by adding schematic representations including stereotaxic surgery coordinates, which facilitate interpretation of rostro–caudal targeting.

(d) Report trial numbers in figure legends, injection site details (e.g., S1 mouse), learning curves, and rationale for low-pass filtering in photometry.

We thank the Reviewer for these suggestions. The average number of successful trials is now reported in the figure legends (Figure 1 and Figure 7). Injection site details are described in the Methods and are now also illustrated in Figure 1a and validated in Supplementary Figure S10. In addition, we have added Supplementary Figure S8 showing the learning curves of the Drd1-Cre and Stard5-Flp mice included in this study.

Regarding the low-pass filtering in photometry analysis: low-pass filtering (1 Hz) was applied to the signal to remove high-frequency noise and isolate slow calcium-dependent fluorescence fluctuations that reflect population-level neural activity as we have done before (Labouesse et al. 2023, 2024). Low-pass filtering is a commonly-used analysis in fiber photometry and often shows a better artifact-corrected signal (Zhang et al. 2023; Keevers and Jean-Richard-dit-Bressel 2025).

Reviewer #2 (Recommendations for the authors):

Major Comments:

(1) As mentioned, I find the part on Stard5-positive neurons a bit disconnected. Ideally, as mentioned in the discussion, the author could cross Stard5-Flp mice with D1-cre to selectively monitor and/or manipulate these neurons. Alternatively, do they have any data regarding D2-positive neurons of the rostral part to show whether they behave differently from D1-positive neurons?

We thank the Reviewer for this suggestion and agree that selectively monitoring or manipulating Stard5⁺ D1-SPNs using an intersectional approach would strengthen the link between the molecular and functional findings. We are pursuing this strategy by crossing Stard5-Flp mice with Drd1-Cre mice; however, as noted above, currently available CreON/FlpON viral tools exhibited leaky expression (a commonly known problem for such AAVs), preventing reliable cell-type–specific targeting. As a result, these experiments are ongoing (including reducing the titers) and will be addressed in a future study.

At present, we do not have equivalent functional data for D2-SPNs in the rostral medNAcSh. Investigating whether rostral D2-SPNs behave differently from caudal D2-SPNs is an important and interesting question, which we hope to address in a future study. This limitation is acknowledged in the discussion.

(2) Do the authors have any data on locomotor activity when they manipulate D1-expressing neurons? Lower food consumption as well as lower activity in the stimulated compartment - interpreted as aversion - could be related to diminished locomotor activity.

We thank the reviewer for the relevant point about locomotion. We ran new analyses of locomotor activity during the feeding task (operant boxes) using a machine-learning model. A small subset of frames (136 frames from 10 video recordings) was manually annotated to define the animal’s body center and nose, as well as the four corners of the operant box. These annotations were used to train a YOLO (Redmon et al. 2015)-based pose estimation model. Locomotion metrics, such as total distance moved were subsequently derived from the temporal integration of positional data and aligned to opto-on and opto-off epochs of the feeding task. During licking periods, the animal’s body center remains largely stationary, which could lead to an overestimation of immobility. Nevertheless, we quantified the total distance traveled in the entire operant box across epochs, shown in Supplementary Figure S9 a-b. In our proof-of-concept experiment (Figure 2c-e), locomotion was increased in rostral ChrimsonR mice compared to controls (Supplementary Figure S9a), a similar effect seen with chemogenetic activation of D1-SPNs (Zhu, Ottenheimer, and DiLeone 2016). In our full experimental cohort, locomotion did not differ between control, rostral and caudal ChrimsonR mice across laser on and laser off epochs. These results indicate that reduced reward consumption during stimulation of rostral D1-SPNs is not due to decreased locomotor activity. Notably, whereas the inhibitory effect on consumption is specific to rostral D1-SPNs activation, locomotor effects are similar for both rostral and caudal D1-SPNs stimulation, indicating they are at least partly dissociated from one another.

Moreover, in the RTPPA task, it is accepted that the percentage of time spent in the light-paired chamber reflects the preference or aversiveness to optogenetic stimulation. We additionally quantified total distance traveled (Supplementary Figure S9c). While optogenetic stimulation of both rostral and caudal D1-SPNs reduced time spent in the light-paired chamber (Figure 4), total distance traveled was unchanged, indicating that the observed aversion is not due to reduced locomotion.

We added the following to the Results section: “To determine whether the reduced reward consumption observed in Rostral ChrimsonR mice could be explained by changes in locomotion, we quantified the total distance traveled during this task. Optogenetic stimulation led to an increase in locomotion in the small cohort of Rostral ChrimsonR mice in the reward consumption experiment shown in Figure 2d-e (Supplementary Figure S9a), while no change in locomotion was observed across epochs in mCherry controls, ChrimsonR Rostral and Caudal mice (Supplementary Figure S9b, related to Figure 2g-i)”

And

“Quantification of locomotion showed no reduction in distance traveled in the light-paired chamber (Supplementary Figure S9c), indicating that the avoidance was not driven by impaired locomotion. These data indicate that medNAcSh D1-SPNs generally promote aversion without affecting locomotion and without major differences along the rostro-caudal axis”

Additionally, we added the following sentence to the Discussion: “Importantly, our behavioral effects of rostral D1-SPNs in the reward consumption and RTTPA assays could not be explained by reduced locomotor activity. Indeed, optogenetic stimulation of D1-SPNs during the reward consumption task did not reduce locomotion; instead, locomotion was either unchanged or increased in a small cohort of Rostral ChrimsonR mice. The increased locomotion likely reflected appetitive behavior and is consistent with past chemogenetic studies (Zhu et al., 2016). In the RTTPA no locomotion differences were detected.“

(3) It would be useful to provide a schematic (or pictures) for the location of fiber implantation in all animals for both photometry and optogenetics.

We validated optic fiber placement in 14 animals by identifying the coronal section in which the fiber tip was centered and aligning this section to the mouse brain atlas (Franklin and Paxinos, The Mouse Brain in Stereotaxic Coordinates). Representative optic fiber placement and viral spread are shown in the newly added Supplementary Figure S10.

Minor Comments:

(1) Figure 6e and g seem mislabeled: "Drd1+ (D2-SPNs)".

Yes, thank you. We corrected it.

(2) Line 395-397: the authors mention Flp minimal Flp Leakage, but could it be low activity of Stard5 promoter in the core and dorsal striatum that allows little expression of the flippase that could be sufficient for recombination?

We thank the Reviewer for this insightful point. We cannot fully distinguish between these possibilities in the current study; however, the overall recombination outside the target region remains minimal, supporting the utility of the Stard5-Flp line for selective targeting of the rostral medNAcSh. Injection of a Flp-dependent AAV into the lateral shell, core and dorsal striatum showed no expression, therefore we think this is unlikely. Moreover, this aligns with Stard5 expression patterns derived from the scRNAseq data (Chen et al. 2021), Allen Brain Atlas quantifications (Figure 5) and our RNAscope analysis (Figure 6). Nevertheless, we acknowledge that histology alone cannot definitively exclude this possibility, and quantitative approaches such as qPCR would be required.

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Reviewer #2 (Public review):

This study examines how curl in the retinal flow field can be used as a control variable for estimating and controlling the heading of a moving observer. The basic idea (which is not entirely new, see Matthis et al. 2022) is that translation along a path with eccentric gaze (meaning that the subject is not heading toward the point they are looking at) produces a pattern of optic flow on the retina with a rotational component around the point of fixation (which can be captured by the mathematical "curl" operator). The sign and magnitude of retinal curl vary with heading relative to the point of fixation, such that curl can be used as a control variable to steer rightward or leftward to move toward the fixated target. The authors perform behavioral experiments and show that there are biases in perceived heading that seem to be largely governed by retinal curl. They also show that a simple controller model can use curl to steer toward a target, and they provide a neural network model that provides a biologically plausible implementation of the controller (although there are some questions about that).

There is a core of interesting work here that I think can be important to the field. However, there is a lack of clarity on several important fronts, including design of the behavioral experiments, presentation of the behavioral data, conceptual framing of what curl can and cannot do, etc. Equally importantly, the manuscript is not written in a manner that will make it accessible to most vision scientists. I consider myself to be pretty knowledgeable about optic flow, and I had to read most of the manuscript 3 or 4 times to be able to understand the bulk of it. And my experience is that most vision scientists do not understand optic flow well, so I fear that most of the readers that the authors should want to reach would struggle to understand the work. As written, this is mainly going to make an impact on a handful of optic flow gurus. Thus, I consider that this manuscript will need a major overhaul to clarify important issues and make it more accessible.

Major issues:

(1) The manuscript contains inconsistent, if not misleading, messaging about what information retinal curl does, and does not, provide regarding heading estimation. In the Abstract, the authors state: "We propose an alternative: the visual system utilizes retinal curl directly to estimate heading, rendering the explicit recovery of the FOE unnecessary." Based on my understanding of the rest of the manuscript, I find this statement to be a misrepresentation for two main reasons:

a) To "directly estimate heading" relative to what? When not qualified, most people interpret "heading" to mean an observer's heading relative to the world (or some allocentric reference frame). But retinal curl only gives information about an observer's heading relative to the point on which their eyes are fixated. Moreover, that point of fixation will change every few hundred milliseconds in natural viewing, so the retinal curl will change with each new fixation even as heading relative to the world remains unchanged. So I think most readers would grossly misinterpret the claim that retinal curl can be used "directly to estimate heading". Indeed, in the authors' controller model, the initial heading needs to be given, and then the controller can work. But from where does the visual system get the initial heading, since it does not come from curl? These issues are left hanging. Thus, while curl can provide a very useful input for steering toward a fixated target, other signals are needed to estimate heading relative to the world. This has to be made much clearer early on, and a conceptual schematic diagram might help. Also, the authors generally do not specify the reference frame of the variables they are talking about, leaving lots of room for misinterpretations. It should be clear each time they are talking about a variable, such as heading, whether it is relative to the fixation target, body, world, etc.

b) It seems to me that retinal curl will depend on other variables, in addition to heading relative to the fixation target. For example, it seems to me that the magnitude of retinal curl will depend on self-motion speed, the depth structure of the scene, the angle of elevation of the fixated target, and perhaps others. This is not discussed at all, and many readers would get the misguided impression that there is a 1:1 mapping from curl to heading (relative to fixation). If I am right that this is not correct, it means that retinal curl can tell the observer whether to steer right or left to move toward the fixated target, but it cannot tell them how much to steer. Indeed, in the authors' controller model, there is a free parameter that calibrates curl to angle. It makes sense that this works to fit trajectory data that are given from a fixed environment, but it is unclear how the brain would use retinal curl to control steering when these other variables are uncertain or changing unpredictably. Moreover, how does the system change the mapping from curl to steering command as the location of fixation changes relative to the current heading? These are issues that need to be brought up in framing the problem and discussed at some length. If the authors can show mathematically that retinal curl is only dependent on heading (relative to fixation) and not any of these other variables, it would be very valuable to show the equations for this relationship.

(2) The description of the behavioral experiment and presentation of behavioral data leaves a lot to be desired.

a) First, it is stated (line 158) that "Participants continuously reported their perceived direction of self-motion while maintaining fixation on the yellow dot." Again, the reference frame is completely unspecified. Participants were reporting their perceived heading relative to what? The fixation target? The world? What exactly were the instructions given to the subjects to perform the task? Based on the description of how perceived paths are computed (line 166-), it seems to be presumed that subjects are reporting their heading relative to the world because those angles are then converted into x and z coordinates in what I presume is a world-centered reference frame. But how do we know that subjects are accurately reporting their heading relative to the world? What if they are biased in their reports by the location of the fixation target relative to the scene, or by some other reference signal? Is it possible for the authors to rule out the possibility that perceptual biases seen in the unaltered curl condition result from observers not fully adopting the assumed reference frame of the task? If this cannot be firmly excluded, it seems to create problems for the rest of the study.

b) I also feel that there is a mismatch between what the behavioral task requires and what the controller model does. Subjects are apparently asked to report their heading relative to the world, but the controller model only controls their heading relative to the point that they are fixating. I understand how this is resolved in the model, but I think this type of distinction is buried and will not be apparent to most readers. Again, the reference frames of what is being measured and controlled need to be specified explicitly in all parts of the paper, and the authors need to explain how the system would combine curl-based control with some other measures of (at least initial) heading for world-centered heading to be computed. All of the assumptions need to be clearly specified.

c) In addition, I found it frustrating that the authors never present raw perceptual data from the observers. Rather, in Figure 2, we see reconstructed trajectories that are perfectly smooth with no indications of noise whatsoever. Since these paths are computed from the perceptual reports, there must be some noise inherent in them. The figures should represent this uncertainty somehow, and it should be explained how these perfectly smooth trajectories are obtained.

(3) "...the magnitude of retinal curl in the fovea can specify the body trajectory relative to gaze (Matthis et al., 2022)." The main idea put forward by the authors here seems to overlap heavily with this statement that they attribute to Matthis et al. 2022. While I think this paper still adds importantly to the topic, the authors do not discuss how their findings are different from those of Matthis et al. 2022, why they are an important extension, etc. Readers should not have to go read this other paper to have any idea how the present findings are placed in importance relative to the literature.

(4) The analysis and treatment of eye movements is extremely weak. The authors discarded trials for which gaze deviated from the fixation point by more than 3 degrees (which is a LOT given that the eye speeds are generally in the neighborhood of 0.5 deg/sec), and they provide basic stats on the distribution of positions. But this largely misses the point: it is not small position errors that are likely to matter, but rather velocity errors. Even a small amount of retinal slip of the target while it is being pursued will cause image motion that is going to alter the optic flow field around the fixation target. So, for example, the retinal curl field may no longer be centered on the fixation target. How do we know that some of the perceptual biases are not influenced by image motion resulting from imperfect tracking of the fixation target? This needs to be analyzed and discussed.

(5) I found the sections of text comparing the separate and joined fits (starting line 287) to be a bit too rosy. The authors show the separate fits in the main text, and it is not very surprising that these fits are good, given that the model has 30 parameters, and these data are pretty low-dimensional. The authors only show the joined fits in the supplement, and they say that they are almost as good as the separate fits (indeed, they are better in a model comparison sense, but this is 30 parameters vs. 2 parameters). However, when I look at the fits of the joined model in the supplement, I don't find them to be very impressive. In particular, the model grossly misses the data for the straight paths for several subjects (e.g., id5, id6, id8, id10). And fitting the straight paths would presumably be easiest. This implies that the joined model is really missing something and that fitting the curved paths interacts strongly with fitting the data for different fixation target locations on the straight path. I think that the authors should discuss the results a bit more soberly and tone down their conclusions here.

(6) The section of the paper on neural simulations (starting line 387) has a few weaknesses. First, why are only straight paths simulated here? This does not seem to provide a very rigorous test of the model. Second, it is awkward that the simulation results are presented in units of pixels, rather than degrees. Third, the authors seem to downplay the fact that the neural estimates of heading seem to oscillate rather wildly (over a range of hundreds of pixels, whatever that means, see especially Figure S16). It was far from clear to me how an estimate of heading with these large oscillations is useful. It would seem to require that heading estimates are integrated over substantial lengths of time to be reliable. It was therefore unclear how the model produces such smooth paths from these oscillating estimates.

One idea from this chapter that stood out to me is the tension between authenticity and anonymity online. I found it interesting that the chapter suggests anonymity can sometimes support authenticity rather than undermine it. At first, that feels counterintuitive because we usually think of anonymous accounts as less trustworthy or even deceptive. But thinking about it more, I agree that anonymity can allow people to express parts of their identity they might hide in real life due to fear of judgment or consequences. For example, people may share honest opinions, personal struggles, or marginalized identities more openly when they are anonymous. At the same time, this creates a difficult balance for platforms, because anonymity can also enable harmful behavior. It makes me wonder: is it even possible for a platform to encourage “authenticity” without limiting anonymity, or are those two goals always in tension?

I like that we are give this open while not required to all but somewhat of our work that we have does throughout the course. I think it will be interesting to post different perspectives and share while receiving them as well! Excited to see the final deliverable.

Author response:

Reviewer 1:

Porte et al. investigate how observers form confidence judgments about the presence vs absence of near-threshold audiovisual stimuli. In two psychophysical detection experiments, human participants judged whether a stimulus (visual, auditory, or audiovisual) was present or absent, reported amodal confidence, and then gave modality-specific detection and confidence ratings using a bidimensional scale. The authors report that audiovisual (AV) stimuli are detected more accurately than unimodal stimuli, but that multisensory stimulation does not improve metacognitive efficiency. Participants are more confident in absence than in presence judgments. They extend a previously proposed model to an audiovisual setting, assuming evidence is available only for presence and that absence is inferred via counterfactual detectability. Detection is modeled with a disjunctive integration rule across modalities, while confidence is explained by a combination of conjunctive (for presence) and disjunctive/negation-of-disjunction (for absence) rules.

We thank the reviewer for thoroughly evaluating our work.

There are several points I wish to have clarified, outlined below:

(1) Framing of bimodal vs unimodal detection

On p.3, the introduction states that "Adults typically show higher detection rates and faster reaction times for bimodal than for unimodal stimuli." This is broadly consistent with the literature, but as written, it obscures the fact that these effects depend critically on experimenter-defined stimulus strengths. It is trivial to construct cases where a strong unimodal stimulus is more detectable than a bimodal stimulus made of two very weak unimodal stimuli. If "bimodal" is understood as the co-presentation of two unimodal components matched in detectability, then Bayes-rule-based arguments indeed predict better detection for the bimodal case; how much better is theoretically interesting, but not quantified in this paper. There is an entire literature on the combination of two unimodal stimuli, which is not touched on. For a pertinent reference, see Ernst & Banks 2002. I recommend clarifying that the statement assumes comparable unimodal intensities.

We will clarify that when discussing bimodal stimuli, we mean the co-presentation of two unimodal stimuli of similar intensity. We will add references to the literature during discrimination tasks that have shown that multisensory cue-combination followed Bayes rule integration (e.g., Ernst & Banks, 2002; Battaglia et al., 2003; Alais & Burr, 2004) and clarify in which ways our work differs from this rich body of work and provides novel contributions.

(2) Relationship to signal detection theory and counterfactual perceptibility

In the introduction, the authors write, "If sensory evidence is only available for presence," motivating counterfactual perceptibility as a necessary ingredient to infer absence. However, standard signal detection theory (SDT) already provides a widely accepted framework in which a continuous internal response is present on both signal and noise (absent) trials, with absence corresponding to the noise distribution and decisions implemented by a criterion. Thus, there is no logical need to invoke counterfactual perceptibility simply to define absence; rather, the Mazor-style framework adds an explicit belief model about detectability and an optimal stopping policy. It would strengthen the paper to more clearly state how the proposed model goes beyond SDT conceptually, acknowledge that SDT can account for presence/absence decisions without counterfactuals, and position the counterfactual account as a hypothesis about how observers actually compute absence/confidence, not as a necessity.

One of the central claims of the paper is that detection in the case of absence requires counterfactual reasoning. The authors should demonstrate whether or not an SDT-based generative model can describe these amodal and uni- and bi-modal stimulus decisions. In such an SDT model, an SDT-based generative model in which the noise distribution is shared across conditions, and unimodal vs bimodal differences are captured by changes in the mean or variance of the signal+noise distribution.

We will clarify that our framework explains how absence judgments (and related confidence) are formed, and what it adds to SDT models, including the reproduction of reaction times and a normative explanation of criterion placement (results about RTs are available in the supplementary materials).We will also run additional model comparisons assessing how an SDT-based generative model performs compared to our Bayesian model based on counterfactual perceivability.

(3) Confidence vs performance: is AV confidence special?

The paper's central claims about multisensory confidence and metacognition would be stronger if the authors showed that AV confidence deviates from what is expected given performance alone. From the reported results, AV accuracy is around 80%, with visual and auditory at about 60% and 40%, respectively. Given that confidence typically monotonically scales with accuracy, the first question is whether AV confidence is entirely explained by improved performance, or whether there is an additional multisensory contribution. A simple, informative analysis would be for each subject, plot mean confidence vs per cent correct for AV, V, A, and absent conditions, and to test whether AV confidence lies above the trend predicted by accuracy alone.

This is an excellent suggestion, and we will conduct the proposed analysis.

(4) Metacognitive measures: logistic regression slopes vs meta-d′/d′

In the "Multisensory effects on metacognitive performance" section, the authors define "metacognitive sensitivity" as the slope of a Bayesian logistic regression predicting accuracy from confidence. There is substantial literature showing that logistic-slope measures of metacognitive sensitivity are criterion-dependent and can be affected by both task and confidence criteria (for one example, see Rausch & Zehetleitner, 2017). In contrast, meta-d′/d′ was specifically developed to provide a bias-invariant measure of metacognitive efficiency. Though this, too, is dated (see Boundy-Singer et al., 2023). Given that the authors already estimate HMeta-d-based M-ratios, it is unclear why they rely on logistic regression slopes as their primary "metacognitive sensitivity" metric in Figure 4A. I suggest either replacing the logistic-slope metric with SDT-based measures (meta-d′, meta-d′/d′) or providing a clear justification for using logistic slopes, along with a discussion of their known limitations.

Additionally, Figure 3 reports M-ratios without showing the corresponding d′ or meta-d′ for judge-present vs judge-absent conditions. Presenting these would help contextualize the metacognitive efficiency results and clarify whether differences are driven mainly by changes in metacognitive sensitivity, changes in task performance, or both. The d' values per condition could be added to Figure 2A.

All typical measures of metacognitive sensitivity are influenced by metacognitive bias and task performance to some extent, and none of them is a pure measure of type-2 sensitivity (e.g., see Rahnev, 2025). Here, we chose logistic regression because it enables modeling interactions with other predictors in a factorial design with a limited number of trials.

We will clarify the limitations of metacognitive sensitivity measures and better explain why we then used Mratio to estimate metacognitive performance while controlling for underlying task performance.

Thank you for this suggestion. We will add the d’ values per condition to Figure 2A.

(5) Interpretation of confidence in absence vs presence

The authors emphasise that it is surprising subjects are more confident in absence than in presence judgments, both at amodal and modality-specific levels. However, Figure 2B suggests that absent responses are very accurate: absent is reported as present only in about 10% of absent trials, implying a high correct rejection rate. If confidence tracks outcome probability, higher confidence for absence may be at least partly expected. Before attributing this asymmetry primarily to counterfactual reasoning, it would be important to explicitly relate confidence to accuracy for hits, misses, false alarms, and correct rejections and show whether absence confidence remains elevated relative to presence after controlling for accuracy differences across judgment types and conditions. Without this, the interpretation that higher absence confidence is inherently "unexpected" seems overstated.

This higher confidence for absence judgments than for presence judgments was observed while controlling for response accuracy. We will clarify this in the main text.

(6) Model: integration rules, confidence, and evidence strength

The modeling section extends the Mazor et al. ideal observer to two modality-specific sensors, with disjunctive integration for detection and then disjunctive vs conjunctive integration rules for confidence. I have a few comments.

First, the detection rule is disjunctive and is reported as a finding. However, the conclusion that detection relies on a disjunctive rule ("present if A or V") closely mirrors the task instructions-participants are explicitly told to respond "present" if they detect the stimulus in any modality. As such, this seems more like a sanity check than a novel empirical finding. Relatedly, the conjunctive detection is a weak null. The conjunctive rule ("present only if both A and V") is behaviorally implausible given the task instructions. A more informative baseline would be an SDT-style scalar-evidence model (see comment 2), rather than a conjunctive rule that participants would have to actively violate the instructions to follow.

Second, confidence in the model is defined as the probability of being correct at the time of the detection decision. However, this implies a fixed amount of evidence at decision time unless additional mechanisms are invoked. This issue is well known in diffusion modeling (see Kiani et al. 2014) and deserves explicit discussion; otherwise, it is unclear how the model produces graded confidence from a bound-crossing rule alone.

Third, the authors do not consider a straightforward evidence-strength account of confidence. When both modalities indicate presence, there is, on average, more total sensory evidence than in unimodal trials, making correct decisions more likely and, under most frameworks, confidence higher. Likewise, weak evidence in both modalities can be stronger evidence for absence than moderate in one and weak in the other. Many of the patterns that motivate the presence-conjunctive/absence-disjunctive mix could arise from a model where confidence simply reflects the amount of evidence for the chosen option, without positing distinct logical integration rules for presence vs absence. As the authors note, purely disjunctive or purely conjunctive confidence rules fail to capture the trends in confidence reports in Figure 7, leading them to adopt a combined presence-conjunctive/absence-disjunctive rule. A more parsimonious alternative-that confidence scales with evidence magnitude and cross-modal agreement-should be explicitly considered and, ideally, implemented as a competing model. Finally, if the model is intended as a good account of the data, it would be useful to report whether it also reproduces the metacognitive efficiency patterns (M-ratios) beyond the mean confidence patterns shown in Figures 7-8. At present, the model appears systematically over-confident, which should be acknowledged and quantified.

Indeed, the disjunctive rule was expected, given our design; we will clarify this. As mentioned above, we will directly compare the results of our current model with those of a more traditional SDT-based generative model, as suggested by the reviewer.

Contrary to a classical drift diffusion model, the model does not assume a fixed decision boundary, but derives an optimal stopping policy per time point and belief state. As a result, and depending on beliefs about perceptual evidence and the temporal discounting factor, optimal decision boundaries can be asymmetric and may collapse asymmetrically toward 0. Furthermore, given the asymmetry in the information value between sensor activations and inactivations, and differences in the information value of sensor activations of the two modalities, boundary crossing can lead to belief states that are far or close to the decision boundary, depending on the nature of the evidence. Together, even without an explicit modeling of post-decisional evidence, the model can account for variability in the total accumulated evidence at decision time.

From our understanding, the proposed alternative is equivalent to our current model, in which confidence scales with evidence magnitude.

The model was not fitted to confidence data, which could explain its overall overconfidence. To further test our model, we will assess its ability to reproduce patterns of metacognitive efficiency (M-ratios).

(7) Confidence asymmetry index (CAI) and modality weighting

The confidence asymmetry index (CAI) is defined as the difference between auditory and visual confidence on AV vs absent trials, and the authors report strong correlations between observed and simulated CAI across participants. They interpret this as evidence that subjects place different weights on auditory vs visual signals. Several questions arise. First, does CAI capture asymmetries beyond what is expected from accuracy differences between modalities and conditions? Second, because the simulated data are generated from model fits to the observed data, a correlation between observed and simulated CAI is expected: the model is built to reproduce the individual patterns it is then compared to. A stronger test would compare CAI from data simulated with modality-specific belief parameters, versus CAI from data simulated with constrained equal belief parameters (same θs). Relatedly, the paper would benefit from a plot showing the distribution of θs for A and V- present stimuli across subjects. These values could also be related to unimodal sensitivity measured in the calibration/training phases. A natural prediction is that higher unimodal sensitivity should correspond to higher belief parameters for presence.

The model was not fitted to either the modality-specific responses or the confidence ratings, so the correlation between observed and simulated CAI was not expected and provides a good test of our model's ability to reproduce the observed patterns. We will test whether the same correlations hold when using the difference in accuracy instead of the confidence.

We found that the best model is the one with the same belief across the visual and auditory sensors. Given this, we cannot investigate how modality-specific belief parameters are linked to unimodal sensitivity for each participant.

Reviewer 2:

Summary:

In this study, across two experiments, the authors wrestle with the question: What is the profile of confidence judgments in presence/absence decisions for audiovisual stimuli? After thresholding observers to 50% target detection rates in each modality, the authors conducted one experiment that included 75% target presence (spread equally across bimodal, auditory, and visual targets) and one experiment with 50% overall target presence. Results showed that, overall, detection performance was higher for audiovisual stimuli compared to unimodal ones, and that a recent model for stimulus detection could be extended to this multisensory scenario. By incorporating a disjunctive rule for absence judgments and a conjunctive rule for presence judgments, the model was able to qualitatively reproduce some of the trends observed in the human data regarding confidence.

Strengths:

(1) The paper makes novel contributions to the study of multisensory confidence judgments for yes/no target detection.

(2) The paper further extends the use of a leading model of stimulus detection (from Mazor et al., 2025).

(3) Pre-registration of the study was implemented, and the code is publicly available (although the GitLab link requires registration to access the materials).

(4) One of the empirical results (higher confidence for absence compared to presence judgments) is especially interesting, contributing another empirical finding to a very mixed literature on this topic (as the authors note).

We thank the reviewer for the positive evaluation of our work.

Weaknesses:

(1) Page 5 - I have concerns about the use of the equal-variance model from Signal Detection Theory to analyze the data. For example, the authors should read the recent paper by Miyoshi, Rahnev, and Lau in iScience, found at this link: https://www.cell.com/iscience/fulltext/S2589-0042(26)00373-1 . In this paper, the authors note how the equal variance model should be used with caution in yes/no detection tasks, since the variances of the "stimulus present" and "stimulus absent" distributions are often different from one another. In a revision, I highly recommend that the authors explicitly discuss this paper and review whether the assumptions for the equal-variance model have been met (e.g., since they have confidence data, one way to do this would be to evaluate if the slope of the line in zROC space differs from 1). The authors may also want to incorporate methods from this iScience paper into the current manuscript, or potentially move to using an unequal variance SDT model and compute d'a and c'a.

This is an excellent suggestion. We will run this analysis and refit the d’ and criterion response using unequal-variance models to see whether we observe the same results.

(2) Related to the computation/measurement of the response criterion, the authors note on page 18 in the Methods that for Experiment 1, signals are actually present on 75% of trials, since a bimodal stimulus is present on 25% of trials, the visual circle only occurs on 25% of trials, the sinusoidal tone occurs on 25% of trials, and then only noise is present on 25% of trials. Did the authors have any a priori hypotheses about the response criteria that participants would exhibit in Experiment 1, considering the unbalanced target presentation rate in this task? Also, in Experiment 2, what did it mean to equate target present and target absent trials? Is it that they broke 50% target present trials down into 16.67% bimodal targets, 16.67% visual targets, and 16.67% auditory targets? A few more details would be good to explicitly note for those trying to replicate the task

We will clarify this point in the manuscript. In Experiment 2, the stimulus was absent on 50% of the trials. As a result, the 50% of stimulus present trials were split into the three possible conditions, resulting in a sixth of the trials being auditory, a sixth visual, and a sixth audiovisual; we will make these proportions clearer in the text.

We did not have any a priori hypotheses about the response criteria for Experiment 1. The reviewer is right, the proportion of absent versus present trials can indeed have an impact on response bias. In fact, one of the goals of Experiment 2 was to test whether the low frequency of absent trials compared to present ones could explain both response bias and higher confidence in absence observed in Experiment 1, which we found was not the case, as we did not observe a difference between the two experiments. We will clarify this in our revision.

(3) It is important to plot the individual data for Figure 2. If the authors didn't match detection performance for the visual and auditory modalities, it would be good to see the individual data to know why. Is it that the thresholding procedure didn't work for some of the participants in the visual modality, and that's why the "yes" response rate is (on average) ~60% or higher across the two experiments? Similarly, in the auditory domain, do the authors have participants that are at floor? Or is it simply that the staircases failed to successfully target 50% detection on average?

We will add individual data to Figure 2.

Indeed, staircases failed to achieve 50% detection on average; participants for whom psychometric curves did not converge were excluded, as were those at floor level in one of the two modalities.

(4) The authors mentioned that data were collected on the Prolific platform. What checks did they conduct to ensure that this data wasn't produced by bots? There are recent high-profile publications in PNAS and Behavioral Research Methods that indicate how online data collection is problematic (e.g., https://www.pnas.org/doi/10.1073/pnas.2535585123and https://link.springer.com/article/10.3758/s13428-025-02852-7 ). What analyses or quality checks are there to ensure that humans were the ones completing the task?

Data were collected on the Prolific platform, which has been shown to yield high-quality data (Kay, 2025). However, we agree that this is a potential concern and will add a note of caution in the revised manuscript, even if the risk that the data do not come from humans but from bots is low (Huskey et al., 2026; Chetverikov, 2026).

(5) Page 7 - Since confidence was collected on a continuous scale, the authors should say a bit more about how they were able to compute measures of metacognitive efficiency. My understanding is that to compute meta-d', the data has to be binned. How was the binning implemented? With whatever bin size the authors chose, would it make any difference to the results if they changed the number of the bins in the analysis?

We will clarify this aspect of the analysis. Data were binned into four quartiles based on the overall distribution of confidence values across participants, based on the binning used in the example in Fleming (2017). We will examine whether changing the number of bins changes the results (Dayan, 2023).

(6) Page 8 - Is there a prior precedent for using slope of the Bayesian logistic regression predicting accuracy from confidence as a measure of metacognitive sensitivity? If so, can the authors cite those papers as a reference? If not, can they place this analysis within the context of other measures of metacognitive sensitivity that exist? (meta-d', AUROC (Type 2), etc.)

Yes, logistic regression has been used to quantify metacognitive sensitivity before. We will add the relevant papers as references (e.g., Sandberg et al., 2010; Norman et al., 2011; Siedlecka et al., 2016; Wierzchoń et al., 2012; Faivre et al., 2018; Pereira et al., 2023)

(7) Page 8 - Another one of the results on page 8 is worth reflecting further upon: the authors note how in Experiment 1, no credible difference was found between unimodal and bimodal trials (DeltaM = -0.25 [-0.59, 0.10]), but in Experiment 2, "we observed higher metacognitive efficiency in unimodal compared to bimodal trials (DeltaM = -0.28 [-0.54, -0.02]. Those DeltaM values are nearly identical, so without a power analysis motivating the number of participants the authors collected, how certain are they that the results from these two experiments are really that distinct? It reminds me a bit of the Andrew Gelman blog post, "The difference between significance and non-significance is not significant".

The number of participants was determined using a Bayesian optional stopping rule, as preregistered. The reviewer is right that the delta values are very similar in the two experiments. Given that a difference was found in only one experiment, we decided not to draw conclusions from it.

(8) Is there any way to look at whether the presence of multisensory hallucinations (or perhaps that word is too strong, and we should simply consider them miscategorizations) increased as the task progressed? That is, the authors have repeated presentations of audiovisual stimuli for at least some percentage of the trials. Since the percentages for auditory stimuli being correctly categorized as auditory are at 85% in Experiment 1 and 79% in Experiment 2, were the trials where they miscategorized these stimuli equally spread throughout the task? Or did they come later in the experiment, after being repeatedly exposed to multisensory trials?

We will examine how the proportion of miscategorisation changed throughout the task.

(9) Would the authors obtain the same results if they got rid of the amodal confidence judgment in their task, and simply had participants report the bimodal confidence following the presence/absence judgment? Part of the reason for asking this is that, according to page 11, the model is only fitted to amodal detection accuracy and response time data. This surprised me. I would have expected that the bimodal confidence would provide more useful information for the model fit. The authors should further explain this rationale in the paper. It seems odd to me to have the multisensory confidence ratings and not have them play a central role in the modeling work.

Our main goal was to investigate how participants form integrated, supramodal confidence judgments on the basis of multisensory sources of information. Therefore, the amodal confidence judgments are required here.

Moreover, the model was fitted to response times that corresponded to the amodal judgment. Because we had no meaningful response times for the modality-specific judgment, we could not use them to fit the model.

(10) In Figure 6, it appears the model is a bit off in its estimate of auditory responses (panel B, E) in the AV condition. Do the authors have any intuitions about why this might be happening?

Indeed, the model does not capture the full behavioral effects reflecting multisensory interference in the modality-specific responses. We suppose that the model does not reproduce these interferences, as it is only fitted to amodal detection accuracy, and as the two sensors are completely independent from one another. We will clarify this aspect in the text.

(11) The authors talk about how the model is reproducing effects in the human data, but there's no systematic comparison, quantitatively, of how the two things relate. The authors should include some quantitative measure that reflects this

In addition to the d’ and criterion comparison between the observed and simulated data, we will compare modality-specific d’ and the correlations between observed and simulated confidence.

(12) Related to this, I am not sure I agree with the characterization in Figure 7 that "when confidence followed a disjunctive rule, the model failed to capture important aspects of the data. On the other hand, when confidence followed a conjunctive rule, it reproduced confidence in presence judgments but failed to capture variability in confidence ratings for absence judgments." What, quantitatively, is the basis of this claim? This applies to Figure 8, too. I am not clear how, specifically, and quantitatively, the authors are justifying their claims about model fits. I don't think the confidence asymmetry index in Figure 8 is enough to quantify the quality of the model fitting procedure.

To further support this claim, we will add a quantitative comparison of the different confidence fits.

(13) Is there any chance the higher metacognitive efficiency for auditory trials is simply driven by differences in the d' values across the modalities? It might be good to probe this effect further.

Thank you for this remark. Indeed, the difference in metacognitive efficiency may be driven by differences in the d’ values, and so a lower d’ for auditory stimuli can lead to higher metacognitive efficiency for a similar metacognitive sensitivity.

Reviewer 3:

This study used a pre-registered novel behavioural paradigm and computational modelling to investigate multi-sensory influences on detection and confidence. Participants performed amodal detection of auditory and visual stimuli (indicating that a stimulus was there when either an auditory stimulus or a visual stimulus or both were present), followed by amodal and unimodal confidence ratings. Detection was higher when both stimuli were present, and the presence of one modality increased the confidence in the presence of the other modality. In contrast to previous detection studies, confidence was higher for absent than for present judgements, but metacognitive efficiency was higher for present judgements. Metacognitive sensitivity was higher for bimodal stimuli, but this was not the case for metacognitive efficiency, suggesting that the sensitivity might be driven by first-order performance. The computational model showed that both detection and confidence in absence followed a disjunctive evidence integration rule, while confidence in presence followed a conjunctive integration rule.

We thank the reviewer for engaging with our work.

Strengths:

The paper has several major strengths. Firstly, it addresses a novel research question using an innovative and well-controlled paradigm. Furthermore, the paradigm and analyses were pre-registered, and all effects that were interpreted were replicated in two independent samples. Finally, the paper uses an advanced computational model to capture counterintuitive patterns in the data.

Weaknesses:

The major weakness of the paper is the narrative structure. It is not always clear how the different analyses relate to the main research question. Many different effects are reported in terms of detection accuracy, bias, confidence and metacognition, as well as cross-modal and unimodal versus bimodal effects. It would help readability if the paper were streamlined in terms of the research question that is being answered, which I believe is specifically about multimodal absence judgements. Relatedly, for a reader not intimately familiar with the metacognition literature, the difference between MRatio, metacognitive sensitivity and metacognitive efficiency is not obvious. It would be good to clarify this more in the manuscript.

We will improve the narrative structure so that each result clearly relates to the research question.

We will also add a clearer definition of the various metacognition metrics to improve readability.

In general, the conclusions drawn by the authors seem to be supported by the results. However, I was missing quantitative model comparisons between the conjunctive and the disjunctive models and an explanation of why the models systematically overestimated the confidence ratings. Furthermore, the 'perceptual multisensory interference' section reports on very interesting effects, but these are not supported by statistical tests in the main text. It would help to assess the strength of the claims if the statistical evidence in favour of these claims were presented together in the main text.

The model was not fitted to confidence data, which could explain its overall overconfidence. As stated in previous responses, we will perform additional analyses to evaluate the model’s ability to reproduce confidence ratings. As some of the results were not replicated across experiments, we decided to put all statistical results related to multisensory interference in the supplementary materials and to focus only on consistent results across experiments.

One other concern is that in real-world multi-sensory perception, such as the mosquito example in the introduction, the auditory and visual signals have a strong natural association, which means that if you hear the auditory signal, you expect that you will see the visual signal soon and vice versa. As far as I understood, this association was not present in the current paradigm, which might influence the type of effects that one would expect to see.

The relation here is indeed artificial; we try to reinforce it as much as possible in the instructions of the task by indicating to the participants that they have to “detect a mosquito” that could be present auditory, visually, or both. But we acknowledge that the association between the visual and auditory stimuli is artificial, which may indeed influence our results.

References

Alais, D., & Burr, D. (2004). The Ventriloquist Effect Results from Near-Optimal Bimodal Integration. Current Biology, 14(3), 257‑ 262. https://doi.org/10.1016/j.cub.2004.01.029

Battaglia, P. W., Jacobs, R. A., & Aslin, R. N. (2003). Bayesian integration of visual and auditory signals for spatial localization. JOSA A, 20(7), 1391‑ 1397. https://doi.org/10.1364/JOSAA.20.001391

Chetverikov, A. (2026). Online behavioral studies are safe for now : Unusual RTs do not imply bots (A reply to Van der Stigchel et al., 2026) (Gjw5u_v1). PsyArXiv. https://osf.io/preprints/psyarxiv/gjw5u_v1/

Dayan P. (2023). Metacognitive Information Theory. Open mind : discoveries in cognitive science, 7, 392–411. https://doi.org/10.1162/opmi_a_00091

Ernst, M. O., & Banks, M. S. (2002). Humans integrate visual and haptic information in a statistically optimal fashion. Nature, 415(6870), Article 6870. https://doi.org/10.1038/415429a

Faivre, N., Filevich, E., Solovey, G., Kühn, S., & Blanke, O. (2018). Behavioral, Modeling, and Electrophysiological Evidence for Supramodality in Human Metacognition. Journal of Neuroscience, 38(2), 263‑ 277. https://doi.org/10.1523/JNEUROSCI.0322-17.2017

Fleming, S. M. (2017). HMeta-d : Hierarchical Bayesian estimation of metacognitive efficiency from confidence ratings. Neuroscience of Consciousness, 2017(1),

Huskey, R., Zhao, Z., Parry, D. A., & Fisher, J. T. (2026). An AI agent can complete the Attention Network Test with human-like behavioral signatures : Implications for the bot-or-not debate (T2jru_v1). PsyArXiv. https://osf.io/preprints/psyarxiv/t2jru_v1/

Kay, C.S. Why you shouldn’t trust data collected on MTurk. Behav Res 57, 340 (2025). https://doi.org/10.3758/s13428-025-02852-7nix007. https://doi.org/10.1093/nc/nix007

Norman, E., Price, M. C., & Jones, E. (2011). Measuring strategic control in artificial grammar learning. Consciousness and Cognition, 20(4), 1920-1929. https://doi.org/10.1016/j.concog.2011.07.008

Pereira, M., Skiba, R., Cojan, Y., Vuilleumier, P., & Bègue, I. (2023). Preserved Metacognition for Undetected Visuomotor Deviations. Journal of Neuroscience, 43(35), 6176‑ 6184. https://doi.org/10.1523/JNEUROSCI.0133-23.2023

Rahnev, D. (2025). A comprehensive assessment of current methods for measuring metacognition. Nature Communications, 16(1), 701. https://doi.org/10.1038/s41467-025-56117-0

Sandberg, K., Timmermans, B., Overgaard, M., & Cleeremans, A. (2010). Measuring consciousness : Is one measure better than the other? Consciousness and Cognition, 19(4), 1069‑ 1078. https://doi.org/10.1016/j.concog.2009.12.013

Siedlecka, M., Paulewicz, B., & Wierzchoń, M. (2016). But I Was So Sure ! Metacognitive Judgments Are Less Accurate Given Prospectively than Retrospectively. Frontiers in Psychology, 0. https://doi.org/10.3389/fpsyg.2016.00218

Wierzchoń, M., Asanowicz, D., Paulewicz, B., & Cleeremans, A. (2012). Subjective measures of consciousness in artificial grammar learning task. Consciousness and cognition, 21(3), 1141-1153. https://doi.org/10.1016/j.concog.2012.05.012

Reviewer #2 (Public review):

Summary:

In this study, across two experiments, the authors wrestle with the question: What is the profile of confidence judgments in presence/absence decisions for audiovisual stimuli? After thresholding observers to 50% target detection rates in each modality, the authors conducted one experiment that included 75% target presence (spread equally across bimodal, auditory, and visual targets) and one experiment with 50% overall target presence. Results showed that, overall, detection performance was higher for audiovisual stimuli compared to unimodal ones, and that a recent model for stimulus detection could be extended to this multisensory scenario. By incorporating a disjunctive rule for absence judgments and a conjunctive rule for presence judgments, the model was able to qualitatively reproduce some of the trends observed in the human data regarding confidence.

Strengths:

(1) The paper makes novel contributions to the study of multisensory confidence judgments for yes/no target detection.

(2) The paper further extends the use of a leading model of stimulus detection (from Mazor et al., 2025).

(3) Pre-registration of the study was implemented, and the code is publicly available (although the GitLab link requires registration to access the materials).

(4) One of the empirical results (higher confidence for absence compared to presence judgments) is especially interesting, contributing another empirical finding to a very mixed literature on this topic (as the authors note).

Weaknesses:

(1) Page 5 - I have concerns about the use of the equal-variance model from Signal Detection Theory to analyze the data. For example, the authors should read the recent paper by Miyoshi, Rahnev, and Lau in iScience, found at this link: https://www.cell.com/iscience/fulltext/S2589-0042(26)00373-1. In this paper, the authors note how the equal variance model should be used with caution in yes/no detection tasks, since the variances of the "stimulus present" and "stimulus absent" distributions are often different from one another. In a revision, I highly recommend that the authors explicitly discuss this paper and review whether the assumptions for the equal-variance model have been met (e.g., since they have confidence data, one way to do this would be to evaluate if the slope of the line in zROC space differs from 1). The authors may also want to incorporate methods from this iScience paper into the current manuscript, or potentially move to using an unequal variance SDT model and compute d'a and c'a.

(2) Related to the computation/measurement of the response criterion, the authors note on page 18 in the Methods that for Experiment 1, signals are actually present on 75% of trials, since a bimodal stimulus is present on 25% of trials, the visual circle only occurs on 25% of trials, the sinusoidal tone occurs on 25% of trials, and then only noise is present on 25% of trials. Did the authors have any a priori hypotheses about the response criteria that participants would exhibit in Experiment 1, considering the unbalanced target presentation rate in this task? Also, in Experiment 2, what did it mean to equate target present and target absent trials? Is it that they broke 50% target present trials down into 16.67% bimodal targets, 16.67% visual targets, and 16.67% auditory targets? A few more details would be good to explicitly note for those trying to replicate the task.

(3) It is important to plot the individual data for Figure 2. If the authors didn't match detection performance for the visual and auditory modalities, it would be good to see the individual data to know why. Is it that the thresholding procedure didn't work for some of the participants in the visual modality, and that's why the "yes" response rate is (on average) ~60% or higher across the two experiments? Similarly, in the auditory domain, do the authors have participants that are at floor? Or is it simply that the staircases failed to successfully target 50% detection on average?

(4) The authors mentioned that data were collected on the Prolific platform. What checks did they conduct to ensure that this data wasn't produced by bots? There are recent high-profile publications in PNAS and Behavioral Research Methods that indicate how online data collection is problematic (e.g., https://www.pnas.org/doi/10.1073/pnas.2535585123 and https://link.springer.com/article/10.3758/s13428-025-02852-7). What analyses or quality checks are there to ensure that humans were the ones completing the task?

(5) Page 7 - Since confidence was collected on a continuous scale, the authors should say a bit more about how they were able to compute measures of metacognitive efficiency. My understanding is that to compute meta-d', the data has to be binned. How was the binning implemented? With whatever bin size the authors chose, would it make any difference to the results if they changed the number of the bins in the analysis?

(6) Page 8 - Is there a prior precedent for using slope of the Bayesian logistic regression predicting accuracy from confidence as a measure of metacognitive sensitivity? If so, can the authors cite those papers as a reference? If not, can they place this analysis within the context of other measures of metacognitive sensitivity that exist? (meta-d', AUROC (Type 2), etc.)

(7) Page 8 - Another one of the results on page 8 is worth reflecting further upon: the authors note how in Experiment 1, no credible difference was found between unimodal and bimodal trials (DeltaM = -0.25 [-0.59, 0.10]), but in Experiment 2, "we observed higher metacognitive efficiency in unimodal compared to bimodal trials (DeltaM = -0.28 [-0.54, -0.02]. Those DeltaM values are nearly identical, so without a power analysis motivating the number of participants the authors collected, how certain are they that the results from these two experiments are really that distinct? It reminds me a bit of the Andrew Gelman blog post, "The difference between significance and non-significance is not significant".

(8) Is there any way to look at whether the presence of multisensory hallucinations (or perhaps that word is too strong, and we should simply consider them miscategorizations) increased as the task progressed? That is, the authors have repeated presentations of audiovisual stimuli for at least some percentage of the trials. Since the percentages for auditory stimuli being correctly categorized as auditory are at 85% in Experiment 1 and 79% in Experiment 2, were the trials where they miscategorized these stimuli equally spread throughout the task? Or did they come later in the experiment, after being repeatedly exposed to multisensory trials?

(9) Would the authors obtain the same results if they got rid of the amodal confidence judgment in their task, and simply had participants report the bimodal confidence following the presence/absence judgment? Part of the reason for asking this is that, according to page 11, the model is only fitted to amodal detection accuracy and response time data. This surprised me. I would have expected that the bimodal confidence would provide more useful information for the model fit. The authors should further explain this rationale in the paper. It seems odd to me to have the multisensory confidence ratings and not have them play a central role in the modeling work.

(10) In Figure 6, it appears the model is a bit off in its estimate of auditory responses (panel B, E) in the AV condition. Do the authors have any intuitions about why this might be happening?

(11) The authors talk about how the model is reproducing effects in the human data, but there's no systematic comparison, quantitatively, of how the two things relate. The authors should include some quantitative measure that reflects this.

(12) Related to this, I am not sure I agree with the characterization in Figure 7 that "when confidence followed a disjunctive rule, the model failed to capture important aspects of the data. On the other hand, when confidence followed a conjunctive rule, it reproduced confidence in presence judgments but failed to capture variability in confidence ratings for absence judgments." What, quantitatively, is the basis of this claim? This applies to Figure 8, too. I am not clear how, specifically, and quantitatively, the authors are justifying their claims about model fits. I don't think the confidence asymmetry index in Figure 8 is enough to quantify the quality of the model fitting procedure.

(13) Is there any chance the higher metacognitive efficiency for auditory trials is simply driven by differences in the d' values across the modalities? It might be good to probe this effect further.

(14) Lastly, I think it would be interesting to look at how instructions about modality-specific attention could modulate these findings, in terms of how unimodal (unimodal visual, unimodal auditory) or bimodal attention might modulate these effects. This is an idea for future work.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Mutations in CDHR1, the human gene encoding an atypical cadherin-related protein expressed in photoreceptors, are thought to cause cone-rod dystrophy (CRD). However, the pathogenesis leading to this disease is unknown. Previous work has led to the hypothesis that CDHR1 is part of a cadherin-based junction that facilitates the development of new membranous discs at the base of the photoreceptor outer segments, without which photoreceptors malfunction and ultimately degenerate. CDHR1 is hypothesized to bind to a transmembrane partner to accomplish this function, but the putative partner protein has yet to be identified.

The manuscript by Patel et al.makes an important contribution toward improving our understanding of the cellular and molecular basis of CDHR1-associated CRD. Using gene editing, they generate a loss of function mutation in the zebrafish cdhr1a gene, an ortholog of human CDHR1, and show that this novel mutant model has a retinal dystrophy phenotype, specifically related to defective growth and organization of photoreceptor outer segments (OS) and calyceal processes (CP). This phenotype seems to be progressive with age. Importantly, Patel et al, present intriguing evidence that pcdh15b, also known for causing retinal dystrophy in previous Xenopus and zebrafish loss of function studies, is the putative cdhr1a partner protein mediating the function of the junctional complex that regulates photoreceptor OS growth and stability.

This research is significant in that it:

(1) Provides evidence for a progressive, dystrophic photoreceptor phenotype in the cdhr1a mutant and, therefore, effectively models human CRD; and

(2) Identifies pcdh15b as the putative, and long sought after, binding partner for cdhr1a, further supporting the theory of a cadherin-based junction complex that facilitates OS disc biogenesis.

Nonetheless, the study has several shortcomings in methodology, analysis, and conceptual insight, which limits its overall impact.

Below I outline several issues that the authors should address to strengthen their findings.

Major comments:

(1) Co-localization of cdhr1a and pcdh15b proteins

The model proposed by the authors is that the interaction of cdhr1a and pcdh15b occurs in trans as a heterodimer. In cochlear hair cells, PCDH15 and CDHR23 are proposed to interact first as dimers in cis and then as heteromeric complexes in trans. This was not shown here for cdhr1a and pcdh15b, but it is a plausible configuration, as are single heteromeric dimers or homodimers. Regardless, this model depends on the differential compartmental expression of the cdhr1a and pcdh15b proteins. Data in Figure 1 show convincing evidence that these two proteins can, at least in some cases, be distributed along the length of photoreceptor membranes that are juxtaposed, as would be the case for OS and CP. If pcdh15b is predominantly expressed in CPs, whereas cdhr1a is predominantly expressed in OS, then this should be confirmed with actin double labeling with cdhr1a and pcdh15b since the apicobasal oriented (vertical) CPs would express actin in this same orientation but not in the OS. This would help to clarify whether cdhr1a and pcdh15b can be trafficked to both OS and CP compartments or whether they are mutually exclusive.

First let me thank the reviewer for taking the time to comprehensively evaluate our work and provide constructive criticism which will improve the quality of our final version.

To address this issue, we are completed imaging of actin/cdhr1a and actin/pcdh15b using SIM in both transverse and axial sections (Fig 1C-H). Additionally, we have recently established an immuno-gold-TEM protocol and showcase co-labeling of cdhr1a and pcdh15b at TEM resolution along the CP (Fig 1I).

Photoreceptor heterogeneity goes beyond the cone versus rod subtypes discussed here and it is known that in zebrafish, CP morphology is distinct in different cone subtypes as well as cone versus rod. It would be important to know which specific photoreceptor subtypes are shown in zebrafish (Figures 1A-C) and the non-fish species depicted in Figures 1E-L. Also, a larger field of view of the staining patterns for Figures 1E-L would be a helpful comparison (could be added as a supplementary figure).

The revised manuscript includes labels for the location of different cone subtypes in figure 1. All of the images showcasing CHDR1 localization across species concentrate on the PNA positive R/G cones. Larger fields of view were not collected as we prioritized the highest resolution possible and therefore collected small fields of view.

(2) Cdhr1a function in cell culture

The authors should explain the multiple bands in the anti-FLAG blots. Also, it would be interesting to confirm that the cdhr1a D173 mutant prevents the IP interaction with pcdh15b as well as the additive effects in aggregate assays of Figure 2.

The multiple bands on the WB is like our previous results (Piedade 2020), which we believe arise due to ubiquitination and proteolytic cleavage of cdhr1a. We expect the D173 mutation to result in a complete absence of cdhr1a polypeptide, based on the lack of in situ signal in our WISH studies.

Is it possible that the cultured cells undergo proliferation in the aggregation assays shown in Figure 2? Cells might differentially proliferate as clusters form in rotating cultures. A simple assay for cell proliferation under the different transfection conditions showing no differences would address this issue and lend further support to the proposed specific changes to cell adhesion as a readout of this assay.

This is a possibility; however we did not use rotating cultures, this was a monolayer culture. We did not observe any differences in total cell number between the differing transfections. As such, we do not feel proliferation explains the aggregation of K562 cells.

Also, the authors report that the number of clusters was normalized to the field of view, but this was not defined. Were the n values different fields of view from one transfection experiment, or were they different fields of view from separate transfection experiments? More details and clarification are needed.

This will be clarified in the revised manuscript, in short we replicated this experiment 3 times, quantifying 5 different fields of view in each replicate.

(3) Methodological issues in quantification and statistical analyses

Were all the OS and CP lengths counted in the observation region or just a sample within the region? If the latter, what were the sampling criteria? For CPs, it seems that the length was an average estimate based on all CPs observed surrounding one cone or one-rod cell. Is this correct? Again, if sampled, how was this implemented? In Fig 4M', the cdhr1a-/- ROS mostly looks curvilinear. Did the measurements account for this, or were they straight linear dimension measurements from base to tip of the OS as depicted in Fig 5A-E? A clearer explanation of the OS and CP length quantification methodology is required.

The revised manuscript will clearly outline measurement methods. In short, we measured every CP/OS in the imaged regions. We did not average CPs/cell, we simply included all CP measurements in our analysis. All our CP measurements (actin or cdhr1a or pcdh15), were measured in the presence of a counter stain, WGA, prph2, gnb1 or PNA to ensure proper measurements (landmark) and association with proper cell type. Our new figure 7 now includes cone OS counter staining to better highlight the OS.

All measurements were taken as best as possible to reflect a straight linear dimension for consistency.

How were cone and rod photoreceptor cell counts performed? The legend in Figure 4 states that they again counted cells in the observation region, but no details were provided. For example, were cones and rods counted as an absolute number of cells in the observation region (e.g., number of cones per defined area) or relative to total (DAPI+) cell nuclei in the region? Changes in cell density in the mutant (smaller eye or thinner ONL) might affect this quantification so it would be important to know how cell quantification was normalized.

The revised manuscript will clearly outline measurement methods. In short, rod and cone cell counts were based on the number of outer segments that were observed in the imaging region and previously measured for length. We did not observe any eye size differences in our mutant fish.

In Figure 6I, K, measuring the length of the signal seems problematic. The dimension of staining is not always in the apicobasal (vertical) orientation. It might be more accurate to measure the cdhr1a expression domain relative to the OS (since the length of the OS is already reduced in the mutants). Another possible approach could be to measure the intensity of cdhr1 staining relative to the intensity within a Prph2 expression domain in each group. The authors should provide complementary evidence to support their conclusion.

The revised manuscript will clearly outline measurement methods. In short, all of our CP measurements (actin or cdhr1a or pcdh15), were done in the presence of a counter stain, WGA, prph2, gnb1 or PNA to ensure proper measurements and association with proper cell type.

A better description of the statistical methodology is required. For example, the authors state that "each of the data points has an n of 5+ individuals." This is confusing and could indicate that in Figure 4F alone there were ~5000 individuals assayed (~100 data points per treatment group x n=5 individuals per data point x 10 treatment groups). I don't think that is what the authors intended. It would be clearer if the authors stated how many OS, CP, or cells were counted in their observation region averaged per individual and then provided the n value of individuals used per treatment group (controls and mutants), on which the statistical analyses should be based.

This has been addressed in the revised manuscript. In short, we had an n=5 (individual fish) analyzed for each genotype/time point.

There are hundreds of data points in the separate treatment groups shown in several of the graphs. It would not be correct to perform the ANOVA on the separate OS or CP length measurements alone as this will bias the estimates since they are not all independent samples. For example, in Figure 6H, 5dpf pcdh15b+/- have shorter CPs compared to WT but pcdh15b-/- have longer compared to WT. This could be an artifact of the analysis. Moreover, the authors should clarify in the Methods section which ANOVA post hoc tests were used to control for multiple pairwise comparisons.

We have re-analyzed the data using multiple pairwise comparison ANOVA with post hoc tests (Tukey test). This new analysis did not significantly alter the statistical significance outcome of the study.

(4) Cdhr1a function in photoreceptors

The Cdhr1a IHC staining in 5dpf WT larvae in Figure 3E appears different from the cdhr1a IHC staining in 5dpf WT larvae in Figure 1A or Figure 6I. Perhaps this is just the choice of image. Can the authors comment or provide a more representative image?

The image in figure 3E was captured using a previous non antigen retrieval protocol which limits the resolution of the cdhr1a signal along the CP. In the revised manuscript we have included an image that better represents cdhr1a staining in the WT and mutant.

The authors show that pcdh15b localization after 5dpf mirrored the disorganization of the CP observed with actin staining. They also show in Figure 5O that at 180dpf, very little pcdh15b signal remains. They suggest based on this data that total degradation of CPs has occurred in the cdhr1a-/- photoreceptors by this time. However, although reduced in length, COS and cone CPs are still present at 180dpf (Figure 5E, E'). Thus, contrary to the authors' general conclusion, it is possible that the localization, trafficking, and/or turnover of pcdh15b is maintained through a cdhr1a-dependent mechanism, irrespective of the degree to which CPs are maintained. The experiments presented here do not clearly distinguish between a requirement for maintenance of localization versus a secondary loss of localization due to defective CPs.

We agree, this point has been addressed in our revised manuscript. Additionally, we have also included data from 1 and 2 year old samples.

(5) Conceptual insights

The authors claim that cdhr1a and pcdh15b double mutants have synergistic OS and CP phenotypes. I think this interpretation should be revisited.

First, assuming the model of cdhr1a-pcdh15b interaction in trans is correct, the authors have not adequately explained the logic of why disrupting one side of this interaction in a single mutant would not give the same severity of phenotype as disrupting both sides of this interaction in a double mutant.

Second, and perhaps more critically, at 10dpf the OS and CP lengths in cdhr1a-/- mutants (Figure 7J, T) are significantly increased compared to WT. In contrast, there are no significant differences in these measurements in the pcdh15b-/- mutants. Yet in double homozygous mutants, there is a significant reduction of ~50% in these measurements compared to WT. A synergistic phenotype would imply that each mutant causes a change in the same direction and that the magnitude of this change is beyond additive in the double mutants (but still in the same direction). Instead, I would argue that the data presented in Figure 7 suggest that there might be a functionally antagonistic interaction between cdhr1a and pcdh15b with respect to OS and CP growth at 10dpf.

If these proteins physically interacted in vivo, it would appear that the interaction is complex and that this interaction underlies both OS growth-promoting and growth-restraining (stabilizing) mechanisms working in concert. Perhaps separate homodimers or heterodimers subserve distinct CP-OS functional interactions. This might explain the age-dependent differences in mutant CP and OS length phenotypes if these mechanisms are temporally dynamic or exhibit distinct OS growth versus maintenance phases. Regardless of my speculations, the model presented by the authors appears to be too simplistic to explain the data.

We agree with the reviewer, as such we have revised the discussion in our revised manuscript.

Reviewer #2 (Public review):

Summary:

The goal of this study was to develop a model for CDHR1-based Con-rod dystrophy and study the role of this cadherin in cone photoreceptors. Using genetic manipulation, a cell binding assay, and high-resolution microscopy the authors find that like rods, cones localize CDHR1 to the lateral edge of outer segment (OS) discs and closely oppose PCDH15b which is known to localize to calyceal processes (CPs). Ectopic expression of CDHR1 and PCDH15b in K652 cells indicates these cadherins promote cell aggregation as heterophilic interactants, but not through homophilic binding. This data suggests a model where CDHR1 and PCDH15b link OS and CPs and potentially stabilize cone photoreceptor structure. Mutation analysis of each cadherin results in cone structural defects at late larval stages. While pcdh15b homozygous mutants are lethal, cdhr1 mutants are viable and subsequently show photoreceptor degeneration by 3-6 months.

Strengths:

A major strength of this research is the development of an animal model to study the cone-specific phenotypes associated with CDHR1-based CRD. The data supporting CDHR1 (OS) and PCDH15 (CP) binding is also a strength, although this interaction could be better characterized in future studies. The quality of the high-resolution imaging (at the light and EM levels) is outstanding. In general, the results support the conclusions of the authors.

Weaknesses:

While the cellular phenotyping is strong, the functional consequences of CDHR1 disruption are not addressed. While this is not the focus of the investigation, such analysis would raise the impact of the study overall. This is particularly important given some of the small changes observed in OS and CP structure. While statistically significant, are the subtle changes biologically significant? Examples include cone OS length (Figures 4F, 6E) as well as other morphometric data (Figure 7I in particular). Related, for quantitative data and analysis throughout the manuscript, more information regarding the number of fish/eyes analyzed as well as cells per sample would provide confidence in the rigor. The authors should also note whether the analysis was done in an automated and/or masked manner.

First let me thank the reviewer for taking the time to comprehensively evaluate our work and provide constructive criticism which will improve the quality of our final version.

The revised manuscript outlines both methods and statistics used for quantitation of our data. (please see comments from reviewer 1). While we do not include direct evidence of the mechanism of CDHR1 function, we do propose that its role is important in anchoring the CP and the OS, particularly in the cones, while in rods it may serve to regulate the release of newly formed disks (as previously proposed in mice). We do plan to test both of these hypothesis directly, however, that will be the basis of our future studies.

Reviewer #3 (Public review):

Summary:

The manuscript by Patel et al investigates the hypothesis that CDHR1a on photoreceptor outer segments is the binding partner for PCDH15 on the calyceal processes, and the absence of either adhesion molecule results in separation between the two structures, eventually leading to degeneration. PCDH15 mutations cause Usher syndrome, a disease of combined hearing and vision loss. In the ear, PCDH15 binds CDH23 to form tip links between stereocilia. The vision loss is less understood. Previous work suggested PCDH15 is localized to the calyceal processes, but the expression of CDH23 is inconsistent between species. Patel et al suggest that CDHR1a (formerly PCDH21) fulfills the role of CDH23 in the retina.

The experiments are mainly performed using the zebrafish model system. Expression of Pcdh15b and Cdhr1a protein is shown in the photoreceptor layer through standard confocal and structured illumination microscopy. The two proteins co-IP and can induce aggregation in vitro. Loss of either Cdhr1a or Pcdh15, or both, results in degeneration of photoreceptor outer segments over time, with cones affected primarily.

The idea of the study is logical given the photoreceptor diseases caused by mutations in either gene, the comparisons to stereocilia tip links, and the protein localization near the outer segments. The work here demonstrates that the two proteins interact in vitro and are both required for ongoing outer segment maintenance. The major novelty of this paper would be the demonstration that Pcdh15 localized to calyceal processes interacts with Cdhr1a on the outer segment, thereby connecting the two structures. Unfortunately, the data presented are inadequate proof of this model.

Strengths:

The in vitro data to support the ability of Pcdh15b and Cdhr1a to bind is well done. The use of pcdh15b and cdhr1a single and double mutants is also a strength of the study, especially being that this would be the first characterization of a zebrafish cdhr1a mutant.

Weaknesses:

(1) The imaging data in Figure 1 is insufficient to show the specific localization of Pcdh15 to calyceal processes or Cdhr1a to the outer segment membrane. The addition of actin co-labelling with Pcdh15/Cdhr1a would be a good start, as would axial sections. The division into rod and cone-specific imaging panels is confusing because the two cell types are in close physical proximity at 5 dpf, but the cone Cdhr1a expression is somehow missing in the rod images. The SIM data appear to be disrupted by chromatic aberration but also have no context. In the zebrafish image, the lines of Pcdh15/Cdhr1a expression would be 40-50 um in length if the scale bar is correct, which is much longer than the outer segments at this stage and therefore hard to explain.

First let me thank the reviewer for taking the time to comprehensively evaluate our work and provide constructive criticism which will improve the quality of our final version.

To address this issue, we have added images of actin/cdhr1a and actin/pcdh15b using SIM in both transverse and axial sections. Additionally, we have established an immuno-gold-TEM protocol and provide data showcasing co-labeling of cdhr1a and pcdh15b at TEM resolution.

(2) Figure 3E staining of Cdhr1a looks very different from the staining in Figure 1. It is unclear what the authors are proposing as to the localization of Cdhr1a. In the lab's previous paper, they describe Cdhr1a as being associated with the connecting cilium and nascent OS discs, and fail to address how that reconciles with the new model of mediating CP-OS interaction. And whether Cdhr1a localizes to discrete domains on the disc edges, where it interacts with Pcdh15 on individual calyceal processes.

The image in figure 3E was captured using a previous non antigen retrieval protocol which limits the resolution of the cdhr1a signal along the CP. In the revised manuscript we include an image that better represents cdhr1a staining in the WT and mutant.

(3) The authors state "In PRCs, Pcdh15 has been unequivocally shown to be localized in the CPs". However, the immunostaining here does not match the pattern seen in the Miles et al 2021 paper, which used a different antibody. Both showed loss of staining in pcdh15b mutants so unclear how to reconcile the two patterns.

We agree that our staining appears different, but we attribute this to our antigen retrieval protocol which differed from the Miles et al paper. We also point to the fact that pcdh15b localization has been shown to be similar to our images in other species (monkey and frog). As such, we believe our protocol reveals the proper localization pattern which might be lost/hampered in the procedure used in Miles et al 2021.

(4) The explanation for the CRISPR targets for cdhr1a and the diagram in Figure 3 does not fit with crRNA sequences or the mutation as shown. The mutation spans from the latter part of exon 5 to the initial portion of exon 6, removing intron 5-6. It should nevertheless be a frameshift mutation but requires proper documentation.

This was an overlooked error in figure making, we have corrected this typo in the revised manuscript.

(5) There are complications with the quantification of data. First, the number of fish analyzed for each experiment is not provided, nor is the justification for performing statistics on individual cell measurements rather than using averages for individual fish. Second, all cone subtypes are lumped together for analysis despite their variable sizes. Third, t-tests are inappropriately used for post-hoc analysis of ANOVA calculations.

As we discussed for reviewer 1 and 2, all methods and quantification/statistics will be clearly described in the revised manuscript.

(6) Unclear how calyceal process length is being measured. The cone measurements are shown as starting at the external limiting membrane, which is not equivalent to the origin of calyceal processes, and it is uncertain what defines the apical limit given the multiple subtypes of cones. In Figure 5, the lines demonstrating the measurements seem inconsistently placed.

As we discussed for reviewer 1 and 2, all methods and quantification/statistics will be clearly described in the revised manuscript. We have also clarified that CP measurements were made based on a counterstain for the cone/rod OS so that the actin signal was only CP associated. We have included the counter stain in our revised Figure 7.

(7) The number of fish analyzed by TEM and the prevalence of the phenotype across cells are not provided. A lower magnification view would provide context. Also, the authors should explain whether or not overgrowth of basal discs was observed, as seen previously in cdhr1-null frogs (Carr et al., 2021).

The revised manuscript now includes the n number for our TEM samples. We have also added text comparing our results directly to Carr 2021.

(8) The statement describing the separation between calyceal processes and the outer segment in the mutants is not backed up by the data. TEM or co-labelling of the structures in SIM could be done to provide evidence.

We have completed both more SIM as well as immuno-gold TEM to support our conclusions, see new Figure 1.

(9) "Based on work in the murine model and our own observations of rod CPs, we hypothesize that zebrafish rod CPs only extend along the newly forming OS discs and do not provide structural support to the ROS." Unclear how murine work would support that conclusion given the lack of CPs in mice, or what data in the manuscript supports this conclusion.

In the revised manuscript we have adjusted our discussion to hypothesize that the small length of rod CPs is most likely to represent their interaction with newly forming discs rather than connect with mature discs which are enclosed in the OS.

(10) The authors state "from the fact that rod CPs are inherently much smaller than cone CPs" without providing a reference. In the manuscript, the measurements do show rod CPs to be shorter, but there are errors in the cone measurements, and it is possible that the RPE pigment is interfering with the rod measurements.

We have included references where rod CPs have been found to be shorter. We have no doubt that in zebrafish the rod CPs are significantly shorter. All our CP measurements are done with a counter stain for rods and cones to be sure that we are measuring the correct cell type.

(11) The discussion should include a better comparison of the results with ocular phenotypes in previously generated pcdh15 and cdhr1 mutant animals.

The revised manuscript has included these points.

(12) The images in panels B-F of the Supplemental Figure are uncannily similar, possibly even of the same fish at different focal planes.

We assure the reviewer that each of the images in supplemental figure 1 are distinct and represent different in situ experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In the second sentence of the Introduction section, the acronym 'PRC' should be defined.

This has been corrected

(2) In the Discussion section, it would be useful to comment on differences between the published Xenopus cdhr1-/- OS phenotypes and the published zebrafish pcdh15b-/- OS phenotypes compared to the present zebrafish cdhr1a-/- phenotypes. In the published studies, OS in these mutants demonstrated dysmorphic and overgrown disc membranes compared to the relatively minor disc layering defects shown for cdhr1a-/- in the present study.

This discussion has been added.

(3) CDHR1 mutations in patients cause cone-rod dystrophy, but mutations in PCDH15 (Usher 1F) cause rod-cone dystrophy. In the Discussion section, the authors should comment on what might lead to these different phenotypic trajectories in humans in the context of their proposed model.

We have added to our discussion highlighting that is not possible to assess rod-cone dystrophy in the pcdh15b model as the mutation is lethal by 15dpf, which is still before most rods mature.

Reviewer #2 (Recommendations for the authors):

In addition to defining the 'n' for animal and cell numbers (as well as methods of analysis - automated/masked), there are a few additional recommendations for the authors.

(1) Expression of USH1 genes in larval zebrafish (Figure S1) is not very convincing. SC RNAseq data exists and argues against this cell type restriction.

Based on extensive experience with WISH we are confident that our interpretation of the data are valid. Furthermore, analysis of the daniocell data base confirms that cdh23, ush1ga, ush1c (harmonin) and myo7aa all have either no expression in photoreceptors or very low levels especially compared to pcdh15b and cdhr1a.

(2) The model in Figure 1 is great. The coloring was a bit confusing. Cdhr1 and axoneme are both in green, while Pcdh15 and actin are both in red. Can each have its own color?

Changed pcdh15b color to blue

(3) Figure 2A: Please explain the multiple bands in some lanes. What do the full blots look like?

Full blots were uploaded to eLife and do not exhibit any additional bands. The multiple bands are likely due to ubiquitination or proteolytic cleavage of cdhr1a and have been documented in our previous publication (Piedade 2020).

(4) Is "data not shown" permissible? (lack of compensation of cdh1b in cdh1a mutants) (nonsense-mediated decay of the mutant transcript).

We have added a supplementary figure showcasing this data.

(5) Figure 4: Is there a TEM phenotype in discs before 15dpf? One would think there would be...?

Due to technical limitations, we have not been able to examine disc phenotypes prior to 15dpf.

(6) Figure 5: How are calyceal processes discriminated from cortical/PM-associated actin? A bonafide calyceal marker seems to be needed. Espin or Myo3, for example.

We discriminate to identify CPs as actin signal that originates at the base of the OS and travels along the OS. Pcdh15b is a bonafinde CP marker which we show overlaps with actin signal along CPs.

(7) Figures 5A-J: How is actin staining for CPs discriminating between rod and cones??? Apical - basal level imaging? This could be better clarified.

CP identification is based on co-stain for either rod or cone Oss

(8) Figure 6: Het phenotype for pcdh15b+/- (cone OS length and CP length at 5 and 10 dpf) is surprising ... worth discussing. (Figures 6E, H).

The discussion section has been updated to discuss this finding.

(9) Last, the authors state "Data not shown" throughout the manuscript. I do not believe this is allowed for the journal.

This data (cdhr1b expression in cdhr1a mutants as well as cdhr1a WISH in cdhr1a mutants) has been added as supplementary figures.

Reviewer #3 (Recommendations for the authors):

Major comments are addressed above and the most important is the need for a convincing demonstration of Cdhr1a localization on the outer segment and proximity to Pcdh15b. The SIM could be a powerful tool, but the images provided are impossible to assess without any basis for context. Could a membrane, Prph2, and/or actin label be added? And lower magnification views?

Minor comments.

(1) The mention of "short CPs" in rodents is not an accurate description. Particular rodents (e.g. mouse, rat) lack CPs altogether or have a single vestigial structure.

We have adjusted the text to reflect this point.

(2) Inconsistent spacing between numbers and units.

We have corrected these inconsistencies

(3) Missing references.

We have added missing references

(4) Indicate the mean or median for bar graphs.

The materials and methods section now specifies that all of our graphs depict a mean value

(5) Unclear how rods are distinguished from cones in the cone analysis if both are labeled with prph2 antibody.

Rods are physiological separate from cones in zebrafish retina and therefore easily identified by location as well as their distinct pattern of actin staining.

(6) Red and green should not be used together for microscopy images.

(7) The diagram in Figure 1D is confusing because of the repeated use of red and green for disparate structures. Also, the location and structure of actin are misrepresented, as is the transition of disc structure during maturation in rods.

We have adjusted the color of pcdh15b to blue.

Author response:

General Statements

We thank the reviewers for their insightful and constructive comments, which have substantially strengthened the manuscript. We have addressed all concerns and replaced the previous nonquantitative RNA-seq analysis with a new analysis that allowed for quantitative assessment. We were encouraged to find that the revised analysis not only confirmed our original observations but also reinforced and extended our conclusions.

Point-by-point description of the revisions

Reviewer #1:

Significance

At its current stage, this work represents a robust resource for molecular parasitology research programs, paving the way for mechanistic studies on multilayered gene expression control and it would benefit from experimental evidence for some of the claims concerning the in silico regulatory networks. Terms like "regulons", "recursive feedback loop" are employed without solid confirmation or extensive literature support. In my view, the most relevant contribution of this study is centered in the direct association between proteasome-dependent degradation and Leishmania differentiation.

We thank the reviewer to acknowledge the impact of our work as a robust resource for further mechanistic studies. We agree that the new concepts emerging from our multilayered analysis should be experimentally assessed. However, given the scope of our analysis (i.e. a complete systems-level analysis of bona fide, hamster-isolated L. donovani amastigotes and derived promastigotes) and the amount of data presented in the current manuscript, such functional genetic analysis will merit an independent, in-depth investigation. The current version has been very much toned down and modified to emphasize the impact of our work as a powerful new resource for downstream functional analyses.  

Evidence, reproducibility and clarity

The narrative becomes somewhat diffuse with the shift to putative multilevel regulatory networks, which would benefit from further experimental validation.

We agree with the reviewer and toned down the general discussion while suggesting putative multilevel regulatory networks for follow-up, mechanistic analyses. We now emphasize those networks for which evidence in trypanosomatids and other organisms has been published. Experimental validation of some of these regulatory networks is outside the scope of our manuscript and will be pursued as part of independent investigations.

Major issues

Fig.1D suggests a significant portion of the SNPs are exclusive, with a frequency of zero in one of the two stages. Were only the heterozygous and minor alleles plotted in Fig.1D, since frequencies close to 1 are barely observed? Is the same true in Sup Fig. S2B? Why do chrs 4 and 33 show unusual patterns in S2B?

We thank the reviewer for this observation. The SNPs exclusive to either one or the other stage are likely the result of the 10% cutoff we use for this kind of analysis (eliminating SNPs that lack sufficient support, i.e. less than 10 reads). Due to bottle neck events (such as in vitro culture or stage differentiation), many low frequency SNPs are either ‘lost’ (filtered out) or ‘gained’ (passing the 10% cutoff) between the ama and pro samples. All SNPs above 10% were plotted. The absence of SNPs at 100% is one of the hallmarks of the Ld1S L. donovani strain we are using. Instead, these parasites show a majority of SNPs at a frequency of around 50%, which is likely a sign of a previous hybridization event. Chr 4 and chr 33 show a very low SNP density, most likely as they went through a transient monosomy at one moment of their evolutionary history, causing loss of heterozygosity. We now explain these facts in the figure legend.

Chr26 revealed a striking contrasting gene coverage between H-1 and the other two samples. While a peak is observed for H-1 in the middle of this chr, the other two show a decrease in coverage. Is there any correlation with the transcriptomic/proteomic findings?

This analysis is based on normalized median read depth, taking somy variations into account. This is now more clearly specified in the figure legend. We do not see any significant expression changes that would correlate with the observed (minor) read depth changes. As indicated in the legend, we do not consider such small fluctuations (less than +/- 1,5 fold) as significant. The reversal of the signal for chr 26 sample H1 eludes us (but again, these fluctuations are minor and not observed at mRNA level).

The term "regulon" is used somewhat loosely in many parts of the text. Evidence of co-transcriptomic patterns alone does not necessarily demonstrate control by a common regulator (e.g., RNA-binding protein), and therefore does not fulfill the strict definition of a regulon. It should be clear whether the authors are highlighting potential multiple inferred regulons within a list of genes or not. Maybe functional/ gene module/cluster would be more appropriate terms.

We thank the reviewer for this important comment. We replaced ‘regulon’ throughout the manuscript by ‘co-regulated, functional gene clusters’ (or similar).

It is unclear whether the findings in Fig.3E are based on previous analysis of stagespecific rRNA modifications or inferred from the pre-snoRNA transcriptomic data in the current work or something else. I struggle to find the significance of presenting this here.

We thank the reviewer for this comment. Yes, these data show stage-specific rRNA modifications based on previous analyses that mapped stage-specific differences of pseudouridine (Y) (Rajan et al., Cell Reports 2023, DOI: 10.1016/j.celrep.2024.114203) and 2'O-modifications (Rajan et al., Nature Com, in revision) by various RNA-seq analyses and cryoEM. This figure has been modified in the revised version to consider the identification of stageregulated snoRNAs in our new and statistically robust RNA-seq analysis. These data are shown to further support the existence of stage-regulated ribosomes that may control mRNA translatability, as suggested by the enriched GO terms ‘ribosome biogenesis’, ‘rRNA processing’ and ‘RNA methylation’ shown in Figure 2. We better integrated these analyses by moving the panels from Figure 3 to Figure 2.

The protein turnover analysis is missing the critical confirmation of the expected lactacystin activity on the proteasome in both ama and pro. A straightforward experiment would be an anti-polyUb western blotting using a low concentration SDS-PAGE or a proteasome activity assay on total extracts.

We thank the reviewer for this comment and have now included an anti-polyUb Western blot analysis (see Fig S7).

The viability tests upon lactacystin treatment need a positive control for the PI and the YoPro staining (i.e., permeabilized or heat-killed promastigotes).

This control is now included in Fig S7 and we have added the corresponding description to the text.

I found that the section on regulatory networks was somewhat speculative and less focused. Several of the associated conclusions are, in some parts, overstated, such as in "uncovered a similar recursive feedback loop" (line 566) or "unprecedented insight into the regulatory landscape" (line 643). It would be important to provide some form of direct evidence supporting a functional connection between phosphorylation/ubiquitination, ribosome biogenesis/proteins and gene expression regulation.

We agree with the reviewer and have considerably toned down our statements. Functional analyses to investigate and validate some of the shown network interactions are planned for the near future and will be published separately.

Minor issues

(1) The ordinal transition words "First,"/"Second," are used too frequently in explanatory sections. I noted six instances. I suggest replacing or rephrasing some to improve flow.

Rectified, thanks for pointing this out.

(2) Ln 168: Unformatted citations were given for the Python packages used in the study.

Rectified, thanks for pointing this out.

(3) Fig.1D: "SNP frequency" is the preferred term in English.

Corrected.

(4) Fig.2A: not sure what "counts}1" mean.

This figure has been replaced.

(5) Ln 685: "Transcripts with FC < 2 and adjusted p-value > 0.01 are represented by black dots" > This sentence is inaccurate. The intended wording might be: "Transcripts with FC < 2 OR adjusted p-value > 0.01 are represented by black dots"

We thank the reviewer and corrected accordingly.  

(6) Ln 698: Same as ln 685 mentioned above.

We thank the reviewer and corrected accordingly.

(7) Fig.2B and elsewhere: The legend key for the GO term enrichment is a bit confusing. It seems like the color scales represent the adj. p-values, but the legend keys read "Cluster efficiency" and "Enrichment score", while those values are actually represented by each bar length. Does light blue correspond to a max value of 0.05 in one scale, and dark blue to a max value of 10-7 in the other scale?

This was corrected in the figure and the legends were updated accordingly.

(8) Sup Figure S3A and S4A: The hierarchical clustering dendrograms are barely visible in the heatmaps.

Thanks for the comment. Figure S3 was removed and replaced by a hierarchical clustering and a PCA plot.

(9) S3A Legend: The following sentence sounds a bit awkward: "Rows and columns have been re-ordered thanks to a hierarchical clustering". I suggest switching "thanks to a hierarchical clustering" to "based on hierarchical clustering".

This figure was removed and the legend modified.

(10) Fig.5D: The font size everywhere except the legend key is too small. In addition, on the left panel, gene product names are given as a column, while on the right, the names are shown below the GeneIDs. Consistency would make it clearer.

Thank you, this is now rectified. To ensue readability, we reduced the number of shown protein kinase examples.

Reviewer #2 Evidence, reproducibility and clarity:

In the absence of riboprofiling the authors return to the RNA-seq to assess the levels of pre-Sno RNA (the role of the could be more explicitly stated).

We thank the reviewer for this comment. We moved the snoRNA analysis from Fig 3 to Fig 2 (see also the similar comment of reviewer 1), which better integrates and justifies this analysis. Based on the new and statistically robust RNA-seq analysis, the volcano plot showing differential snoRNA expression and possible ribosome modification has been adjusted (Figures 2C and D).

The authors provide a clear and comprehensive description of the data at each stage of the results and this in woven together in the discussion allowing hypotheses to be formed on the potential regulatory and signalling pathways that control the differentiation of amastigotes to promastigotes. Given the amount and breadth of data presented the authors are able to present a high-level assessment of the processes that form feedback loops and/or intersectional signalling, but specific examples are not picked out for deeper validation or exploration.

We thank the reviewer to acknowledge the amount and breadth of data presented. As indicated above (see responses to reviewer 1), mechanistic studies will be conducted in the near future to validate some of the regulatory interactions. These will be subject of separate publications. As noted above (response to reviewer 1), we toned down the general discussion, suggest follow-up mechanistic analyses and emphasize those networks for which evidence in trypanosomatids and other organisms has been published.

Major comments:

(1) As I have understood it from the description in the text, and in Data Table 4, the RNA-seq element of the work has only been conducted using two replicates. If this is the case, it would substantially undermine the RNA-seq and the inferences drawn from it. Minimum replicates required for inferential analysis is 3 bio-replicates and potentially up to 6 or 12. It may be necessary for the authors to repeat this for the RNA-seq to carry enough weight to support their arguments. (PMID: 27022035)

We agree with the reviewer and conducted a new RNA-seq analysis with 4 independent biological replicates of spleen-purified amastigotes and derived promastigotes. Given the robustness of the stage-specific transcriptome, and the legal constrains associated with the use of animals, we chose to limit the number of replicates to the necessary. We thank the reviewer for this important comment, and the new data not only confirm the previous one (providing a high level of robustness to our data) but allowed us to increase the number of identified stage-regulated snoRNAs, thus further supporting a possible role of ribosome modification in Leishmania stage development.   

(2) There are several examples that are given as reciprocal or recursive signalling pathways, but these are not followed up with independent, orthogonal techniques. I think the paper currently forms a great resource to pursue these interesting signalling interactions and is certainly more than just a catalogue of modifications, but to take it to the next level ideally a novel signalling interaction would be demonstrated using an orthogonal approach. Perhaps the regulation of the ribosomes could have been explored further (same teams recently published related work on this). Or perhaps more interestingly, a novel target(s) from the ubiquitinated protein kinases could have been explored further; for example making precision mutants that lack the ubiquitination or phosphorylation sites - does this abrogate differentiation?

We agree with the reviewer that the paper currently forms a great resource. In-depth molecular analysis investigating key signaling pathways and regulatory interactions are outside the scope of the current multilevel systems analysis but will be pursued in independent investigations.

(3) I found the use of lactacystin a bit curious as there are more potent and specific inhibitors of Leishmania proteasomes e.g. LXE-408. This could be clarified in the write-up (See below).

We thank the reviewer for this comment. We opted for the highly specific and irreversible proteasome inhibitor lactacystin that has been previously applied to study the Leishmania proteasome (PMID: 15234661) rather than the typanosomatid-specific drug candidate LXE408 as the strong cytotoxic effect of the latter makes it difficult to distinguish between direct effects on protein turnover and secondary effects resulting from cell death, limiting its utility for dissecting proteasome function in living parasites. We have added this information in the Results section.

(4) If it is the case that only 2 replicates of the RNA-Seq have been performed it really is not the accepted level of replication for the field. Most studies use a minimum of 3 bioreplicates and even a minimum of 6 is recommended by independent assessment of DESeq2.

See response to comment 1 above.

(5) As far as I could see, the cell viability assay does not include a positive control that shows it is capable of detecting cytotoxic effects of inhibitors. Add treatment showing that it can differentiate cytostatic vs cytotoxic compound.

This control has now been added to Fig S7.

(6) It is realistic for the authors to validate the cell viability assay. If the RNA-seq needs to be repeated then this would be a substantial involvement.

Redoing the RNA-seq analysis was entirely feasible and very much improved the robustness of our results.

(7) All the methods are written to a good level of detail. The sample prep, acquisition and data analysis of the protein mass spectrometry contained a high level of detail in a supplemental section. The authors should be more explicit about the amount of replication at each stage, as in parts of the manuscript this was quite unclear.

We thank the reviewer for this comment and explicitly state the number of replicates in Methods, Results and Figure legends for all analyses. The number of replicates for each analysis is further shown in the overview Figure S1.

(8) Unless I have misunderstood the manuscript, I believe the RNA-seq dataset is underpowered according to the number of replicates the authors report in the text.

See response to comment 1 above.

(9) Looking at Figure 1 and S1 and Data Table 4 to show the sample workflow I was surprised to see that the RNA-seq only used 2 replicates. The authors do show concordance between the individual biological replicates, but I would consider that only having 2 is problematic here, especially given the importance placed on the mRNA levels and linkage in this study. This would constitute a major weakness of the study, given that it is the basis for a crucial comparison between the RNA and protein levels.

We agree and have repeated the RNAseq analysis using four independent biological replicates - see response to comment 1.

(10) It also wasn't clear to me how many replicates were performed at each condition for the lactacystin treatment experiment - can the authors please state this clearly in the text, it looks like 4 replicates from Figure S1 and Data Table 8.

Indeed, we did 4 replicates. This is now clarified in Methods, Results and Figure legends and shown in Figure S1.

(11) Four replicates are used for the phosphoproteomics data set, which is probably ok, but other researchers have used a minimum of 5 in phosphoproteomics experiments to deal with the high level of variability that can often be observed with low abundance proteins & modifications. The method for the phosphoproteomics analysis suggests that a detection of a phosphosite in 1 sample (also with a localisation probability of >0.75) was required for then using missing value imputation of other samples. This seems like a low threshold for inclusion of that phosphosite for further relative quantitative analysis. For example, Geoghegan et al (2022) (PMID: 36437406) used a much more stringent threshold of greater than or equal to 2 missing values from 5 replicates as an exclusion criteria for detected phoshopeptides. Please correct me if I misunderstood the data processing, but as it stands the imputation of so many missing values (potentially 3 of 4 per sample category) could be reducing the quality of this analysis.

We thank the reviewer for this remark and for highlighting best practices in phosphoproteomics data analysis. Unlike other studies that use cultured parasites and thus have access to unlimited amounts, our study employs bona fide amastigotes isolated from infected hamster spleens. In France, the use of animals is tightly controlled and only the minimal number of animals to obtain statistically significant results is tolerated (and necessary to obtain permission to conduct animal experiments).

Regarding the number of biological replicates, we would like to emphasize that the use of four biological replicates is fully acceptable and used in quantitative proteomics and phosphoproteomics, particularly when combined with high-quality LC–MS/MS data and stringent peptide-level filtering. While some studies indeed employ five or more replicates, this is not a strict requirement, and many high-impact phosphoproteomics studies have successfully relied on four replicates when experimental quality and depth are high. In the present study, we adopted a discovery-oriented approach, aimed at detecting as many confidently identified phosphopeptides as possible. The consistency between replicates, combined with the depth of coverage and signal quality, indicates that four replicates are adequate for both the global proteome and the phosphoproteome in this context. Importantly, the quality of the MS data in this study is supported by (i) a high number of confidently identified peptides and phosphopeptides (identification FDR<1%), (ii) robust phosphosite localisation probabilities (localisation probability >0.75), and (iii) reproducible quantitative profiles across replicates. Notably, most of the identified phosphopeptides are quantified in at least two replicates within a given condition (between 73.2% and 83.4% of all the identified phosphopeptides among replicates of the same condition).

Regarding missing value imputation, we appreciate that our initial description may have been unclear and we have revised the Methods to avoid misunderstanding. Phosphosites were only considered if detected with high confidence (identification FDR<1%) and high localisation confidence (localisation probability >0.75) in at least one replicate. This criterion was chosen to retain biologically relevant, low-abundance phosphosites, which are more difficult to identify and are often stochastically sampled in phosphoproteomics datasets. For statistical analyses, missing values within a given condition were imputed with a well-established algorithm (MLE) only when at least one observed value was present in that condition. Notably, they were replaced by values in the neighborhood of the observed intensities, rather than by globally low, noise-like values.

We agree that more stringent exclusion rules, such as those used by Geoghegan et al. (2022), are appropriate in some contexts. However, there is no universally accepted standard for missingness thresholds in phosphoproteomics, and different strategies reflect trade-offs between sensitivity and stringency. In our discovery-oriented approach, we deliberately prioritized biological coverage while maintaining data quality. Our main conclusions are supported by coherent biological patterns, rather than by isolated phosphosite measurements.

(12) For the metabolomics analysis it looks like 2 amastigote samples were compared against 4 promastigote samples. Why not triplicates of each?

We thank the reviewer for noticing this point. It is an error in the figure file (Sup figure S1). Four biological replicates of splenic amastigotes were prepared (H130-1, H130-2, H133-1 and H133-2). Amastigotes from 2 biological replicates (H131-1 and H131-2) were seeded for differentiation into promastigotes in 4 flasks (2 per biological replicate) that were collected at passage 2. We have updated the figure file accordingly.

Minor comments:

Are prior studies referenced appropriately?

Yes

Are the text and figures clear and accurate?

The write up is clear, with the data presented coherently for each method. The analyses that link everything together are well discussed. The figures are mostly clear (see below) and are well described in the legends. There is good use of graphics to explain the experimental designs and sample names - although it is unclear if technical replicates are defined in these figures.

We thank the reviewer for these positive comments. We now included the information on replicates in the overview figure (Figure S1).

As I have understood it, the authors have calculated the "phosphostoichiometry" using the ratio of change in the phosphopeptide to the ratio of the change in total protein level changes. This is detailed in the supplemental method (see below). Whilst this has normalised the data, it has not resulted in an occupancy or stoichiometry measurement, which are measured between 0-1 (0% to 100%). The normalisation has probably been sufficient and useful for this analysis, but this section needs to be re-worded to be more precise about what the authors are doing and presenting. These concepts are nicely reviewed by Muneer, Chen & Chen 2025 (PMID: 39696887) who reference seminal papers on determination of phosphopeptide occupancy - and may be a good place to start. An alternative phrase should be used to describe the ratio of ratios calculated here, not phosphostoichiometry.

We thank the reviewer for this insightful comment and fully agree with the conceptual distinction raised. The reviewer is correct that the approach used in this study does not measure absolute phosphosite occupancy or stoichiometry, which would indeed require dedicated experimental strategies and would yield values bounded between 0 and 1 (0–100%). Instead, we calculated a normalized phosphorylation change, defined as the ratio of the change in phosphopeptide abundance relative to the change in the corresponding total protein abundance (a ratio-of-ratios approach – see doi :10.1007/978-1-0716-1967-4_12), and we tested whether this normalized phosphorylation change differed significantly from zero. This normalization approach is comparable to those previously published in the « Experimental Design and Statistical Analysis of the Proteome and the Phosphoproteome » section of the following paper (DOI: 10.1016/j.mcpro.2022.100428).

Our intention was to account for protein-level regulation and thereby better isolate changes in phosphorylation dynamics. While this normalization is informative and appropriate for the biological questions addressed here, we agree that the term “phosphostoichiometry” is imprecise and not correct in this context.

In response, we (i) replaced the term “phosphostoichiometry” throughout the manuscript with a more accurate description, such as “normalized phosphorylation level”, or “relative phosphorylation change normalized to protein abundance”, and (ii) revised the corresponding Methods and Results text to clearly state that absolute occupancy was not measured.

This rewording will improve conceptual accuracy without altering the validity or interpretation of the results.

From the authors methods describing the ratio comparison approach: "Another statistical test was performed in a second step: a contrasted t-test was performed to compare the variation in abundance of each modified peptide to the one of its parent unmodified protein using the limma R package {Ritchie, 2015; Smyth, 2005}. This second test allows determining whether the fold-change of a phosphorylated peptide between two conditions is significantly different from the one of its parent and unmodified protein (paragraph 3.9 in Giai Gianetto et al 2023). An adaptive Benjamini-Hochberg procedure was applied on the resulting pvalues thanks to the adjust.p function of R package cp4p {Giai Gianetto, 2016} using the Pounds et al {Pounds, 2006} method to control the False Discovery Rate level."

The references have been formatted.

Several aspects of the figures that contain STRING networks are quite useful, particularly the way colour around the circle of each node to denote different molecular functions/biological processes. However, some have descended into "hairball" plots that convey little useful information that would be equally conveyed in a table, for example. Added to this, the points on the figure are identified by gene IDs which, while clear and incontrovertible, are lacking human readability. I suggest that protein name could be included here too.

We thank the reviewer for this comment but for readability we opted to keep the figure as is. We now refer to Tables 8, 9, and 12 that allow the reader to link gene IDs to protein name and annotation (if available).

It is also not clear what STRING data is being plotted here, what are the edges indicating - physical interactions proven in Leishmania, or inferred interactions mapped on from other organisms? Perhaps as supplemental data provide the Cytoscape network files so readers can explore the networks themselves?

We thank the reviewer for this comment. While the STRING plugin in Cytoscape enables integrated network-based analyses, it represents protein–protein associations as a single edge per protein pair derived from the combined confidence score. Consequently, the specific contribution of individual evidence channels (e.g. experimental evidence, curated databases, coexpression, or text mining) cannot be disentangled within this framework. However, this representation was considered appropriate for the present study, which focused on global network topology and functional enrichment rather than on the interpretation of individual interaction types. The information on stringency has been added to the Methods section and the Figure legends (adding the information on confidence score cutoff).

We decided not to submit the Cytoscape files as they were generated with previous versions of Cytoscape and the STRING plugin. Based on the differential abundance data shown in the tables it will be very easy to recreate these networks with the new versions for any follow up study.

The title of columns in table S10 panel A are written in French, which will be ok for many people particularly those familiar with proteomics software outputs, but everything else is in English so perhaps those titles could be made consistent.

We apologize and have translated the text in English.

I would suggest that the authors provide a table that has all the gene IDs of the Ld1S2D strain and the orthologs for at least one other species that is in TriTrypDB. This would make it easy to interrogate the data and make it a more useful resource for the community who work on different strains and species of Leishmania. Although this data is available it is a supplemental material file in a previous paper (Bussotti et al PNAS 2021) and not easy to find.

We thank the reviewer for this very useful suggestion and have added this table (Table S13).

Figure 5b - from the legend it is not clear where the confidence values were derived in this analysis, although this is explained in the supplemental method. Perhaps the legend can be a bit clearer.

We have the following statement to the legend: ‘Confidence values were derived as described in Supplementary Methods’.

Can the authors discuss why lactacystin was used? While this is a commonly used proteasome inhibitor in mammalian cells there is concern that it can inhibit other proteases. At the concentrations (10 µM) the authors used there are off-target effects in Leishmania, certainly the inhibition of a carboxypeptidase (PMID: 35910377) and potentially cathepsins as is observed in other systems (PMID: 9175783). There is a specific inhibitor of the Leishmania proteasome LXE-408 (PMID: 32667203), which comes closer to fulfilling the SGC criteria (PMID: 26196764) for a chemical probe - why not use this. Does lactacystin inhibit a different aspect of proteasome activity compared to LXE-408?

We have add the following justification to the results section (see also response above to comment 3 for reviewer 2): We chose the highly specific and irreversible proteasome inhibitor lactacystin over the typanosomatid-specific, reversible drug candidate LXE408 as the latter’s potent cytotoxicity can confound direct effects on protein turnover with secondary consequences of cell death, limiting its utility for dissecting proteasome function in living parasites.

The application of lactacystin is changing the abundance of a multitude of proteins but no precision follow up is done to identify if those proteins are necessary and/or sufficient from driving/blocking differentiation. This could be tested using precision edited lines that are unable to be ubiquitinated? There is a lack of direct evidence that the proteins protected from degradation by lactacystin are ubiquitinated? Perhaps some of these could be tagged and IP'd then probed for ubiquitin signal. Di-Gly proteomics to reveal ubiquitinated proteins? These suggestions should be considered as OPTIONAL experiments in the relevant section above.

We very much appreciate these very interesting suggestions, which we will be considered for ongoing follow-up studies.

In the data availability RNA-seq section the text for the GEO link is : (https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc= GSE227637) but the embedded link takes me to (https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE165615) which is data for another, different study. Also, the link to the GEO site for the DNA seq isn't working and manual searches with the archive number (BioProject PRJNA1231373 ) does not appear to find anything. The IDs for the mass spec data PRIDE/ProteomeXchange don't seem to bring up available datasets: PXD035697 and PXD035698

The links have now been rectified and validated. For those data that are still under quarantine, here is the login information: To access the data:

DNAseq data: https://dataview.ncbi.nlm.nih.gov/object/PRJNA1231373?reviewer=6qt24dd7f475838rbqfn228d 0

RNAseq data: https://www.ebi.ac.uk/biostudies/ArrayExpress/studies/E-MTAB-16528?key=65367b55-d77f4c06-b4bd-bc10f2dc0b14

Proteomic data:  http://www.ebi.ac.uk/pride

Phosphoproteomic data: http://www.ebi.ac.uk/pride

Significance

Strengths:

(1) The molecular pathways that regulate Leishmania life-stage transitions are still poorly understood, with many approaches exploring single proteins/RNAs etc in a reductionist manner. This paper takes a systems-scale approach and does a good job of integrating the disparate -omics datasets to generate hypotheses of the intersections of regulatory proteins that are associated with life-cycle progression.

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

(2) The differentiation step studied is from amastigote to promastigote. I am not aware that this has been studied before using phosphoproteomics. The use of the hamster derived amastigotes is a major strength. While a difficult/less common model, the use of hamsters permits the extraction of parasites that are host adapted and represent "normal", host-adapted Leishmania ploidy, the promastigote experiments are performed at a low passage number. This is a strength or the work as it reduces the interference of the biological plasticity of Leishmania when it is cultured outside the host.

We thank the reviewer for the acknowledgment of our relevant hamster system, for which we face many challenges (financial, ethical, administrative as protocols need to be approved by the French government).

Limitations:

Potential lack of appropriate replication (see above).

See response to comment 1.

Lack of follow up/validation of a novel signalling interaction identified from the systems-wide approach. There is a lack of assessment of whether a single signalling cascade is driving the differentiation or these are all parallel, requisite pathways. The authors state the differentiation is not driven by a single master regulator, but I am not sure there is adequate evidence to rule this in or out.

See response to comment 2 above.

The study applies well established techniques without any particular technical stepchange. The application of large-scale multi-omics techniques and integrated comparisons of the different experimental workflows allow a synthesis of data that is a step forward from that existing in the previous Leishmania literature. It allows the generation of new hypotheses about specific regulatory pathways and crosstalk that potentially drive, or are at least active, during amastigote>promastigote differentiation.

We thank the reviewer for these positive comments.

This manuscript will have primary interest to those researchers studying the molecular and cell biology of Leishmania and other kinetoplastid parasites. The approaches used are quite standard (so not so interesting in terms of methods development etc.) and given the specific quirks of Leishmania biology it may not be that relevant to those working more broadly in parasites from different clades/phyla, or those working on opisthokont systems- yeast, humans etc. Other Leishmania focused groups will surely cherry-pick interesting hits from this dataset to advance their studies, so this dataset will form a valuable reference point for hypothesis generation.

We thank the reviewer for this assessment and agree that our data sets will be very valuable for us and other teams to generate hypotheses for follow-up studies.

Relevant expertise: Trypanosoma & Leishmania molecular & cell biology, RNA-seq, proteomics, transcriptional/epigenetic regulation, protein kinases - some experience of UPS system.

I have not provided comment on the metabolomics as it is outside my core expertise. However, I can see it was performed at one of the leading parasitology metabolomics labs.

We thank the reviewer for sharing expertise, investing time and intelligence in the assessment of our manuscript, and the highly constructive criticisms provided.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

The study presents a comprehensive multi-omics investigation of Leishmania differentiation, combining genomic, transcriptomic, proteomic, phospho-proteomic and metabolomic data. The authors aim to uncover mechanisms of post-transcriptional and post-translational regulation that drive the stage-specific biology of L. donovani. The authors provide a detailed characterization of transcriptomic, proteomic, and phospho-proteomic changes between life stages, and dissect the relative contributions of mRNA abundance and protein degradation to stage-specific protein expression. Notably, the study is accompanied by comprehensive supplementary materials for each molecular layer and provides public access to both raw and processed data, enhancing transparency and reproducibility. While the data are rich and compelling, several mechanistic interpretations (e.g., "feedback loops," "recursive networks," "signaling cascades") are overstated. Similarly, the classification of gene sets as "regulons" is not adequately supported, as no common regulatory factor has been identified and only a single condition change (amastigote to promastigote) was assessed.

We thank the reviewer for these comments and have corrected the manuscript to eliminate all unjustified mechanistic interpretations.

Major Comments:

(1) Across several sections (incl abstract, L559-565, L589-599, L600-L603, L610-612, L613-614, L625, L643-645, L650-652), the manuscript describes "recursive or self-controlling networks", "signaling cascades", "self-regulating", and "recursive feedback loops" - involving protein kinases, phosphatases, and translational regulators. While the data convincingly demonstrate stage-specific changes in phosphorylation and abundance changes in key molecules, the language used implies causal, direct and directional regulatory relationships that have not been experimentally validated.

We agree with the reviewer and have corrected the text, replacing all expressions that may allude to causal or directional relationships by more neutral expressions such as ‘coexpression’.  

(2) Co-expression and shared function alone do not define a regulon (L363, and several other places in the manuscript). A regulon also requires the gene set to be regulated by the same factor, for which there is no evidence here. Regulons can be derived from transcriptomic experiments, but then they need to show the same transcriptional behavior across many biological conditions, while here just 1 condition change is evaluated. Therefore, this analysis is conventional GO enrichment analysis and should not be overinterpreted into regulons.

We agree with the reviewer and have replaced ‘regulon’ with ‘co-regulated gene clusters’ (or similar).

(3) LFQ intensity of 0 (e.g., L389): An LFQ intensity of 0 does not necessarily indicate that a protein is absent, but rather that it was not detected. This can occur for several reasons: (1) true biological absence in one condition, (2) low abundance below the detection threshold, or (3) stochastic missingness due to random dropout in mass spectrometry. While the authors state that adjusted p-values for the 1534 proteins exclusively detected in either amastigotes or promastigotes are below 0.01, I could not find corresponding p-values for these proteins in Table 8 ('Global_Proteomic'). An appropriate statistical method designed to handle this type of missingness should be used. In this context, I also find the following statement unclear: "identified over 4000 proteins at each stage in at least 3 out of 4 biological replicates, representing 3521 differentially expressed proteins (adjusted p-value < 0.01), 1534 of which were exclusively detected in either ama or pro." If a protein is exclusively detected in one stage, then by definition it should not be detected in that number of replicates at both stages. This apparent contradiction should be clarified.

We fully agree with the reviewer, an LFQ intensity of 0 may results from various reasons. We realize that our wording may have been ambiguous. For clarity, we have modified the original text to: ‘Label-free quantitative proteomic analysis of 4 replicates of amastigotes and derived promastigotes identified over 4000 proteins, including 1987 differentially expressed proteins (adjusted p-value < 0.01), and 1534 that were exclusively detected in either ama or pro (Figure 3A left panel, Table 6).’ We also modified the legend of the Figure 3B. Concerning missing values that could be either missing not at random (MNAR) or missing completely at random (MCAR), rather than introducing potentially misleading imputed values, we chose to treat these missing values as genuine stage-specific differences (presence/absence): quantitative statistics are restricted to proteins with measurable LFQ in both stages, while proteins with consistent presence in one stage and non-detection in the other are reported as stage-restricted detections. We believe this strategy is transparent and minimizes modeling assumptions, while still highlighting robust stage-specific signals. Our approach is supported by independent validation through RNA-seq data, which corroborates the differential presence/absence patterns observed at the protein level. Furthermore, our enrichment analyses reveal significant over-representation of specific biological terms among these stage-specific proteins, providing biological coherence to these findings. Therefore, we believe our conservative approach of treating these as genuine presence/absence differences, validated by orthogonal data, is more appropriate than introducing imputed values based on arbitrary statistical assumptions.  

(4) L412 - Figure 3B: The figure shows proteins with infinite fold changes, which result from division by zero due to LFQ intensity values of zero in one of the compared conditions. As previously noted, interpreting LFQ zero values as true absence of expression is problematic, since these zeros can arise from several technical reasons - such as proteins being just below the detection threshold or due to stochastic dropout during MS analysis. Therefore, the calculated fold changes for these proteins are likely highly overestimated. This concern is visually supported by the large gap on the y-axis (even in log scale) between these "infinite" fold changes and the rest of the data. Moreover, given Leishmania's model of constitutive gene expression, it seems biologically implausible that all these proteins would be completely absent in one stage. This issue applies not only to Figure 3B, but also to the analyses presented in Figures 4D and 4E.

We thank the reviewer for this comment. To clarify this section, we modified the text as follows: ‘Only expression changes were considered that either showed statistically significant differential abundance at both RNA and protein levels (p < 0.01), or showed significant RNA changes (p < 0.01) with the corresponding protein being detected in only one of the two stages. These latter proteins are identified by signals that were arbitrarily placed at the upper (detected in ama) or the lower (detected in pro) parts of the graph. Whether these proteins just escape detection due to low expression or are truly not expressed remains to be established.’ We also deleted the ‘infinity’ symbol from the Figure.

Minor Comments:

Methods

L132: Typo: "A according" should be "according."

The ‘A’ refers to RNase A. We added a comma for clarification (…RNase A, according to…)

L158: How exactly were somy levels calculated? Please specify the method used, as I could not find a clear description in the referenced manuscript.

We thank the reviewer for this comment. Aside the already quite detailed description in Methods and the reference there to the paper describing the pipeline, we now added a link to the description of the karyotype module of the giptools package (https://gip.readthedocs.io/en/latest/giptools/karyotype.html). There the following explanation can be found: “The karyotype module aims at comparing the chromosome sequencing coverage distributions of multiple samples. This module is useful when trying to detect chromosome ploidy differences in different isolates. For each sample the module loads the GIP files with the bin sequencing coverage (.covPerBin.gz files) and normalizes the meancoverage values by the median coverage of all bins. The bin scores are then converted to somy scores which are then used for producing plots and statistics.” The description then goes into further detail.  

L158: Chromosome 36 is not consistently disomic, as stated. It has been observed in other somy states (e.g., Negreira et al. 2023, EMBO Reports, Figure 1), even if such occurrences are rare in the studied context. Normalizing by chr36 remains a reasonable choice, but it would be helpful to confirm that the majority of chromosomes appear disomic post-normalization to support the assumption that chr36 is disomic in this dataset as well.

We thank the reviewer for this comment. Unlike the paper cited above (using longterm cultured promastigotes), our analysis uses promastigote parasites from early culture adaptation (p2) that were freshly derived from splenic amastigotes known to be disomic (and confirmed here), which represents an internal control validating our analysis.

L163: Suggestion: Cite the GIP pipeline here rather than delaying the reference until L173.

Corrected

L188: "Controlled" may be a miswording. Consider replacing with "confirmed" or "validated."

Corrected to ‘validated’

L214: Please specify which statistical test was used to assess differential expression at the protein level. L227: Similarly, clarify which statistical test was applied for determining differential expression in the phospho-proteomics data.

As noted in the Methods section, a limma t-test was applied to determine proteins/phosphoproteins with a significant difference in abundance while imposing a minimal fold change of 2 between the conditions to conclude that they are differentially abundant {Ritchie, 2015; Smyth, 2005}.

Results

L337-339: The interpretation here is too speculative. Phrases like "suggesting" and "likely" are too strong given the evidence presented. Alternative explanations, such as mosaic variation combined with early-stage selective pressure in the culture environment, should be considered.

We thank the reviewers for these suggestions and have reformulated into: ‘In the absence of convergent selection, it is impossible to distinguish if these gene CNVs provide some strain-specific advantage or are merely the result of random genetic drift.’

L340: The "undulating pattern" mentioned is somewhat subjective. To support this interpretation, consider adding a moving average (or similar) line to Figure 3A, which would more clearly highlight this trend across the data points.

These lines have been added to Figure 1C (not 3A).

L356: It may be more accurate to say "control of individual gene expression," since Leishmania does have promoters - the key distinction is that initiation does not occur on a gene-by-gene basis.

Corrected

L403-405: The statement "this is because these metabolites comprise a glycosomal succinate shunt..." should be rephrased as a hypothesis rather than a definitive explanation, as this causal link has not been experimentally validated.

Thank you for the comment – we followed your advice.

L407: Replace "confirming" with "matching" to avoid overstating the agreement with previous observations.

Corrected

L408: Replace "correlated" with "matched" for more accurate interpretation of results.

Corrected

L433: It is unclear how differential RNA modifications were detected. Please specify which biological material was used, the number of replicates per life stage, and how statistical evaluation of differential modifications was performed.

This figure has now been updated using our statistically robust RNA-seq analysis conducted for the revision. See comments above.

L436: This conclusion appears incomplete. While the manuscript mentions transcript-regulated proteins, it should also note that other proteins showed discordant mRNA/protein patterns. A more balanced conclusion would mention both the matching and non-matching subsets.

We thank the reviewer for this comment and have made the necessary adjustments to better balance this conclusion.

L441: The phrase "poor correlation" overgeneralizes and lacks nuance. Earlier sections of the manuscript describe hundreds of genes where mRNA and protein levels correlate well, suggesting that mRNA turnover plays a key regulatory role. Please rephrase this sentence to clarify that poor correlation applies only to a subset of the data.

This has been corrected to ‘The discrepancies we observed in a sub-set of genes between….’.

L454: The claim that "epitranscriptomic regulation and stage-adapted ribosomes are key processes" should be supported with references. If this builds on previously published work, please cite it accordingly.

Corrected

L457: Proteasomal degradation is a well-established mechanism in Leishmania. These findings are interesting but should be presented in the context of existing literature (e.g. Silva-Jardim et al.2014, [PMID: 15234661]) rather than as entirely novel.

Corrected

L459: The authors shoumd add a microscopy image of promastigotes treated with lactacystin. This would provide insight into whether treatment affects morphology, as is known in T. cruzi (see Dias et al., 2008). It would be particularly informative if Leishmania behaves differently.

We added this information to Figure S7.

L472 + L481: Table 9 shows several significant GO terms not discussed in the manuscript. Please clarify how the subset presented in the text was selected.

We added this information to the text (‘some of the most significantly enrichment terms included …’).

L482: The argument that a single master regulator can be excluded is unclear. Could the authors please elaborate on the reasoning or data supporting this conclusion?

This statement was too speculative and has been removed. Instead, we added ‘Thus, Leishmania differentiation correlates with the expression of complex signaling networks that are established in a stage-specific manner’.

L494: The term "unexpected" may not be appropriate here, as protein degradation is a wellestablished regulatory mechanism in trypanosomatids. Consider omitting this term to better reflect the field's current understanding.

We deleted the term as suggested and reformulated to ‘….our results confirm the important role of protein degradation….’.

L543: The term "feedback loop" should be used more cautiously. The current data are correlative, and no interventional experiments are provided to support a causal regulatory loop between proteasomal activity and protein kinases. As such, this remains a hypothesis rather than a confirmed mechanism.

We fully agree and have toned down the entire manuscript, referring to feedback loops only as a hypothesis and not as a fact emerging from our datasets, which set the stage for future functional analyses.

Discussion

L555: As noted in L494, reconsider using the word "unexpected."

Removed

L589: The data do not fully support the presence of stage-specific ribosomes. Rather, they suggest differential ribosomal function through changes in abundance and regulation. Please consider rephrasing.

We thank the reviewer for this comment and have follow the advice reformulating the sentence according to the suggestion.

L657-658: The discussion of post-transcriptional and post-translational regulation of gene dosage effects would benefit from citing additional literature beyond the authors' own work. E.g. the study by Cuypers et al. (PMID: 36149920) offers a relevant and comprehensive analysis covering 4 'omic layers.

We apologize for this omission and now describe and cite this publication in the Results section when concluding the results shown in Figure 1.

L659-664: The reference to deep learning for biomarker discovery appears speculative and loosely connected to the current findings. As no such methods were applied in the study, and the manuscript does not clarify what types of biomarkers are intended, this statement could be seen as aspirational rather than evidence-based. Consider either omitting or elaborating with clear justification.

We agree and have deleted this section.

L690 + L705 (Figure 2): The phrase "main GO terms" is vague. Please clarify the criteria for selecting the GO terms shown - were they chosen based on adjusted p-value, enrichment score, or another metric? Additionally, define "cluster efficiency," explaining how it was calculated and what it represents.

Corrected to ‘some of the most significantly enriched GO terms’.

Referee cross-commenting

Overall, I think the other reviewers' comments are fair. They seem to align particularly on the following points:

(1) Reviewers agree that this is a comprehensive body of work with original contributions to the field of Leishmania/trypanosomatid molecular biology, and that it will serve as a valuable reference for hypothesis generation.

(2) Several reviewers raise concerns about overinterpretation of the data, particularly regarding regulatory networks, regulons, and master regulators. The interpretation and large parts of the discussion are considered too speculative without additional functional validation.

(3) There are comments about the incorrect statistical treatment of missing values in the proteomics experiments, which affects confidence in some of the conclusions.

(4) While the correlation between the two RNA-Seq replicates is high, the decision to include only two biological replicates is seen as unfortunate and not ideal for statistical robustness.

(5) The use of lactacystin should be more clearly motivated, and its limitations discussed in the context of the experiments.

Even though I did not remark on the last two points (4 and 5) in my own review, I agree with them.

We thank the reviewer for this cross-comparison, which served us as guide to revise our manuscript. We believe that we have responded to all these concerns.

Reviewer #3 (Significance):

This study provides a rich, integrative multi-omics dataset that advances our understanding of stage-specific adaptation in the transcriptionally unique parasite Leishmania. By dissecting the relative contributions of mRNA abundance and protein turnover to final protein levels across life stages, the authors offer valuable insights into post-transcriptional and post-translational regulation. The work represents a resource-driven yet conceptually informative contribution to the field, with comprehensive supplementary materials and transparent data sharing standing out as additional strengths.  

However, the mechanistic insights proposed are speculative in several places and require more cautious language. The study is most impactful as a resource and descriptive atlas, initiating hypotheses for future validation. The broad scientific community working on Leishmania, trypanosomatids, and post-transcriptional regulation in eukaryotes would benefit from this work.

We thank the reviewer for this positive assessment and have modified the manuscript to further emphasize its strength as an important resource to incite mechanistic follow-up studies.

Field of reviewer expertise: multi-omics integration, bioinformatics, molecular parasitology, transcriptomics, proteomics, metabolomics, Leishmania, Trypanosoma.

Reviewer #4 (Evidence, reproducibility and clarity):

Summary:

This study investigates the regulatory mechanisms underlying stage differentiation in Leishmania donovani, a parasitic protist. Pesher et al., aim to address the central question of how these parasites establish and maintain distinct life cycle stages in mostly the absence of transcriptional control. The authors employed a five-layered systems-level analysis comparing hamster-derived amastigotes and their in vitro-derived promastigotes. From those parasites, they performed a genomic, transcriptomic, proteomic, metabolomic and phosphoproteomic analysis to reveal the changes the parasites undertook between the two life stages.

The main conclusion stated by the authors are:

- The stage differentiation in vitro is largely independent of major changes in gene dosage or karyotype.

- RNA-seq analysis identified substantial stage-specific differences in transcript abundance, forming distinct regulons with shared functional annotations. Amastigotes showed enrichment in transcripts related to amastins and ribosome biogenesis, while promastigotes exhibited enrichment in transcripts associated with ciliary cell motility, oxidative phosphorylation, and posttranscriptional regulation itself.

- Quantitative phosphoproteome analysis revealed a significant increase in global protein phosphorylation in promastigotes. Normalizing phosphorylation changes against protein abundance identified numerous stage-specific phosphoproteins and phosphosites, indicating that differential phosphorylation also plays a crucial role in establishing stage-specific biological networks. The study identified recursive feedback loops (where components of a pathway regulate themselves) in post-transcriptional regulation, protein translation (potentially involving stage-specific ribosomes), and protein kinase activity. Reciprocal feedback loops (where components of different pathways cross-regulate each other) were observed between kinases and phosphatases, kinases and the translation machinery, and crucially, between kinases and the proteasomal system, with proteasomal inhibition disrupting promastigote differentiation.

We thank the reviewer for the time and implication dedicated to our manuscript.  

Further details are organised by order of apparition in the text:

Material and Methods: while the authors are indicating some key parameters, providing the codes and scripts they used throughout the manuscript would improve reproducibility.

We thank the reviewer for this comment and added the URL for the codes to the data availability section.

Why only 2 biological replicates for RNA while the others layers have 3 or 4?

We agree with the other reviewers and have repeated this analysis to have statistically more robust results.

Is the slight but reproducible increase in median coverage observed for chr 1, 2, 3, 4, 6 and 20 stable on longer culture derived promastigotes and sandfly derived promastigotes ?

No, as published in Barja et al Nature EcolEvol 2017 (PMID: 29109466) and Bussotti et al PNAS 2023 (PMID: 36848551), these minor fluctuations are not predicting subsequent aneuploidies in long-term culture nor in sand fly-derived promastigotes. This information has been added to the text.

Is this change of ploidy a culture adaptation representation rather than a life cycle event as the authors discuss later on? (This is probably an optional request that would be nice to include, if the authors have performed the sequencing of such parasites. Otherwise, it should be mentioned in the discussion).

Yes, this is a well-known culture adaptation phenomenon, on which we have published extensively. We added this conclusion and the references to the text.

L333 "Likewise, stage differentiation was not associated with any major gene copy number variation (Figure 1C, Table 2)". The authors are looking here at steady differentiated stages rather than differentiation itself. "Likewise, stage differentiation was.." would be more appropriate.

We corrected this sentence to ‘Likewise, differentiation of promastigotes was not associated with any major gene copy number variation at early passage 2’.

L349-355: have the mRNA presenting change in abundance between stages been normalised by their relative DNA abundance ? Said otherwise, can the wave patterns observed at the genome level explain the respective mRNA level ? Can the authors plot in a similar way the enrichment scores in regards to the position on the genome and can the authors indicate if there is a positional enrichment in addition to the functional one they observe ? This may affect the conclusion in L356-358.

As noted above, we did not see any significant read depth changes at DNA level when comparing amastigotes and promastigotes. Thus there is no need to normalize the RNAseq results to DNA read depth. Furthermore, in our comparative transcriptomics analysis, we only consider 2-fold or higher changes in mRNA abundance (which is far beyond the non-significant read depth change we have observed on DNA level). Manual inspection of the enrichment scores with respect to position did not reveal any significant signal (other than revealing some overrepresented tandem gene arrays where all gene copies share the same location and GO term).

L415 "stage-specific expression changes correlate between protein and RNA levels, suggesting that the abundance of these proteins is mainly regulated by mRNA turn-over". Overstatement. Correlation does not suggest causation. "suggesting that the abundance of these proteins could be regulated by mRNA turn-over" would be more appropriate.

We thank the reviewer for this comment and have corrected the statement accordingly.

Figure 3B, could the authors clarify what are the "unique genes" that are on the infinite quadrants? It seems these proteins are identified in one stage and not the other. This implies that the corresponding missing values are missing non-at random (MNAR). Rather than removing those proteins containing NMAR from the differential expression analysis, the authors should probably impute those missing values. Methods of imputation of NMAR and MAR can be found in the literature. Indeed, the level of expression in one stage of those proteins is now missing, while it could strongly affect the conclusions the authors are drawing in figure 4E regarding the proteins targeted for degradation and rescued in presence of the proteasome inhibitor.

We thank the reviewer for this important comment. However, we would like to clarify several key points regarding the treatment of proteins identified in only one condition.

First, the reviewer assumes that proteins identified in one stage but not the other are necessarily missing not-at-random (MNAR). However, this cannot be definitively established, as these missing values could equally be missing completely at random (MCAR). Without additional information, categorizing them specifically as MNAR may be an oversimplification. More importantly, we have concerns about the reliability of imputation methods in this specific context. Algorithms designed to impute MNAR values (such as QRILC) replace absent data using random sampling from arbitrary probability distributions, typically assuming low intensity values. However, when no intensity value has been detected or quantified for a protein in a given condition, imputing an arbitrary low value raises significant concerns about data interpretation. Such imputed values would not reflect actual measurements but rather statistical assumptions that could introduce bias into downstream analyses. For instance, imputed values could lead to the conclusion that a protein is not differentially abundant, when in reality it is detected in one condition but completely absent in the other. In our view, there are two biologically plausible scenarios: either these proteins are expressed at levels below our detection threshold, or they are genuinely absent (or present at negligible levels) in the corresponding stage. Rather than introducing potentially misleading imputed values, we chose to treat these as genuine stage-specific differences (presence/absence), which results in infinite fold-changes in Figure 3B. Critically, our approach is strongly supported by independent validation through RNA-seq data, which corroborates the differential presence/absence patterns observed at the protein level. Furthermore, our enrichment analyses reveal significant over-representation of specific biological terms among these stagespecific proteins, providing biological coherence to these findings. These converging lines of evidence (proteomics, transcriptomics, and functional enrichment) strengthen our confidence that these represent biologically meaningful differences rather than technical artifacts.Therefore, we believe our conservative approach of treating these as genuine presence/absence differences, validated by orthogonal data, is more appropriate than introducing imputed values based on arbitrary statistical assumptions. To clarify this section, we modified the text as follows: ‘Only expression changes were considered that either showed statistically significant differential abundance at both RNA and protein levels (p < 0.01), or showed significant RNA changes (p < 0.01) with the corresponding protein being detected in only one of the two stages. These latter proteins are identified by signals that were arbitrarily placed at the upper (detected in ama) or the lower (detected in pro) parts of the graph. Whether these proteins just escape detection due to low expression or are truly not expressed remains to be established.’

L430-435 "These data fit with the GO [...] the ribosome translational activity (34)." This discussion feels out of place and context. It is too speculative and with little support by the data presented at this stage of the manuscript. It should be removed as Figure 3E or could be placed in the discussion and supplementary information.

We agree with the reviewer. In response to a comment from reviewer 1, we have moved both panels to Figure 2, which much better integrates these data.  

The authors present an elegant way to show stage specific degradation through the comparison of stage specific proteasome blockages that show rescue in ama of proteins present in pro and vice versa. L494 "reveal an unexpected but substantial" the term unexpected is inappropriate, as several studies have shown in kinetoplastids the essential role of protein turnover through degradation / autophagy during differentiation. Furthermore the conclusions may be strongly affected by the level of expression of the proteins in the infinite quadrants as we discussed above, and should be revised accordingly.

We rephrased the conclusion to ‘In conclusion, our results confirm the important role of protein degradation in regulating the L. donovani amastigote and promastigote proteomes and identify protein kinases as key targets of stage-specific proteasomal activities.’ Please see the response to comment 9 regarding the unique proteins.

L518 "These data reveal a surprising level of stage-specific phosphorylation in promastigotes, which may reflect their increased biosynthetic and proliferative activities compared to amastigotes." Overstatement. Could also be due to culture adaptation - What is the overlap of stage-specific phosphorylations with previous published datasets in other species of Leishmania? Looking at such comparisons could help to decipher the role of culture adaptation response, species specificity and true differentiation conserved mechanisms.

We agree with the reviewer and have toned this statement down by adding the statement ‘….or simply be a consequence of culture adaptation’.

The discussion is extremely speculative. While some speculation at this stage is acceptable, claiming direct link and feedback without further validation is probably far too stretched. For example, the changes of phosphorylation observed on particular sets of proteins, such as phosphatase and DUBs, need to be validated for their respective change of protein activity in the direction that fits the model of the authors. Those discussions should be toned down.

We agree with the reviewer and have strongly toned down the entire discussion, emphasizing the hypothesis-building character of our results, which provide a novel framework for future experimental analyses.

A couple of typos:

In the phosphoproteome analysis section, "...0,2 % DCA..." should be "...0.2 % DCA..." (use a decimal point).

L225 "...peptide match was disable." should be "...peptide match was disabled."

Both corrected

Reviewer #4 (Significance):

While there is not too much novelty around the emphasis of gene expression at post-translational level in kinetoplastid organisms, the scale of the work presented here, looking at 5 layers of potential regulations, is. Therefore, this study represents a substantial amount of work and provides interesting and comprehensive datasets useful for the parasitology community.

We thank the reviewer for this positive statement.

Several potential concerns regarding the biological meaning of the findings were identified. These include the limitations of in vitro systems promastigote differentiation potentially limiting the conclusions, the challenge of inferring causality from correlative "omics" data, and the complexities of functional interpretation of changes in phosphorylation and metabolite levels. The proposed feedback loops and functional roles of specific molecules would require further experimental validation to confirm their biological relevance in the natural life cycle of Leishmania, but that would probably fall out of the scope of this manuscript.

We agree with the reviewer and have modified pour manuscript throughout to remove any causal relationships. Indeed, this work is setting the stage for future investigations on dissecting some of the suggested regulatory mechanisms.

Area of expertise of the reviewers: Kinetoplastid, Differentiation, Signalling, Omics

I actually think that the tweets coming from Trump himself in this context are MORE authentic than the ones coming from his campaign team. As users of the platform and people living in this country, we expect a certain flavor of content out of Trump's tweets. Seeing posts from his campaign next to posts from Trump in some ways acts to muddy the waters. If the public face of a presidential candidate was always angry and negative, many voters may be turned away from that candidate. But by intermixing calm, structured posts, it makes the candidate appear able to switch their anger and negativity on and off. Which may be more appealing to voters.

Author response:

Public Reviews:

Reviewer #1:

Summary:

The authors aim to study mutational paths connecting WW domains with different binding specificities. Their approach combines an unsupervised sequence generative model based on RBMs with a path-sampling algorithm. The key result is that most intermediate sequences along the designed transition paths retain measurable binding activity in wet-lab assays, whereas paths containing the same mutations introduced in a randomized order are largely nonfunctional. This difference is attributed to epistatic interactions captured by the RBM model.

Strengths:

Exploring mutational paths in high-dimensional protein sequence space is a challenging problem. The computational framework used here is state-of-the-art and is strengthened by systematic experimental characterization of binding activity. The study is comprehensive in scope, including multiple transition paths both within and across WW specificity classes, and the integration of modeling with high-throughput experimental validation is a clear strength.

Weaknesses:

A major concern is whether the stated goal of specificity switching is fully achieved. Along the sampled transition paths, most intermediate variants appear to retain specificity close to either the initial or the final class, rather than exhibiting gradually shifting specificity. For example, in Figure 4G (Class I to Class II/III), binding appears largely binary, with intermediates behaving similarly to one of the endpoints. A similar pattern is observed in Figure 3H for the Class I to Class IV transition, where binding responses are close to 0 or 1. In this sense, the specificityswitching objective is only partially realized by assigning two endpoints with different specificity. This raises a broader conceptual question: is it possible that different WW specificities evolved from a common ancestor without passing through intermediates that exhibit mixed or intermediate specificity? If so, then inferring specificity-switching pathways purely from extant natural sequences may be fundamentally challenging.

This is a key question, which was one of the original motivations of our work. Both hypothesis of ‘abrupt switches’ (punctuated equilibria, corresponding to distinct specificities) and more gradual changes (smooth transition, through intermediate that exhibit mixed or intermediate specificity) are possible.

Many natural specificity-switching events have probably resulted from the need to adapt to environmental change and selection for a different specificity, which can be compatible with an abrupt change in specificity. Others may reflect the gradual evolution of promiscuous ancestral sequences to more specialized ones, loosing cross-reactivity. A molecular mechanism that could allow abrupt switching is gene duplication, a frequent mechanism for WW domain diversification, beyond standard mutational-driven evolution processes.  

As for the specificity-switching paths for WW domains found in this work, the presence of weakly responsive cross-reactive intermediates along the designed paths for I<->IV, and their absence in the I<->II path, suggests that designing promiscuous domains is hard (see also related response to point 3 of Reviewer 2) and generally not selected by natural evolution (as seen from the clear clustering of extant proteins in different specificity classes). 

For a small domain such as WW, mutations that favor some specificity classes are known to have detrimental effects on fundamental properties, such as folding kinetics and stability, see Ref [72]. It is possible that larger, less constrained protein domains could allow for more crossreactive variants and smoother specifity switching. However, experiments on fluorescent proteins looking for interpolation between two wave-lengths have shown that the switch was abrupt [Poelwijk et al. Nature Communications (2019)].

Our scope was to achieve a functional switch (imposed by the two extant end-points) through a path of designed, functional intermediates and to correctly predict, with our RBM model, the location of the specificity transition and of the cross-reactivity region (which we expected only along the I-IV path). This scope was successfully reached as demonstrated by experiments.  

Reviewer #2:

This is an extremely important work that shows how one can use generative models to construct specificity-switching mutational paths in complex fitness landscapes. The experimental evidence is very clear, and the theoretical tools are innovative.

The work will likely have a deep impact on future research aimed at understanding how evolution navigates fitness landscapes as well as reconstructing ancestral sequences.

The manuscript is extremely clear and well written, the experimental evidence is strong, and the methods are clearly described, so I do not have major issues to raise. A few minor issues are listed below.

(1) I consider the WW domain as an 'easy' case from the point of view of generative modelling. The domain is rather short, epistatic effects are not very strong (e.g. Boltzmann learning usually converges very quickly to a very paramagnetic state), and the resulting models are well interpretable (e.g. the hidden units of the RBM correlate well with subclasses).

This is not always (not often?) the case, however. In more complex proteins, the learning procedures can be slower and the resulting models less interpretable. Just for completeness, perhaps the authors could comment on the generality of the results and what they would expect for other systems based on their experience.

We agree with Reviewer 2 that WW sequences are short and simple to handle from a computational point of view, and was chosen for this reason to test the design of full mutational paths (after having benchmarked it to lattice-protein models, see Refs. [30] and [44]). Our work gives additional support to the effectiveness of generative models learned from sequence data.  This said, from a biological point of view, WW is a highly constrained domain, see comment by Reviewer 1 above and our answer.

In longer and more complex proteins, we expect it will be more difficult to disentangle specificityswitching latent units, see Fernandez-de-Cossio-Diaz et al., Physical Review X 2023 for a discussion and a possible computational approach to this issue. Notice that, while relating the latent units to specificity classes was convenient, it was not used to generate the paths themselves. Therefore, we believe that our method is quite robust and easily generalizable to applications to more complex and longer proteins. As an illustration, we have recently used it to sample viral trajectories (more precisely, variants of the Receptor Binding Domain of the SARSCoV-2 spike protein) capable of escaping antibody recognition, see Huot et al., PNAS 2026. In this recent work, we projected the paths onto the principal antigenic space, defined by the top two Principal Components of the viral variant binding affinities to 32 antibodies. In this representation, sampled paths displayed trends similar to natural paths, drawn from the sequences sampled during the pandemics. This finding supports the applicability and interpretation of our method for more complex proteins.

(2) In Section 3.3, the authors say that direct paths connecting Class I and Class IV behave similarly to indirect paths, despite having lower scores according to the RBM. How generic is this? Does it also happen for other classes? This might be an important point to address, as direct paths are easier to sample.

We think that this finding, true for paths connecting classes I and IV, is not general. In a previous paper we have benchmarked our path-designing approach on simple models of insilico lattice proteins and shown that indirect path led to gains in the overall fitness (computed according with the ground-truth model) [Mauri, Cocco, Monasson, Physical Review E 2023, fig. 9-12].

In general, we would expect that indirect paths could explore alternative mutations, important to compensate for transitory destabilizing mutations that could occur along the path. We speculate that these stabilizing mutations happen for non-direct paths at its extremity near class-I wildtype. A slightly decrease in binding response to peptide C1 for direct path is nevertheless observed (see Suppl Table 4), but our experimental detection, focused on binding response, is not tailored to directly detect a difference in stability. When approaching the class-IV anchoring point, we observe that paths interpolating between classes I and IV are very constrained and show limited diversity, going through a funnel in sequence space corresponding to the direct path. We agree with Reviewer 2 that a more exhaustive comparison with direct paths would be interesting, and will add a sentence in conclusion.

(3) The path shown in Figure 4 goes through a region of non-functionality around sequences 1819. It seems that the sample path is basically exploring the functional regions for Class I and Class II/III separately, trying to approach the other class, but then it can't really make the switch.

By contrast, the path going from Class I to Class IV seems able to perform the functional switch in a single step (20-21) without losing too much of the function.

Perhaps the authors could better comment on this? Is this a limitation of the sampling method, or a fundamental biological fact?

Class I to Class IV paths and Class I to Class II paths fundamentally differ because the binding pocket in Class I WW domains is different from the one of Class IV WWs, while Classes I and II/III share the same binding region. This important difference may explain why class I specificity can switch to class IV specificity (steps 20-21), without completely loosing affinity to the peptide of class I. To investigate if the two binding regions are really independent or not, we have tested some additional specific mutations along the I-IV mutational paths. In our attempts to engineer cross-reactivity, we have observed that it is important to substantially lower affinity to class I peptide to acquire class IV specificity, in agreement with previous studies [72]. Moreover, the I to IV path seems to go through a funnel-like part in the region with no natural sequences, with the same transition intermediates obtained in several designed paths. This indicates that the Class I to Class IV functional switch is more constrained than the Class I to II switch. Let us also emphasize that our assessment of class specificity is based on one peptide for each class. It would be interesting to test multiple WW-binding peptides with similar biochemical properties to acquire a more complete view of the specificities. 

(4) On page 12, it is stated that the temperature was chosen to 1/3 to maximize the score. This is important and should be mentioned earlier (I didn't notice it until that point).

Section 3.5 explains that RBM samples can be biased, by lowering the sampling temperature to 1/3 to obtain high-scores sequences, which are more likely to be functional as proven in [Russ et al., Science 2020]. We acknowledge (as also noted by Reviewer 1) that this section comes at the end of the manuscript, while differences in scores along the path are shown before, so the discussion of this important point is somewhat delayed. We will add a sentence earlier in Results to explain this point.  

(5) On page 13, it is stated that: "However, the scores of the ancestral sequences along the phylogenetic pathways assigned by the RBM are significantly lower than the ones of the RBMdesigned sequences. This result is expected as ASR reconstruction does not take into account epistasis, differently from RBM, and we expect ASR sequences to generally be of lesser quality."

I was very surprised by this result. My own experience with ASR shows that, on the contrary, sequences found by ASR (via maximum likelihood) tend to have high scores in the (R)BM, and tend to be more stable than extant sequences. I attribute this to the fact that ASR typically finds a "consensus" sequence that maximizes the contribution to the score coming from the fields (the profile), which is typically dominant over the epistatic signal, resulting in a bigger score. Maybe the authors did not use maximum likelihood in the ASR? Some clarification might be useful here.

We agree with Reviewer 2 that the consensus sequence is an atypical sequence for an independent model with a large RBM score. We will update Figure 5 of the manuscript to show that this is also happening in our case. 

We use Maximum Likelihood in ASR but our ASR path corresponds to all internal nodes of the reconstructed tree joining the two extant sequences, not only to the most ancestral node. Overall, the ancestral sequences along the ASR paths are different from the consensus sequence (mean identity of 76% and 60% respectively). The most ancestral nodes in the paths  are also different from the consensus having 81% (paths between type I and IV domains) or 54%(paths between type I and II/III domains) similarity, and an RBM score  of -21, or -58, respectively. We agree that some ASR internal-node sequence have a higher score than the natural wild-types (extant sequences). This is shown in Fig. 6: several points have larger RBM score than the two anchoring points at the extremities of the path, possibly due to the fact that natural sequences are not always the most stable ones. As discussed in conclusion, ASR nodes have moreover generally better scores than the sequences obtained by sampling an independent model. Phylogenetic reconstruction implicitly takes into account some degree of co-variation between sites in natural sequences, as shown by the success of the use of the phylogenetic distance of a mutated sequence to the wild-type for predicting the fitness effect of these mutations [Laine, Mol. Biol. Evol. 2019]. 

To better show this effect we will update Figure 6, reporting also the scores of the « scrambled » sequences, which do not respect potential epistasis extracted by the RBM. It appears that ASR sequences generally have better scores than the scrambled sequences, and lower than RBM sequences (sampled at T=1/3). RBM models takes into account multiple-residues correlations, which could contribute to reaching better scores than ASR and BM models. Ongoing studies on larger proteins show that the score of sequences sampled from ASR reconstruction, including the Maximum Likelihood one, can still be improved according to the RBM score by a few mutations consistent with the ASR posterior probabilities (unpublished). 

Mistakes in the reference list will be amended in the updated version.

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

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Reply to the reviewers

1. General Statements [optional]

We thank to all reviewers on their careful consideration of our manuscript. We highly appreciate their thoughtful comments and suggestions, that helped us to improve the quality of our work. We address each comment point-by-point below.

2. Description of the planned revisions

__Reviewer #1 __

Minor comments:

Figure 5 would be more informative if it included more higher magnification images that would reveal the staining at the cellular level.

To fulfil the suggestion, we will perform a new round of immunostaining followed by high-resolution confocal imaging. This requires additional time for laboratory work.

__Reviewer #2: __

Major comments

1d. The authors tried to attribute the minor phenotype to the incomplete depletion of S100A4+ cells. However, it is possible that if the S100A4+ cells only represented a minor population, their function may be compensated by other populations. This might be confirmed by quantification of S100A4+ cells or S100A4-Cre; GFP+ cells in fibroblast or CD45 populations from images showed in Figure 5.

We will address this comment by performing required quantifications.

Moreover, we have now included data on the presence of S100A4+ cells in S100a4-Cre;DTA mice (Figure for Reviewers 5a,b; Supplementary Figure 7a,b in the revised manuscript), which demonstrate incomplete depletion of the S100A4+ cells in the nipple and the mammary gland. This is likely due to ongoing tissue remodeling and continuous S100A4+ replenishment/ supply. Another study using the same S100a4-Cre;DTA mouse model reported an efficient S100A4+ cell depletion in mandibular condyle (Tuwatnawanit et al., 2025), which suggests that the presence of S100A4+ cells in the S100a4-Cre;DTA mammary gland and nipple is due to tissue-specific dynamics rather than lack of depletion efficiency.

        We have included in Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

The images in Figure 5 and Figure S4 are difficult to confirm colocalization. A higher magnification image would be required for each panel. Furthermore, a precise quantification based on the current images would be more supportive of the conclusion regarding the discrepancy of the composition of S100A4 lineage between epidermis and mammary gland (lines 163-165).

To address this comment, we will perform a new round of immunostaining and high-resolution confocal imaging and quantifications and include the results in the fully revised manuscript.

Line 163, the author hypothesis the Langerhans cells due to morphology. Those cells should be able to be confirmed by a co-staining with F4/80 in addition to the current form of Fig 5h.

To address this comment, we will perform co-staining of GFP and F4/80 (or, eventually, AIF1, depending on antibody availability) and include the results in the fully revised manuscript.

Reviewer #3

Minor comments

Figure 2c: The H&E images are not fully convincing. Immunofluorescence analysis of epithelial architecture would support the authors' interpretation and should be feasible if tissues are already available.

We will perform immunostaining for epithelial markers, such as keratins, and include the results in the fully revised manuscript.

Figure 4f: The proliferation data are compelling, but the authors could extend this by examining how cell differentiation and epithelial organisation are affected.

We will perform immunostaining for epithelial markers (keratins, αSMA) and include the results in the fully revised manuscript.

Figure 5b: To more convincingly show that GFP+ cells contact endothelial cells, co-labelling with an endothelial marker such as CD31 would be helpful.

We will perform the requested co-labeling of GFP and CD31 and include the results in the fully revised manuscript.

Figure 5f-h: The structures referenced in the text (lines 159-163) should be clearly indicated on the immunofluorescence images.

We will incorporate these explanations into the new, high-resolution/detailed Figure 5 in the fully revised manuscript.

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

Reviewer #1:

Major comments

1. It is rather difficult to conclude whether the observed nipple phenotype reflects an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these).

The data raise a couple of additional questions: Is there a nipple phenotype at 3 wk of age? It would not be totally unsurprising if ablation of a major fraction of dermal fibroblasts in the nipple area would lead to an early embryonic/prepubertal phenotype but there is no data on this. Hence, is there a "congenital" nipple deformity, as concluded by the authors (line 191)?

We appreciate the reviewer’s insightful comments. We have now included data on embryonic nipple development. These data demonstrate abundant S100A4-lineage cells in E15.5 and E18.5 skin of S100a4-Cre;mT/mG embryos (Figure for Reviewers 1a, corresponding to Figure S3a in the revised manuscript) and normal appearance of nipple sheath in S100a4-Cre;DTA embryos at E18.5 (Figure for Reviewers 1b, corresponding to Figure S3b in the revised manuscript), suggesting no embryonic defect.

Unfortunately, we cannot provide data on 3-weeks old mice (we have not collected this timepoint previously and currently we do not have this mouse line alive). Instead, however, we provide in situ pictures of DTA and S100a4-Cre;DTA nipples at 7 weeks of age (Figure for Reviewers 1c; Figure S3c in the revised manuscript), which demonstrate that the phenotype of defective nipple is fully established at this timepoint. Because the late embryonic data did not support the “congenital” establishment of the nipple deformity and we could not provide any more data from early postnatal development, we have corrected the statement “we describe a congenital nipple deformity” in the discussion to “we describe a nipple deformity”.

Are there S100a4+ cells in the nipple area of pubertal S100a4-Cre/DTA mice? I.e. is there a continuous supply of new S100a4+ cells and thereby continuous cell death and DTA expression as one might expect based on the RNA-seq data?

The S100A4+ cells are present in the nipple area of S100a4-Cre;DTA mice, suggesting a continuous supply of new S100A4+ cells (Figure for Reviewers 1b, corresponding to Figure S3b in the revised manuscript; and Figure for Reviewers 5a,b, corresponding to Figure S7a,b in the revised manuscript). In the revised manuscript, we comment on this in Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

Figure for Reviewers 1 (Figure S3 in the revised manuscript): Embryonic and pubertal nipple phenotype. (a) Representative images of cleared whole-mount S100a4-Cre;mT/mG nipple tissue at embryonic developmental time-points: E15.5 and E18.5. Scale bar = 100 µm. (b) Immunofluorescent labeling for S100A4 on embryonic DTA and S100a4-Cre;DTA whole-mount skin (E18.5). Scale bar = 100 µm. (c) Representative in situ photographs of nipples from DTA and S100a4-Cre;DTA pubertal (7-weeks old) mice. Scale bar = 1 mm.

The subtitle on line 54 implies that that S100a4-Cre/DTA mice display a branching phenotype. However, it looks to me as if there is a pubertal outgrowth defect (as is also written in the body text, line 64) rather than a branching phenotype, potentially reflecting the much smaller size of S100a4-Cre/DTA mice (Fig. 2a). Unless there is a change in branch point frequency, I suggest rephrasing the title and discussion. Instead, I suggest the authors discuss the observed outgrowth delay considering the gross overall growth defect (Fig. 2a). If ductal outgrowth was normalized to the overall growth defect, would one still observe 'a delay in branching morphogenesis'?

We apologize for the section title confusion. We have analyzed branching frequency in 7-weeks-old females and observed reduced total number of branching points in S100a4-Cre;DTA mice (Figure for Reviewers 2a, corresponding to Figure 2f in the revised manuscript). A significant difference in number of branching points remained also after their normalization to body weight, (Figure for Reviewers 2c, corresponding to Figure 2h in the revised manuscript). We have now added the new quantifications to the revised manuscript with accompanying descriptions in the main text “Analysis of mammary epithelial development using whole-mount carmine staining revealed no significant differences in the prenatal establishment of the mammary epithelial tree but did reveal significantly delayed epithelial outgrowth and reduced branching in pubertal (7 weeks old) S100a4-Cre;DTA mice (Figure 2e,f). Normalization of epithelial outgrowth and branching to body weight indicates that the observed defect represents a mammary-specific impairment rather than a consequence of reduced body growth (Figure 2g,h).”.

__Figure for Reviewers 2 (Figure 2 in the revised manuscript): __Pubertal branching morphogenesis is delayed in S100a4-Cre;DTA. (a-c) The plots show total number of branching points (a), epithelial outgrowth [mm] normalized to body weight [g] (b), and total number of the branching points normalized to body weight [g] (c) in 7 weeks old DTA and S100a4-Cre;DTA mice. All plots show the mean ± SD, *p

Fig. 4e shows Masson's Trichrome and Picrosirius Red staining and the authors report the findings as follows (lines 120-124): "collagen fibers were loosened in the DTA nipples and more densely packed in the S100a4-Cre;DTA nipples". Perhaps the authors could help non-specialists to observe the loosened fibers and if they wish to make quantitative statements ("more densely packed"), such statements should be backed-up by quantifications.

Picrosirius Red staining viewed under polarized light is a classic way to assess collagen organization, thickness, and packing. Red / orange / yellow color typically marks thicker, more mature, and more tightly packed collagen fibers (often associated with type I collagen), while green color usually marks thinner, less organized, or less densely packed fibers (often associated with type III collagen or immature collagen). We had included this explanation in the Figure legend of the submitted manuscript already: “Typically, thicker collagen fibers exhibit stronger birefringence and appear red or orange, while thinner fibers exhibit weaker birefringence and appear green or yellow.” To help with the quantification, we have extracted the red channel and quantified color intensity. The results are shown in Figure for Reviewers 3, corresponding to Figure S4 in the revised manuscript. Moreover, we will also quantify the differences in pattern of the collagen fibers. The fibers in DTA nipples look shorter and more curved, while the fibers in S100a4-Cre;DTA nipples look longer and straighter, more aligned. The results will be included in the fully revised manuscript.

Figure for Reviewers 3 (Figure S4 in the revised manuscript): Collagen fibers are densely packed in S100a4-Cre;DTA nipples contain more . (a) Representative pictures of histological sections of DTA and S100a4-Cre;DTA stained for collagen by Picrosirius red. Polarized light images and the red channel (mature/densely packed collagen) are shown alongside detail pictures of selected regions A and B. Scale bar = 200 µm and 100 µm (in detail pictures). (b) Quantification of Intensity Mean Value for the red channel (densely packed collagen), showing statistically non-significant difference. The plot shows the mean ± SD, ns p > 0.05 (Mann-Whitney test), n = 3 DTA / 4 S100a4-Cre;DTA.

I found the Discussion on the various mouse models somewhat problematic. Overall, the paper is written is a way that it often remains unclear whether it refers to studies addressing the role of S100a4 itself, studies addressing the function of S100a4+ cells via ablation approaches (S100a4-Cre or S10 0a4-CreERT2 crossed with floxed DTA), or those where S100a4-Cre has been used to delete gene X/Y/Z. These are all very different experimental approaches where one approach is not necessarily informative when trying to understand the results from another one. The authors should make these points clear and consider whether all their discussion points are relevant.

We apologize for the confusion. We have carefully reviewed the references and their interpretations, and corrected them as necessary.

The abstract states S100a4 (fibroblast-specific protein 1) is "expressed by mesenchymal cells and has been implicated in the development of eccrine glands, hair follicles, and mammary branching morphogenesis". However, the study on eccrine glands (ref. 19) shows that S100A4+ cells play a role in eccrine gland development but it does not address the role of S100a4 itself, while the study on hair follicles (ref.20) in turn reports the expression pattern of S100a4 in hair follicles but does not address its function, nor the role of S100a4+ cells. Finally, I failed to find references in the paper to studies addressing the role of S100a4, or S100a4+ cells in the mammary gland.

Instead, the paper had references to studies where S100A4-Cre had been used to delete different genes and these mice had various mammary phenotypes - which, as indicated above, is a very different approach compared to deleting S100a4 or ablating S100a4+ cells.

Thank you for your comment. We addressed the concern in the Abstract and further in the Discussion. We revisited the present the cited studies more carefully, clearly distinguishing the different approaches and particular findings.

In our literature review, we also considered studies that used S100a4-Cre mouse model, to manipulate gene expression within S100A4+ cells. We believe that these studies bring indirect evidence of S100A4+ cell involvement in development and/or homeostasis of a tissue, such as mammary gland. Please, find the rephrased part of Abstract in the text, and below:

“S100A4 (S100 calcium binding protein A4, also known as fibroblast-specific protein 1) is expressed by mesenchymal cells and has been associated with hair follicle regeneration. S100A4-expressing cells have been implicated in the development of eccrine glands, and studies using S100a4-Cre to manipulate gene function have suggested that S100A4-expressing cells may contribute to mammary branching morphogenesis.”

__In Discussion (lines 197-200), __the authors write: "We described significant delay in mammary branching morphogenesis in puberty, confirming an important role for S100A4+ cells in mammary development, as it was previously described (refs 37-39)."

It should be noted that none of these studies addressed the role of S100A4+ cells:

• Ref 37 used S100a4-Cre to delete sharpin

• Ref 38 used the same Cre line to delete Ptch1, did not address the role of S100a4 or S100a4 expressing cells

• Likewise ref 39 deleted another gene using S100a4-Cre

Later on in Discussion, the authors compare the reported phenotype to previous studies (lines 248-255): "...targeting S100A4+ cells through knockout experiments can result in severe phenotypes, such as a reduction in adipose tissue (ref 26), skin phenotypes, a disrupted estrous cycle, reduced fertility (ref. 38), and complete infertility, hypogonadism and defects in pituitary endocrine function (ref. 28).

Of these, Ref. 26 used the same approach as the current study (S100a4-Cre; DTA) (Fig. 7A in the paper)

• these mice were significantly lean, with markedly reduced fat compared with the control mice - also the mice in the current study are very small, so perhaps they could also be described as 'lean'. Yet ref. 26 reports that female mice had comparable food uptake, respiratory exchange ratio and physical activity, and slightly increased energy expenditure

Ref. 38 (as mentioned above) reports deletion of Ptch1 using S100a4-Cre lines and these mice "displayed a disrupted estrous cycle and dramatically reduced fertility over 6.5 weeks". However, this has nothing to do with the approaches where Fsp1/S100a4+ cells are depleted with DTA. Likewise, reference 28 analyzed the phenotype of S00a4-Cre;Ptch1fl/fl mice. Obviously, deleting Ptch1 using S100a4-Cre mice is quite a different approach than "targeting S100A4+ cells" through knockout experiments". Ptch1 deletion leads to a combination of gain-of-function (of Hedgehog activation) and loss-of-function (loss of Hh-independent functions of Ptch1) and hence comparisons with these phenotypes is rather challenging. I suggest the authors focus their phenotype comparisons to ref. 26 where S100a4/Fsp1+ cells were ablated with DTA, i.e. the same approach as in the current study.

Please, find the rephrased part of Discussion in the text (lines 236-256), and below:

“A key consideration when interpreting studies involving S100A4 is that fundamentally different experimental approaches have been used to investigate its role. These include descriptive analyses of S100A4 expression, functional studies targeting the S100A4 protein itself, genetic models using S100a4-Cre to manipulate unrelated genes in S100A4-expressing cells, and ablation models such as S100a4-Cre;DTA, which deplete S100A4⁺ cells. These approaches are not equivalent and provide distinct types of information. In the present study, we specifically assess the consequences of ablating S100A4-expressing cells, and comparisons to other studies should therefore be interpreted within this context.

Studies using S100a4-Cre to manipulate specific signaling pathways (e.g. Wnt or Hedgehog signaling via gene deletion) in S100A4-expressing cells have reported diverse phenotypes, including effects on fertility and endocrine function28,34. However, these phenotypes primarily reflect the consequences of pathway perturbations within S100A4-expressing cells rather than the role of S100A4⁺ cells themselves. This is fundamentally different from the ablation approach used here, which removes the S100A4⁺ cell population.

In contrast, studies employing S100a4-Cre–driven DTA–mediated ablation represent a directly comparable approach. Such studies have reported systemic phenotypes, including reduced adipose tissue and altered metabolic parameters26, indicating that S100A4-expressing cells contribute to multiple aspects of tissue homeostasis. Consistent with these previous reports, S100a4-Cre;DTA mice used in our study were significantly smaller than their littermates. Our findings extend these observations by identifying a specific and previously unrecognized role for this cell population in nipple morphogenesis.”

I find the Discussion is somewhat off the topic by starting with WHO recommendations on breastfeeding and linking this to observed mouse phenotype. Overall, the discussion is rather long and from time-to-time more like a literature review. I would recommend keeping the Discussion more succinct and focused.

To improve the conciseness and focus of Discussion, we have deleted this part of text.

**Referee cross-comenting**

I agree with the comments of other reviewers. However, to me it seems that the analysis of S100a4 knockout mice would not be feasible within a reasonable timeframe and would represent a study of its own. My understanding was that the authors were not interested in S100a4 itself. Rather, S100a4-Cre was used as a tool to understand the importance of a certain (fibroblast) cell population for mammary gland morphogenesis.

Indeed, our goal was to study the role of a specific cell population (S100A4+ cells) in mammary gland morphogenesis, not to study the role of S100A4 protein per se.

Reviewer #1 (Significance (Required)): General assessment:

This study reveals the importance of the S100a4+ cell lineage for nipple formation while showing the same cells are dispensable for mammary gland morphogenesis. The main limitation is that it remains unclear whether the observed nipple phenotype is derived from an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these). Hence its relevance as a model of human inverted nipple condition remains rather speculative.

Thank you for consideration of our work and valuable feedback. We did not intend to claim that S100a4-Cre;DTA mouse represents a model of human inverted nipple condition. However, considering morphological features, it might resemble it. We now rephrased the Discussion so it is clearer and more concise.

Reviewer #2

Major comments:

1. My key concern is the discussion part. I think the authors need to re-organize/re-phrase the discussion part, it confused me a bit in terms of logic, phrases and interpretation of literatures.

We have significantly re-organized and re-phrased the Discussion.

Here are few examples:

1. The lines 195-199 contain lot of repeated information

We have rephrased the paragraph and removed repeated information. The new text can be found in lines 201-206 in the revised manuscript.

1. The authors mentioned the studies in ref 26,28 and 38 using "targeting S100A4+ cells through knockout experiment can result in sever phenotypes". This is very misleading. Those studies using the same (or similar if the origin is different) S100A4-Cre line as the current study but induced the activation of Wnt and sHH signalling pathways, respectively. The observed phenotypes are largely due to the pathway function, rather than the S100A4 gene or normal S100A4+ cell itself. This is significantly differed from the current study.

We apologize for the confusion; we have now rephrased our claims (lines 236-256):

“A key consideration when interpreting studies involving S100A4 is that fundamentally different experimental approaches have been used to investigate its role. These include descriptive analyses of S100A4 expression, functional studies targeting the S100A4 protein itself, genetic models using S100a4-Cre to manipulate unrelated genes in S100A4-expressing cells, and ablation models such as S100a4-Cre;DTA, which deplete S100A4⁺ cells. These approaches are not equivalent and provide distinct types of information. In the present study, we specifically assess the consequences of ablating S100A4-expressing cells, and comparisons to other studies should therefore be interpreted within this context.

Studies using S100a4-Cre to manipulate specific signaling pathways (e.g. Wnt or Hedgehog signaling via gene deletion) in S100A4-expressing cells have reported diverse phenotypes, including effects on fertility and endocrine function28,34. However, these phenotypes primarily reflect the consequences of pathway perturbations within S100A4-expressing cells rather than the role of S100A4⁺ cells themselves. This is fundamentally different from the ablation approach used here, which removes the S100A4⁺ cell population.

In contrast, studies employing S100a4-Cre–driven DTA–mediated ablation represent a directly comparable approach. Such studies have reported systemic phenotypes, including reduced adipose tissue and altered metabolic parameters26, indicating that S100A4-expressing cells contribute to multiple aspects of tissue homeostasis. Consistent with these previous reports, S100a4-Cre;DTA mice used in our study were significantly smaller than their littermates. Our findings extend these observations by identifying a specific and previously unrecognized role for this cell population in nipple morphogenesis.”

1. In the lines 253-255, why the author believe complete S100A4+ depletion would leads to the fatal of mouse? Is there study suggest that? Or have authors checked the expression of S100A4 in the S100A4-Cre;DTA model to confirm the efficiency?

We have now included, also in response to other Reviewers’ comments, data on S100A4 expression in the S100A4-Cre;DTA model (Figure for Reviewers 5, corresponding to Figure S7 in the revised manuscript), and commented on these results in lines 257-262: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle48. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

In Fig. 1, the authors described the impaired nursing capacity of S100A4-Cre;DTA dam. However, it seems the little size is also smaller (Fig 1a). Do authors have any explanation or hypothesis?

Thank you for this insightful observation. It is well established that metabolic and nutritional condition directly affect female reproductive functions. Adult S100A4-Cre;DTA mice are generally smaller compared to their litter counterparts, potentially because of lower body fat content or other anatomic/metabolic condition that might negatively influence fecundity, for instance, lowering ovulation rate and/or embryonic survival. In support of this, earlier studies have reported a positive correlation between growth rate/body condition and litter size (Eisen & Durrant, 1980). Unfortunately, in the case of S100A4-Cre;DTA mice, we can only speculate about the possible explanations, as we do not have supporting data which could confirm it.

In lines 181-184, the authors states "the results showed that the tissue reacted to a foreign chemical or an endogenous compound....." , which results are referring here? I could not find any inflammation related GO terms in figure 6b. It would be more accurate to specify them in lines 179-181, which appears to be a technical statement rather than a result in current form.

Thank you for this comment. Indeed, there are no GO terms explicitly labeled as “inflammation” and “repair”; however, several GO terms are functionally related to these processes. Our interpretation was based on broader biological context rather the explicit annotation. To clarify this, we revisited the text and included GO terms that reflect the tissue response (lines 187-193).

“The GO terms indicated that the tissue reacted to a foreign chemical or an endogenous compound (xenobiotic metabolic process, cellular response to xenobiotic stimulus, response to xenobiotic stimulus, epoxygenase P450 pathway), and responded to inflammation and repair (actin filament-based process, actin cytoskeleton organization; eicosanoid and lipid metabolic processes) (Figure 6b).”

The lines 182-184 was not clear. Does the author refer the "nipple tissue response" in general as malfunction of development or inflammation and tissue repair as mentioned in the previous sentence? If the later cases, the authors should consider the failure of lactation might mimic the involution, which may cause the apoptosis and inflammation as well. This might be independent of the DTA expression.

Thank you for raising this point. Indeed, in this line, we refer to ongoing tissue inflammation and repair. We also considered the hypothesis that the ejection incapability (and consecutive milk stasis) triggers involution. However, tissues were collected within a few hours after parturition, when only very early signs of involution, if any, would be detectable; therefore, we expect minimal influence of involution. To reflect this comment, we added new text to the Discussion (lines 272– 277). “The observed tissue response can be also associated with hallmarks of mammary involution, the process which is triggered by the milk stasis. However, the tissues were collected within few hours after parturition, when the effect of involution should be minimal53. Rather, we hypothesize that immune cell recruitment, and the upregulation of the lipid skin barrier might be caused in response to the continuous apoptosis of S100A4+ cells and their replacement.”

Minor comments:

1. The authors demonstrated in Figure S1 and lines 92-96 that no significant differences were observed in pituitary glands and ovaries in S100a4-Cre:DTA and DTA mice. Have the authors checked the S100A4 expression or lineage cells in these organs, or have been reported by others?

Yes, we checked the S100A4-lineage cells in the pituitary gland and ovary and have now included the results here (Figure for Reviewer 4a,b corresponding to Figure S1a,b in the revised manuscript), along with relevant text description (lines 94-95 in the revised manuscript). “We observed S100A4-lineage traced cells in pituitary gland and ovaries using S100a4-Cre;mT/mG model (Figure S1a,b).” The presence of S100A4+ cells in these organs was also reported previously (Ren et al., 2019).

Figure for Reviewers 4 (Figure S1 in the revised manuscript): S100A4-lineage cells are abundant in the pituitary gland and ovary. (a) Representative images of a cleared whole-mount pituitary gland from a S100a4-Cre;mT/mG mouse. (b) Representative images of a cleared whole-mount ovary from a S100a4-Cre;mT/mG mouse. Scale bar = 100 µm.

The authors have performed live imaging to evaluate the contraction of alveoli. It would be better to include a video together with the snapshots showed in Figure S2.

We have included the videos as supplementary movies, Movie S1 (DTA) and Movie S2 (S100a-Cre;DTA).

Since the study is mainly using S100a4, it would be better to avoid using FSP1 in the results, for example Fig 5h.

We apologize for this oversight; it has now been corrected.

What does L1 stand for? Lactation Day 1? It should be spelt out in the first instance.

Yes, indeed, L1 is lactation day 1. Please note that it was already spelled out in the first version of the manuscript, now in line 48.

Line 150. Figure S4 should be Figure S4a.

(Please note, that by adding new Supplementary figures, this comment is referring to Figure S6 in the new version of manuscript.) Thank you for this comment. In the text, we state “GFP+ cells were spread throughout the fat pad but were also localized in the periepithelial stroma and infiltrated the epithelium”. This we show in Figure S6a and in S6b; therefore, we now changed the reference accordingly, as it might be more accurate.

**Referee cross-comenting**

I agree with the other reviewers, as well as the Consultation Comments. The manuscript would benefit greatly from a thoroughly optimised Discussion section to address issues raised by all reviewers.

__ Reviewer #2__ (Significance (Required)):

• Overall, this study is well designed and the key findings are valid, especially the role of S100A4 during nipple development is novel and interesting.

-One limitation of the study is that RNA-seq was performed using a mixture of all cell types present in the nipple. While this approach is reasonable-given that depletion of the S100A4+ lineage may exert both direct and indirect effects contributing to nipple dysfunction-it should be more clearly acknowledged and discussed in the manuscript. Additionally, this experimental design may limit the utility of the dataset for other researchers interested in nipple development and the specific functions of S100A4.

Reviewer #3

Major comments:

2) The differential systemic versus mammary-specific effects of DTA-mediated S100A4 cell ablation are intriguing. The authors should address why the mammary fat pad appears unaffected.

Thank you for this comment. The role of S100A4+ cells in adipose tissue was previously reported (Zhang et al., 2018). Authors reported significantly smaller adipose tissue of S100a4-Cre;DTA mice (males and females), measured as the weight of the dissected fat pad. In our work, we measured the in-situ area of the fat pad, which appeared to be unaffected. It is possible that the volume (weight) of the fat pad would be different, however we do not have data to confirm / reject this hypothesis.

Are S100A4 expressing cells present during embryonic mammary development, or are they mainly postnatal? Would an inducible S100A4CreERT model lead to similar phenotypes, or might the timing of depletion influence the outcome? Discussing these points would reinforce the conclusions regarding the contribution of S100A4-expressing cells to mammary and nipple development and could also clarify the transient nature of the ductal branching phenotype.

S100A4-expressing cells are present during embryonic mammary development, too. Please, refer to the embryonic lineage-tracing time-points incorporated in the first version of the manuscript (Figure 5a and Figure S6a). Now, we have added Figure for Reviewers 1 corresponding to Figure S3 in the revised manuscript), which focuses on the embryonic nipple phenotype but also provides information on the presence of S100A4+ cells.

We agree that the use of inducible S100a4-CreERT model could potentially bring new insights toward developmental stage-specific roles of S100A4+ cells, and thus would be interesting to use in a follow-up study. Currently, such experiments are beyond our capacity.

Therefore, we have included a new subsection on Limitations of the study, where we comment:

“A major limitation of this study is that the timing of DTA-mediated cell depletion cannot be precisely defined in the constitutive mouse model employing S100a4-Cre because recombination may occur continuously following the initial expression of S100a4 (E8.518). This limitation could be overcome by usage of inducible S100a4-CreERT instead. With this approach, it could be more feasible to determine if the nipple deformity arises as a defect of embryonic development or postnatal morphogenesis.”

3) Although the authors attribute lactation failure primarily to defects in nipple architecture, the RNA seq data reveal downregulation of key milk production genes and luminal differentiation keratins, strongly suggesting impaired secretory activation. The authors should more explicitly discuss the relative contributions of epithelial functional maturation defects versus nipple structural abnormalities to the lactation failure observed upon S100A4+ cell depletion. Thank you for this comment. We believe that performing an immunofluorescence labeling of epithelial architecture (requested in the Minor comment 2) could bring more light into this. However, we deduce that secretory activation is not impaired, as the presence of the milk observed on in situ wholemounts, and H&E-stained alveoli (Figure 3d) implies luminal secretion of milk components. The observed phenotype of the lactating mammary gland strongly suggests there is a structural abnormality inhibiting the milk ejection.

The downregulation of key milk production genes and luminal keratins in the bulk RNA-seq data may be influenced by differences in tissue composition between samples. In control mice, more fully developed nipples and an extended ductal network likely contribute to a greater representation of differentiated luminal epithelial cells, thereby increasing the expression of these markers.

Minor comments:

1. Figure 1: Including an immunohistochemistry or immunofluorescence control confirming depletion of S100A4 expressing cells would strengthen the conclusions.

We have now included Figure for Reviewers 5 that corresponds to Figure S7 in the revised manuscript and comment on the results in sections Results (lines 169-171) and Discussion (lines 257-262).

In Results: “Interestingly, S100A4 antibody labeling revealed presence of S100A4+ cells in S100a4-Cre;DTA tissues (Figure S3b, Figure S7a,b).”

In Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle48. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

Figure for Reviewers 5 (Figure S7 in the revised manuscript): S100A4+ cells are found in S100a4-Cre;DTA nipple and mammary tissues. (a) Immunofluorescent labeling for S100A4 and vimentin on FFPE sections of DTA and S100a4-Cre;DTA L1 nipples. (b) Immunofluorescent labeling for S100A4 and smooth muscle actin on FFPE sections of DTA and S100a4-Cre;DTA L1 mammary gland. Scale bar = 100 µm.

Figure 3c: The histological defects more accurately reflect failure of secretory activation rather than "lactation failure" per se. The terminology should be refined to reflect this more precisely.

Thank you for this comment. As explained in the response to your major comment 3, we believe our results show that the secretory activation is conserved in S100a4-Cre;DTA lactating mice. We understand that “lactation failure” might be misleading terminology, as the production of the milk is conserved as well. We therefore change the phrasing into “nursing defect” (line 51, 73, 83), as this could reflect the phenotype most precisely.

**Referee cross-comenting**

I agree with the Reviewer, the authors do not need to do knockout experiments in the revised manuscript. However, it would be great if they could address my comment in the discussion.

Reviewer #3 (Significance (Required)):

This is an important study for mammary developmental biology, addressing the relatively understudied mechanisms that govern nipple development at the stromal-epithelial interface, and the determinants of lactational performance. A major strength is the elegant integration of DTA-mediated cell ablation, advanced imaging, lineage tracing, and transcriptomics to uncover previously uncharacterised roles for S100A4-expressing stromal populations in shaping nipple morphology and function. The work lays a foundation for future studies into nipple biology and pathologies and mechanisms underlying successful lactation.

Although the study is already mature, it could be further strengthened by incorporating more specific genetic models, such as inducible S100A4CreERT or S100A4 gene knockout/knockdown approaches.

Thank you for appreciation of our work.

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

Reviewer #1

Major Comment 1.

It is rather difficult to conclude whether the observed nipple phenotype reflects an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these). The data raise a couple of additional questions: Is there a nipple phenotype at 3 wk of age?...

Unfortunately, we cannot provide data on 3 weeks old mice because we did not collect such samples before and we had to terminate our mouse colony due to an infection in the animal house (mouse line reanimation is possible because we had stored sperm of the mouse line but it would take a lot of time and resources). Nevertheless, we tried to address this comment by providing other relevant available data (see Figure for Reviewers 1).

Reviewer #2

Major Comment 3.

In Fig S1c, d and lines 93-96, the authors investigated the estrus cycles to determine the potential cause of lactation failure. The data was presented as the number of mice in each stage. A more intuitive approach would be to follow the same mice for two to three cycles and observe the duration of each stage.

We agree that the suggested approach would be more accurate in determining truly cycling females. Unfortunately, we cannot perform this experiment currently because we do not have these mice alive anymore. Nevertheless, because the S100a4-Cre;DTA females bore pups, they had cycled and were fertile.

Reviewer #3

Major comment 1.

While the S100A4Cre::DTA model is powerful for evaluating the roles of S100A4 expressing cells, the authors should discuss the potential outcomes of using S100A4 knockout or knockdown approaches. If the authors have such data available, this could help distinguish phenotypes caused by loss of S100A4 function itself from those arising due to ablation of S100A4 expressing cell populations and would add mechanistic depth to the study.

We thank the Reviewer for this insightful suggestion. We agree that genetic approaches targeting S100A4 function (e.g., knockout or knockdown) could, in principle, help disentangle cell-autonomous effects of S100A4 from those resulting from the loss of S100A4-expressing cell populations. However, we would like to clarify that the primary objective of our study is to investigate the functional contribution of S100A4⁺ stromal cells at the population level, rather than to dissect the molecular function of S100A4 protein per se. In this context, the S100A4-Cre;DTA model provides a well-established and appropriate strategy to ablate this cell population and assess its role in tissue development. Importantly, S100A4 is not only a functional protein but also a widely used marker of a heterogeneous stromal cell population. Genetic ablation of S100A4 itself would not eliminate these cells, and may result in relatively subtle or compensable phenotypes due to functional redundancy within the S100 protein family or context-dependent roles of S100A4. Therefore, such approaches would address a distinct biological question and may not directly recapitulate the phenotypes observed upon cell ablation.

References

Eisen, E. J., & Durrant, B. S. (1980). Genetic and Maternal Environmental Factors Influencing Litter Size and Reproductive Efficiency in Mice. Journal of Animal Science, 50(3), 428–441. https://doi.org/10.2527/jas1980.503428x

Ren, Y. A., Monkkonen, T., Lewis, M. T., Bernard, D. J., Christian, H. C., Jorgez, C. J., Moore, J. A., Landua, J. D., Chin, H. M., Chen, W., Singh, S., Kim, I. S., Zhang, X. H. F., Xia, Y., Phillips, K. J., MacKay, H., Waterland, R. A., Cecilia Ljungberg, M., Saha, P. K., … Richards, J. A. S. (2019). S100a4-Cre–mediated deletion of Ptch1 causes hypogonadotropic hypogonadism: Role of pituitary hematopoietic cells in endocrine regulation. JCI Insight, 4(14). https://doi.org/10.1172/jci.insight.126325

Tuwatnawanit, T., Wessman, W., Belisova, D., Sumbalova Koledova, Z., Tucker, A. S., & Anthwal, N. (2025). FSP1/S100A4-Expressing Stem/Progenitor Cells Are Essential for Temporomandibular Joint Growth and Homeostasis. Journal of Dental Research, 104(5), 551–560. https://doi.org/10.1177/00220345251313795

Zhang, R., Gao, Y., Zhao, X., Gao, M., Wu, Y., Han, Y., Qiao, Y., Luo, Z., Yang, L., Chen, J., & Ge, G. (2018). FSP1-positive fibroblasts are adipogenic niche and regulate adipose homeostasis. PLoS Biology, 16(8). https://doi.org/10.1371/journal.pbio.2001493

Author Response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Mancl et al. present a comprehensive integrative study combining cryo-EM, SAXS, enzymatic assays, and molecular dynamics (MD) simulations to characterize conformational dynamics of human insulin-degrading enzyme (IDE). In the revised manuscript, the study now also includes time-resolved cryo-EM and coarse-grained MD simulations, which strengthen the mechanistic model by revealing insulin-induced allostery and β-sheet interactions between IDE and insulin. Together, these results expand the original mechanistic insight and further validate R668 as a key residue governing the open-close transition and substrate-dependent activity modulation of IDE.

Strengths:

The authors have substantially expanded the experimental scope by adding time-resolved cryo-EM data and coarse-grained MD simulations, directly addressing requests for mechanistic depth and temporal insight. The integration of multiple resolution scales (cryo-EM heterogeneity analysis, all-atom and coarse-grained MD simulations, and biochemical validation) now provides a coherent description of the conformational transitions and allosteric regulation of IDE. The addition of Aβ degradation assays strengthens the claim that R668 modulates IDE function in a substrate-specific manner. Finally, the manuscript reads more clearly: figure organization, section headers, and inclusion of a new introductory figure make it accessible to a broader audience. Overall, the revision reinforces the conceptual advance that the dynamic interdomain motions of IDE underlie both its unfoldase and protease activities and identifies structural motifs that could be targeted pharmacologically.

Weaknesses:

While the authors acknowledge that future studies on additional IDE substrates (e.g., amylin and glucagon) are warranted, such experiments remain outside the present scope. Their absence modestly limits the generalization of the R668 mechanism across all IDE substrates. Despite improved discussion of kinetic timescales and enzyme-substrate interactions, experimental correlation between MD timescales and catalysis remains primarily inferential. The moderate local resolution of some cryo-EM states (notably O/pO) continues to limit atomic interpretation of the most flexible regions, though the authors address this carefully.

Reviewer #2 (Public review):

Summary:

The manuscript describes various conformational states and structural dynamics of the Insulin degrading enzyme (IDE), a zinc metalloprotease by nature. Both open and closed state structures of IDE have been previously solved using crystallography and cryo-EM which reveal a dimeric organization of IDE where each monomer is organized into N and C domains. C-domains form the interacting interface in the dimeric protein while the two N-domains are positioned on the outer sides of the core formed by C-domains. It remains elusive how the open state is converted into the closed state but it is generally accepted that it involves large-scale movement of N-domains relative to the C-domains. Authors here have used various complementary experimental techniques such as cryo-EM, SAXS, size-exclusion chromatography and enzymatic assays to characterize the structure and dynamics of IDE protein in the presence of substrate protein insulin whose density is captured in all the structures solved. The experimental structural data from cryo-EM suffered from high degree of intrinsic motion amongst the different domains and consequently, the resultant structures were moderately resolved at 3-4.1 Å resolution. Total five structures were generated in the originally submitted manuscript using cryo-EM. Another cryo-EM reconstruction (sixth) at 5.1Å resolution was mentioned after first revision which was obtained using time-resolved cryo-EM experiments. Authors have extensively used Molecular dynamics simulation to fish out important inter-subunit contacts which involves R668, E381, D309, etc residues. In summary, authors have explored the conformational dynamics of IDE protein using experimental approaches which are complimented and analyzed in atomic details by using MD simulation studies. The studies are meticulously conducted and lay ground for future exploration of protease structure-function relationship.

Comments after first peer-review:

The authors have addressed all my concerns, and have added new data and explanations in terms of time-resolved cryo-EM (Fig. 7) and upside simulations (Fig. 8) which in my opinion have strengthened the merit of the manuscript.

We are grateful for the dedication and constructive feedback provided by the editors and reviewers. We have revised our manuscript according to the suggestions by both reviewers.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The new version of the manuscript reads exceedingly well and the corrections the authors have made during their revision made the manuscript much easier to read and digest than the first version. Below are minor details that may be corrected:

Abstract:

Line 45-47: "IDE is known to transition between a closed state, poised for catalysis, and an open state, able to release cleavage products and bind a new substrate." (consider adding a)

Fixed

Line 48-50: "Combining cryo-EM heterogeneity analysis with all-atom molecular dynamics (MD) simulations, we identified the structural basis and key residues for IDE conformational dynamics that were not previously revealed by IDE static structures." (consider adding previously)

Changed

Line 52-54: "Our small-angle X-ray scattering analysis and enzymatic assays of an R668A mutant indicate a profound alteration of conformational dynamics and catalytic activity." (consider adding analysis)

Changed

Line 54: Consider leaving out "Upside" in the abstract (to avoid confusion when reading the abstract) and leave it to be introduced in the introduction when Upside MD simulations are first mentioned.

Changed

Results:

Figure 5D: There seems to be an error in the legend for Figure 5D. It says "... presence of varying amounts of insulin", but this must be Aβ1-40. Please add info on whether the replicates are technical or biological.

The legend has been revised as suggested.

Line 125: Consider switching the order of "here" and "we"

“here” has been removed.

Line 128: Replace "5" with "five"

Changed

Line 137: Replace "when insulin is present" with "in the presence of insulin"

Changed

Line 228: Replace "5" and "6" with "five " and "six"

Changed

Line 229: Consider adding the word "form": "First, the open subunits did not close to form a singular structure."

We have adjusted the sentence to read “close to a singular consensus structure”

Line 327: Replace "2" with "two"

Changed

Line 276: Consider replacing "Conversely" with a more suitable connecting term as it implies that the observation presented in the two sentences are reverse or rephrase what is being compared. Is it the fact there is a dose dependency or not between the substrates or is it the actual kinetic parameters that are described. I just don't think conversely is fair with the current formulation as "the R668A mutant did not exhibit a dose-dependent response to the presence of Aβ" not that the Ki is reduced for WT compared to the R668A construct when looking at Aβ.

The connecting term has been removed completely, beginning the sentence with “When Abeta…”

Line 359: Replace "6" with "six"

Changed

Consider getting rid of possessive apostrophes to keep a formal tone, e.g. lines 211 (cryoSPARC's), 259 (IDE's) and 382 (IDE's). Exception to this is Alzheimer's disease.

All instances of possessive apostrophes, aside from Alzheimer’s, have been replaced alter more formal wording.

Figure 7 supplement 1: The color scheme for the local resolution is missing the unit (Å).

This has been corrected.

Finally, the supplementary videos illustrating IDE conformational dynamics are difficult to interpret and somewhat redundant in their current form. The transitions occur very rapidly, making it hard to appreciate the described motions, and the uniform coloring of IDE further limits visual clarity. I apologize for not including this point in my initial review. I recommend either removing the videos or re-rendering them to improve interpretability, for example by slowing down the motion and applying the same domain color scheme introduced in the new Figure 1 (and used in the MD trajectory video). This would greatly aid readers in connecting the descriptions in the text to the visual representations in the movies.

Figure 3 videos 1-4 were slowed down, simplified, and recolored to improve clarity.

Reviewer #2 (Recommendations for the authors):

Comments after first revision for authors:

Thanks a ton to the authors for the detailed explanation on my comments. I believe the discussions will help a large group of audience, especially the non-experts. Please address the minor comment below:

Minor comment:

Please update Supplementary file 1 (Cryo-EM data collection, refinement, and validation statistics) regarding the new volume obtained by time-resolved cryo-EM. Kindly also check line 47 in the abstract: "Here, we present five cryo-EM structures" , which may need an update (six structures and resolution 3.0-5.1 Å) or rephrase the sentences accordingly. If similar instances are found in the manuscript, where list of all the structures are mentioned together, please update accordingly if necessary.

The cryo-EM statistics for the time-resolved cryo-EM are shown in supplementary file 2 to differentiated two datasets. The abstract has been changed, as has line 149.

Author Response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Age-related synaptic dysfunction can have detrimental effects on cognitive and locomotor function. Additionally, aging makes the nervous system vulnerable to late-onset neurodegenerative diseases. This manuscript by Marques et al. seeks to profile the cell surface proteomes of glia to uncover signaling pathways that are implicated in age-related neurodegeneration. They compared the glial cell-surface proteomes in the central brain of young (day 5) and old (day 50) flies and identified the most up- and down-regulated proteins during the aging process. 48 genes were selected for analysis in a lifespan screen, and interestingly, most sex-specific phenotypes. Among these, adult-specific pan-glial DIP-β overexpression (OE) significantly increased the lifespan of both males and females and improved their motor control ability. To investigate the effect of DIP-β in the aging brain, Marques et al. performed snRNA-seq on 50-day-old Drosophila brains with or without DIP-β OE in glia. Cortex and ensheathing glia showed the most differentially expressed genes. Computational analysis revealed that glial DIP-β OE increased cell-cell communication, particularly with neurons and fat cells.

Strengths:

(1) State-of-the-art methodology to reveal the cell surface proteomes of glia in young and old flies.

(2) Rigorous analyses to identify differentially expressed proteins.

(3) Examination of up- and down-regulated candidates and identification of glial-expressed mediators that impact fly lifespan.

(4) Intriguing sex-specific glial genes that regulate life span.

(5) Follow-up RNA-seq analysis to examine cellular transcriptomes upon overexpression of an identified candidate (DIP-β).

(6) A compelling dataset for the community that should generate extensive interest and spawn many projects.

Weaknesses:

(1) DIP-β OE using flySAM:

(a) These flies showed a larger increase in lifespan compared to using UAS-DIP-β (Figure 2 C, D). Do the authors think that flySAM is a more efficient way of OE than UAS? Also, the UAS construct would be specific to one DIP-β isoform, while flySAM would likely express all isoforms. Could this also contribute to the phenotypes observed?

We agree with the reviewer that both can contribute to the different lifespan effect. In the original paper presenting flySAM1.0 and flySAM 2.0 (Jia et al., 2018), the authors first tested how flySAM1.0 overexpression (OE) phenotypes compare to several VPR (CRISPRa) and UAS:cDNA OE lines. They found that flySAM1.0 reliably outperforms (i.e., produces stronger OE phenotypes) than VPR in most cases, and produces OE phenotypes that are comparable (i.e., generally equivalent) to UAS:cDNA (Jia et al., 2018). After determining how flySAM1.0 performance compares to VPR and UAS:cDNA, the authors next tested if flySAM2.0 also outperforms VPR; they found that like flySAM1.0, flySAM2.0 outperforms VPR in most cases (Jia et al., 2018). In general, the data suggest that we should expect comparable overexpression phenotypes for our flySAM2.0 and UAS:cDNA lines.

We chose to proceed with the DIP-β flySAM line for the climbing assays and snRNA-seq, as it gave a stronger lifespan effect and we thought it was likely to be the more robust OE line. While our glial cell-surface proteomics initially identified DIP-β isoform C as the candidate, it is possible that other DIP-β isoforms were also present (such as isoform F, which is identical in polypeptide sequence to isoform C) (FlyBase). Ultimately, we believe that the larger increases in lifespan observed for DIP-β flySAM are likely because flySAM targets all isoforms, whereas UAS:cDNA lines target only one isoform. Importantly, our UAS- DIP-β line was specific to DIP-β isoform C, which is the same isoform that was identified by our proteomics.

We have made clarifications in the manuscript to address these comments.

(b) The Glial-GS>DIP-β flySAM flies without RU-486 have significantly shorter lifespans (Figure 2C) than their UAS-DIP-β counterparts. flySAM is lethal when expressed under the control of tubulin-GAL4 (Jia et al. 2018), likely due to the toxicity of such high levels of overexpression. Is it possible that a larger increase in lifespan is due to the already reduced viability of these flies?

This is a good point. The flySAM lines do exhibit a shorter baseline lifespan compared to the traditional UAS lines. This is likely due to the specific genetic background of the flySAM transgenic insertions, or a low level of "leaky" expression, as previously noted in the literature (Jia et al., 2018).

However, we believe that the lifespan extensions we observed for DIP-β flySAM is a robust biological effect, rather than an artifact of reduced viability for the following reasons. First, by utilizing the GeneSwitch (GS) system, we can compare the lifespan of flies with the exact same genetic background (+/- RU-486). This ensures that the extension we report is specifically due to the induction of the transgene, rather than a comparison between disparate lines with different basal fitness levels. Second, if the lifespan extensions merely represented a recovery from lower baseline viability, we would expect to see similar improvements across other flySAM lines in our screen. However, DIP-β was the only candidate across our screen that significantly increased lifespan in both sexes (Extended Data Figs. 7 & 8). Third, the lifespan-extending effect of DIP-β was independently confirmed using a traditional UAS-cDNA line, which importantly does not share the same baseline viability issues as the flySAM lines.

(c) Statistics: It is stated in the Methods that "statistical methods used are described in the figure legend of each relevant panel." However, there is no description of the statistics or sample sizes used in Figure 2.

We have updated the figure legends for Figure 2 to include the missing statistical details and sample sizes.

Specifically, for Fig. 2A: The reviewer is correct that with only two replicates of each time point (5d vs. 50d) in the initial proteomic screen, traditional p-value calculations lack the necessary power for meaningful interpretation. We have revised the legend to clarify that this panel represents a discovery-based screen. Candidates were selected based on biological relevance and specific enrichment thresholds to narrow the 872 proteins down to the 48 top candidates for screening (we were initially aiming to identify approximately 50 candidate genes for screening). For Fig. 2B: We have updated the legend to detail the parameters used for the Gene Ontology (GO) enrichment analysis.

(2) Figure 3: The authors use a glial GeneSwitch (GS) to knock down and overexpress candidate genes. In Figure 3A, they look at glial-GS>UAS-GFP with and without RU. Without RU, there is no GFP expression, as expected. With RU, there is GFP expression. It is expected that all cell body GFP signal should colocalize with a glial nuclear marker (Repo). However, there is some signal that does not appear to be glia. Also, many glia do not express GFP, suggesting the glial GS driver does not label all glia. This could impact which glia are being targeted in several experiments.

We thank the reviewer for this careful observation regarding the expression pattern of the GSG3285-1 line and acknowledge that the overlap between this driver and the Repo-positive cells is not absolute.

Our selection of this specific GeneSwitch line was based on several critical experimental considerations: 1) To minimize background toxicity. We initially tested multiple Repo-GeneSwitch lines; however, we found they exhibited significant, genotype-dependent lifespan reductions upon RU486 administration, even in control crosses. This baseline toxicity confounded the interpretation of any potential lifespan effects. GSG3285-1 was chosen for this study, as it provided a robust control baseline and didn’t show lifespan effects with RU486 treatment in multiple control lines. This is essential for lifespan studies. 2) The driver breadth and specificity. As noted in its original characterization (Nicholson et al., 2008) and a later study (Catterson et al. 2023), GSG3285-1 is characterized as a pan-glial driver, though it may include a small population of sensory neurons. Furthermore, while Repo is a standard glial marker, its antibody does not label all glial subtypes with equal intensity. The "non-overlapping" signal observed in Figure 3A may reflect this staining bias. 3) The expression mosaicism. The fact that some glial cells do not show GFP expression suggests a degree of mosaicism, which is common to many GeneSwitch lines (Osterwalder et al., 2001). While we acknowledge this means our manipulations may target a broader subset — rather than every single glial cell — the fact that we still observed significant lifespan effects across two independent platforms (UAS and CRISPRa) suggests that the targeted population is sufficient to mediate these systemic effects.

We have added a clarifying statement to contextualize the choice of the GSG3285-1 driver and its relationship to the Repo population.

(3) It is interesting that sex-specific lifespan effects were observed in the candidate screen.

(a) The authors should provide a discussion about these sex-specific differences and their thoughts about why these were observed.

We agree that the sex-specific effects observed in our lifespan screen are one interesting aspect of this study. We have added a dedicated section to the Discussion exploring these differences from both a technical and biological perspective.

On the technical side, the GeneSwitch inducer, RU486, can have sex-specific effects on metabolism and lifespan, depending on the nutritional environment (Dos Santos & Cocheme, 2024). Specifically, RU486 has been shown to counteract the lifespan-shortening effects of mating in females, an effect that is less pronounced in males (Landis et al., 2015; Tower et al., 2017). While we optimized our media and used the GSG3285-1 line to minimize these baseline effects, it remains possible that certain genotypes exhibited a sex-specific sensitivity to the inducer itself. Beyond the technical considerations, sex differences in aging are well-documented in Drosophila and other organisms (Regan et al., 2016; Austad & Fischer, 2016). Male and female flies exhibit distinct transcriptional trajectories and metabolic shifts as they age. Furthermore, recent studies have highlighted that glial function and the neuroinflammatory landscape can differ significantly between sexes, which may dictate how a specific genetic manipulation impacts the aging process in a sex-dependent manner (PMID: 40951920). While our screen identifies DIP-β as a rare candidate that extends lifespan in both sexes, the prevalence of female-specific hits in our data suggests that the female "aging program" may be more plastic or responsive to the specific glial pathways we targeted. These observations provide a valuable foundation for future studies into the mechanisms of sex-specific neuroprotection.

(b) The authors should also provide information regarding the sex of the flies used in the glial cell surface proteome study.

It is a mixture of half male and half female flies. This information has been added to the main text, Fig. 1, and to the methods section.

(c) Also, beyond the scope of this study, examining sex-specific glial proteomes could reveal additional insights into age-related pathways affecting males and females differentially.

Agreed, this would be a great idea for future studies.

(4) The behavioral assay used in this study (climbing) tests locomotion driven by motor neurons. The proteomic analysis was performed with the adult brain, which does not include the nerve cord, where motor neurons reside. While likely beyond the scope of this study, it would be informative to test other behaviors, including learning, circadian rhythms, etc.

We thank the reviewer for this insightful point. While our initial proteomic screen focused on the adult central brain, our behavioral validation used a pan-glial driver, which targets glia throughout the entire nervous system, including the ventral nerve cord (VNC). We have addressed the reviewer's comment as below:

Additional behavioral data: As suggested, we performed Drosophila Activity Monitoring (DAM) assays to evaluate circadian locomotor rhythms in 50-day-old DIP-β overexpression flies compared to negative controls. Interestingly, we did not detect significant changes in circadian activity at this time point.

The difference between our climbing and circadian results highlights the complexity of age-related decline. In Drosophila, locomotor performance (i.e., climbing) and circadian coordination often decouple. For example, specific isoforms of human Tau (hTau) can induce severe cognitive and neurodegenerative deficits without affecting lifespan or motor coordination in the same manner (Sealey et al., 2017). Furthermore, motor-specific defects can emerge independently of systemic lifespan changes, as seen in certain SOD1 models of ALS (Hirth, 2010). It is possible that the 50-day timepoint represents a specific window where motor coordination is improved by DIP-β, while circadian circuits — governed by distinct glial-neuronal interactions — remain largely unaffected, or require a different temporal window for observation.

We agree that identifying the specific glial populations (central brain vs VNC) responsible for the improved climbing would be highly informative. While the current study establishes the pro-longevity effect of DIP-β, future work utilizing in-situ proteomics on the fully intact CNS (including the VNC) or specific VNC will be essential to map the stereotyped progression of these effects across the peripheral and central nervous systems.

(5) It is surprising that overexpressing a CAM in glia has such a broad impact on the transcriptomes of so many different cell types. Could this be due to DIP-β OE maintaining the brain in a "younger" state and indirectly influencing the transcriptomes? Instead of DIP-β OE in glia directly influencing cell-cell interactions? Can the authors comment on this?

We agree that the observed changes likely represent a combination of direct cell-cell interactions and a broader, more indirect maintenance of a "younger" physiological state.

Direct: Among the DIP family, DIP-β exhibits some of the strongest and most promiscuous binding affinities, interacting with a wide array of partners including Dpr6, 8, 9, 15, and 21 (Cosmanescu et al., 2018; Sergeeva et al., 2020). This biochemical flexibility allows DIP-β to potentially interface with a much broader range of neuronal subtypes than other DIP family members, such as DIP-δ, which exclusively binds Dpr12 and did not extend lifespan in our screen. It is possible that by overexpressing DIP-β, we may be partially compensating for the global downregulation of CAMs that typically occurs during aging, thereby preserving essential glial-neuronal communication integrity.

Indirect: By maintaining these primary glial functions and communication activities, DIP-β overexpression likely delays the overall "aging" of the brain. This preservation of neural health can have downstream effects on systemic physiology, such as the improved glia-fat body communication we observed in 50-day-old flies. In this model, the broad transcriptomic shifts are not necessarily all direct targets of DIP-β, but rather a signature of a brain that has successfully avoided the catastrophic breakdown of homeostasis typically seen in aged wild-type flies.

We have expanded the Discussion to clarify this distinction, adding that DIP-β likely acts as a "scaffold" or “bridge” for maintaining a younger brain state, which in turn preserves multi-organ communication.

Reviewer #2 (Public review):

This manuscript presents an ambitious and technically innovative study that combines in situ cell-surface proteomics, functional genetic screening, and single-nucleus RNA sequencing to uncover glial factors that influence aging in Drosophila. The authors identify DIP-β as a glial protein whose overexpression extends lifespan and report intriguing sex-specific differences in lifespan outcomes. Overall, the study is conceptually compelling and offers a valuable dataset that will be of considerable interest to researchers studying glia-neuron communication, aging biology, and proteomic profiling in vivo.

The in-situ proteomic labeling approach represents a notable methodological advance. If validated more extensively, it has the potential to become a widely used resource for probing glial aging mechanisms. The use of an inducible glial GeneSwitch driver is another strength, enabling the authors to carefully separate aging-relevant effects from developmental confounds. These technical choices meaningfully elevate the rigor of the study and support its central conclusions. The discovery of new candidate genes from the proteomics pipeline, including DIP-β, is intriguing and opens new avenues for understanding glial contributions to organismal lifespan. The observation of sex-specific lifespan effects is particularly interesting and warrants further exploration; the study sets the stage for future work in this direction.

At the same time, several areas would benefit from clarification or additional analysis to fully support the manuscript's claims:

(1) The manuscript frequently refers to "improved" or "increased" cell-cell communication following DIP-β overexpression, but the meaning of this term remains somewhat vague. Because the current analysis relies largely on transcriptomic predictions, it would be helpful to define precisely what metric is being used, e.g., increased numbers of predicted ligand-receptor interactions, enrichment of specific signaling pathways, or altered expression of communication-related components. Strengthening the mechanistic link between DIP-β, cell-cell communication, and lifespan extension, potentially through targeted validation of specific glial interactions, would substantially reinforce the interpretation.

We agree that a more precise description of “improved” or “increased” cell-cell communication is necessary.

Our conclusion that DIP-β overexpression is associated with “increased” cell-cell communication is based on the quantification of our CCC scores, which was performed using FlyPhoneDB2, a computational tool used to estimate cell-cell signaling from single-cell RNA-sequencing data (Liu et al., 2021; Qadiri et al., 2025). To infer cell-cell signaling, FlyPhoneDB2 and its predecessor, FlyPhoneDB, calculate “interaction scores,” comparing the expression levels of a curated list of ligand-receptor pairs between cell types (Liu et al., 2021; Qadiri et al., 2025). For example, if we detect a ligand in cell type A and its receptor in cell type B in DIP-β overexpression flies but didn’t detect both ligand and receptor in control flies, the CCC score is increased by 1. FlyPhoneDB2 additionally enables users to estimate signaling activity by also taking into consideration the expression of downstream reporter genes (Qadiri et al., 2025).

“Improved cell-cell communication” is our interpretation based on the CCC analysis. It is important to note that the metric being used here (increased CCCs) is the number of predicted ligand-receptor interactions, and that our CCC analysis was based entirely on inferences from snRNA-seq data. We have added further clarification to our manuscript, which now further expands on the results of our CCC analysis (i.e., the increased expression for 61% and decreased expression for 39% of ligand-receptor pairs we observed in our DIP-β overexpression group, compared to our negative control), which ultimately led us to conclude that DIP-β overexpression is associated with improved cell-cell communication.

(2) The lifespan screen is central to the paper, and clearer visualization and contextualization of these results would significantly improve the manuscript's impact. For example, Figure 3D is challenging to interpret in its current form. More explicit presentation of which manipulations extend lifespan in each sex, along with effect sizes and significance values, would provide clarity. Including positive controls for lifespan extension would also help contextualize the magnitude of the observed effects. The reported effects of DIP-β, while promising, are modest relative to baseline effects of RU feeding, and a discussion of this would help appropriately calibrate the conclusions.

We appreciate the reviewer’s suggestion to improve the clarity of the lifespan screen results. We have significantly revised Figures 3D, 3E, and 3F to provide a more intuitive summary of the candidate gene manipulations. Figures 3D and 3E now explicitly include the effect sizes and p-values for each candidate gene, broken down by sex. We also added a new Figure 3G with a visual layout that has been streamlined to allow for quick identification of manipulations that successfully extended lifespan.

The reviewer raises an important point regarding the use of positive controls to calibrate the magnitude of lifespan extension. We carefully considered adding a standard control (such as Rapamycin treatment); however, we opted against it for several methodological reasons:

As noted in the literature, the magnitude of lifespan extension from standard controls can vary drastically depending on genetic background and lab environment. For instance, Rapamycin-induced extension ranges from ~10% (Schinaman et al., 2019), to over 80% (Landis et al., 2024). We felt that adding a single positive control might provide a false sense of "calibration" rather than a true universal benchmark.

To ensure the robustness of our findings, we instead employed a dual-validation strategy. We confirmed the lifespan-extending effects of our candidates using both traditional UAS:cDNA and CRISPR-based overexpression. The fact that two independent genetic systems yielded consistent results provides strong internal evidence for the reported effects.

We acknowledge that the effects of DIP-β are modest when compared to the baseline impact of RU486 feeding. We have added a section to the Discussion addressing this. While the effects are subtle, their reproducibility across different overexpression platforms suggests they are biologically relevant, even if they do not reach the dramatic shifts seen in some caloric restriction or drug-based models.

We have further addressed this in the results section.

(3) Several figures would benefit from improved labeling or more detailed legends. For instance, the meaning of "N" and "C" in Figure 1D is unclear; Figure 3A should clarify that Repo is a glial marker; and Figure 5C appears to have truncated labels. Reordering certain panels (e.g., moving control data in Figure 4A-B) may also improve narrative flow. These refinements would greatly aid reader comprehension.

We have modified and improved the labeling of these figures to increase the clarity. For Fig. 1D, we added the explanation to the Figure legends. In brief, in the Tandem Mass Tag (TMT) isobaric labeling system, 128N is one of many channels (126, 127N, 127C, 128N, 128C, etc.) used to index and compare up to 18 samples simultaneously, improving throughput and reducing missing values.

Fig. 3A has been updated to clarify that Repo is the glial marker. Fig. 4A-D have been reordered so that the DIP- β lifespan results are presented before the control lifespan, which hopefully improves the narrative flow of this figure. The Fig. 4 references in the manuscript have also been updated to match these changes. Additionally, Fig. 5C has been updated to include the truncated x-axis and y-axis labels.

(4) A few claims would be strengthened by more specific references or acknowledgment of alternative interpretations. Examples include the phenoxy-radical labeling radius, the impact of H₂O₂ exposure, and the specificity of neutravidin. Additionally, downregulation of synapse-related GO terms may reflect age-related transcriptional changes rather than impaired glia-neuron communication per se, and this possibility should be recognized. The term "unbiased" to describe the screen may also be reconsidered, given the preselection of candidate genes.

These are good suggestions. We have added references for the phenoxy-radical labeling radius (Durojaye, 2021), the impact of H₂O₂ exposure (J. Li et al., 2021), and the binding specificity of neutravidin (J. Li et al., 2021). We have also removed the term “unbiased” from our manuscript.

Regarding the request to further address the downregulation of synapse-related GO terms, we believe this indicates a lack of clarity on our part. We did not intend to suggest that our GO analyses, which were based on our proteomics data, were necessarily indicative of impaired neuron-glia communication. Our conclusions regarding altered neuron-glia communication have come from our later snRNA-seq data and analyses. Inspired by this comment, we agree that our differential gene analysis may reflect transcriptional changes rather than impaired glia-neuron communication. We have added such alternative interpretation.

(5) Clarifying the rationale for focusing on central brain glia over optic-lobe glia would be useful. 

Agreed! As the intended focus of this study was the more general changes occurring during normal brain aging, we chose to focus on the central brain for our glial cell-surface proteomics, which is responsible for most of the brain’s higher order functions, including learning and memory, signal integration, behavior, etc. As the optic lobes account for approximately half of all neurons in the adult Drosophila brain and are specialized to process visual stimuli (Robinson et al., 2025), we were concerned that including the optic lobes in our glial cell-surface proteomics could strongly bias our findings towards age-related changes in visual function, rather than the more general changes we intended to focus on. Such clarification has been added to the results section (Quantitative comparison of young and old proteomes).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Line 62: Can the authors expand on "several changes"?

We have added a sentence expanding upon this in the manuscript draft.

(2) Line 137: Can the authors provide a reference for the phenoxyl radical half-life?

Thanks for catching this. We’ve added our reference for the phenoxyl radical half-life.

(3) Figure 1B: The authors state that neutravidin stained glia; however, there is no glial marker (e.g., anti-Repo) in this panel.

We acknowledge the reviewer’s point. The lack of anti-Repo staining in Figure 1B is due to the requirements of the Neutravidin-Alexa 647 detection method. Because this procedure bypasses traditional primary and secondary antibody incubation to preserve the biotin signal, co-staining with Repo was not technically feasible. Nevertheless, we utilized the Repo-GAL4 driver to express UAS-CD2-HRP; since this driver is well-documented and specific to glial cells, the Neutravidin signal serves as a functional readout of the targeted glial population.

(4) Line 254: There is no Figure 2D.

We’ve corrected this to Fig. 2C.

(5) Lines 390-396: No reference to the respective figures.

We’ve made a couple corrections to reference all the respective figures.

(6) Figure 5C: The X-axis is cut off.

This has been corrected.

Reviewer #2 (Recommendations for the authors):

Minor inconsistencies (e.g., figure references-line 254 references "Figure 2D" where none exists) should be corrected.

We’ve corrected this to Fig. 2C.

Author Response:

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

Reviewer #1 (Public review):

Genetically encoded fluorescent proteins expressed in specific cell types allow recognising them in vivo and, if the protein is a functional indicator, as in the case of genetically encoded calcium indicators (GECIs), to record activity from the same cellular ensemble. Ideally, if proteins (fluorophores) have perfectly distinct spectral properties, signals can be distinguished from as many cell types as the number of employed fluorophores. In practice, fluorescent proteins have non-negligible crosstalk both in absorption and emission bands. In addition, fluorescence contribution of each fluorophore normally varies from cell to cell and therefore spectral properties of cells expressing two or more proteins are different. The work of Phillips et al. addresses this challenge. The authors present an approach defined as "Neuroplex", allowing identification of up to nine cell types from the same number of fluorophores. The fingerprint of each cell is then associated with functional fluorescence from the GECI GCaMP, allowing recording calcium activity from that specific cell. The method is implemented in vivo using head-mounted miniscopes.

The authors used a mouse line expressing GCaMP in cortical pyramidal neurons and developed an experimental pipeline. First, they injected the nine AAV viruses, causing expression of fluorophores in a different brain area. The idea was not to image that area, but a non-infected medial prefrontal cortex (mPFC) section where neurons could be infected by their axons projecting in an injected area, in this way being identified by their targeting region(s). A GRIN lens, allowing spectral analysis, was mounted in the mPFC section, and GCaMP fluorescence was then recorded during behavioural tasks and analysed to identify regions of interest (ROIs) corresponding to neuron somata. After functional imaging, the head of the mouse was fixed, spectral analysis was performed, and after necessary correction for chromatic distortions, the fluorophore contribution was determined for each ROI (neuron) from where GCaMP signals were detected. Notably, the procedures for estimation and correction of chromatic aberration and light transmission (described in Figure 2) were a major challenge in their technical achievements. The selection of the nine fluorophores was another big effort. This was done by combining computer simulations and direct measurement of spectra from individual proteins expressed in HEK293 cells. It is important to say that the authors could simulate arbitrary combinations of two or more different fluorophores and evaluate the ability of their algorithm to detect the correct proteins against wrong estimations of false-negative (absence of an expressed protein) or false-positive (presence of a non-expressed protein). Not surprisingly, this ability decreases with the level of GCaMP expression. The authors underline that most errors were false-negatives, which have a milder impact in terms of result interpretation, but the rate of false positives was, nevertheless, relevant in detecting a second fluorophore from a cell expressing only one protein. The experimental profiles of fluorophores were dependent both on the specific fluorescent protein and on the projecting area, and the distribution of double-labelled did not match anatomical evidence. This result should be taken as the limitation of the present pioneering experiments, presented as proof-of-principle of the approach, but Neuroplex may provide far improved precision under different experimental conditions.

In my view, the work of Phillips et al. represents a significant advance in the state-of-the-art of the field. The rigorous analysis of limitations in the use of Neuroplex must be considered an important guideline for future uses of this approach.

We appreciate the reviewer’s positive evaluation and thoughtful comments.

Reviewer #2 (Public review):

Summary:

The manuscript introduces Neuroplex, a pipeline that integrates miniscope Ca²⁺ imaging in freely moving mice with multiplexed confocal and spectral imaging to infer projection identities of recorded neurons. This technical approach is promising and could broaden access to projection-resolved population imaging. However, the core quantitative analyses apply a winner-take-all single-label assignment per neuron even when multiple fluorophores exceed threshold, with additional labels treated descriptively as "secondary hits." While the authors acknowledge and simulate dual labeling, the extent to which this single-label decision rule affects subtype fractions and behavioural comparisons remains uncertain without a multi-label (or probabilistic) sensitivity analysis and propagation of classification uncertainty.

We thank Reviewer #2 for the careful statistical perspective and focus on assignment strategy and uncertainty. Importantly, we emphasize that Neuroplex is presented as a methodological proof-of-principle, not as a definitive quantification of projection convergence.

Strengths:

(1) Conceptual advance and practicality: Decoupling acquisition from identity readout constitutes an innovative approach that is, in principle, applicable in laboratories currently using single-color miniscopes.

(2) Engineering thoroughness: The manuscript offers detailed consideration of GRIN optics, spectral libraries, registration procedures, and simulations that address signal-to-noise ratio, background, and class imbalances.

(3) Immediate community value: If demonstrated to be robust, the pipeline could enable projection-resolved analyses without reliance on specialized multicolor miniscopes.

Weaknesses:

(1) Single-label assignment in the main analyses: When multiple fluorophores exceed threshold for a neuron/ROI, the workflow applies a winner-take-all rule and assigns a single label (the fluorophore with the largest standardized beta), while additional above-threshold fluorophores are retained only as "secondary hits." This is a reasonable specificity-first choice, but because cortical excitatory neurons can collateralize, collapsing dual-threshold ROIs to one identity may under-represent dual-projecting cells and could bias estimated subtype fractions and behavioural comparisons.

We thank the reviewer for raising this important conceptual point.

We agree that cortical excitatory neurons frequently collateralize and therefore may legitimately express more than one retrograde fluorophore. Our use of a winner-take-all (WTA) rule in the primary analyses was an intentionally conservative methodological choice designed to prioritize specificity over sensitivity in this proof-of-principle study.

As demonstrated in our simulations (Supp. Fig. 5–6), under realistic background and noise conditions, secondary assignments are more susceptible to false-positive errors than primary assignments. For this reason, we chose to assign a single primary identity for quantitative behavioral stratification while retaining additional above-threshold fluorophores as “secondary hits” and reporting their distribution separately (Supp. Fig. 7).

We did not intend to imply that projections are exclusive. Rather, the WTA strategy provides a conservative lower-bound estimate of subtype proportions and avoids inflation of dual-label rates under conditions where spectral separability is imperfect.

We agree that this rationale should be stated more explicitly in the manuscript, and that the potential impact of assignment strategy on subtype fractions and behavioral comparisons should be acknowledged clearly as a methodological trade-off rather than a biological claim.

Importantly, the biological analyses presented in this manuscript are illustrative demonstrations of functional stratification capability and do not depend on exclusivity of projection identity. We have revised the manuscript to clarify this framing as follows:

“If multiple fluorophores exceeded the threshold for an ROI, the fluorophore with the largest z-scored beta value was assigned as the primary identity (winner-take-all rule). This conservative approach was chosen to prioritize specificity under realistic noise and background conditions. Additional above-threshold fluorophores were retained as ‘secondary hits’ but were not incorporated into primary subtype stratification analyses.” (Methods, Single Pass Algorithm)

“For quantitative behavioral comparisons, each ROI was assigned a single primary fluorophore identity using a winner-take-all rule. We emphasize that this assignment strategy does not imply projection exclusivity. Rather, it provides a conservative lower-bound estimate of subtype proportions, as ROIs exceeding threshold for multiple fluorophores were classified according to their strongest spectral contribution.” (Result, Fluorophore distribution in behaviorally relevant ROIs)

“These analyses were performed using conservative single-label assignments; dual-threshold ROIs were not treated as co-identities in order to avoid overinterpretation of potentially ambiguous multi-label cells. Because identity assignment prioritizes specificity and classification uncertainty was not formally propagated into downstream comparisons, subtype fractions and behavior-by-subtype differences should be interpreted as qualitative demonstrations of projection-resolved functional stratification rather than precise anatomical quantifications. ” (Results, Neuronal Cell Type and Behavior)

“Cortical pyramidal neurons frequently collateralize to multiple downstream targets, and accordingly some ROIs exceeded threshold for more than one fluorophore. In this proof-of-principle implementation, we adopted a specificity-first winner-take-all assignment rule for primary analyses to minimize false-positive multi-label calls under realistic noise conditions. This strategy likely underestimates the true prevalence of dual-projecting neurons and should therefore be interpreted as a conservative stratification approach rather than a statement of projection exclusivity.” (Discussion)

(2) Dual-label detection is acknowledged but remains descriptive in vivo: the manuscript explicitly discusses the possibility of dual projection, evaluates dual-fluorophore detection in simulations (including performance under realistic noise/background), and reports in vivo rates of secondary hits. However, these dual-threshold events are not incorporated as co-identities in the main statistical analyses, making it difficult to judge how robust the principal biological conclusions are to the single-label decision rule.

We thank the reviewer for this important clarification request.

We agree that dual-projection neurons are biologically plausible and that dual-threshold ROIs were detected in vivo. In this manuscript, however, our primary goal was to establish the feasibility of high-dimensional spectral assignment and projection-resolved stratification, rather than to provide a definitive quantification of projection convergence.

For this proof-of-principle study, we chose a conservative winner-take-all (WTA) framework for primary behavioral analyses in order to minimize false-positive multi-label assignments under realistic noise and background conditions, as demonstrated in our simulations (Supp. Fig. 5–6). Secondary hits were retained and reported descriptively (Supp. Fig. 7), but not incorporated into the primary statistical comparisons to avoid overinterpretation of potentially ambiguous dual-label calls.

Importantly, the principal biological conclusions presented in the manuscript are qualitative demonstrations that projection-defined stratification is feasible within a single animal. These conclusions do not rely on projection exclusivity or on precise quantification of dual-projecting fractions.

We agree that this distinction should be made clearer in the manuscript, and we have revised the text as follows:

“Although dual-threshold ROIs were detected in vivo, these secondary assignments were not incorporated as co-identities in the primary behavioral analyses. This decision reflects a conservative specificity-first framework designed to minimize false-positive multi-label calls under realistic noise conditions. Accordingly, dual-label rates reported here should be interpreted descriptively. The present study focuses on demonstrating the feasibility of projection-resolved stratification, rather than providing definitive quantification of projection convergence.” (Results, Fluorophore distribution in behaviorally relevant ROIs)

“We then stratified these neurons by projection target and examined behaviorally selective activity across cell types. These analyses were performed using conservative single-label assignments; dual-threshold ROIs were not treated as co-identities in order to avoid overinterpretation of potentially ambiguous multi-label cells. Because identity assignment prioritizes specificity and classification uncertainty was not formally propagated into downstream comparisons, subtype fractions and behavior-by-subtype differences should be interpreted as qualitative demonstrations of projection-resolved functional stratification rather than precise anatomical quantifications.” (Results, Behavioral Analysis)

(3) Uncertainty is not propagated: False-positive/false-negative rates from simulations and uncertainty from registration/segmentation are not carried forward into quantitative confidence bounds on subtype proportions or behaviour-by-subtype effects.

We agree that formal propagation of classification and registration uncertainty into subtype proportions and behavioral comparisons would be appropriate in a study primarily focused on precise anatomical quantification. However, the central goal of the present manuscript is methodological and to demonstrate that high-dimensional spectral identity can be reliably linked to miniscope-recorded functional activity within a single animal.

We have shown that simulations under realistic noise, background, and class imbalance conditions (Supp. Fig 5-6) show that errors are predominantly false negatives rather than false positives. However, behavioral analyses are presented as qualitative demonstrations of the feasibility of projection-resolved stratification rather than as definitive quantitative anatomical measurements.

In the revised manuscript, we clarified that 1) subtype proportions and behavioral effects are assignment-dependent estimates, 2) simulation-derived error rates provide guidance for experimental design rather than formal confidence intervals, and 3) future studies centered on precise quantification of projection fractions would benefit from formal uncertainty modeling, as follows:

“These simulation-derived accuracy estimates characterize expected performance under defined noise and background conditions but were not formally propagated into confidence bounds on subtype proportions or behavioral comparisons. In this proof-of-principle study, subtype fractions are presented as assignment-dependent estimates rather than definitive anatomical measurements.” (Results, Assessment of spectral unmixing approach)

“Because classification uncertainty was not formally propagated into these analyses, behavior-by-subtype comparisons should be interpreted as qualitative demonstrations of functional stratification rather than precise quantitative estimates.” (Results, Neuronal cell types and behavior)

“The modeling framework was designed to characterize expected classification behavior across a range of experimental regimes, including background fluorescence, class imbalance, and reduced signal-to-noise ratio. These simulations provide practical performance guidance but were not used to compute formal error bars or propagate uncertainty into downstream biological analyses.” (Methods, Modeling of experimental variables to assess accuracy of algorithms)

“Because the present study is designed to establish methodological feasibility rather than precise anatomical quantification, simulation-derived false-positive and false-negative regimes were not formally propagated into confidence bounds on subtype proportions or behavioral effect sizes. Accordingly, subtype fractions should be interpreted as assignment-dependent estimates rather than definitive anatomical measurements. Future implementations could incorporate Bayesian or likelihood-based classifiers to generate posterior identity probabilities and enable formal uncertainty propagation when quantitative estimation of projection convergence is central to the biological question.” (Discussion)

Reviewer #3 (Public review):

This manuscript presents Neuroplex, a technically rigorous and carefully validated pipeline that links miniscope calcium imaging in freely behaving animals with high-dimensional fluorophore-based cell-type identification using in vivo multiplexed spectral confocal imaging through the same implanted GRIN lens. The work overcomes a major practical limitation of head-mounted microscopy by enabling the identification of up to nine projection-defined neuronal populations within the same animal, without post-fixation histology. The approach is well motivated and supported by extensive calibration and simulation. While the biological results are primarily illustrative, the methodological contribution is clear and likely to be broadly useful.

Major comments

(1) The approach relies on the assumption that fluorophore identity assigned during anesthetized confocal imaging accurately reflects the identity of neurons recorded during prior behavioural sessions. While the use of the same GRIN lens and in vivo co-registration mitigates many concerns, the manuscript would benefit from a more explicit discussion, or empirical demonstration, if available, of the stability of fluorophore assignments across time. Even limited repeat spectral imaging in a subset of animals would strengthen confidence in longitudinal applicability.

We thank the reviewer for highlighting this important conceptual assumption.

Fluorophore identity in Neuroplex is genetically encoded via AAVretro delivery and therefore does not depend on transient physiological state. Spectral imaging is performed in vivo through the same GRIN lens and field of view used during behavioral imaging, and co-registration relies on anatomical landmarks. While repeat spectral imaging was not formally performed as a longitudinal experiment, the underlying fluorescent protein expression is stable over weeks, and there is no biological mechanism in this paradigm that would alter fluorophore identity across sessions.

We revised the manuscript to explicitly state this assumption and clarify why identity stability is expected as follows:

“…fluorophore signals and reduce unmixing fidelity, leading to an increased false positive rate. Fluorophore identity in this framework is genetically encoded via retrograde AAV delivery and is therefore expected to remain stable across behavioral and spectral imaging sessions. Because both functional and spectral data are acquired in vivo through the same GRIN lens and co-registered using anatomical landmarks, assignment stability is not expected to vary across time unless expression levels change substantially. While repeat spectral imaging was not performed as a formal longitudinal experiment in this study, the stability of fluorescent protein expression supports the assumption that fluorophore identity reflects a persistent cellular attribute.” (Discussion)

(2) Fluorophore identity is determined using thresholding of linear unmixing coefficients relative to an empirically defined baseline, followed by a second adaptive pass for over-represented fluorophores. While this heuristic is extensively validated via simulations, it remains ad hoc from a statistical perspective. The authors should more explicitly justify this choice and discuss its limitations relative to probabilistic or likelihood-based classifiers, particularly with respect to uncertainty estimation at the single-ROI level.

We agree that the dual-pass thresholding approach is heuristic rather than fully probabilistic. More formal probabilistic classifiers are possible but would introduce additional modeling assumptions and training requirements beyond the scope of this proof-of-principle study.

We revised our manuscript to clarify this as follows:

“The current classification framework relies on linear unmixing followed by empirically defined thresholding rather than full probabilistic inference. This approach provides transparency and practical robustness under realistic noise and background conditions but does not generate single-ROI posterior uncertainty estimates. ” (Discussion)

(3) Identifiability of fluorophores is demonstrated empirically, but the manuscript does not explicitly quantify spectral separability (e.g., similarity metrics between basis spectra or conditioning of the unmixing matrix). A brief analysis of spectral independence or sensitivity of beta estimates to noise would provide mathematical reassurance, especially given the reliance on linear regression in a high-dimensional feature space.

We agree that spectral separability is conceptually important. In this manuscript, separability is demonstrated empirically through 1) In vitro fingerprint acquisition under identical optical conditions, 2) simulation under background and noise, and 3) successful in vivo classification across regimes. We did not compute formal matrix conditioning metrics, but we agree that the separability rationale should be described more explicitly. We revised our manuscript as:

“While formal conditioning metrics were not explicitly computed empirical fingerprint acquisition and simulation-based perturbation analyses demonstrate sufficient spectral independence for reliable linear unmixing under the tested regimes.” (Discussion)

(4) The spectral unmixing treats CNMF-derived ROIs as fixed supports. I wonder whether ROI boundaries, neuropil contamination, and partial overlap can introduce structured uncertainty that could bias spectral estimates. If so, the authors should acknowledge this dependency more explicitly and discuss how ROI quality or overlap might influence false negatives or false positives, particularly in densely labelled regions.

We agree that ROI definition influences spectral extraction. Spectral fingerprints are derived by averaging all pixels within the ROI mask, and therefore neuropil contamination, partial ROI overlap, and dense labeling could influence beta estimates. In the revised manuscript, we have acknowledged this dependencies more explicitly.

“Spectral unmixing operates on CNMF-derived ROI masks treated as fixed supports. Accordingly, segmentation quality, neuropil contamination, and partial overlap between neighboring cells can influence extracted spectral fingerprints and may contribute to false negatives or secondary assignments, particularly in densely labeled regions. These structured sources of uncertainty are expected to have the greatest impact under regimes of extreme class imbalance, low fluorophore brightness, strong neuropil signal, or pairing of spectrally overlapping reporters. Use of refined segmentation strategies or nuclear-localized reporters could reduce such structured uncertainty in future implementations.” (Discussion)

(5) The manuscript reports meaningful rates of secondary fluorophore detection, but also nontrivial false-positive rates for secondary labels under realistic conditions. The authors appropriately caution against over-interpretation, but the Discussion should more clearly delineate when dual-label assignments are likely to be biologically interpretable versus methodologically ambiguous, and how experimental design (e.g., fluorophore pairing) should be optimized accordingly.

We agree and will delineate interpretability boundaries explicitly.

“Dual-label assignments are most reliable when fluorophores are spectrally well separated and when signal-to-noise ratios are high. In contrast, spectrally adjacent fluorophore pairs or densely labeled regimes increase ambiguity and false-positive risk. Experimental design should therefore prioritize pairing spectrally distant fluorophores when projection convergence is of primary interest.” (Discussion)

(6) I suspect that Neuroplex will be most effective in certain regimes (moderate convergence, bright and spectrally distinct fluorophores) and less reliable in others. A more explicit discussion of best practices, anticipated failure modes, and experimental scenarios where the method may be inappropriate would increase the practical value of the paper for adopters.

“More broadly, Neuroplex is expected to perform most robustly in regimes characterized by moderate projection convergence, balanced fluorophore representation, bright and spectrally distinct reporters, and adequate signal-to-noise ratio. Imaging directly within a projection target that has received dense retrograde labeling may introduce substantial class imbalance, which simulations predict will reduce detection sensitivity for the dominant fluorophore. In such cases, conservative assignment strategies, reduced spectral complexity, or refinement of ROI definition may improve interpretability. Careful fluorophore selection and pilot validation under intended imaging conditions are therefore recommended prior to large-scale application. Future implementations incorporating nuclear-localized reporters may further reduce segmentation-dependent ambiguity by constraining spectral signals to somatic compartments.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors should address a few points that are not clear.

(1) At the end of the Results, the authors assess their approach using only four fluorophores and conclude that Neuroplex works "even" under reduced complexity. There is something I am missing. In my mind, lower complexity should be easier and should work better. As a researcher, I would first assess a four-fluorophores scenario and then step up with complexity, but the authors did the opposite. Also, I think that the present Supplementary Figure 9 should be in the main text; I don't understand why the authors decided to relegate a clear result to the bottom of everything. The authors should give some explanations.

We agree that reduced spectral complexity should, in principle, improve separability and classification performance. Our original presentation order was intended to first demonstrate feasibility under the most challenging condition (nine fluorophores plus GCaMP), thereby establishing maximal multiplexing capacity. The reduced-complexity experiment was included to demonstrate scalability and generalizability under more typical experimental regimes. However, we agree that this rationale was not sufficiently clear and that the reduced-complexity results merit presentation in the main text.

Accordingly:

We have moved former Supplementary Figure 9 into the main Results (Fig. 6).

We have clarified explicitly why the nine-fluorophore condition was presented first as follows:

“To evaluate the performance of Neuroplex under more typical experimental regimes with reduced-complexity, we applied the pipeline to two GCaMP transgenic animals injected with a subset of four fluorophores.”

(2) The question of relative expression is crucial. Among the infected regions, there is the contralateral mPFC and I imagine that if they image there, the contribution of the expressed protein might dominate all other components, preventing detection of other fluorophores, including GCaMP. But is it the case, or would it be possible to detect projecting neurons in that region? I would be surprised that the authors never tried it; this test would simply imply mounting the GRID lens on the other hemisphere.

This is an important conceptual point.

Our simulations (Supp. Fig. 5) explicitly model over-representation of a single fluorophore. These results show that heavy class imbalance primarily increases false negatives (due to baseline normalization) rather than false positives.

In the revised manuiscript, we discussed this limitation more explicitly.

“Relative fluorophore representation within the imaged field of view influences classification robustness. As demonstrated in our simulations of class imbalance (Supp. Fig. 5g–h), extreme over-representation of a single fluorophore primarily increases false-negative rates due to baseline normalization effects. In the present study, we intentionally avoided imaging directly within heavily infected projection targets (e.g., contralateral mPFC) in order to maintain moderate fluorophore representation across ROIs. Imaging in a densely labeled region would represent a more challenging regime, and we would expect reduced sensitivity for the dominant fluorophore under such conditions.” (Dicussion)

(3) The possibility to utilise Neuroplex goes beyond the type of experiment presented as proof-of-concept in this technical paper. In the Discussion, the authors mention genetically defined subtypes and activity-tagged neurons. But, if one changes the pipeline, can it be used by expressing GECIs with different spectra, or GECIs and genetically-encoded voltage indicators (GEVIs)? I would be very interested in knowing what the authors think about this putative "shortcut".

We thank the reviewer for this forward-looking and insightful question.

In principle, the Neuroplex framework could be extended to incorporate spectrally distinct genetically encoded functional indicators, including multi-color GECIs or combinations of GECIs and GEVIs. However, it is important to distinguish this from the identity-assignment strategy implemented in the present study.

Simultaneous multi-color functional imaging under a head-mounted miniscope is optically more demanding than assigning cell identity from single-color functional recordings followed by high-dimensional spectral readout. Multi-color GECI or GEVI imaging requires real-time excitation and emission separation during dynamic recording, increases optical complexity, and is particularly sensitive to chromatic aberration, photon efficiency, and signal-to-noise constraints imposed by GRIN lenses.

In contrast, Neuroplex decouples functional acquisition from spectral identity determination. Functional activity is recorded using a single optimized channel, while spectral separation is performed separately under controlled confocal conditions with multiplexed excitation and emission sampling. This design substantially reduces optical burden during behavioral imaging.

While integration of multiple functional reporters is conceptually feasible within this framework, successful implementation would require careful validation of brightness, spectral separability, and temporal stability for each reporter combination.

Reviewer #2 (Recommendations for the authors):

(1) Implement a principled multi-label calling mode for cells with >1 above-threshold fluorophore (e.g., per-fluorophore FDR control or Bayesian posteriors). Report cell-wise weights and re-run key results three ways: single-label, hard multi-label, and soft (probabilistic) assignments; state explicitly how conclusions change.

We appreciate this suggestion and agree that multi-label or probabilistic calling frameworks are well motivated, particularly for studies in which projection convergence is the central biological question. In the current manuscript, however, our goal is to establish a practically deployable proof-of-principle pipeline for linking miniscope functional recordings to a high-dimensional spectral-identity readout. Consistent with this scope, we used a conservative winner-take-all (WTA) strategy for primary analyses to prioritize specificity under realistic noise and background conditions, and we treated multi-hit events descriptively. Importantly, the qualitative conclusions regarding projection-resolved functional stratification are unchanged when secondary-hit distributions are examined.

In the revised manuscript, we explicitly stated that: (i) single-label assignment is a conservative analysis choice rather than a biological claim of exclusivity, and (ii) multi-label or probabilistic calling is a natural extension for future work, as follows:

“If multiple fluorophores exceeded the threshold for an ROI, the fluorophore with the largest z-scored beta value was assigned as the primary identity (winner-take-all rule). This conservative approach was chosen to prioritize specificity under realistic noise and background conditions. Additional above-threshold fluorophores were retained as ‘secondary hits’ but were not incorporated into primary subtype stratification analyses.” (Methods, Single Pass Algorithm)

“Because the present study is designed to establish methodological feasibility rather than precise anatomical quantification, simulation-derived false-positive and false-negative regimes were not formally propagated into confidence bounds on subtype proportions or behavioral effect sizes. Accordingly, subtype fractions should be interpreted as assignment-dependent estimates rather than definitive anatomical measurements. Future implementations could incorporate Bayesian or likelihood-based classifiers to generate posterior identity probabilities and enable formal uncertainty propagation when quantitative estimation of projection convergence is central to the biological question.” (Discussion)

(2) Add ground truth for dual projectors in a subset (paired orthogonal tracers or staged injections) and provide a confusion matrix including dual-positives; use this to calibrate thresholds/priors.

We agree that ground truth validation of dual projectors using orthogonal tracers or staged injections would be valuable, particularly for calibrating priors and enabling confusion-matrix-based evaluation. However, these experiments require additional cohorts and experimental design beyond the scope of the current proof-of-principle technical manuscript. Our goal here is to demonstrate the feasibility of multiplexed identification and projection-resolved stratification within a single animal, not to provide definitive anatomical quantification of collateralization.

We have revised the manuscript to clearly state that dual-label in vivo observations are descriptive and that studies aimed at quantitative convergence mapping should incorporate orthogonal ground truth validation.

“Accurate quantification of projection convergence would benefit from orthogonal ground-truth validation (e.g., paired tracers or staged injections) to establish confusion matrices for dual positives and to calibrate thresholds or priors.”

(3) Propagate uncertainty from simulations and registration/segmentation to subtype fractions and behavior effects (error bars or sensitivity analyses).

We agree that formal uncertainty propagation is appropriate for studies focused on precisely quantifying subtype proportions or effect sizes. In this manuscript, subtype fractions and behavioral comparisons are presented primarily as demonstrations of the feasibility of projection-resolved functional stratification, rather than definitive anatomical measurements. Simulation analyses are included to characterize expected performance under defined noise and background regimes, but we did not propagate these uncertainties into downstream confidence bounds in this proof-of-principle work.

We have revised the manuscript to clarify this explicitly as follows:

“These simulation-derived accuracy estimates characterize expected performance under defined noise and background conditions but were not formally propagated into confidence bounds on subtype proportions or behavioral comparisons. In this proof-of-principle study, subtype fractions are presented as assignment-dependent estimates rather than definitive anatomical measurements.” (Results, Assessment of spectral unmixing approach)

“These analyses were performed using conservative single-label assignments; dual-threshold ROIs were not treated as co-identities in order to avoid overinterpretation of potentially ambiguous multi-label cells. Because identity assignment prioritizes specificity and classification uncertainty was not formally propagated into downstream comparisons, subtype fractions and behavior-by-subtype differences should be interpreted as qualitative demonstrations of projection-resolved functional stratification rather than precise anatomical quantifications.” (Results, Neuronal cell types and behavior)

“The modeling framework was designed to characterize expected classification behavior across a range of experimental regimes, including background fluorescence, class imbalance, and reduced signal-to-noise ratio. These simulations provide practical performance guidance but were not used to compute formal error bars or propagate uncertainty into downstream biological analyses.” (Methods, Modeling of experimental variables to assess accuracy of algorithms)

“Because the present study is designed to establish methodological feasibility rather than precise anatomical quantification, simulation-derived false-positive and false-negative regimes were not formally propagated into confidence bounds on subtype proportions or behavioral effect sizes. Accordingly, subtype fractions should be interpreted as assignment-dependent estimates rather than definitive anatomical measurements. Future implementations could incorporate Bayesian or likelihood-based classifiers to generate posterior identity probabilities and enable formal uncertainty propagation when quantitative estimation of projection convergence is central to the biological question.” (Discussion)

(4) Mitigate sources of spurious multi-hits (neuropil handling, ROI mask erosion, nuclear-localized reporters, spectral basis choices) and quantify their impact on dual-label recovery.

We agree that neuropil contamination, ROI boundary choices, and spectral basis selection can influence multi-hit rates. In the current manuscript, we already implement background subtraction and evaluate multi-hit behavior through simulations under realistic background and noise regimes. Quantitative evaluation of additional mitigation strategies (e.g., ROI erosion comparisons) would require new analyses beyond the current scope.

We have revised the Discussion to include concrete best-practice recommendations (e.g., fluorophore pairing, conservative interpretation of multi-hits, and potential use of nuclear-localized reporters).

“Multi-hit events can reflect true biological collateralization but may also arise from structured sources of ambiguity such as neuropil contamination, partial ROI overlap, or imperfect ROI boundaries. These factors may bias spectral estimates and contribute to secondary assignments, particularly in densely labeled regions. Practical mitigation strategies include conservative assignment rules, improved segmentation, and use of nuclear-localized reporters to reduce neuropil contribution. ”

(5) Clarify claims in the main text/figures wherever exclusivity is implied; label which panels use single-label vs multi-label/soft assignments.

We agree and thank the reviewer for emphasizing clarity. We did not intend to imply projection exclusivity. We have revised the manuscript text and figure legends to explicitly state where single-label (winner-take-all) assignment is used, and to avoid language that could be read as claiming exclusive projection identity as follows:

“For quantitative behavioral comparisons, each ROI was assigned a single primary fluorophore identity using conservative winner-take-all rule. This assignment reflects the strongest spectral contribution and does not imply projection exclusivity. Rather, it provides a conservative lower-bound estimate of subtype proportions, as ROIs exceeding threshold for multiple fluorophores were classified according to their strongest spectral contribution.”

Reviewer #3 (Public review):

Summary:

This important work provides a web-based tool to contextualize effect sizes in psychiatry with respect to reliability and base rates (collectively referred to as predictive utility analysis). The methods for the tool incorporate established psychometric principles that I think are of use for multiple fields in this seemingly easy-to-use tool. I agree with the critical importance of this tool and the methodological points made in this manuscript. Enthusiasm for the manuscript is weakened by a lack of clarity on the formulation of the paper and stated goals of the examples used, with the inferences and impact on clinical decision making from various parameterizations via this tool left open-ended.

Strengths:

This paper presents a well-considered and, what I think will be highly useful, web-based tool to contextualize effect sizes with respect to reliability and base rates. As the authors rightly point out, such a tool could be used in conjunction with widespread analytic power analysis tools in study planning. The paper also well contexualizes the need for such a tool in the relatively recent history of concerns of power, reliability, and inference in psychiatry specifically, and more general meta-scientific debates in psychology and neuroscience.

Weaknesses:

My primary feedback on this manuscript is the lack of clarity in what the paper itself, specifically, separate from the tool, is hoping to achieve. There is a central, but unresolved, tension in whether the reader is supposed to:

(1) focus on the specifics of the examples used and whether to reevaluate the substantive claims from the studies, (2) buy in to how various reliability and base rate parameters impact modeling outcomes, (3) receive an introduction to the tool itself.

In my estimation, the largest contribution to the field here is in (2) and (3), but currently much of the real estate of the paper is dedicated to several examples of (1). While these specific examples may be illustrative to some degree, I think given the number and brevity of such, they are unlikely to incidentally achieve points (2) and (3) above. Specific examples include the assertion of kappas for DSM diagnoses, without much nuance (e.g., see https://psycnet.apa.org/buy/2015-27500-001). Given the relatively limited space given to this example, however, it's hard to be entirely certain what the reviewer should take away.

A second point of concern is where this tool would be situated in the research pipeline. I agree with the authors that this tool could be used in ways that parallel power analysis. With that in mind, it seems the most common use of this tool for an individual investigator is likely to be in a priori study planning. In contrast, and with my point above in mind, the use of the tool for existing results is likely best done with multiple estimates of effect sizes, reliability, and base rates, as is common in meta-analysis or consensus reviews. Nevertheless, there is no real example or guidance around how this influences new study planning.

A third point is that more nuance would be useful in the introduction about the current state of psychiatry research. For example, I share many of the authors' concerns about reliability, power, reproducibility, and barriers to translation. That said, it is the case that while effect sizes should be considered considerably more, they are widely considered in psychiatry research via the common place of meta-analysis and other data pooling approaches. Another such example that the authors state in the context of reliability: "However, this [reliability] attenuation is rarely accounted for in routine analyses in psychiatry". This is true in practice, but somewhat misleading insofar as the method by which to do this remains unclear. For example, should we all report disattenuated associations, assuming there is no error and everything is perfectly reliable? This, of course, would be unrealistic to expect zero error. That we can achieve this with the new tool is clear, but the nuance of how and under what circumstances it should be done is not clear, and such nuance should be better reflected in the framing of the problem. That is, there is also a lack of clarity on what ought to be best practices and field-wide goals, rather than simply the lack of an ability to model these factors.

Minor point

For conceptual clarity, it would benefit the manuscript to at least briefly mention the role of validity in translational importance. Of course, the current psychometric issues of reliability, base rate, power, etc are critical, but it should at least be mentioned, given the potential wide audience of this manuscript, validity is important as well. For example, highly reliable measures may not be valid indicators of underlying disease etiology (e.g., fMRI head motion is a highly reliable trait-level feature, but typically not considered an important predictor or consequence of mental health worth investing translational resources in). Relatedly, confounding as a general topic would be useful to mention just briefly, to help with the spirit of considering underlying issues in translation.

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Reply to the reviewers

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

Summary: In this manuscript, the authors examine how peripherin-2 (PRPH2) contributes to the localization of CNGβ1 within rod outer segment structures. PRPH2 and its homolog ROM1 are structural components of rod discs and are required for disc morphogenesis. In the absence of PRPH2, rod outer segments do not form, and various outer segment materials accumulate and are released as cilia-derived ectosomes. PRPH2 is thought to be transported through an unconventional secretory pathway, whereas cGMP-gated channels follow a conventional trafficking route. Although these components reach the outer segment through distinct pathways, PRPH2 is necessary for the proper delivery of CNGB1, a subunit of the cGMP-gated channel, to its correct destination. It was previously reported that a small fraction of PRPH2 reaches the outer segments through the conventional pathway when it forms a complex with Rom1 in mouse photoreceptors. Using Rom1 KO mice, the authors show that this conventionally trafficked PRPH2 fraction is not required for CNGB1 transport to the outer segment. Using various chimeric constructs, the authors verified that tetraspanin core of PRPH2, delivered to the OS, is sufficient to promote OS localization of CNGB1. Ct and Nt cytoplasmic regions of PRPH2 are dispensable for the role. Overall, the majority of the experiments are well-executed with statistical rigor, written in a way that others can reproduce, and support the major conclusion indicated in the title, "PRPH2 is essential for OS localization of CNGB1".

Major comments: I believe that the majority of the conclusions are well-supported in this manuscript. Below, I am listing the major points that may need additional experiments or clarifications: 1) CNGA1 subunit is transported to and enriched within ciliary exosomes or the outer segment in PRPH2 deficient mice (Figure 1). The reduced levels of CNGA1 and CNGB1 in rds-/- mice suggest limited stability of these proteins. Their diminished abundance is also influenced by decreased mRNA expression of the corresponding genes. These findings imply that CNGB1 may not be essential for outer segment delivery of cGMP-gated channels if CNGA1 alone contains adequate targeting information. Related to these points, it is unclear whether CNGB1 exhibits a trafficking defect or encounters other problems before leaving the endoplasmic reticulum. Such problems may involve deficiencies in folding, holo-channel assembly, or related quality control processes.

RESPONSE: We agree with this reviewer and have added additional data and interpretation to address this point. Our new data finds that in fact a low level of CNGB1 can reach ectosomes in rds-/- rods, which makes sense since we and others had observed CNGA1 was present and we know that channel assembly occurs in the ER. This suggests that the CNG channel can properly fold and assemble. Furthermore, overexpressing CNGB1 did not restore ciliary localization in Rds-/-, leading to our interpretation that in the absence of an outer segment membrane compartment, there is no place to deliver the CNG channel and it is subsequently degraded. Apart from perihperin’s binding partner, ROM1, this is unique to the CNG channel. CNG channel subunits are still significantly lower at P21 than other outer segment membrane proteins, such as ABCA4 (shown here), rhodopsin, and PCDH21(shown elsewhere).

2) CNGB1 overexpression in rds-/- mice does not result in outer segment localization of CNGB1 channels (Figure 2A). These findings do not clarify whether CNGB1 successfully transits through the Golgi apparatus or associates properly with CNGA1 subunits. Elevating expression levels alone would not compensate for problems in folding or assembly.

RESPONSE: We recognize that our previous submission lacked clarity on this point. Therefore, we have restructured the order of figures and provided additional controls to improve our manuscript. First, the fact that CNG channel is present at P21 and even increases over time suggests that in rds-/- rods channel processing (folding and assembly) is unaffected. Second, we recognize that channel stoichiometry is important for proper channel assembly, so we added a new supplementary figure that shows endogenous CNGA1 expression increases in rds-/- rods that are overexpressing myc-CNGB1 and FLAG-peripherin-2. This adds credence to our CNGB1 overexpression experiments and shows that CNGB1 being trapped is not due to inefficient channel assembly.

3) Claims related to Figure 6 (P45 rds-/-) need further evidence. It remains uncertain whether CNGA1 and CNGB1 are delivered to lamellar ciliary membranes or to a distinct plasma membrane compartment comparable to that observed in wild type rod outer segments, or whether they accumulate in ciliary ectosomes. Those lamellar structures could be a part of cone outer segments. The observed GARP signal may originate solely from soluble GARP proteins. It is also unclear if CNGA1 and ROM1 colocalize in P45 rds-/- mice. Clarifying these points would strengthen the conclusion that lamellar formation, rather than specific function of PRPH2, is sufficient for CNGB1 delivery to the cilium or outer segment plasma membrane.

RESPONSE: CNGA1/B1 are not expressed in cones, so the elevated outer segment localization observed at P45 must be coming from rods. In mouse retina, cones make up only 3% of the photoreceptor population. The SEM data clearly show that the lamellar ciliary protrusions are present on the majority of the photoreceptors. We now include CNGB1 staining from Rds-/- P45 sections that corroborate these data and show that CNGB1 is present at P45 and not P21 (Supplemental Figure 2).

Below are minor comments: 1) The study does not establish whether a direct interaction between PRPH2 and CNGB1 is required for CNGB1 delivery to rod outer segments. Prior work by the senior author (ref 13) suggests that this interaction is not essential, since the PRPH2 binding site within the GARP domain is distinct from outer segment transport signal of CNGB1. Including a discussion of the PRPH2-GARP (or CNGB1) interaction and its relevance to CNGB1 trafficking would help readers interpret the findings more fully.

RESPONSE: We have included this in our discussion.

2) The authors propose that the ROM1 core is sufficient for outer segment delivery of CNGB1 based on experiments with chimeric constructs. However, in Figure 1, ROM1 is present in the outer segments (or ciliary ectosomes) of rds-/- mice even though CNGB1 is not delivered to these structures.

RESPONSE: Our new data, including MS analysis and Western analysis from an enriched ectosome preparation, reveal that, along with ROM1, low levels of the CNG channel are delivered to ciliary ectosomes in Rds-/- mice. However, at this early timepoint photoreceptor cilia do not produce a membrane protrusion, which we observe is required to augment CNG delivery. We expressed a FLAG-ROM1 construct to try to drive earlier creation of these membrane protrusions, but this was unsuccessful, as we observed ROM1 was primarily localized to the inner segment. This suggests that overexpression of ROM1 did not increase ROM1 delivery to the cilia. Luckily, we were able to overcome this bottleneck with several of our chimeric ROM1/Prph2 constructs that did localize to the cilia and restore CNG localization. All of these new results have been included in the revised manuscript.

3) Line 80: "Theouter" A space shall be inserted between "The" and "outer".

RESPONSE: Done

**Referee cross-commenting**

Both reviewer #2 and reviewer #3 express views that align with mine. They clearly described the study's limitations, and their comments are highly valuable.

Reviewer #1 (Significance (Required)):

Prior studies showed that CNGB1 is not present in cilia-derived ectosomes of rds-/- mice, indicating that PRPH2 is necessary for ciliary or outer segment localization of CNGB1 in rods. Building on these earlier findings, I consider this study significant for the following reasons: 1) Using detailed analysis of different PRPH2 domains and chimeric constructs, it clarifies that PRPH2 core region, delivered to OSs, is essential and sufficient for OS localization of CNGB1. 2) PRPH2 and CNGB1 are thought to travel through different post-ER transport routes, with one pathway bypassing Golgi regions and the other passing through them. This study shows that CNGB1 depends on PRPH2, which suggests that these two routes may converge or interact at later stages and opens new directions for future investigation. 3) The study is relevant to basic scientists and biologists investigating how membrane structures acquire specialized functions in neurons, and its implications extend beyond photoreceptor biology.

Limitation of the study: I believe that clarifying these points will make the manuscript more significant. 1) Is it not clear, as mentioned above, how PRPH2 contributes to the delivery of CNGB1 to the OSs in the different secretory pathways.

RESPONSE: In the absence of ROM1, Prph2 only travels through the unconventional secretory pathway directly from the ER. By looking at CNG trafficking and localization in ROM1-/- mice, we rule out the possibility that the small portion of PRPH2/ROM1 complexes that traffic conventionally through the Golgi are required for channel localization (Figure 3). Further, our Rho-Prph2 chimera that includes the trafficking signal from Prprh2 did not rescue CNGB1 localization (Figure 4). These findings suggest that it is unlikely that these proteins engage during secretory transport to the outer segment.

2) The prior study using a fluorescence complementation approach (Ritter et al, 2011) suggests that PRPH2 and CNGB1 can associate within rod ISs, likely before their delivery to OSs. However, it remains unclear whether this interaction supports the potential cotransport of CNGB1 and PRPH2 or whether the authors view these proteins as being transported independently.

RESPONSE: As described above, our experiments rule out the notion that co-transport through the Golgi is driving CNG channel ciliary localization. We now note in our discussion that this data does not rule out the possibility of an earlier association between these proteins. However, the bulk of our data supports that any early interaction is not required for ciliary delivery.

3) At the end of the result section (Figure 6, rds-/- P45), the authors suggest that lamellar formation (evaginations?) is required for CNGB1 transport. However, CNGB1 is normally not seen in evaginations or lamellar structures, and thus the assumption is not consistent with prior findings.

RESPONSE: Absolutely, we agree that the CNG channel does not enter newly forming disc membranes, which has been shown by multiple groups. We included this in our discussion and have now added a clearer statement of our hypothesis: “Together, these data suggest that the partitioning of disc membranes from the plasma membrane by tetraspanin proteins is a key step for localizing the CNG channel and could play a role in segregating other proteins into the plasma membrane.”

Overall, the manuscript is insightful and has the potential to advance our field and related disciplines.

RESPONSE: Thanks!

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

Cyclic nucleotide gated channels (CNG) localize to the plasma membrane of the rod photoreceptor outer segments, and are a key component of the phototransduction cascade. Understanding how outer segment proteins are trafficked and sequestered to the outer segments is an important field of investigation as it addresses both a fundamental aspect of cell biology and mechanism of disease, many of which have trafficking defects at the core of the pathogenic process. Using primarily IHC analysis of rodent models in combination with introduction of various expression constructs to the retina (through electroporation), this study finds that two rod outer segment structural proteins, peripheral-2 and ROM1, facilitate CNG channel localization to the outer segment.

While this conclusion is interesting, a major concern that tempers enthusiasm is that in peripherin-2 null photoreceptors, there are no outer bona fide segments. In lieu of outer segments, there are rudimentary membranous protrusions and vesicles distal to the connecting cilia where outer segments should be. So the basis for concluding that peripherin-2 is required for CNG localization to the outer segment seems a bit wobbly. It is understood that the authors assumed the membranous materials distal to cilia as proxy for outer segments in their analysis and narrative. This assumption may have some merits. However, it is well known that when outer segment morphogenesis is severely compromised, all normally outer segment-bound proteins are ectopically localized or largely absent due to increased degradation. This could be simply due to the loss of their destination compartment, among other things. It is not clear how the authors could distinguish between a direct causal relationship where loss of one protein leads to the mislocalization of another, from secondary outcomes due to loss of the outer segments. The last sentence of the Abstract is telling. "Interestingly, this notion is supported by endogenous staining of CNGB1, which reappears in aged Rds-/- rods that have produced ciliary membrane protrusions." So in aged mice CNGB1 did localize to the OS, but what changed? There was more OS like material to house the CNGB1 protein in the aged mice.

RESPONSE: We agree that the loss of the OS compartment is likely driving downregulation of all OS proteins and have included a statement as such in our manuscript. We also performed additional qRT-PCR analysis on ROM1 and ABCA4 to show global downregulation at the mRNA level – consistent with the notion that there are reduced outer segment proteins when morphogenesis is compromised. However, our Westerns and IHC (as well as published data) clearly find a specific decrease in the CNG channel at the protein level, suggesting that not all proteins behave similarly when the outer segment is not formed. We included additional discussion on this point as well. While not directly examined in our manuscript, previous reports have shown the reverse effect: some outer segment proteins (e.g. PCDH21, Prom1) are upregulated in rds-/- retinas (Rattner et al JBC 2004). Therefore, it is an oversimplification to state that all outer segment proteins behave the same when outer segments are not formed properly. Other models of outer segment dysmorphia (e.g. RhoKO, PCDH21KO, Prom1KO, or WASF3) localize the CNG channel properly. We have added this to the discussion and hope that by restructuring our manuscript, we clearly outline that we do think that membrane retention at the tip of the cilia is driving CNG channel localization and that molecularly the tetraspanin proteins play a role in organizing these membranes.

Reviewer #2 (Significance (Required)):

Trafficking of nascent proteins to the outer segment in support of its renewal is an important subject, which has significant impact in understanding the mechanisms of retinal degeneration. The conclusion from this study, that peripherin-2 and ROM1 have a direct role in supporting CNG subunit trafficking may well be meritorious. However the data presented are less than fully convincing, and specifically the question of a direct vs secondary effect needs to be better addressed.

RESPONSE: We appreciate this reviewer’s enthusiasm for investigating this process. The initial premise of our study was to investigate whether a direct effect of peripherin-2 on CNG delivery was possible, which was meritorious based on previously published data. However, we now find no direct trafficking link between CNG and peripherin-2; instead, our data largely find that CNG delivery is dependent on the presence of retained membranes at the ciliary tip – either through natural mechanisms or by driving “rudimentary” outer segment membrane lamination by overexpression of tetraspanin domains. We have restructured the manuscript to help guide the discussion.

The following quote underpins some of the reasoning in the study. Lines 139-144, "(Figure 2A). This localization pattern suggests that the CNGB1 subunit is trapped in the biosynthetic pathway. In contrast, when FLAG-tagged rhodopsin is overexpressed in Rds-/- rods it traffics properly to outer segment ectosomes (Figure 2B, (19)). We posit that without proper exit from the biosynthetic pathway, the endogenous CNGB1 protein is rapidly degraded to undetectable levels, which we circumvent through overexpression. These data suggest the localization defect of CNGB1 in Rds-/- rods is in the trafficking of CNGB1. " This in my view is an over- interpretation of limited data. The statement implies that rhodopsin and CNGB1 qualitatively differ in their fate but I would argue that both proteins are heavily degraded intracellularly except more of rhodopsin escaped to the "OS" and shows up in IHC. In many rhodopsin mutant transgenic mice, mutant rhodopsin appeared in OS even though intracellular degradation (gumming up the system) is a major factor in the disease process. The claim "rhodopsin trafficked properly to outer segment ectosomes" is not grounded in solid data.

RESPONSE: We do fundamentally agree that the endogenous CNG channel is heavily degraded, which we confirm by overexpressing an exogenous CNGB1-myc and finding it trapped in the biosynthetic pathway. As stated by the reviewer, this localization pattern is in contrast to what we and others have observed for endogenous rhodopsin, and now show for overexpressed FLAG-rhodopsin – that rhodopsin does traffic to the OS ectosomes. By comparing the localization of both endogenous and overexpressed constructs (using the same promoter), we feel that our conclusion is well supported. We appreciate that our wording of “rhodopsin trafficked properly to the outer segment” is misleading, as traffic of membrane proteins in Rds-/- rods is generally affected and not “proper”. Importantly, we follow up this “limited data” with additional experiments showing that at high expression levels, we are unable to drive CNGB1 localization to OS ectosomes unless we co-express with a tetraspanin domain.

A further minor comment is that the scope of the study appear limited, with no attempted experiments on how these proteins might interact to effect facilitation of trafficking.

RESPONSE: Our approach was to be agnostic to the outcome of our hypothesis that peripherin-2 was directly involved in CNG channel trafficking. The experiments we performed to test this (ROM1-/- analysis and Prph2 C-terminal chimeras) did not support a role for peripherin-2 in CNG trafficking. Instead, our data support a model in which membrane retention and organization at the ciliary tip drives CNG channel delivery. We feel that our approach was not limited.

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

in the gene encoding tetraspanin protein peripherin 2 (Prph2), i.e., Rds-/-, examining the requirements for various portions of the Prph2 protein in the context of an assortment of chimeric constructs expressed via transfection into photoreceptor cells, to restore localization of the beta subunit of the cyclic nucleotide-gated channel (CNGbeta1) to photoreceptor outer segments (OS) (in a small number of experiments) or, in the majority of experiments, to do so for a recombinant tagged version of this protein also overexpressed by transfection.

The concluding sentences of the Discussion, which summarize the major conclusions are as follows: "Our data clearly show that localization of the CNG channel is dependent upon peripherin-2 after biosynthetic exit, further suggesting that the necessary action is at the ciliary base. Supporting evidence for this comes from analysis of Rhodopsin knockout outer segments which have internal disc-like structures and localize CNG channel properly. Therefore, in the absence of a fully elaborated outer segment, peripherin-2's ability to delineate a disc is sufficient to drive CNG channel delivery. Together, these data suggest that the partitioning of disc membranes from the plasma membrane by tetraspanin proteins is a key step for trafficking the CNG channel and could play a role in segregating other proteins into the plasma membrane.

The first sentence contains both reasonable conclusions and phrases whose meaning is unclear or not supported by the results presented. The statement: 'localization of the CNG channel is dependent upon peripherin-2 is supported by the data but, of course, has long been known from previous studies of Rds-/- mice. What is meant by "...after biosynthetic exit..." is unclear. If, by this term, apparently newly invented, the authors mean "after its synthesis of the protein is complete," the statement is accurate, but also a truism.

RESPONSE: The absence of CNGB1 was reported in previous studies, but the mechanism driving its absence has not been investigated. In our resubmission, we have added additional data that now shows CNGB1 is present at very low levels in Rds-/- ectosomes but remains undetectable by IHC, which is consistent with previous studies mentioned by the reviewer, but is also a novel finding. Importantly, we find specific downregulation of CNG channel subunits in Rds-/- retinas compared to ABCA4, supported by Western blot analysis (Figure 1), and we investigate the mechanism driving this result.

We appreciate the reviewer pointing out that “biosynthetic exit” is a niche term not broadly understood. We have removed this statement.

The statement, "the necessary action is at the ciliary base," is NOT supported by the data presented, as the effect of the "successful" Prph2 constructs on CNGbeta1 localization is primarily to increase its levels at the distal end of cilia and at the base of OS-related structures formed in response to the presence of the Prph2 constructs. The restoration of these membranes, which, as the authors note, has been previously reported, is overwhelmingly the biggest effect of these constructs, and it could be argued that the restored localization, rather than degradation, of CNGbeta1 is merely a downstream consequence of the formation of these structures, with perhaps, an element of stabilization of CNGbeta1 toward degradation from direct binding to Prph2, which has also been previously reported.

RESPONSE: We agree with the reviewer. Our interpretation of our data is that the presence of Prph2 (or its variants) at the distal end of the cilia localizes CNGB1, likely due to the formation of outer segment membrane structures. Previous to this work, there was a possibility that targeting information of Prph2 was required for CNGB1. That had never been explored. We definitively rule this possibility out when we express the C-terminal tail of Prph2, which is unable to rescue CNGB1 localization. Because the tetraspanin domain of Prph2 (or ROM1) can localize CNGB1, we do agree that the definition of an outer segment structure is the driving force for CNGB1 delivery – these are new findings. We’ve restructured and added additional discussion to the manuscript to clarify this point.

The next suggested conclusion is, "Therefore, in the absence of a fully elaborated outer segment, peripherin-2's ability to delineate a disc is sufficient to drive CNG channel delivery," is partly accurate and partly misleading. If the word "localization" were to replace the term, "delivery," concerning which there are no data (aside from those confirming that Prph2 and CNGbeta1 pass through distinct secretory pathways), this statement would be an accurate summary.

RESPONSE: We have updated to “localization”, but the fact that we confirm these two proteins do not traffic together through the Golgi would suggest that delivery is independent of trafficking.

The final sentence, "Together, these data suggest that the partitioning of disc membranes from the plasma membrane by tetraspanin proteins is a key step for trafficking the CNG channel and could play a role in segregating other proteins into the plasma membrane," sentence, would also be accurate if the word "localization," were to replace the term, "trafficking." The key point for these qualifications is that the experiments presented measure steady state levels of CNGbeta1 constructs at certain locations, which are determined not only by rates of trafficking, but also rates of synthesis and degradation, and the data presented confirm that total levels of CNGbeta1 are greatly diminished in the absence of functional Prph2, rendering any conclusions about the relative roles of trafficking kinetics and degradation kinetics speculative in nature.

RESPONSE: We agree and have revised.

Aside from these major conceptual issues, there is one overriding technical question: why are almost all the experiments presented carried out with a highly over-expressed engineered version of CNGb1 with a tag, which is clearly context far from the physiological one, as opposed to examining redistribution of the endogenous CNGbeta1, which is of much greater interest. In some results relegated to a Supplemental figure (Supp. Fig. 2), the authors clearly demonstrate that sufficient signal can be obtained from immunofluorescence staining the endogenous proteins for such experiments to be readily interpretable. If the concern was cross-reactivity with non-covalently attached GARP proteins, a few experiments showing that similar results are obtained for immunostaining of the endogenous protein or of the tagged construct would haver been sufficient, and the paper could have had more physiological relevance and impact.

RESPONSE: We agree that endogenous CNG staining is important and valuable, which is why we included it in our manuscript. We were able to confirm that overexpressed CNG recapitulated the endogenous staining. We proceeded with analyzing overexpressed, tagged CNG for the reasons stated by the reviewer. Yes, cross-reactivity with soluble GARP proteins was one consideration, as was the fact that the GARP antibody is a mouse monoclonal antibody. Increased IgG due to inflammation in the RDS-/- model can obscure the outer segment region in these retinas, confounding our quantification. The tagged versions of CNGB1 and corresponding quantification offered the most clarity and continuity for the reader; therefore, we relegate the endogenous staining to the supplement.

The remaining concerns are generally of less significance and mostly conceptual or quite minor technical concerns. Technically, the imaging data and their quantification are of good quality and analyzed with reasonable rigor.

RESPONSE: Thanks!

Abstract: "In this study, we investigate how peripherin-2 is engaged in CNG channel delivery to the outer segment. Might this not be more a question of how the absence of properly formed discs impacts the formation of outer segments with plasma membranes surrounding the disks? Is this really a question of "delivery" or "lack of address to make the delivery"?

RESPONSE: Our interpretation of this comment is that it boils down to semantics. Delivery is inclusive of both trafficking and localization, which we investigate in our manuscript.

Page 3, "fluorescence complementation between peripherin-2 and CNGb1 in the inner segment of transgenic Xenopus rods (23) ". The wording is unclear. It should be stated clearly that they are describing results of "bimolecular fluorescence complementation assays" of highly overexpressed recombinant proteins expressed from transgenes.

RESPONSE: We have revised.

Page 4, "...trapped in the biosynthetic pathway," It is unclear what the authors mean by this phrase. Obviously, "biosynthesis," i.e., translation is indeed complete, but biochemical pathways are not places. Is the intention to suggest that post-translational processing, such as addition and editing of carbohydrate chains or assembly with the alpha subunit has not been completed? If so, it would be better just to say so clearly. Or, is it meant to imply that it is physically "trapped" in the ER and/or Golgi apparatus? In any case the meaning should be made clear. Co-staining with ER and Golgi markers would have been very informative with respect to the compartments in which the highly overexpressed recombinant protein is trapped.

RESPONSE: We acknowledge that our phrasing here was indirect. We have revised. Co-staining with Calnexin (an ER-marker) was attempted, but proved to be uninformative.

It should also be noted that accumulation of highly overexpressed membrane proteins within internal membranes and membrane aggregates is a very commonly observed experimental phenomenon, and not restricted to the highly specialized trafficking routes in photoreceptors.

RESPONSE: We agree that exogenous expression of membrane proteins can lead to increased presence within internal membranes of the inner segment, which we routinely see in our experiments. Importantly, our analysis is restricted to the ability of these exogenously expressed proteins to reach the ciliary compartment in Rds mice. We also conduct these experiments in wild-type retinas to ensure that our constructs are expressed, and the proteins reach the ciliary outer segment under normal conditions.

Page 4, " peripherin-2 facilitates trafficking of the CNGb1 subunit to the outer segment " The data presented to this point do not demonstrate an enhancement of transport, but only of steady-state levels. There is nothing to rule out the possibility that some beta subunit is trafficked in Rds-/-, but is unstable to degradation in the region near the cilium when peripherin-2 and outer segments are not available. An increase in transport is certainly a possible explanation for the results, but should not be taken as an unambiguous conclusion.

RESPONSE: We have altered the description of these results to allow for more interpretation of our data, which show that CNGB1 delivery to the outer segment is reduced in Rds-/- mice and enhanced when peripherin-2 is re-expressed.

Page 4, " We confirmed that the fraction of peripherin-2 that traffics conventionally through the Golgi is indeed absent in Rom1-/- retinas and found that trafficking of the CNG channel via the conventional pathway is unaffected (Figure 3A) . This is one of the stronger and more interesting results in this manuscript, and tilts the argument against trafficking as being the mechanism for enhancement by overexpressed peripherin-2 of beta subunit levels in the distal region of the photoreceptor layer.

RESPONSE: We agree.

Page 5, " Our finding that secretory trafficking of peripherin-2 and CNGb1 is distinct . Clumsy syntax- needs to be rewritten for clarity.

RESPONSE: Revised

Page 5, "two previously characterized fusion proteins... have been shown to localize to the outer segment and build a rudimentary membrane structure (19) " This previous result, which is critical to interpretation of the results in this manuscript, should be introduced early, before any experimental results using related constructs are presented, in order to avoid confusion.

RESPONSE: Prior to these experiments, we used only full-length peripherin-2, rhodopsin, or CNGB1. This paragraph is the first introduction of any chimeric protein, and we explain these two constructs thoroughly. We believe this satisfies this reviewer’s request.

Page 5, " We confirmed these data by staining for endogenous CNGb1 in Rds-/- rods electroporated with each construct (Supplemental Figure 2B,C) " This is the most informative result in this manuscript with regard to the ability of these constructs to restore proper localization of CNGB1- it is not clear that the overexpression constructs for CNGB1 present any advantage beyond stronger signal and they may not be assumed, a priori, to be faithfully reporting on interactions of Prph2 with endogenous CNGB1, which is the biologically significant question. A big problem with Supp. Fig. 2 is that there is no real control, i.e., one without any Prph2 construct electroporated. Even the Rho-Prph2CT construct has some ROS-related structures and some CNGB1 localized to the one shown at higher magnification. The Prph2-RhoCT construct seems to lead to a substantial increase in endogenous CNGB1 in inner segment membranes. This looks like a phenomenon that is potentially very interesting, although it doesn't fit with any of the models put forth in the manuscript.

RESPONSE: We agree that endogenous staining (shown in Supplemental Figure 3 of our revised manuscript) is informative, but it was technically challenging. Once we verified that our overexpression system recapitulated results for endogenous CNGB1, we went forward with the epitope-tagged CNGB1, which was clearer when quantifying CNGB1 localization to rudimentary outer segments.

Our electroporation method provides an excellent internal control, as all of the non-electroporated cells show no endogenous CNGB1 localization without peripherin expression (Sup Fig 3A).

Page 5, " cytosolic N- and C-termini of peripherin-2 are dispensable for CNGb1 outer segment localization " No- if you could simply remove them and get proper localization, that would show they are "dispensable." In these experiments they are always replaced with the corresponding region of some other protein that is localized to OS, or in one case, with 3 copies of the FLAG tag at the N-terminus. There are also clear differences in the efficacy of the different "successful" constructs, but these results and their implications are not really discussed.

RESPONSE: We make this statement in the context of these termini being dispensable to CNGB1 localization, not to peripherin-2’s stability, function, or localization. A complete truncation of either domain results in a non-functioning protein. Our supplemental data shows reduced expression with a truncated N-terminus, preventing analysis (Sup Fig 5C). The 3X-FLAG has no known function in the cell, and we believe it serves as a proxy for removing the N-terminus altogether. Removing the C-terminus would prevent proper outer segment targeting, which is key to determining how peripherin-2 impacts CNGB1 ciliary delivery. Replacing this C-terminus with an outer segment targeting domain from another protein is an established method of investigation.

Page 6, " We then wanted to determine whether the ROM1 tetraspanin region was sufficient to facilitate CNGb1 delivery by further replacing ROM1's cytoplasmic N-terminus with that of peripherin-2 (Prph2NT/CT-ROM1) . " This experiment obviously does NOT test "sufficiency" of the TM segments, as the construct has the termini replaced with the corresponding regions of Prph2, which might functionally substitute for the missing ROM1 regions.

RESPONSE: Our previous results had already ruled out a role for these termini in CNGB1 localization.

Page 6, " We show a dramatic increase in GARP staining in the aged Rds-/- retinal sections " The age dependence of this phenomenon is quite interesting and puzzling. Any thoughts on the mechanism?

RESPONSE: We agree that this natural process is very interesting. We have restructured the order of our figures and provided additional controls to support this finding. We have added this to the discussion and hope that by restructuring our manuscript, we clearly outline that we do think that membrane retention at the tip of the cilia is driving CNG channel localization and that molecularly the tetraspanin proteins play a role in organizing these membranes.

Page 6, " Although CNGα1, known to form homotetramers, can localize to the extracellular vesicles released into the outer segment area. " Not a sentence.

RESPONSE: Revised

Page 6, " Our data now shows that the population of peripherin-2 in complex with ROM1 that travels through the conventional trafficking pathway does not play a role in CNGb1 localization to the outer segment. " This is an oddly accurate, albeit somewhat contradictory sentence. Yes, you have failed to answer the question you claim this work was designed to address. Apart from this negative result, nothing is learned about trafficking, per se, from the experiments in this manuscript.

RESPONSE: Please see our response to the reviewer’s comment above that clarifies our thinking regarding our results on trafficking.

Page 7, " anticipated " Hopefully, the authors mean to say, "hypothesized," here.

RESPONSE: Revised

**Referee cross-commenting**

My impression from reading the reviewers' comments is that there is general agreement on both the strengths and the limitations of this work. In my opinion, the issues raised by the reviewers could be addressed by editing the manuscript to be more circumspect in drawing definite conclusions from data that are not fully conclusive, without necessarily adding new experiments.

Reviewer #3 (Significance (Required)):

This study addresses a problem of great interest in the photoreceptor field and in cell biology more generally of trafficking and localization of specialized membrane proteins to specialized ciliary membranes. The strengths are technical quality of data with good controls, in most cases. The limitations are largely conceptual in nature and derive from the rather simplistic approach to the experimental design, as described above. The rather dated, "mix and match" approach based on chimeric construct with pieces of sequences removed and replaced at will does not properly account for the conclusion reached many times from many experiments, including some this manuscript, that the "roles" of stretches of amino acid sequence depend exquisitely on the multidimensional context in which they are tested, not simply on their position in the linear sequence. The paper presents interesting and convincing results with respect to functional requirements for formation disc-like membranes, but very little with respect to 'trafficking."

On 2023-02-23 20:27:02, user Olavo Amaral wrote:

I recently reviewed this manuscript for a journal. For the sake of transparency, I thought it was worth it to post my comments here on bioRxiv as well, as it brings the review effort within the public domain. Let me know if you have any feedback and congratulations on the work: it's a nice paper on a very important topic.

Summary:

The manuscript addresses the question of “shortcut citations” in methods description. Although this problem is frequently mentioned in debates about methodological reproducibility, it is understudied and it’s nice to see actual research about it.<br /> The results contain three main sections, which study (a) the prevalence of various types of citations in the methods sections of articles in highly cited journals, including shortcut ones, (b) examples of what happens when shortcut citations are followed and (c) a review of journal policies. This is followed by a reasonably extensive discussion focused on (d) guidelines on how to use shortcut citations.<br /> I generally agree that this is an interesting structure, as it (a) documents the phenomenon, (b) evaluates to what degree it represents a problem, (c) inquires what is being made to address it and (d) suggests additional measures. The weakest link in the chain, however, seems to be point (b) (i.e. measuring the impact of the problem), as I am not sure the case studies provided are enough to quantify this. I will try to make this clear in my main point below.

Main point:

• While the numbers of articles and citations in the first section of the study are probably sufficient to provide an overview of the use of citations, the 15 articles included as case studies in the second section are not. The authors seem to acknowledge this limitation, as they refrain from making a quantitative synthesis of these articles. That said, this leads this section of the manuscript to fall short in accurately presenting the importance of the problem. <br /> Although I found the visualization for each case study provided in Fig. S2 interesting, I would doubt that most readers will really make the effort to go through each one of them, much less be able to synthesize the data in their own heads to reach meaningful conclusions. Thus, I would strongly recommend that the authors provide some kind of quantitative synthesis of the problem in this section (i.e. What percentage of shortcut citations can ultimately be traced to the original reference? What’s the average number of steps? What percentage is behind a paywall? What percentage reaches a dead end or an insufficient description?).<br /> I note that 15 articles are probably too few for this purpose, and that the sample of articles in which citations are followed would have to be expanded. Thus, I would recommend that the authors perform a sample size calculation to reach the number of citations/articles that can provide reliable estimates within a given confidence interval. For this purpose, it’s worth noting that it would be desirable to perform synthesis both at the level of citations (i.e. what percentage of citations in the sample can be traced?) and at the level of articles (i.e. what percentage of articles in the sample have at least one untraceable citation?), as citations within a single article should not be considered as fully independent units when it comes to representing the whole population of citations. Thus, using articles as units for the purpose of sample size calculation might be the better option.

Other general points:

• The categorization of scientific fields is somewhat strange: most people would probably consider neuroscience is a subfield of biology, so presenting both as separate categories may puzzle some readers. I understand that this is a consequence of the JCR categories used, but making this clearer from the start (e.g. “examine the use of shortcut citations in neuroscience, biology and psychiatry journals in the abstract) and perhaps referring to the biology journals as “general biology” would help to avoid confusion.<br /> Still on this point, the selection of fields is narrow and ad hoc. I understand that this is a limitation posed by the authors’ own expertise, but it is nevertheless one of the main weaknesses of the manuscript. Thus, the narrow range of scientific fields examined should probably be mentioned in the limitations section.

• Even within this relatively narrow sample of fields, the kinds of methods that deserve a protocol probably varies a lot: I’d guess that psychiatry journals include a lot of surveys and instruments, while biology and neuroscience might have predominantly wet lab protocols. It would be interesting if somewhere in the paper (possibly in the example cases provided) we could get a feeling of what kind of “protocols” we are talking about, even if only in a general sense. If quantifying/classifying them is not feasible, at least some illustrative examples could be provided. Are we talking about methods to quantify proteins? Scales to measure depression? Electrophysiology setups for rodents)? The citation culture probably depends a lot on the particular method, so the whole discussion sounds a bit disembodied without touching on this point somewhere.

• Why are only minimum/maximum numbers of citations within shortcuts and the youngest/oldest citation coded? This looks like an approach to simplify data extraction, but it ends up providing very limited information (i.e. especially if there are many citations per paper, the oldest and youngest ones give very little information on the actual range).<br /> Moreover, this ends up making data visualization in Fig. 3 much less intuitive than it could be (i.e. it would clearer and more informative to provide the full range of citation ages). If the authors could provide the full ranges (although I’m not sure that this is feasible), this would likely strengthen the paper. If not, I’d reconsider whether Fig. 3 should be included in the main results, as I don’t think the results as displayed say much about the sample of citations as a whole.

• Some points in the case series description and discussion mention that some references “provided a description that was no longer state-of-the-art” and that this may be a problem. I don’t really get the idea here: methods citation are supposed to provide an accurate description of what was done in a study, not of what’s the current state of the art of the method. In this sense, descriptions shouldn’t age badly or become “not-state-of-the art”.<br /> I understand the concern that a very old shortcut citation raises suspicions that it might not really describe what was done in the paper (as it may be likely that no one uses certain methods in exactly the same way after 50 years). But if this is what the authors meant, this should be stated more clearly, as it is not really the impression that comes out of reading these passages.<br /> In the same vein, mentioning in the discussion that “supplemental methods cannot be updated” is technically correct, but is not a limitation in terms of making methods sections reproducible (which seems to be the point of the paper). For the purpose of methods description, whatever was used in a paper should remain static, even though the method may evolve in subsequent study.

• In terms of data sharing, one thing I could not find in the manuscript or in the OSF was the DOI and title of the articles used as case studies in Fig. S2. I may have missed it, but as there was no folder for the case series section I didn’t know where to look for it. As this seems important for reproducing the findings, this list should be provided somewhere (possibly as a document within the OSF) and cited within the text and legend to figure S2.

Minor points:

Introduction:<br /> - The correct name of the project mentioned in the first paragraph is Reproducibility Project: Cancer Biology (not “for Cancer Biology”).

• “This risk of bias for randomization sequence generation and allocation concealment was unclear…” – this sentence seems odd (in particular the “This” at the start), please revise the wording.

Figure 1:<br /> - Isn’t the methods section a viable alternative for sharing details needed to reproduce experiments as well? While I agree that in many cases a separate protocol may be a better option, that depends on the length of detail that is needed, which will vary greatly depending on the method. Therefore, I would argue that the methods section should be included as an option in the figure – saying that the information “should” be shared in a separate document sounds overprescriptive.

• The second “readers” can be omitted from the third sentence of the figure legend.

Methods:

• Instead of citing the full OSF page for “protocols, data and code for the prevalence study and journal policy studies” using a single link, wouldn’t it make sense to cite a specific DOI for each of these resources? The same thing hold for points in the text in which specific resources are cited (e.g. “The full search strategy is available on the OSF repository” could point to a direct link to the search strategy rather to the full OSF page).<br /> I think this is optional, as the Readme files in the OSF are clear. But providing specific links to each resource would be more consistent with the authors’ recommendation of providing pages for book citations, for example (in the sense of sparing the reader the trouble to search for a resource within a larger space).

• What is meant by “top journals” exactly? Are those the ones with the highest impact factor in the JCR in their specific fields? Although this would be my guess, it is not clear from the description.

• The data on whether papers were related to SARS-Cov2 sounded rather gratuitous, as Covid-19 was not mentioned anywhere in the introduction. If this data is to be kept in the paper (I personally don’t think it adds much), the rationale for extracting this should be mentioned somewhere.

• Though this eventually became clear, I initially had a hard time to understand what was meant by “number of citations per shortcut”. This could be made clearer when this variable is first introduced.

• The description of a probable shortcut states that “additional details are not provided in the following sentences or elsewhere in the methods sections”. But what happens if the method is fully explained outside of the methods section (i.e. in the supplementary material or in a repository)? I was unsure how these cases were classified, so it’s probably worth commenting explicitly on it.

• Electronic searches were performed using the terms “[journal name]”, “journal citation reports ranking”, “author guidelines”, “journal policy”, and “impact factor”. I don’t quite get what this search means to achieve. Why would one need to search for “impact factor” to look for policies?

Results:

Figure 2:

• The different areas have different mean numbers of methods citations per paper (being somewhat higher in Biology). Thus, showing the results for different categories in percentages as in Fig. 2A may cause misleading impressions – although there are still less “How” citations in Biology than in Neuroscience or Psychiatry when measuring absolute numbers, the actual difference is smaller (while that in “Who or what” citations is even larger). Having the bars represent absolute numbers (possibly still displaying the percentage within the bars) – with overall longer bars for Biology – would likely provide a more accurate impression of what’s going on.
• It took me a while to understand the right panel in Fig. 2B. While the fact the two sides of the violin plots represent different data eventually becomes clear, wouldn’t it make it easier on the reader to break the information for probable and possible citation into separate plots (especially as the left panel uses symmetric violin plots)?

Tables S5 and S6:<br /> - Can’t the information in these tables be included in the legend for Fig.2 and Fig.3 (as it is relatively short and essentially synthesizes the data in the figures)? This is optional, but would leave the information in one place instead of creating a lot of supplements.

Figure 5:<br /> - Are the categories in Fig.5A and 5D mutually exclusive? It would seem to me that a journal could encouragd providing sufficient methodological details both in the author guidelines and as policy, and that they may encourage sharing methods in more than one place (i.e. repository or supplemental files). This is likely worth commenting on in the legend.

Discussion:

• I don’t think the Germany and California examples mentioned in Box 1 are needed: there are plenty of places of the world with much worse access, and these particular examples are not particularly representative of difficulties faced by the world at large.

• While I agree with the recommendation to “make all methods publications open access”, I don’t think that there’s any particular reason why methods papers are different from the rest of science (in the sense that they should be open access), so I’m not sure the recommendation really belongs here.

• The discussion about copyright issues described in the list of recommendations is long for an item in a list. Thus, it probably would fit better in the main text or in a box.

Table S7:<br /> - I get the feeling that Table S7 would read better if lines and columns were reversed (i.e. methods as lines, features as columns), but it may be a matter of taste.<br /> - Why are supplemental files and protocol journals deemed static while shortcut citations are not? This does not make much sense to me.<br /> - I’d say supplemental files would generally be expected to have been peer reviewed. I agree that this is likely not always the case, but that probably depends more on the reviewer than on the journal (e.g. I don’t know of journals that explicitly exempts supplementary material from the peer review process), so I’d remove “depending on the journal”. <br /> - The comment “protocols remain available over time” made for repositories stands for all categories – it makes sense when comparing a protocol repository to a lab notebook, not to the other forms of describing protocols. Thus, I’d probably not include it as an advantage here.<br /> - I’d argue that both shortcut citations and supplemental files are “findable” for whoever’s reading the paper (which is likely what matters here), so I’d be inclined to remove this category. <br /> - Clinical journals are not the only one to publish protocols as articles (the systematic review community has a tradition of publishing protocols, for example).

Figure 6:<br /> - In the last no/no option, describing the method in the main text (if it is simple enough to fit) should also be included as an alternative.

On 2022-09-22 21:33:39, user Jason Shepherd wrote:

The question of how information is stored in neuronal ensembles during learning and memory has recently become accessible with IEG tagging approaches. How precisely tagged ensembles relate to the engram, or memory trace, is still not clear. Another important question is how do tagged ensembles mature or change over time and what is the precise engram that is required for remote memory recall. This preprint shows strong data supporting the idea of overlapping, but distinct ensembles involved in recent and remote memories. The authors show that tagged ensembles change their network connectivity over time, using innovative viral tracing techniques. For example, dCA1 neurons that project to the ACC are more likely to be engram cells at remote recall than recent recall timepoints, and fewer ACC to dCA1 cells are active at remote recall compared to recent recall time points.

We think there are some additions that could be made to improve the conclusions and data presentation:

1.Showing individual data-points for all bar graphs would improve the interpretability of the data throughout the paper. We also noticed that in some experiments, the N values for controls vs manipulated/activated animals is vastly different (eg Fig. 4).

1. Include individual statistical tests in each figure/panel.

3.The authors quantify the overlap of engrams tagged at different time points by calculating the overlap compared to expected overlap. While this is useful to show that Fos-tagged ensembles are not random, we believe it is important to also include the absolute percentage of overlapping cells to determine the similarity of engrams. It appears from the IHC images that the absolute overlap is a low percentage of the total number of neurons tagged as engram cells at any particular timepoint. This should also include the total % of Fos-tagged cells in each experiment. Since the total % would greatly alter the expected value by chance. Indeed, in many cases it seems that there is less than the expected chance value indicating that ensembles are not activated randomly but may be distinct.

1. We appreciate the design of the first set of functional experiments where 4-OHT is administered during recall (Fig 1K). This approach shows that the same cells active in the recent recall engram are those inhibited by CNO a month later at the remote test. To take this experiment one step further, one could add a group where 4-OHT treatment is administered 2 days post-acquisition without a recall test, or with a recall test in a different context, and evaluation of fear conditioning at the remote time-point. This would be a convincing way to show that CNO is not simply inhibiting enough neurons to block the remote memory, but rather that it is the activity of those specific neurons in the original recall engram which are necessary for remote recall.

Review made by Shepherd lab members

On 2022-04-11 16:37:49, user Leslie Kay wrote:

This is a review I posted on Qeios, thinking it was biorXiv asking me for the review. (Aside: Can someone explain to me what Qeios is, and how it's related to open access?)

This paper tests the hypothesis that the olfactory bulbectomy (OBx) model of major depressive disorder (MDD) is caused by a lack of OB gamma band oscillatory input to the limbic system. OBx is a catastrophic surgery accompanied by significant blood loss and requires weeks of recovery. This leads to a confound with neurodegeneration. The current paper used DREADDs to silence the OBs bilaterally and chronically for several weeks. Additionally, they used short term silencing and cancellation / enhancement of gamma oscillations in an LPS model of MDD.

Several findings support the hypothesis that it’s loss of OB input to the limbic system that causes the depressive phenotype. There are some differences dependent on the type of silencing. The open field test (OFT) is the gold standard for OBx depression, with hyperactivity and avoidance of the center the classic behaviors indicative of MDD. With chemogenetic silencing, animals avoid the center but are not hyperactive, and they do not exhibit anhedonia. Short term silencing does the opposite - anhedonia but not OFT hyperactivity/center avoidance. These opposite results are interesting and may help get at different mechanisms for anhedonia and anxiety in the OBx model.

The authors use closed-loop stimulation locked to the gamma bursts in the OB to determine whether gamma burst activity in the PC reduces depressive symptoms. In the LPS model of MDD, they stimulated to either enhance or cancel out gamma transmission to PC from OB. Enhancing gamma reduced depressive symptoms in LPS, and blocking gamma by stimulating in antiphase with the OB gamma did not reduce symptoms. The authors conclude that loss of gamma is the cause of OBx depression.

I am not sure I agree 100% with their conclusions, even though I have no substantive criticisms with the methods and results. Amplifying gamma is sufficient to reduce symptoms, but does canceling it out tell us that it is gamma per se that causes the antidepressant effect? Canceling out gamma does stimulate the fibers going in to the PC but what does the antiphase stimulation do exactly to the PC? Are the same number of action potentials produced, or is the antiphase stimulation doing something fundamentally different to the PC inputs?

For the rest of my comments, I need to tell a story, one which I shared with Gyuri the other day. I reminded him of our conversation years ago, when I discussed the idea that OBx depression is due to loss of OB input to the PC and the rest of the limbic system. I envisioned a similar experiment to this one. A few years later we met again at Walter Freeman’s Festschrift in Tucson, the day after Walter had passed away. We discussed the idea again and I told him we were working on it. We never got anywhere with what we tried and Gyuri rightly went ahead. No hard feelings at all, and I am really glad that you all did such a great job on this.

I think there is a crucial piece missing though, on the provenance of this idea, and it comes from Walter. I shared with Gyuri way back when we first spoke about this idea one of Walter’s little-known papers, a 1968 J Neurophys article “Effects of surgical isolation and tetanization on prepyriform cortex in cats.” This paper was published the same year as the Becker and Freeman paper cited in this report. While the Becker and Freeman paper shows that PC activity changes when the olfactory bulb is removed, the single authored 1968 paper gets at its cause.

The origin of the idea comes from Walter Freeman, as most good ideas in olfaction do. In the 1968 paper, he bulbectomized cats and showed that a normal shock stimulus to the remaining LOT no longer induced the normal oscillatory evoked potential in the PC – there was a single peak in voltage dying off after one cycle. Two hypotheses were considered, 1) the OB drives the oscillation in the PC, when the LOT is stimulated it produces an oscillatory evoked response in the OB, which drives the same response in the PC, and 2) the OB input is necessary for the PC to produce an oscillation.

The second hypothesis was the one favored by his results. He replaced the missing OB with tetanic 200Hz low level stimulation of the stump of the LOT and then stimulated with the normal larger shock stimulus during a pause in the tetanic stimulation. Et voila, the oscillatory evoked potential was reinstated in the PC. This relatively obscure paper showed an important role for the OB – it provides abundant excitatory drive to the rest of the system, keeping everything in the right dynamic range. These results were replicated for the entorhinal cortex by Kurt Ahrens (Ahrens and Freeman, Brain Research 2001).

The rescue of depressive behavior with gamma enhancement in the LPS model in the current study is intriguing, and the cancellation effect of the antiphase stimulation is compelling. Would the same type of stimulation rescue a silenced olfactory bulb? If it does not, does this mean that different mechanisms are at play for different models of depression? The methods used here may be able to make sense of the mechanisms and usefulness of different models of depression for different types of treatment studies. Already the difference in behavioral effects among the several methods post some very interesting questions.

I appreciate the space to tell Walter’s story and the format of biorXiv that allows public discourse about research reports.

On 2021-10-14 16:31:13, user Colin Hawco wrote:

Overall important work but I'd like to raise some issues.

First the Destrieux atlas is not a functional atlas. People keep using these sorts of atlases in fMRI work and I have no idea why. The Superior temporal lobe is not a functional unit. That giant big mid-frontal region is not the DLPFC and not well overlapped with what may be reasonable activity patterns for tasks such as the NBack.

Also, the analysis appears to use Beta values from various contrasts. IME the average t-value is more reliable as a metric because it is (de)weighted by the noise in the voxel/vertex/region. In any analysis of general patterns of activity, I have found more robust using individual t stats rather than betas.

Also you included many contrasts, including several that have obviously lower ICCs, and in most of the paper appear to collapse across all regions and contrasts. For the Nback, I'd mainly focus on the 0 Bk, 2Bk, and most importantly, the commonly used 0vs2Bk contrast. Those look like they have relatively decent ICCs to me.

Relatedly in the figures you average across all contrasts, but some of them are not very good contrasts and as a result, your reported regional ICCs are dragged down. Rather than a take all approach, I think it would be better to focus on the primary contrasts as the ones being used.

I object to the use of ROI as regions which you found interesting when the entire analysis is based off an atlas; the more conventional use of ROI is parcels, etc, in the broader sense, rather than 'parcels I think are interesting versus those I think may be less interesting'. I'm being pedantic but it confused me.

(everything after this is me pontificating on things I think are interesting in general). <br /> Interesting and important point that contrasts vs baseline have higher stability than two task contrasts, but I also think we forget this is a truism. If you have an imperfect measurement, and subtract another imperfect measurement from it, the reliability of the difference must, by definition, be lower than the reliability of the two separate things (of I see this is mentioned later in the discussion).

Important that the SST and MID tasks had much poorer reliability. My opinion has between that reward tasks generally have very poor reliability, potentially because the signal is not strong enough, but also because people may vary quite a bit with themselves even how they respond to trials, and oscillate.

One point of potential import is that a lot of these analyses being done across the field are assuming task activation should be stable, but the brain, and fMRI, is inherently dynamic. Averaging activity by model fit across these relativity short tasks may not provide a very stable metric. Considerations of dynamic processes may yield greater information, but a big challenge there is motion (its always motion...) which makes dynamic measures really hard.

On 2021-09-20 11:28:54, user Aalok Varma wrote:

This preprint was presented at our lab journal club and we thought we’d start an open discussion about these results.

We would first like to note that it was a pleasure to discuss the results in this paper, which we found rather interesting, and we had a very fruitful discussion. Nevertheless, we had several questions and clarifications that we were hoping you would be able to help resolve:

1. Could you please describe a bit more in detail how exactly bouts are defined and how bursts and bouts are distinguished from one another in the processed VNR signal? Is there an interbout interval threshold set to separate bouts, for instance? If yes, what was the value used?

2. Proof of the idea of measuring conduction velocities using voltage imaging is neat. However, is there some validation of the conduction velocities, as measured by the sub-Nyquist interpolated spike timing (SNAPT) method? For instance, can you compare measurements of conduction velocity by this method with, say, measurements from dual recordings with downstream partners to compare the delay between activation of a cell and the arrival of a PSC? It is not perfect, of course, but given that actually recording from dendrites etc is so challenging in small preps like larval zebrafish, it would be a useful reference value for comparison of how accurate the SNAPT measurements are.

3. The analysis of Figure 4 involves sorting bouts as those having >50% of active V3. This is a rather arbitrary classification, especially since there aren’t too many neurons per field of view so the difference between 40% and 60% might be just one neuron or so. Why not go the other way around, and first classify bouts as strong/weak and then ask what fraction of V3s was active, across all trials, by plotting bout strength against % of V3 active as a scatter plot? Moreover, we have some concerns with the definition of bout strength. Taking the average cumulative value as the bout strength doesn’t really capture the true bout strength, in our view, since it only captures amplitude, and not so much duration. In Fig 4A (bottom), for instance, bout #2 looks much weaker than bout #7 (which is longer). Yet, their computed “bout strength” is very similar. Why not use Area Under the Curve as a proxy for bout strength? It would capture both amplitude and duration in the definition of “strength”. This analysis may not change the results or the overall story, but is a more objective way of analysing the data, we think.

4. From the representative plots shown in Fig 5C and D, it seems that when V3 neurons’ activation is turned off, the bout ends. Yet, from the earlier figures, it seems that V3 activity is sustained even after a bout ends. Is it possible with the resources available to perform acute inhibition of these neurons during a bout, to test if shutting their activity suppresses swims? It would lend support to the hypothesis that V3 activity sustains bouts?

5. The switch to free swimming with optomotor response for the experiment in Fig 6 wasn’t very clear. Moreover, we don’t agree with the interpretation of the result about bout speed modulation in Fig 6C. From the raw data points, the distributions seem largely overlapping, and the difference being detected may simply be because of the large difference in the sample sizes between the control and the ablated groups. Also, how about doing the ablation experiment using the same paradigm as in Fig 5? That way, results may be easier to compare. Furthermore, it is interesting that there is no difference in bout durations in vivo with V3 ablation, although all previous experiments suggest that one should expect a reduction in bout duration on V3 ablation. This may be because of functional compensation/adaptation because of a genetic ablation of V3 neurons from birth. Hence, it may be better to perform acute inhibition in the V3 population during free-swimming OMR, provided you have lines to do the same.

Other general comments:<br /> 1. Could the legends please include all n’s, as appropriate? Some legends have it, others don’t. It would make the reading much easier.<br /> 2. Fig 1G and Supplementary Fig 3 - clarify the dorsoventral axis schematic. What does 0-1 mean - as in, which is ventral and which dorsal? I think 1 would be ventral, given that active motor interneurons seem to be positioned that way, but a clarification is needed and would make the figure easier to interpret.<br /> 3. Could you please describe the filters being used in a bit more detail, instead of simply stating “high-pass filtered”? What filter type was used (Butterworth, etc.)? What were the cutoff frequencies (sometimes time constants are mentioned, but it would be better to be consistent in the reporting of these details)?<br /> 4. In the introduction, it is stated that “adapting motor output can also happen via changes in tail amplitude or force, without substantial changes in frequency.” Recent work from our lab - Jha and Thirumalai (Current Biology, 2020) - has supported this claim, and we have also shown using whole-cell recordings that this can be explained by changes in the intrinsic properties and recruitment of primary motor neurons at lower speeds. We hope you go through our paper and find it useful, in which case a citation of our work would be much appreciated.

We hope you find some of our comments useful, and we eagerly look forward to hearing back from you.

Thanks in advance.<br /> Best,<br /> Aalok Varma<br /> Neural Circuits and Development Lab<br /> National Centre for Biological Sciences (NCBS),<br /> India

On 2021-07-15 04:53:29, user Derek Beaton wrote:

Overview of “On stability of Canonical Correlation Analysis and Partial Least Squares with application to brain-behavior associations”

Derek Beaton, PhD<br /> Director, Advanced Analytics <br /> Data Science & Advanced Analytics (DSAA)<br /> St. Michael’s Hospital, Unity Health Toronto

This manuscript provides an in-depth look at reliability and stability of CCA and PLS through the use of a generative modelling approach with synthetic data (and their software gemmr), and subsequently show CCA and PLS applied to large and modern brain-behavior data sets (HCP, UKBB). The manuscript also provides multiple perspectives: (1) assessment of brain-behavior CCA & PLS when sample sizes change for the number of features, (2) a meta-analysis/review of brain-behavior CCA studies, and (3) tools, suggestions, and advice on how to approach interpretation of CCA & PLS-based studies for brain-behavior neuroimaging studies. There is a substantial amount of work and the contributions of the manuscript are quite valuable. Overall I think this is a strong manuscript and there are many good things about this paper and the software.

However I focus my review on my concerns. I think if some of these are clarified or responded to, then the paper would possibly be stronger and clearer. Below I first bullet point my primary concerns with the manuscript, and how those concerns relate to the overall conclusions and generalizability of the work. Following that, I provide my other concerns generally in order of appearance in the manuscript.

My first major concern is that the manuscript generally reads as potential limitations of CCA and PLS. However, only these two methods are discussed and, I believe, that the core issues of stability (and generalizability, replicability, etc…) in neuroimaging are because of (1) small samples, and (2) noisy measurements. So are the issues presented exclusive to CCA/PLS? Or should we expect to see the same effects in other techniques (e.g., standard GLMs, multivariate regressions, statistical/machine learning approaches such as SVM or random forests)?

While comparing CCA and PLS is (very, very) useful for many fields, especially neuroimaging, I believe that some of the comparisons here are in effect unfair. In particular, CCA doesn’t really work without extra preprocessing to data when those data have more variables than samples. CCA effectively requires us to reduce the dimensionality of data so that we have more samples than variables or to allow us to invert X’X and/or Y’Y. However, PLS does not require additional preprocessing in order to work (correctly). The pipelines for the data were designed around the limitations of CCA but applied to both PLS and CCA. How does PLS perform when these extra steps are not taken? Effectively, how does PLS vs. PLS with CCA-friendly data vs. CCA compare? Though I comment on it more later, I believe that the observed “bias towards the first principal components” in the PLS results may be due to this.

Taken together, I think the general conclusion to take away from the manuscript is that these are the behaviors and limitations of CCA/PLS under these specific conditions, but not necessarily any condition. I expand on this in additional comments and provide some references throughout.

Abstract:

You’ve noted that the “Application of CCA/PLS to high-dimensional datasets raises critical questions about reliability and interpretability”. Perhaps a small but important distinction here is that these techniques provide a lot of things to interpret, but comparatively are relatively easy to interpret (they are interpreted like PCA). I think there should be a de-emphasis of interpretability and most of the emphasis on reliability and stability. To note: these techniques are still easy to interpret even when results are not reliable (which is, perhaps, a drawback of their use).

I apologize for the following comment as it will be repeated a few more times, but I believe that “For PLS [there is a] bias toward leading principal component axes.” is more likely an artifact of how the data were prepared for use in PLS and not strictly a drawback of PLS. If both X and Y data sets are principal components (which include their subsequently decreasing variance), then PLS will (correctly) pick up on those “variables” (components). This is particularly true if/when data submitted to PLS are not normed or scaled in some way (which principal components are likely not, as that destroys the inherent variance in the principal components).

Introduction:

I think “the dominant latent patterns of association linking individual variation in behavioral features to variation in neural features” would be better rephrased as “the dominant common latent patterns shared between behavioral and neural features”. Or something along these lines as it’s a bit clearer and doesn’t emphasis linking one thing to another thing (as this sounds a bit directional, where CCA and this flavor of PLS is symmetric)

When you say “[...] a number of open challenges exist regarding [CCA/PLS] stability in characteristic regimes of dataset properties”, I wonder if it’s more appropriate to also discuss the open challenges of the data themselves. Noisy instruments and measurements are difficult to analyze with most approaches, and this isn’t a problem for just CCA and PLS. In effect, do we have data that are stable and reliable?

I find the mixtures of terminology difficult to follow. Could you provide a clearer set of definitions for terminology, and then stick specifically to certain terms? You’ve mentioned both the SVD and eigendecompositions. It might make things clearer to connect CCA & PLS terminology directly to SVD/eigen results, and just use those terms instead. For one particularly confusing example: “weights”. I’m not sure what “weights” are to mean here, especially because “weights” has so many meanings in stats/machine learning.

I think the discussions of stability rely too heavily on relatively older literature (e.g., references 10-12) which are also generally from other domains. The same points from those are likely still true (or even more so in larger and noisier data) but I think more modern works that directly discuss high dimensional problems would be helpful. Furthermore, these generally discuss CCA and not PLS. So additional literature on PLS here would be good.

For reference 13, the manuscript says “cross-validated association strengths that are markedly lower than in-sample estimates”. Isn’t that expected based on this (and other) work? Should we not expect the smaller sample sizes (e.g., folds) to produce lower (or less stable) estimates?

To echo a previous point: most of the literature discussing (in)stability is for CCA and not PLS. This should be clarified or further supported.

Though this work is important and well done, I don’t think it’s fair to say “to our knowledge, no framework exists [...]”. There has been a lot of work on the systematic assessment of these techniques, and the SVD/eigen in general. Could you clarify this a bit more? Or instead show that this is an additional element in our understanding of CCA/PLS behaviors? The field of chemometrics in particular has an extensive literature on the stability of PLS (although typically the regression flavor, not the PLSC flavor here).

I think this is misleading and possibly incorrect: “CCA and PLS differed in their dependences and robustness, in part due to PLS exhibiting a detrimental bias of weights toward principal axes”. PLS may exhibit this behavior under these data processing conditions (which are required for CCA, but not for PLS).

Another repeated point: the manuscript says that “typical CCA/PLS studies in neuroimaging are prone to instability”. Is this because of CCA/PLS? Are other techniques also unstable? Is this because of the data?

Results:

“Number of features” as the additive number between X and Y is strange, because each set has a different number of features. And the sizes of X and Y (as well as their internal covariance structures) can have substantial influence on the results. For example, if X were only 1 or 2 (strongly correlated) measures and Y had many 100s or 1000s of measures, then the (joint) solution is fairly limited and (to a degree) constrained by X.

The finding of the “average of the cross-validated and in-sample” results struck me, especially given that the bootstrapped results didn’t converge to the expected estimate (but the previous average did). I didn’t expect this, but I think it’s a positive finding. Could you provide more details on these procedures, and could you possibly explain these behaviors/findings in more detail?

Why are you quantifying error as the greater of the two errors (X and Y) from their true weights? Why not present them separately? That would tell us if/how CCA/PLS can estimate one set but perhaps not the other.

I don’t follow what the authors did to get around the sign-flips in the results. The manuscript says “it is chosen to obtain a positive between-set correlation”, but I’m not sure what this means here.

To repeat a previous point about terminology: the term “loadings” has many meanings, too. Here it seems the authors used the correlation between datasets and scores, correct? These correlation loadings are one type of loading, where, say, the singular/eigen vectors are another type of loading.

Why switch between Spearman and Pearson correlations for the distance estimate for the various scores? Why not both in both cases or choosing one?

I find Figure 3---in particular panels A and B---unclear. First, it’s not entirely clear to me what “weights” and “feature id” convey here. Figure 3B seems to show that PLS weights are spherical. This is not what I would expect from PLS. Could you explain these results in more detail?

A reiterated point: The description of what it means for PLS to converge to “the first principal component” is unclear. The first principal component of what? There are two data sets (X, Y) that are sets of PCs (if I am understanding correctly).

I think the permutation tests may be too conservative and/or incorrect (as described in CCA/PLS analysis of empirical data). While it is typical to permute just the rows of one matrix vs. the other, this is potentially problematic for CCA/PLS. That’s because each X & Y has an internal covariance structure. If at least one of those structures is strong, then the results will resemble the strong internal structure. This is particularly true when, for example, behavioral data are already very correlated. So a more appropriate permutation may be within each column of the data matrices. However, this is only appropriate in the original data matrices. Permutation should not be done on the PC scores (I am presuming that was the case, but please correct me if I am wrong).

For the line that starts with “After modality-specific preprocessing (see Methods)”, I will reiterate and expand on one of my sticking points. CCA requires invertible or rank reduced matrices when there are too many variables but PLS does not. So to reduce specifically to 100 PCs is a limitation of CCA. PLS does not require this. How would the results change if PLS were run directly on the data? Furthermore, 100 principal components is not informative nor a meaningful choice. How many total components were there? How much variance did 100 components explain? Could just 10 or 20 components explain almost as much variance as 100? For analyses based on PCs, it is important to select based on something meaningful: that could be explained variance or by performing tests on the PCs themselves for selection. Though almost any approach is somewhat arbitrary, to select 100 is seemingly unmotivated or unguided.

In Figure 4, how are you computing 95% CIs from permutations? Permuations are for null distributions, not distributions around the effects (CIs). I would expect other resampling approaches (e.g., bootstrap) to provide CIs.

By the time I get to Figure 4, I’m wondering why are the CCA and PLS results not directly compared? As in, why not present, for examples, correlations or other similarities between the CCA & PLS results? I think it would be important to directly quantify the similarity between CCA & PLS results.

Later in the manuscript, you indicate that you “considered reducing the data to different numbers of principal components than 100.” While this is certainly a benefit, the description of the results is unclear. You indicate that “Retaining more than 10 behavioral PCs lead to marginal increases [...]”. But 10 here is not informative. How much variance was explained by those 10? By the 100? How much is explained by 1 PC? The total number of PCs is not particularly informative, rather, the amount of (cumulative) explained variance, the number of retained components, and the total number of possible components makes for something more informative.

Discussion:

The authors mention that CCA is (more) attractive (than PLS) because it’s scale invariant, which is nice when measures are not commensurate. However, when data are normalized or scaled (e.g., z-scored), then data are commensurate. Did you use normed or scaled data for PLS? How would that change the conclusions about commensurate scales and CCA’s scale invariance?

You mention in limitations that you “assume data are described in a PC basis” and then you “expect that a dataset whose features have been rotated into a new coordinate system by an orthogonal transformation matrix to have the same sample size requirements as the untransformed dataset.” In this particular case for PLS: you don’t need to assume that. You can run the same pipelines you have with the untransformed data to see how CCA vs. PLS vs. (untransformed) PLS compare. This would provide a very interesting case regardless of the results (whether the sample size requirements are the same or different).

You say that the generative model points out the pitfalls of CCA and PLS. Could you also apply this generative approach to other techniques, even simple linear models? Do the pitfalls also exist there? Are these pitfalls of the methods, or are these pitfalls reflective of the kinds of data we analyze?

You note that there are regularized versions of CCA and PLS to “mitigate the problem of small sample sizes”. I have two issues (one small, one a bit bigger) with this statement. Regularized (and penalized, and sparsified, etc…) methods are not necessarily designed to allow for small sample sizes. Rather they help with mitigating overfitting (which sometimes could be due to too small of sample). My second issue is that the line between CCA and PLS becomes especially blurred, and even disappears, when it comes to regularized techniques. In particular, we should look to Witten et al.’s penalized approach for CCA. Witten et al., note that “[in] high dimensional problems, treating the covariance matrix as diagonal can yield good results” where they reframe their CCA equation (4.2) and in a different way, where their “penalized CCA criterion, [they] substitute in the identity matrix” for X’X and Y’Y in their equation 4.3. Witten et al., then further note that their CCA “is simply [eq. 2.7] with X replaced with X'Y”. That means that when it comes to penalized CCAs, most drift towards or even start out as PLS. This can make any suggestions as to which is better (CCA or PLS) moot as in the penalized approaches, they are effectively much closer to one another than in the standard approaches. (Furthermore, using a subset of PCs for each data set is, effectively, a soft form of regularization.)

Though brief, I think you’ve placed too much emphasis on PLS regression as being “conceptually different from PLSC/PLS-SVD” because in virtually all implementations of PLS regression, the first component/latent variable is identical to PLSC’s first component/latent variable. This is because both approaches model X’Y and (in most cases) use the SVD to do so. It’s just that PLSC is one pass of the SVD (so effectively a PCA of X’Y) where as PLSR is iterative, deflates X and Y in each iteration, and (asymmetrically) emphasizes certain properties for X (e.g., orthogonal latent variables for X, but not necessarily Y).

Methods:

The approach to the behavioral data is not particularly realistic when it comes to studies, is it? In most cases some form of imputation would be used and the behavioral data in particular would be directly used, not a projection (PCs) of the data. Would the behavioral PCs change substantially in your pipeline if you were to impute instead of using the method you did?

References and literature:

Below I provide some references and literature to supplement some of my points and to help strengthen some of the points you’ve made in the paper. Please note that some are mine. I’m not providing my (or the other) citations because I want them to be or am expecting them to be cited, rather these are for reference. Furthermore, these articles also provide quite a bit of citations that are worth looking into.

These two articles provide more unified perspectives on PLS, CCA, and many related techniques. The Borga et al., article is quite a good one. I provide my article moreso for the supplemental materials (https://www.biorxiv.org/con... "https://www.biorxiv.org/content/10.1101/598888v3.supplementary-material)"). In my supplemental materials, I further unify and generalize more approaches like the Borga article. Both of these show (at least algebraically) that these techniques can be thought of as variations of one another, and in some cases not very different.

Borga, M., Landelius, T., & Knutsson, H. (1997). A unified approach to pca, pls, mlr and cca. Linköping University, Department of Electrical Engineering.

Beaton, D., Saporta, G., & Abdi, H. (2019). A generalization of partial least squares regression and correspondence analysis for categorical and mixed data: An application with the ADNI data. bioRxiv, 598888.

To further emphasize why CCA/PLS can be very different or very similar, please see another one of my articles (see below). Like above, most of this article can just be skipped. Starting in section 4 on Page 22, I show CCA, PLS, and reduced rank regression (RRR) because they are all variants of one another. In Figure 5 the data are centered and scaled, and each technique produces comparable results. In Figure 7, however, the data are only centered and produce different results. This highlights that when norming/scaling, CCA and PLS can in fact be more similar than different:

Beaton, D. (2020). Generalized eigen, singular value, and partial least squares decompositions: The GSVD package. arXiv preprint arXiv:2010.14734.

Some recent work has been published to show what happens to results when sample sizes are small and as sample sizes change:

Grady, C. L., Rieck, J. R., Nichol, D., Rodrigue, K. M., & Kennedy, K. M. (2021). Influence of sample size and analytic approach on stability and interpretation of brain-behavior correlations in task-related fMRI data. Human brain mapping, 42(1), 204-219.

The above article is an interesting companion to yours because it shows that there is an advantage to multivariate over univariate techniques because multivariate approaches provide consistent (stable) results. However, Grady et al., concluded that small samples wouldn’t be sufficient to get reliable results, regardless of approach.

These would be more suitable PLS articles to reference, especially for neuroimaging:

Krishnan, A., Williams, L.J., McIntosh, A.R., & Abdi, H. (2011). Partial Least Squares (PLS) methods for neuroimaging: A tutorial and review. NeuroImage, 56, 455-475.

Abdi, H. (2010). Partial least square regression, projection on latent structure regression, PLS-Regression. Wiley Interdisciplinary Reviews: Computational Statistics, 2, 97-106.

McIntosh, A. R., & Mišic, B. (2013). Multivariate statistical analyses for neuroimaging data. Annual review of psychology, 64, 499-525.

McIntosh, A. R., & Lobaugh, N. J. (2004). Partial least squares analysis of neuroimaging data: applications and advances. Neuroimage, 23, S250-S263.

McIntosh, A. R., Bookstein, F. L., Haxby, J. V., & Grady, C. L. (1996). Spatial pattern analysis of functional brain images using partial least squares. Neuroimage, 3(3), 143-157.

Additional PLS & CCA articles:

Gatius, F., Miralbés, C., David, C., & Puy, J. (2017). Comparison of CCA and PLS to explore and model NIR data. Chemometrics and Intelligent Laboratory Systems, 164, 76-82.

Goodhue, D. L., Lewis, W., & Thompson, R. (2012). Does PLS have advantages for small sample size or non-normal data?. MIS quarterly, 981-1001.

To determine the number of PCs especially when detecting the space to interpret (which applies to PLS and CCA):

Peres-Neto, P. R., Jackson, D. A., & Somers, K. M. (2005). How many principal components? Stopping rules for determining the number of non-trivial axes revisited. Computational Statistics & Data Analysis, 49(4), 974-997.

On 2021-06-10 08:38:06, user Sebastian Dresbach wrote:

Dear Xingfeng Shao, Fanhua Guo, Qinyang Shou, Kai Wang, Kay Jann , Lirong Yan, Arthur W. Toga, Peng Zhang and Danny JJ Wanga,

We have discussed the manuscript entitled “Laminar perfusion imaging with zoomed arterial spin labeling at 7T” in the Maastricht layer-fMRI seminar on Monday June 7th. In this letter, we would like to share a summary of our discussion points.

The manuscript describes a sophisticated study about the implementation and application of functional layer-dependent CBF mapping in sensory and motor cortex. The authors use a pseudo-continuous ASL sequence with an optimized (relatively superiorly aligned) labeling plane and locally-focused 3D-GRASE readout at UHF. The method is validated with previously described “test-tasks” that evoke laminar-specific modulations in vascular responses.<br /> The study addresses one of the most pressing questions of the emerging field of human layer-fMRI. Namely, how to efficiently capture layer-specific signal changes that resemble laminar-specific neuronal activation changes. Thus, we believe that this manuscript will be of wide interest to the field.

The study increases an already long list of non-BOLD layer-fMRI method studies that are currently being published in the field. This study stands out in the sense that it provides more than “just” a usable MRI sequence with extremely clear interpretable layer-profiles. It also shows expected modulations of activation changes for subtle task modulations of sensory feedback into the primary motor cortex, as well as attention modulations in V1.

Some of the specific findings of the study are:<br /> -> The relative CBF change at these laminar resolutions can be as large as 150-200%. This is an extremely valuable piece of information to know in the field of laminar signal modeling. This will help with the interpretation of CBV results and it will help the with understanding of the vascular physiology in general. Until now, the field had to assume underestimated CBF-values from low resolution experiments (partial voluming), and from non-human animal experiments (anesthesia).<br /> -> pCASL is a usable sequence to study subtle cognitive modulations across depth within a conventional human neuroscience acquisition setting.

While there are a few specific points that the manuscript could be revised on, we are extremely enthusiastic about the manuscript.

Some aspects that lower our enthusiasm a little bit, refer to <br /> (i) the unclear influence of short-TI back-ground suppression, <br /> (ii) over-stated claims on novelty and superiority over other modalities, <br /> (iii) limited information about some methodological aspects, <br /> and (iv) the restricted data availability.

An itemised list of potential improvements is given below.

1.) Influence of background suppression is unclear.<br /> The authors use a single-inversion background suppression. Due to the long T1 at 7T, this background-suppression results in the fact that the CSF magnetisation is aligned along the opposite direction of the external magnetic field (negative phase). This results in signal cancellation at the superficial layers. While the control images (underlays of many figures) have a beautiful structural contrast, they exhibit a clear dark line of the transition between CSF and the superficial layers of GM. This might have substantial effects on the interpretation of the CBF profiles. With a net-negative phase of the z-magnetisation, an increase of CBF would result in a decrease of the MRI magnitude signal.<br /> Thus, for any voxel with partial voluming of CBF and GM, this might make the CBF quantification a bit tricky. For partial voluming of 50% and more, it might make the CBF quantification impossible? Given the nominal resolution of 1mm, this artifact might concern up to half of the cortical thickness. <br /> We would advise the authors to discuss potential influence of the background suppression as used here. <br /> Was the TI of the background suppression kept constant for all post-label-delays?

2.) Details about the “deblurring” in the partition direction can be extended.<br /> We applaud the authors’ efforts to acknowledge and account for the blurring in the partition direction of 3D-GRASE. Unfortunately, we are afraid that the method's description is not really sufficient to help us fully appreciate how appropriate and effective the method works.

On page 7, it is mentioned that partial Fourier sampling is applied in the partition direction and furthermore it is mentioned that variable refocusing flip angles are used. Furthermore, the spatial variance of non-180deg pulses will result in stimulated echoes and a sensitivity to T1 as well as local B1+. All of those features have substantial effects on the k-space signal evolution in the partition direction. However, based on the descriptions of the deblurring and based on the depiction of the simulated k-space signal (Fig. S5A), those effects do not seem to be incorporated in the deblurring model.<br /> We would advise the authors to comment on the limits of the used deblurring method and the potential of introducing artificial edge-enhancement features into the data. E.g. the ringing effect of the PSF in Fig. 4D might have the same spatial frequency as the layer-fMRI double peak in Fig. S5E. Is it possible that the edge enhancement-filter introduced layer-signatures across cortical depth based on the sharp border at the GM-CSF transition? Could the overcorrection of T2-blurring be responsible for the vertical stripes in the axial view of Fig. S5G?

3.) <br /> a) We don’t follow the claim about VASO’s lack of capturing absolute CBV changes.<br /> The authors claim that the proposed method is superior to CBV-based (VASO) methods because “VASO only measures relative CBV changes that may be confounded by different baseline CBV values across cortical layers” (page 3). This claim is repeated on page 7. <br /> We believe that this statement is untrue. VASO measures "absolute" CBV changes. VASO is sensitive to volume redistributions within the voxel. Thus, the percent VASO signal change refers to “absolute” physical units of ml of CBV change per 100 ml of tissue. The “relative” part about CBV changes does not refer to a normalization to baseline CBV, however it refers to the relativity of 100ml of tissue. This is identical to the “absolute” CBF quantification in ASL. The authors quantify their “absolute” CBF values in “relative” units (per 100ml of tissue). VASO’s lack of a baseline CBV quantification (without the use of multiple inversion times) should not be misunderstood as an inherent normalization of CBVrest.<br /> For more background about the “absolute” units of VASO in layer-fMRI, see Fig. 4 and section 4.4 in Huber et al., 2021, as well as Fig. 8 in Huber et al., 20215

Huber L, Poser BA, Kaas AL, et al. Validating layer-specific VASO across species. Neuroimage. 2021. doi:10.1016/j.neuroimage.2021.118195

Huber L, Goense J, Kennerley AJ, et al. Cortical lamina-dependent blood volume changes in human brain at 7T. Neuroimage. 2015;107:23-33. doi:10.1016/j.neuroimage.2014.11.046

There are plenty of VASO approaches from the Johns-Hopkins group, from NIH, and the Yale group quantifying absolute CBV changes by means of multiple TI’s.

Hua J, Qin Q, Pekar JJ, van Zijl PCM. Measurement of absolute arterial cerebral blood volume in human brain without using a contrast agent. NMR Biomed. 2011;24(10):1313-1325. doi:10.1002/nbm.1693

Ciris PA ksi., Qiu M, Constable RT. Noninvasive MRI measurement of the absolute cerebral blood volume-cerebral blood flow relationship during visual stimulation in healthy humans. Magn Reson Med. 2014;72(3):864-875. doi:10.1002/mrm.24984

Gu H, Lu H, Ye FQ, Stein EA, Yang Y. Noninvasive quantification of cerebral blood volume in humans during functional activation. Neuroimage. 2006;30(2):377-387. doi:10.1016/j.neuroimage.2005.09.057

b) Furthermore, the authors claim that due to the (wrongly presumed) CBVrest sensitivity of VASO, it fails to capture the fact that layers II/III have a stronger activation than layer Vb during finger tapping (page 5).<br /> This statement is not supported by the literature. A finger tapping task has been conducted in about a dozen layer-fMRI VASO studies and every single one shows a stronger activation in layers II/III compared to layer Vb. See the studies below, just to name a few:

Guidi M, Huber L, Lampe L, Gauthier CJ, Möller HE. Lamina-dependent calibrated BOLD response in human primary motor cortex. Neuroimage. 2016;141:250-261. doi:10.1016/j.neuroimage.2016.06.030

Beckett AJS, Dadakova T, Townsend J, Huber L, Park S, Feinberg DA. Comparison of BOLD and CBV using 3D EPI and 3D GRASE for cortical layer fMRI at 7T. Magn Reson Med. 2020:1-18. doi:10.1101/778142

Persichetti AS, Avery JA, Huber L, Merriam EP, Martin A. Layer-Specific Contributions to Imagined and Executed Hand Movements in Human Primary Motor Cortex. Curr Biol. 2020;30:1-5. doi:10.2139/ssrn.3482808

Chai Y, Li L, Huber L, Poser BA, Bandettini PA. Integrated VASO and perfusion contrast: A new tool for laminar functional MRI. Neuroimage. 2020;207. doi:10.1016/j.neuroimage.2019.116358

Huber L, Goense J, Kennerley AJ, et al. Cortical lamina-dependent blood volume changes in human brain at 7T. Neuroimage. 2015;107:23-33. doi:10.1016/j.neuroimage.2014.11.046

Guidi M, Huber L, Lampe L, Merola A, Ihle K, Möller HE. Cortical laminar resting-state fluctuations scale with the hypercapnic bold response. HBM. 2020;41:2014-2027. doi:10.1002/hbm.24926

c) In the paragraph on comparisons with VASO (first paragraph on page 7) the authors claim that “the proposed ASL fMRI is robust to potential BOLD contamination”. We believe that this claim needs further explanations and/or rephrasing. The authors use the CBF model in (Alsop et al., 2015), which does not account for T2/T2’ contaminations (and lacks any discussion of BOLD or functional imaging). The model in (Alsop et al., 2015) is in fact the one that was developed in (Buxton et al. 1998) and has been developed for much lower field strengths and different voxel sizes with assumed average vascular distribution. While we agree that the intra-vascular BOLD contamination is indeed negligible at 7T (maybe even with GRASE), we do not believe that the extra-vascular BOLD contamination around the microvasculature can be neglected at 7T. <br /> While layer-fMRI VASO studies account for such T2/T2’ contaminations, by means of a dynamic division, this extra-vascular BOLD contamination is not taken care of in this study. In the setup used here, the labeled water magnetization that permeated through the capillary walls (during the label condition and not during the control condition) will experience a T2/T2’ contamination during the readout and linearly scale the CBF signal.<br /> Maybe the authors can elaborate a bit about the reasoning behind the claim that their BOLD contamination is 1-2%. How was this number obtained?

Alsop DC, Detre JA, Golay X, et al. Recommended implementation of arterial spin-labeled Perfusion mri for clinical applications: A consensus of the ISMRM Perfusion Study group and the European consortium for ASL in dementia. Magn Reson Med. 2015;73(1):102-116. doi:10.1002/mrm.25197

4.) Claim about first in-vivo depth-dependent CBF dynamics. <br /> On page 5, the authors claim “this is the first time that the dynamics of labeled blood flowing from pial arteries, arterioles to downstream microvasculature is shown in vivo on the cerebral cortex”. This claim is repeated on page 3.<br /> Aside from our general hesitance to appreciate novelty as scientific value, we do not believe this statement is true. Please compare the reference below:

Zappe AC, Pfeuffer J, Merkle H, Logothetis NK, Goense JBM. The effect of labeling parameters on perfusion-based fMRI in nonhuman primates. J Cereb Blood Flow Metab. 2008;28(3):640-652. doi:10.1038/sj.jcbfm.9600564

Along those lines of claims on CBF dynamics, the authors might be interested in the fact that a number of other studies investigated and depict time courses of the temporal evolution of CBF. The manuscript at hand, however, does not show a single time course of the CBF dynamics.

Kim T, Kim SG. Cortical layer-dependent arterial blood volume changes: Improved spatial specificity relative to BOLD fMRI. Neuroimage. 2010;49(2):1340-1349. doi:10.1016/j.neuroimage.2009.09.061

Kashyap S, Ivanov D, Havlicek M, Huber L, Poser BA, Uludag K. Sub-millimetre resolution laminar fMRI using Arterial Spin Labelling in humans at 7 T. PLoS One. 2021;16(4 April):1-23. doi:10.1371/journal.pone.0250504

5.) The data are solely available given there is a MTA contract. Compared to other papers in the field, this is quite restrictive and highly unconventional. Without access to the sequence and the data, the impact of the manuscript on the field is substantially reduced. We would advise the authors to provide more details about the terms and conditions of the MTA.

6.) The nominal resolution of 1mm iso is unconventionally low for laminar fMRI. Even for non-BOLD laminar fMRI. We believe that the “proof is in the budding” and the shown specificity of the layer-profiles justify usability of the resolution used. However, we still think that the manuscript would benefit from a brief discussion on the laminar specificity across the two investigated brain areas (M1 and V1) with respect to the cortical thickness.

7.) The y-axis of %-perfusion changes in Fig. 2E and Fig. 3E are two orders of magnitude smaller than Fig. 4E. We assume there is a conversion to 100% missing? Maybe it does refer to a different baseline? Maybe %-perfusion in Fig. 2E and 3E are referring to % of units of M0? And %-perfusion in Fig. 4E refers to % of units of CBFrest?

8.) The figure key and the axes descriptions in Fig. S3 are hard to read in printouts of the figure. We had to zoom in quite a bit on the electronic version to be able to read them. We would advise the authors to align the panels vertically to cover more space on the page. The y-axis range of panel G has huge implications for the field and it would be a pity, if it stays unreadable.

9.) The qualification of M0 is unclear to us. The fact that the FAs are not exactly 180deg in the GRASE readout leads to stimulated echoes. While these stimulated echoes are helpful to obtain a better PSF and increase the signal efficiency, they introduce a T1 weighting into the final contrast. This means that (unlike single shot methods with very long TRs) the readout module itself makes it impossible to obtain a reference image without any T1-weighting (M0). We would like to encourage the authors to add a few details how they estimated the equilibrium z-magnetization with the 3D-GRASE radout used.

Scheffler K, Engelmann J, Heule R. BOLD sensitivity and vessel size specificity along CPMG and GRASE echo trains. Magn Reson Med. 2021:1-8. doi:10.1002/mrm.28871

10.) It is mentioned that the study would use a “segmented” readout. We find this terminology confusing. Are the authors referring to multiple excitation pulses per volume? If we understand the sequence correctly, we believe “partitioned” would be an alternative term.

11.) We are puzzled about the message of the depicted run-averaged motion traces in Fig. S7. What should the reader take away from this? Is it concerning that there are common motion patterns that are repeatable across runs? How many participants are averaged here? A more informative depiction of the subject-motion might be the average frame-wise displacement for all runs and participants? The manuscript might become clearer by revising this figure and/or removing it.

12.) We found Fig. S6 is quite puzzling too. While we are excited that the described methodology can be used for functional connectivity analyses, there are way too many open questions about the underlying processes and assumptions to just dump it in the supplementary material. This figure feels like a completely new study in itself that is pushed into a single figure caption. WE would advise the authors to provide more information about how this figure is generated and/or consider removing it?<br /> How should functional connectivity be interpreted, if there is no “resting-state”. Since the task data are used from M1 (dominated by the main effect), does it mean that the seed-timecourse resembles the block-design activation? Then, it refers more to a correlation-analysis of a block-design task than “functional connectivity”. How come that there are three slices shown sometimes with target regions, sometimes not? Where is the seed ROI? Does it span across cortical depth?

13.) We would advise the authors to be a bit more specific about the terminology of “BOLD”. Most readers might interpret this as the conventional GE-BOLD. Maybe the authors can rephrase it to “GRASE-BOLD” or “SE-BOLD”, or something similar? E.g. in the abstract introduction and some figure captions, if they agree?

14.) Performing pCASL is not trivial at 7T. While the authors circumvent many challenges with the superiorly aligned labeling plane, I feel that a successful replication of the experiment would require a more detailed description of the sequence parameters. What was the pulse shape, what was the pulse duration and inter-pulse interval? Gradient strengths? Does the yellow line width in Fig. 1B represents the bandwidth for a given flow velocity?

15.) The choice of ROIs. Both finger tapping and flickering checkerboard tasks usually evoke widespread signal changes along the hand knob of M1 and in the visual cortex, respectively. We appreciate that you show the corresponding activation maps in figures 4B and 5B. You also state on page 9 that you manually drew the CSF/GM and GM/WM outlines in the hand knob area of M1. In addition to that, it might be interesting how you chose your slices of interest or how the lateral extent of the ROI was defined. Is the pattern you show in the layer profiles in figure 4E to be expected along the entire length of the hand-know or only in certain segments?<br /> The same holds for the ROIs in the visual cortex for which the CSF/GM and GM/WM outlines were defined automatically.

Minor comments:<br /> PLD acronym is not introduced<br /> Page 6 reference to fig.6E - should be 5E?

With kind regards,<br /> Sebastian Dresbach, Omer Faruk Gulban, Renzo Huber

On 2021-06-09 20:58:11, user Jenny Zhang wrote:

Hi Dr. Tian, my name is Jenny Zhang and I am an undergraduate student studying biomedical research at UCLA. My classmates and I greatly appreciated reading your paper “Enhancing Mask Activity in Dopaminergic Neurons Extends Lifespan in Flies”. Your writing was very clear and the diagrams you provided in Figure 1A and 7A were very helpful in visualizing the experiments. For figure 1A, we were slightly confused by the different colors used for the dots. Providing a key for that aspect of the figure might be helpful in informing readers. Inspired by your diagrams, we think it would be useful to insert a diagram at the start of each set of survivorship curves to show how the experimental question differs in each set. The labelling in Figure 2 was very clear, particularly in the line drawn at 50% and the notation of p-values; we think it would be useful to standardize this format for the following figures to improve cohesiveness. In addition, standardizing the PAM/0273 notation may be useful as well. It may also be beneficial to use bar graphs (with number of days to reach 50% survival on the y-axis) for the survivorship data in figures 3 and 7. This could be an easy way to get the main findings across to readers. Lastly, we had the following lingering questions. What are the flies dying from that is avoided by Mask overexpression? What are the downstream effects of GPCR signalling in DANS? How is mask interacting molecularly with microtubules? A CoIP and western blot may be useful in determining the proteins that Mask interacts with.

On 2021-06-03 01:02:09, user marci_rosenberg wrote:

Precise and pervasive phasic bursting in locus coeruleus during maternal behavior<br /> Roman Dvorkin, Stephen D. Shea<br /> Biorxiv, April 1st, 2021<br /> Doi: https://doi.org/10.1101/202...<br /> Reviewed by Eszter Kish and Marci Rosenberg as part of the 2021 UCSF Peer Review minicourse with James Fraser

Summary<br /> In the central nervous system, noradrenergic signaling has been implicated in a wide variety of functions, including arousal, learning and memory, and, as this paper highlights, maternal behavior. While acute bursting of noradrenergic neurons has been shown to play an important role in goal directed behaviors, the timescale of the relationship between noradrenergic signaling and social (maternal) behavior is unknown since previous studies have relied on a mix of loss-of-function type approaches (e.g. knocking out the enzyme required to synthesize norepinephrine) and temporally imprecise recordings of noradrenergic activity (e.g. measuring release of noradrenaline while an animal engages in behavior). In this paper, the authors overcome these limitations of previous studies on maternal behavior by employing temporally precise recordings of activity of noradrenergic neurons.

In this article, the authors use a combination of electrophysiology and fiber photometry to evaluate the temporal relationship between firing of noradrenergic neurons in the locus coeruleus (LC-NA) and the stereotyped mouse female social behavior of gathering dispersed pups and bringing them back to the nest. Their major goals are to demonstrate that: 1) there is a phasic LC-NA response closely time-linked to pup retrieval; 2) this LC response is robust over time; 3) this response is not experience-dependent (i.e. present at full-strength upon first retrieval); 4) this response is linked to this specific behavior, and cannot be replicated by other similar types of behaviors (e.g. digging, retrieving a toy mouse, or receiving a food reward); 5) this neuronal response immediately precedes the behavioral output; and 6) LC-NA activity is correlated with locomotion speed only during pup retrieval.

The authors clearly succeed in providing sufficient data to support most of these conclusions, and the major success of this paper is using multiple orthogonal approaches to demonstrate the same, robust response.

The major weakness of this paper is a lack of sufficient context and framing, especially in the introduction and discussion. There are also a few technical concerns related to data presentation and statistics. We think these are easily addressable concerns, and ones that will demonstrably strengthen the significance of the paper, especially to a wider audience.

MAJOR CONCERNS

Technical:<br /> - Figure 6 uses log firing rates to quantify responses in some panels of the figure, while using z-scores in the other. This is concerning as the authors attempt to note differences in the results acquired by these two distinct techniques (ephys vs. fiber-photometry), with e.g. response of female’s LC to licking/grooming pup. Why not compare z-scores across both? If the authors wish to present data using both outputs, they should provide reasoning for the use of each metric and the benefits and drawbacks of each.<br /> - The authors should report the actual p-values of their statistical tests even if they are ‘significant’.<br /> - T-tests work under the assumption that your data is normally distributed. The authors should either confirm that their data is normally distributed or use a non-parametric statistical test that does not rely on such assumptions.

Context/framing:<br /> - The authors comment on a few possible points of significance in this study, including: 1) the link between phasic LC-NA activity and *social* behavior (highlighted in introduction); 2) the timing of phasic LC-NA activity related to behavior (highlighted in discussion); and 3) the uniform response of the LC associated with pup retrieval, which is a possible rebuke to the concept of a sub-specialized LC (highlighted in discussion). To enhance readability, we would encourage the authors to: 1) highlight the same point(s) of significance between introduction and discussion, and 2) spend a few more sentences in the introduction and, especially the discussion, really deliberately laying out ‘why this study matters’ to a generic neuroscientist.

MINOR CONCERNS

• The locus coeruleus is a pontine, not midbrain, nucleus
• What does half-max width of the PSTH mean, conceptually? Why is this a meaningful output measurement? Providing a brief textual description in manuscript or Figure 1 legend would enhance readability.
• Similarly, we would also welcome a brief textual description/explanation of the reasoning behind and methodological detail relating to the Z-score firing rate and the circular permutation analysis in Figure 2
• Why are all the means not centered around zero in the z-score scatter plots?
• Figure 3 looks at change in activity across days but not across individual trials. However, the heatmaps in figure 3 for P0 indicate that there may be some attenuation and temporal shift in the peak of the signal. It would be interesting to note whether this is consistent across animals as it would indicate that there is indeed change in the LC-NA responses across retrievals which would contradict the author’s current conclusions.
• For the electrophysiology experiments, the authors use each individually recorded unit as an independent sample. While their results are robust, they should potentially consider the use of nested statistics as this would be the proper statistical technique.

On 2021-03-04 13:55:35, user Johannes Franz wrote:

Dear Tim van Mourik, Peter J. Koopmans, Lauren J. Bains, David G. Norris, Janneke F.M. Jehee,

Thank you for posting your manuscript as a preprint. We enjoyed reading and discussing it in our layer fMRI journal club (Maastricht University). We would like to provide a few comments compiled from our discussion that we hope will be of use to you.

The manuscript describes a layer-fMRI study with a spatial attention task. The behavioral protocol follows a long tradition in the psychophysics of spatial attention, and the layer fMRI predictions stem from a well-established literature on the neurophysiology of attentional modulation in visual cortex studied with single units. Thus, we think that the experiment is perfectly suited for applications with layer-fMRI. The acquisition and analysis procedures include cutting edge methodologies and both data and analysis code is claimed to be openly available.

We believe a large readership will appreciate your investigation of the effect of spatial attention on laminar BOLD activation profiles in an orientation discrimination task, as well as your intention to drive the young field of laminar fMRI towards more thorough reporting of analysis choices and consequences. Furthermore, we are excited about the pipeline being publicly available.

In this study you show, similar to previous findings, an increase in BOLD response for attended regions, with and without visual stimulation. Yet, unlike previous studies, you did not find an effect of spatial attention across layers.

We believe the manuscript could be improved along the following points:

1.) Data are hard to access:<br /> We fully agree with the lead author in his agenda that open sharing of data is mandatory for modern research. We think this is even more essential for replication studies that do not see the same layer-dependent effects compared to previous studies. Only when the data are available, the community can employ their own set of tools and expertise to help tease out potential layer-specific attention effects and/or potential reasons for a disagreement between studies.<br /> Given the authors' stated support for open science, and the fact that the manuscript mentioned more than 5 times (at most prominent places) that all data are openly available, we were surprised how difficult it was to get access to the data. Many of us did not succeed in getting access to the MRI data straightforwardly. After reading IT manuals on how to use webdav.data, setting up our ORCID settings from scratch, and after requesting a temporary Donders account, we succeeded to download the data of the single participant that is provided.<br /> The time course data are much easier to access. However, we were disappointed that those data do not refer to MRI data per se, but rather refer to model fits, which are highly processed, and upsampled to a temporal resolution that is three times that of the actual fMRI time series. The manuscript might benefit from adding a few details about the shared time course data.

2.) Details on data acquisition:<br /> The acquisition of the functional data is described in one single sentence (line 354f). To aid the importance of reproducibility, we believe this section would benefit from further explanations. <br /> 2a) E.g. application of GRAPPA 8 is rather liberal and unconventional in the field. In fact, some of us first thought it was a typo. Maybe the authors can convince the reader that this is an appropriate choice of acquisition by explaining how this could be achieved (CAIPI = 1/4) and/or reporting basic quality metrics (e.g. tSNR) that allow judgement of the g-factor penalty.<br /> 2b) We were a bit surprised by the application of partial Fourier in both phase encoding directions. We believe that this might be an important piece of information to be reported in the manuscript and might help explain why no high-resolution attention effect was observed. As the MR-physicists in the author list know much better than us, the application of partial Fourier is based on the point-symmetry of the Hermitian k-space. This means that for applications of partial Fourier in both directions, it is not possible to synthesize (recover) the missing outer k-space data that represent the high spatial frequencies. With PF 6/8 for resolutions of 0.827x0.827x0.80mm^3, this results in an effective resolution of 1.15mm in the diagonal direction. Given that V1 has a cortical thickness of at most 2.5 mm, it is perhaps not surprising that the authors failed to observe differences between deep, middle, and superficial cortical layers with this effective spatial resolution.

3.) Interaction of attention and orientation:<br /> Maybe the manuscript could benefit from including a (supplementary) figure of the behavioral data. What was the effect of the attentional manipulation on orientation discrimination? Were the behavioral effects similar in magnitude to previous studies of spatial attention?

4.) Units of signal change:<br /> It was not clear to us why the values on the y-axis in Figure 1 and 2 are so small compared to the percent signal change reported in Figure 3? Do the arbitrary units in Figure 1 refer to the same scaling across task conditions and time steps?

5.) Surprisingly short inter-trial intervals:<br /> We were surprised by the unconventionally short duration of the inter-trial intervals. We wondered whether this timing introduced an HRF-bias that might have confounded the characterization of layer-specific effects. Specifically, it is likely that the shape, and possibly, the linearity, of the HRF varies with cortical depth (Figure 2). Each trial has an average length of 4.7s, followed by a variable inter-trial interval of length 1 to 2.5s. Due to the variable hemodynamic response function across cortical depth (Yacoub 2006, Petridou 2017; full citation attached below), it is expected that the depth-dependent response interacts non-linearly for trials that follow in such quick succession. As such, the accumulating signal in the superficial layers might not return back to baseline as fast as the signal in the deeper layers. In addition to the draining effect, signals might be carried over to the next trial in a depth-dependent way. Specifically, the superficial signal might not only reflect processes across cortical depths from the current trials, but also processes from previous trials while the signal at lower depth could be expected to have less ‘memory’. This layer-dependent bias of non-linear HRF might diminish the attention effect in superficial layers more than in other layers. We feel that this concern could be addressed by additional control experiments with very long inter-trial intervals.

Yacoub E, Ugurbil K, Harel N. The spatial dependence of the poststimulus undershoot as revealed by high-resolution BOLD- and CBV-weighted fMRI. 2006:634-644. doi:10.1038/sj.jcbfm.9600239

Petridou N, Siero JCW. Laminar fMRI: What can the time domain tell us? NeuroImage. http://dx.doi.org/10.1016/j.... Published 2019.

6.) The performance of the spatial GLM is unclear:<br /> Figure 3 has a very appealing layout that nicely conveys the relevant information. When comparing Figure 3 (main analysis with spatial GLM) to Figure 3-Figure supplement 4 (analysis with interpolated laminar signal) we noticed that the effect of ascending/draining veins (the slope of the lines) is comparable in both, if not flatter in the latter case, which is counter-intuitive (the spatial GLM should mitigate the impact of the vascular bias from pial vessels). We would be very interested in a discussion of how the spatial GLM is expected to handle potential carry-over effects between trials such as described in Point 5.

7.) Voxel selections:<br /> We appreciate the additional analyses summarized in Table 1, repeating the analysis including different numbers of vertices. Specifically we wondered whether not using a selection threshold on the vertices of the main experiment but instead purely relying on the ROI definition of the retinotopic localizer would lead to similar conclusions as when imposing an activation threshold. Is there a danger that a statistical activation threshold in the voxel selection could have resulted in the final layer profiles coming from patches of the cortex that are more dominated by ascending and pial veins (blooming)? Could the lack of localization specificity from those veins be responsible for the lack of layer-specific attention effects? In fact, if we could access the data, we would be interested in repeating the analysis and specifically excluding the voxels with the largest responses (which the authors have focused on), as these are the very voxels that are most likely to be contaminated by a vascular bias.

8.) Failed to replicate or a new research question?<br /> We were a bit surprised about the article type this manuscript is listed as. In previous public communication (e.g. workshops and thesis) with the lead author, the study was phrased in the context of a replication attempt. However, the article type chosen here is “New results”, as opposed to BioRxiv’s other available categories: “Confirmatory Results”, or “Contradictory Results”. <br /> While we believe that either category would be of interest to a large readership, we feel that the manuscript would benefit from an in-depth discussion of previous layer-fMRI studies that could indeed replicate a spatial attention effect in superficial layers. Maybe the authors can use these studies to estimate the expected effect size of the layer-specific attention effect in a power analysis explaining why the study at hand might not have been able to detect such modulations. Example studies are listed below:

Liu C, Guo F, Qian C, et al. Layer-dependent multiplicative effects of spatial attention on contrast responses in human early visual cortex. Prog Neurobiol. 2020;(July):101897. doi:10.1016/j.pneurobio.2020.101897

Gau R, Bazin P-L, Trampel R, Turner R, Noppeney U. Resolving multisensory and attentional influences across cortical depth in sensory cortices. Elife. 2020;9:1-26. doi:10.7554/elife.46856

Hollander G De, Zwaag W Van Der, Qian C, Zhang P. Ultra-high resolution fMRI reveals origins of feedforward and feedback activity within laminae of human ocular dominance columns. Neuroimage. 2020. doi:10.1101/2020.05.19.102186

Klein BP, Fracasso A, van Dijk JA, Paffen CLE, te Pas SF, Dumoulin SO. Cortical depth dependent population receptive field attraction by spatial attention in human V1. Neuroimage. 2018;176(October 2017):301-312. doi:10.1016/j.neuroimage.2018.04.055

Lawrence SJD, Norris DG, de Lange FP. Dissociable laminar profiles of concurrent bottom-up and top-down modulation in the human visual cortex. Elife. 2019:1-28. https://doi.org/10.7554/eLi....

Marquardt, I., De Weerd, P., Schneider, M., Gulban, O. F., Ivanov, D., Wang, Y., & Uludag, K. (2020). Feedback contribution to surface motion perception in the human early visual cortex. ELife, 9, 1–28. https://doi.org/10.7554/eLi...

9.) How can a large number of participants account for head motion?<br /> Lastly, while we agree that it can be useful to include larger sample sizes for population statistics we fail to follow the reasoning: “For example, at a resolution this high, even the smallest movement of the participant may cause additional blurring of the data, with potentially detrimental effects on the signal-to-noise ratio. For this reason, we collected data from 17 participants”. It could be argued that to reduce the influence of measurement error, high-resolution fMRI experiments should repeatedly sample a small number of subjects. Given the large number of participants, we would be especially interested in a discussion of individual results, in relation to individual motion estimates.

Stylistic suggestions:

Line 10: “Directing spatial attention towards a particular stimulus location enhances cortical responses at corresponding regions in the cortex.” -> We would suggest to specify that BOLD responses increase with attention, not necessarily neural responses.

Line 80: ‘histiological’ -> histological

Line 356: ‘T2*-weigthed’ -> T2*-weighted

Line 367: ‘3200 m’ -> 3200 ms

Figure 3 and supplementary figures -> Could you elaborate on the gray diamonds?

We would advise the authors to consider changing the color code in all time series figures. E.g. The two types of red and the two types of blue in Figure 1 are indistinguishable. Should the reader infer which line refers to which condition based on the magnitude of the response? If so, it could be mentioned in the caption.

The two types of red in Figure 2 are hardly distinguishable.

In Figure 1–Figure supplement 1, the two panels have no description that distinguishes them. We assume one refers to right and one refers to left hemispheres? It is puzzling why the unattended (blue) line in the right panel has a larger response than the attended (red) line. Is it possible that trials are not labeled correctly for one of the hemispheres? Specifically, does the attention label reflect ‘attention to the left’ instead of ‘attention to the contra-lateral side w.r.t. hemisphere'?

Overall, we find this work presents an important contribution to the field by attempting to replicate a previously observed effect and promoting a replicable pipeline. We hope that our thoughts and comments will be helpful. We are looking forward to seeing this manuscript published.

With kind regards,<br /> Sebastian Dresbach, Lonike Faes, Johannes Franz, Omer Faruk Gulban, Renzo Huber, Miriam Heynckes , Eli Merriam, Alessandra Pizzuti, Yawen Wang

On 2021-02-04 03:36:46, user Sara Sims wrote:

Reviewer #3 (Minor Comments):

P2, ?3. The authors cite To et al. (2011) for the claim that foveal magnification is greater than peripheral magnification. However, to make this claim, To et al. rely on a number of other citations which would be more appropriate here (?2 of their introduction). A clear example of this is Horton and Hoyt (1991). Additionally, it might be more appropriate to describe cortical magnification as having units of square-mm/square-degree rather than only mm/degree. <br /> We appreciate reviewer 3 for her/his suggestion, we cited Horton and Hoyt, 1991; Azzopardi and Cowey 1993 in the third paragraph of Introduction on Page 3.

P2, ?3. Additionally, the final line of this paragraph addresses receptive field size. It might be of interest to review the finding of Harvey and Dumuolin (2011) [10.1523/JNEUROSCI.2572-11.2011], that the product of the pRF size and the cortical magnification factor are approximately constant across human V1 and nearby visual cortex. <br /> We added the information regarding how receptive field size and cortical magnification factor changes as eccentricity increases through V1 constantly in human V1 and near visual areas in the third paragraph of Introduction on Page 3.

P4, continued ?1. in order to understand what the FEF's inclusion in the Dorsal Attention Network means, it might be useful to introduce the Dorsal Attention Network briefly when discussing the DMN and the FPN. <br /> This sentence was reworded for clarity, including removing reference to the Dorsal Attention Network since it was not relevant to the sentence’s main point.

P4, full ?1. Given the amount of work that has been done on the fronto-occipital and inferior longitudinal fasciculi, the following sentence should probably include a citation or three. "Major white matter tracts that connect to the occipital lobe such as the inferior fronto-occipital fasciculus (connects occipital lobe to lateral prefrontal cortex) and the inferior longitudinal fasciculus (connects occipital lobe to anterior temporal lobe) have been well documented using tractography methods in humans." <br /> We have added this citation to the text in the introduction: “Major white matter tracts that connect to the occipital lobe such as the inferior fronto-occipital fasciculus (connects occipital lobe to lateral prefrontal cortex) and the inferior longitudinal fasciculus (connects occipital lobe to anterior temporal lobe) have been well documented using tractography methods in humans (Wu et al., 2016).” <br /> Here is the full citation: Wu, Y., Sun, D., Wang, Y., & Wang, Y. (2016). Subcomponents and Connectivity of the Inferior Fronto-Occipital Fasciculus Revealed by Diffusion Spectrum Imaging Fiber Tracking. Frontiers in Neuroanatomy, 10, 88.

P4, full ?2. This paragraph is a bit hard to follow and might be improved by breaking it up into shorter sentences. In particular, I'm not 100% sure what the authors mean by "direct and indirect structural connections". Additionally, I'm not sure why the end of this sentence follows from its beginning: "Since functional connectivity between two brain regions could come from both direct and indirect structural connections, we used DWI to examine direct connections between regions (Adachi et al., 2012; Honey et al., 2009) that were previously found to show functional connections." <br /> We have changed the wording of this paragraph to the following:<br /> “The goals of the current study are 1) to assess the reproducibility and generalizability of retinotopic effects on functional connections between V1 and functional networks that were found in prior work (Griffis et al., 2017). We aim to extend these findings in a new dataset collected under different task conditions (previous work used blocks of rest during a task with central fixation and the current data was collected as part of a resting-state only scan). 2) Extend prior work on the retinotopic connectivity difference to structural connections between V1 and functional networks. 3) Examine the relationship between functional and structural connections. Since functional connectivity between two brain regions could be derived from measurable structural connections, we used DWI to examine connections between regions (Adachi et al., 2012; Honey et al., 2009).”

P4, full ?3. Again, the concept of a "direct connection" versus an "indirect connection" appears prior to being introduced. Given that this paragraph marks the concept as critical to the point of the paper, the introduction needs to explain what these are. Additionally, it seems that the paper separates the idea of a direct/indirect "structural connection" from that of a direct/indirect "functional connection". This should all be clearer. <br /> In addition to the text added in response to the above comment the following text has been added to the paragraph referenced in this comment: “the pattern of structural and functional connections is similar, suggesting that this lateral frontal functional connection pattern arises from a direct (uni-synaptic) structural connection.” for additional clarification.

P6, ?3. "Previous work has shown that cortical anatomy is a reliable predictor of the retinotopic organization of V1 (O. Hinds et al., 2009; O. P. Hinds et al., 2008) so that the more posterior parts of the visual cortex represent more central portions of the visual field." At the risk of splitting hairs, the publications by Oliver Hinds show mainly that the V1 *boundaries* are reliably predicted by anatomy. A better citation for the V1 *retinotopic organization* is Benson et al. (2012) [10.1016/j.cub.2012.09.014], wherein we actually assessed the retinotopic maps and not just the boundaries. <br /> This citation has been added.

P6, ?3. "The average eccentricity of each segment was estimated from Benson and colleagues' probabilistic retinotopy template (Benson et al., 2012)..." The correct citation for the retinotopic template is Benson et al. (2014) [10.1371/journal.pcbi.1003538], along with Benson and Winawer (2018) [10.7554/eLife.40224] assuming you are using a recent version of the template, which appears to be the case based on Figure 2 (though given that you are using the FreeSurfer V1 boundary also, I can't really tell). Additionally, it isn't technically correct to call this a probabilistic template (such as might be said correctly of the visual area atlas by Wang et al., 2015). The retinotopic template is more accurately a model of retinotopic organization fit to the average retinotopic organization across many subjects-it does not explicitly express or depend on probabilities. <br /> Wording has been changed to retinotopic template.

P6, ?3. "These ROIs were defined in the gray matter on the cortical sheet for the freesurfer template, then moved into the individual anatomical space for each participant." I believe that the authors' intent here is to state that ROIs were defined on FreeSurfer's fsaverage brain using the eccentricity of the retinotopic template (which is also defined on the fsaverage brain) then were interpolated over to individual subject cortical surfaces using FreeSurfer's anatomical registration. However, I don't have a good prior for what the "freesurfer template" is here or what the "gray matter on the cortical sheet" of it might be, so this may all be wrong. Perhaps the implication is that the ROIs were hand-drawn in the voxels of the fsaverage subject's "ribbon," but if so, is the interpolation back to the individual subject done on the surface or using FreeSurfer's newish diffeomorphic volumetric alignment? <br /> The following text has been revised to further clarify for the reviewer: “These V1 eccentricity segment ROIs were defined on FreeSurfer's fsaverage brain using the eccentricity of the retinotopic template then were interpolated to individual subject cortical surfaces using FreeSurfer's anatomical registration. To avoid the potential for artifacts due to differences in ROI size when comparing probabilistic tractography results, the number of vertices were kept similar (on the Freesurfer fsaverage brain) between eccentricity segments.”

P6, ?3. "To avoid the potential for artifacts due to differences in ROI size, the number of segments per eccentricity region were assigned to more evenly distribute ROI size." Again, this is not at all clear. Earlier text in this paragraph implies that the segments *are* eccentricity regions. Does this sentence indicate that the segments were adjusted in each individual subject to be of a similar size? Or that the ROIs were split into several segments each before interpolation? Is there a material difference between what was done and simply starting with a larger number of segments? It's not clear to my why the process is described in terms of three segments whose eccentricities are reported then redescribed in terms of more segments whose eccentricities are not reported. <br /> We acknowledge that the reporting of the V1 ROI eccentricity segments was unclear. We have simplified the text to be more clear so that it now reads: “Based on this template, 3 retinotopic regions were identified: central vision (mean eccentricity estimates of 0-2.2 degrees visual angle), mid-peripheral vision (mean eccentricity estimates of 4.1-7.3 degrees visual angle) and far-peripheral vision (mean eccentricity estimates of 14.1-25.5 degrees visual angle) (Figure 2).”

P7, ?1. "... voxels within the white matter corresponding to the network ROIs were used as track seeds." I found this initially confusing as immediately prior to this section, "ROI" refers to the ROIs of V1, which should have no truck with the white-matter (i.e., a white-matter voxel predicted to be in an ROI derived from the FreeSurfer's V1 label or the retinotopic template must by definition be erroneous). However, I suspect that this is intended to be about a separate set of network ROIs? This should be clearer. <br /> Yes, there are two sets of ROIs, the V1 ROIs and the Network ROIs. The “network ROIs” has been changed to “network-ROIs” to emphasize this point further. Also, whenever the term “ROI” is used, the name of the set of ROIs being referred to is now stated.

P7, Data Analysis. Again, citing the analysis methods is well and good, but this section should make very clear up front which data were collected/analyzed by the authors and which data were collected/analyzed by the HCP. I should be able to easily tell both what analysis steps were performed *and* which set of authors performed each step. <br /> See response to Reviewer #3 Major Comment #2.

P7, ?2. "Next, right-to-left and left-to-right acquisitions were concatenated into a single 4D volume for the functional connectivity analysis." While I understand from this sentence that the preprocessed images were transformed into single 4D volume files, I do not follow the significance of "right-to-left" and "left-to-right" in this context. <br /> The text of the article has been changed to clarify this: “Next, both the acquisitions (those collected right-to-left and those collected left-to-right) were concatenated into a single 4D volume for the functional connectivity analysis.”

P8, ?4. The text references a "2mm2 Gaussian kernel". Is this supposed to be 2 mm (not squared)? If so, does it refer to the FWHM or to the HWHM or to the parameter ?? It says the "surface maps" were smoothed, but was this done on the FreeSurfer cortical sphere (in which case, mm is a curious unit)? Volumetrically? Something else? <br /> This was a typo it has been changed to “2mm” and the text now reads “Surface maps of the track termination probabilities were smoothed using a 2mm FWHM Gaussian filter and averaged across all subjects.”. This was done with mri_glmfit “fwhm” flag.

P9, ?1. More information is needed about the t-tests that were used. Were these tests one-tailed or two-tailed? Corrected for multiple comparisons or not? How was mri_glmfit used to perform these tests? The help-file for mri_glmfit mentions t-tests only in the context that a certain use-case reduces to a t-test in some circumstances. <br /> We have added “two-tailed” to the text. The mri_glmfit function can be used as a t-test under one sample group mean test with the --osgm flag. We did not correct for multiple comparisons due to the analysis’s design with specific, planned comparisons.

P9, Comparison of Functional and Structural Connectivity. Was only one correlation coefficient calculated? Were the authors not interested in these correlations for the non-central V1 regions? It seems irregular that only one of these would be examined given the experimental setup and the hypotheses of the manuscript. <br /> We have now included dice coefficients, per the reviewer’s suggestion, as well as adding non-central V1 regions in this new analysis.

Methods, generally. In a couple of places, the authors refer to commands like "mri_vol2surf" (P8, ?1). It would be ideal if the command lines or scripts were also provided with the manuscript. <br /> The code has now been added to the code repository.

P9, ?4. "The t-test comparing functional connectivity to different eccentricity segments in V1 revealed significant effects (p<.001) and brain regions belonging to FP, CO, and DMN functional networks (Figure 3)" is the "and" here supposed to be "in"? <br /> This edit has been made.

P9, ?4. It's not clear to me how "preference" was evaluated here. For example, "central representing V1 was preferentially connected (over mid-peripheral and far-peripheral V1) to regions associated with the FP network". Was this assessed by visual inspection? A good quantitative metric would be nice to have here, such as the dice coefficient for each ROI-network pair. <br /> We have added dice coefficients to the analysis. See Tables 1 & 2.

P9, ?4. "Those previous results had also shown differences in connectivity between mid-peripheral-representing regions and far-peripheral representing regions, which were not observed here, (Figure 3)" <br /> This text has been reworded for clarity: “However our results differ in that mid-peripheral-representing regions and far-peripheral representing regions differences were not observed here (Figure 3).”

P10, Figure 3. "There, vertices in yellow showed stronger (z>3) connectivity to central V1 than to both Far peripheral and mid-peripheral regions." I do not understand the significance of "(z>3)" in this caption. Additionally, what is the significance of the gray color shown on all brains in the bottom row? <br /> Clarification has been added to the Figure legend, including “The grey regions indicate the location of the other networks.”

P11, ?1. "... we performed pairwise comparisons of functional connections... Results indicate that ... there are preferential connections between central V1 ..." Again, I'm not clear how preference is being assessed here, or what is being compared pairwise. Pairwise comparisons between segments and networks? What values exactly were compared? If these are referring to visual inspection, that is fine, but the language seems to suggest something more programatic, and what that might be is not clear. <br /> The text has been clarified to now state “We performed statistical comparisons (t-test) of functional connections between central vs far-peripheral eccentricity segments of V1 and the FPN (Figure 4).”

P11, Figure 4. Please tell us what exactly is being plotted. What value minus what value? <br /> The values being subtracted have now been added to all figures.

P14, ?2. "A comparison between structure and function showed overall agreement, indicating that the functional connections are likely mediated by direct structural connections (Figure 6, right column)." Depending on what the authors mean by "mediate" I'm not sure that this follows. Please elaborate. <br /> We acknowledge that this wording is unclear. We have therefore changed the wording of this statement to the following: “These relationships indicate that the overall pattern of connectivity of central V1 greater than far peripheral V1 is consistent across modalities with an especially high overlap within the FPN.”

P14, Figure 6. "Far-peripheral and central V1 are statistically different within the FPN..." How was statistical difference within the FPN assessed? <br /> Please refer to the following section:<br /> “Tractography Analysis <br /> To test the hypothesis that patterns of functional connections previously found in V1 (Griffis et al., 2017) are similar to patterns of structural connections, comparisons were made between the central and far-peripheral eccentricity segments of V1 connectivity patterns to the FPN. Differences in track probabilities corresponding to V1 eccentricity segments connections were compared by paired, two-tailed t-test (using Freesurfer’s mri_glmfit with a one sample group mean test). “

Style/Aesthetic Comments <br /> Throughout the manuscript, starting on P3, full ?1, there are several mismatched parentheses that are distracting. These typically look like this: "some claim is made here (e.g., (Someone et al., 2010) then continues here". Almost all of these could be fixed by removing the "(e.g. ". That said, the use of "e.g., "makes me think that there are other citations that *should* appear here, but haven't been filled in yet, especially given that many of these are broad statements somewhat outside my particular expertise, such as "The fronto-parietal network (FPN) directs attentional control (e.g., (Zanto & Gazzaley, 2013)".

P4, L8. "Markov et. al," should be "Markov et al.," <br /> This edit has been made.

P4, full ?2-3. The authors mix the style "Something listable: (1) first thing, (2) second thing..." and the style "Something listable: 1) first thing, 2) second thing." <br /> This formatting has been changed.

P7, ?1. The acronyms "FP" and "CO" were previously reported as "FPN" and "CON". This needs to be fixed throughout. I get that at times the intention is to represent the deduplication of the word "network," i.e., "the fronto-parietal and default mode network" becomes "the FP and DMN". I think this usage is less clear to readers than "the FPN and DMN" and, besides, the text sometimes says "the FP and DMN networks" (P8?3L3, P9?4L4). Alternately, introduce FP et al. as separate acronyms on P7: "Fronto-parietal (FP), cingulo-opercular (CO), and default mode (DM) networks...". <br /> Abbreviations have been edited for consistency.

Reviewer #3 (Additional data files and statistical comments):

As mentioned in the Major and Minor comments, most if not all of the statistical tests need to be more explicitly described. I could not currently reproduce the exact tests from the manuscript, even if I had the data.

Additionally, because the project is a reanalysis of a large dataset, it would be particularly valuable to have the source code used for analysis. It is nearly impossible to reproduce or assess a project like this without such code.

The code for the analysis has now been added to a repository and it is referenced in the paper.

On 2021-02-04 03:34:40, user Sara Sims wrote:

Reviewer #2 (General assessment and major comments (Required)):

In this work, Sims and colleagues use resting-state functional connectivity and diffusion tractography in human connectome project data to examine the connectivity of the central and peripheral aspects of primary visual cortex. They find that central V1 connects more strongly to regions of prefrontal cortex interpreted as the Fronto-parietal network than does peripheral V1.

The idea that central V1 may be directly connected to control-related networks is an interesting one, and has fascinating implications for the study of top-down modulation of visual cortex function. However, I must say I am somewhat skeptical of these findings, for several reasons. <br /> First, I find the a priori anatomical basis for these proposed connections to be dubious. The authors themselves describe how Markov et al. explicitly conducted tract tracing with central V1 and found connections with posterior frontal and parietal cortex, but nothing with areas classically associated with the fronto-parietal cortex. The authors propose that the inferior fronto-occipital fasciculus may connect V1 with lateral prefrontal regions only in humans. However, they provide no evidence for this suggestion. Indeed, my understanding of the iFOF is that it connects to inferior and lateral occipital cortex (see e.g. figures from the Takemura study cited in this work). Can the authors better support the idea that the iFOF might be the route of connection between V1 and frontal cortex?

Thank you for your comments. We agree that while the data and methods we present here don’t address whether the iFOF is the route of connection between the inferior and lateral occipital cortex, more evidence from relevant literature would be helpful. The figures from the (Takemura et al., 2016) paper shows only inferior and lateral occipital cortex and are ambiguous for our regions of interest. However, other papers suggest that iFOF may be the route of connection between V1 and frontal cortex:

A paper by Wu and colleagues shows figures indicating that the IFOF does provide a connection between the medial occipital cortex and IFG. We now cite this in the paper. “Major white matter tracts that connect to the occipital lobe such as the inferior fronto-occipital fasciculus (connects occipital lobe to the lateral prefrontal cortex) and the inferior longitudinal fasciculus (connects occipital lobe to anterior temporal lobe) have been well documented using tractography methods in humans (Wu, Sun, Wang, & Wang, 2016).”

Second, I am concerned that both 1) the Central V1 ROI employed in this work and 2) the inferior frontal cortex region showing strong FC with that Central V1 ROI overlap very closely with regions where we have seen poor BOLD signal in our own fMRI data (I would like to attach a figure if possible). <br /> We are not confident what the source of the poor signal might be in posterior occipital or inferior frontal cortex; we suspect the presence of large veins (possibly the transverse sinus in V1; see Winawer et al., 2010, Journal of Vision). In any case, the data quality is low enough that we believe our data should not be considered to represent actual neural function in those regions. Can the authors demonstrate convincingly that this is not the case in their HCP data?

The reviewer suggests that based on their data, posterior occipital and inferior frontal cortex have relatively poor signal. They suggest that this poor signal would result in spurious correlations between the regions because of large veins. As described in our methods section for preprocessing of resting state scan data, white matter and CSF timecourses were regressed out, which aids in removing average venous artifact. Replication between 2 datasets (HCP and Griffis et al., 2017) and 2 modalities (DWI and resting state) further indicate the reliability of this effect.

The Winawer et al., 2010 article cites (Schira, Tyler, Breakspear, & Spehar, 2009) when discussing this issue; that paper suggests that poor signal in these regions may come largely from partial voluming (conflating signal from gray matter with signal from veins), and that these can be managed through increasing resolution with smaller voxel sizes. Our data are collected at resolutions finer than their recommendations, suggesting that such an effect should be minimal in this dataset. We have added the following text to the limitations section to address this comment: “We also acknowledge that large veins near posterior occipital cortex could impact our functional connectivity measurements in this area. However, we performed extensive pre-processing to reduce the impact of vessels on activity. In addition, the voxel size of our resting state scan is small (2mm isotropic), mitigating contributions from nearby veins due to partial voluming effects (Schira et al., 2009).”

Third, I have an issue with the localization of effects in this paper. The paper describes effects in the fronto-parietal network throughout the manuscript, including the title. How surprising, then, that the strongest effects are not in FP network at all! Figure 4A makes it very clear that the largest effects are in the IFG, which is outside the green outlines describing the extent of the fronto-parietal network, but inside the Default network. <br /> Figure 3A also supports this Default-centric localization, with Central V1 effects in posterior lateral parietal, medial parietal, and superior frontal cortex, all outside FP but inside Default. Since the FC effects are not actually primarily in FP, I see no reason why FP should be used as a mask in Figure 5. Indeed, the authors should show the localization of SC effects throughout the cortex, not just in FP. I also see no reason why these V1-Default connections should be characterized in any way as "attention" or "control".

We appreciate the reviewer’s comment and have made extensive modifications to the paper in response. The reviewer notes that some vertices of the effect we observed in left frontal cortex are in a portion of the IFG that is not classified by Yeo et al, 2011 as part of the frontoparietal network, but instead classified by that paper as the default mode network. We would like to note that most other papers that define DMN would not have included the IFG as part of that network, and in fact, Yeo’s 17-network parcellation from the same paper does not classify that portion of cortex as part of the default mode network. The inclusion of that parcel as part of the DMN is likely an artifact of the requirement of the algorithm in that paper to subdivide the brain into 7 discrete networks. However, the set of vertices can be described as being in the inferior frontal cortex, and we have reworked our discussion to de-emphasize the fronto-parietal network.

This said, we also quantified the similarities between the frontoparietal cortex and the functional connectivity patterns selective for V1, using Dice coefficients. This is now shown in Table 1. <br /> We have described this table within the text as follows: “Table 1 indicates high similarity between central V1 dominant regions and the FPN and partial similarity to portions of the CON and DMN, while the other V1 segments, mid- peripheral and far-peripheral are not strikingly similar to any networks.”

We have also added the following text to the article in reporting of Figure 4: “This inferior frontal gyrus region aligns well with the anterior portion of the FPN as defined by Yeo, but interestingly, it does expand somewhat beyond that border into the IFG (Inferior frontal gyrus) which is related to attention and control (Baldauf & Desimone, 2014; Chong, Williams, Cunnington, & Mattingley, 2008; Fassbender et al., 2004; Hampshire, Chamberlain, Monti, Duncan, & Owen, 2010; Swick, Ashley, & Turken, 2008, 2011).”

The reviewer also suggests that localization of structural connectivity effects should be shown throughout the cortex. We have added a figure 5 that shows the effects in our three networks of interest on the same cortical sheet. This figure shows more clearly the delineations of the strong effects. For technical reasons, we cannot perform these analyses on the cortex’s entirety at once: as described in the methods section, probability tracking for each network was calculated separately. Interestingly, however, despite this, the patterns look continuous across the boundary.

Fourth, I feel that these FC and SC differences are wildly over-interpreted. From the scale, the actual strength of FC and SC between central V1 and lateral parietal cortex is extremely weak (around Z(r) = .1 for FC and p-track = .1 for SC). Under no circumstances would I believe that either of those values represents any sort of real connection. Cortical regions with direct structural connections have much stronger FC values than regions that indirectly influence each other via multi-step connections.

Functional connectivity magnitudes are always influenced by the preprocessing done to obtain them. In this case we regressed out the mean signal, and regressed out white matter and CSF. While this practice decreases the mean correlation strength (Shirer, Jiang, Price, Ng, & Greicius, 2015; Weissenbacher et al., 2009) it also improves across-subject reliability (Burgess et al., 2016). The debate about this practice, now a decade long, has focused on the interpretability of negative correlations, which we do not do here. All sides of the debate agree that the practice of mean signal regression should not influence relative correlations across brain areas.

We are looking at variability in connection strength between different portions of a single brain area, and we would expect roughly similar long-range connectivity between different parts of V1. We have incorporated this point into the discussion on page XX where we say “ While central and peripheral representation portions are still part of the same V1 area, and therefore we would expect similarity in their connectivity patterns, our results indicate that eccentricity differences do exist and are consistent with previously reported differences in information processing on central and peripheral visual information.”

In addition, we added to the limitations section a discussion of this:<br /> “Here, we show functional connectivity strengths on the order of r=0.1. While very reliable, these magnitudes are not as large as connections to other areas, for example, portions of the occipital lobe. Functional connectivity magnitudes are always influenced by the preprocessing done to obtain them. In this case, we regressed out the mean signal and regressed out white matter and CSF. While this practice decreases the mean correlation strength (Shirer et al., 2015; Weissenbacher et al., 2009) it also improves across-subject reliability (Burgess et al., 2016). The debate about this practice, now a decade long, has focused on the interpretability of negative correlations, which we do not do here to examine relative correlations across brain areas.

Further, very large portions of the brain probably have both stronger FC and SC to central V1 than these FP regions (the authors show this for FC but exclude this info for SC). <br /> We have included a new figure to show the SC patterns across more than just the FPN (now includes regions within FPN, DMN, and CON), now Figure 5. Along with the following text, “Next, we investigated similar comparisons between central and far-peripheral V1 in a different modality- structural connections. A t-test comparing the structural connection of central and far-peripheral V1 revealed significant effects (p<.001) in brain regions belonging to FPN, CON, and DMN functional networks (Figure 5). We chose these three networks to compare to functional connectivity findings from Figure 3. <br /> Notably, central representing V1 was preferentially connected (over far-peripheral V1) to regions associated with the FPN, including the mid orbitofrontal and inferior parietal regions of the FPN, as well as lateral portions of the DMN, and the insular portion of the CON. In contrast, far-peripheral representing V1 was preferentially connected (over central V1) to medial portions of the DMN (Figure 5).”

Most glaringly, I certainly don't believe there is a "direct structural connection" as is claimed in the discussion--a claim based, strangely, on the spatial correspondence between the structural and functional maps, which really has nothing to do with any evidence for a direct connection. <br /> As stated in the discussion limitations section “structural tractography analysis only identifies direct connections”. <br /> The probabilistic tractography method can only show connections between Region A and Region B. It cannot indicate if there were connections between Region A and Region B that traveled via Region C. Therefore if a connection is indicated by the method, it must be direct. <br /> The statement of a “direct structural connection” is not an interpretation of the correspondence between structural and functional maps, but an interpretation of the structural maps.

Finally, the authors must note that p values may not be used for spatial correlations between brain maps. This is because these maps are always highly autocorrelated, which violates the independence assumption of the correlation procedure. <br /> We have replaced spatial correlations between brain maps with Dice coefficients, a more field-standard method for comparing spatial maps. We thank the reviewer for the comments and think this new way of analyzing it is a better fit.

Reviewer #2 (Additional data files and statistical comments):

The authors should show the data (maps or scatterplots) going into their spatial correlation on page 13. <br /> Based on comments from reviewers, we changed this part of the analysis to dice coefficients with the following text : “A Dice Coefficient was calculated for comparison of the functional and structural connectivity differences of central vs far-peripheral V1 to the FPN, CON, and DMN. Across all 3 networks the Dice Coefficient (averaged across left and right hemisphere) between structural and functional connectivity patterns was .707.<br /> Within the FPN the Dice Coefficient (averaged across left and right hemisphere) between structural and functional connectivity patterns was .915. Within the CON the Dice Coefficient (averaged across left and right hemisphere) between structural and functional connectivity patterns was .842. Within the DMN the Dice Coefficient (averaged across left and right hemisphere) between structural and functional connectivity patterns was .85. These relationships indicate that the overall pattern of connectivity of central V1 greater than far peripheral V1 is consistent across modalities with an especially high overlap within the FPN.”

On 2021-02-04 03:33:36, user Sara Sims wrote:

We would like to thank the Editor and Reviewers for their helpful comments and suggestions. We have responded to them below. We believe the changes made at the behest of the editor and reviewers have greatly improved this paper.

Reviewer #1 (General assessment and major comments (Required)):

This manuscript extends on prior work by the authors (Griffis et al, 2017), which originally reported eccentricity-dependent differences in resting state connectivity between V1 and regions brain wide. This study builds on that work by expanding the pool of participants, using the HCP dataset, as well as also investigating any eccentricity-dependent effects that may emerge with tractography. Interestingly, both measures find that foveal areas in V1 are more strongly connected to frontoparietal networks. The study is interesting, and I believe warrants publication. I have a few remaining points.

1) While during the resting state scans, there was, in theory, no 'task', participants were asked to maintain fixation on the cross in the center of the screen throughout the scan. I think it would be important for the authors to note that there is a possibility that the resting state correlations observed wherein foveal areas were more correlated with frontoparietal regions (and far periphery with DMN areas) could be due to attention directed towards the fixation cross, and away from the periphery. While I acknowledge the authors have no way to test this with this data set, it is possible that if participants had been asked to covertly attend to a ring in their far periphery the entire time instead, the correlations might have been flipped, with frontoparietal connectivity highest in the periphery towards the attended eccentricity. The authors should either explain why this is not a concern, or acknowledge it in the manuscript.

Explained with point #2. See below.

2) Related to the last point, what was the size of the screen used during the connectivity data acquisition? I ask because the far eccentricity bands determined using Benson et al's technique are *very* eccentric. And if participants had eyes opened and were fixating, was that eccentricity outside the outer edge of the screen? Because then it would be encouraged to be 'unattended', thereby potentially influencing connectivity results.

We now acknowledge these concerns (1 &2) in the limitations sections and have added the following text: “It should also be acknowledged that functional connectivity can be influenced by attention (Gratton et al., 2018; Griffis, Elkhetali, Burge, Chen, & Visscher, 2015; Salehi et al., 2020). In both, the work by Griffis and colleagues (2017) and the current study’s resting-state scan, a fixation cross presented on a screen at the end of the bore, and participants were scanned while inside the MRI bore. Participants may, therefore, have been allocating more attention toward the visual space in the center (the screen) than the periphery (the bore). However, the fact that we observed complementary effects in the structural data indicates that these data are likely not due to transient states of attention and are likely to represent biological organization.”

3) Was there any attempt at replicating these results in extra striate cortex? Are these patterns still there, both in structural and functional connectivity, for V2 or V3?

Investigation of the extra striate cortex was out of the scope of the present study. However we acknowledge that this is an important avenue of research in the future. We have therefore added the following text to the future directions section: “The investigation of connectivity between retinotopic visual areas and functional networks could be expanded to other retinotopically mapped extra-striate cortex in future studies.”

On 2020-12-18 13:49:48, user Karen wrote:

Beautiful paper! I think there may be some confusion on the VM6 glomerulus. This glomerulus was renamed VC5 in the Bates paper and continued here. The Bates paper noted that there has been confusion on VM6 in the past, presumably due to its poorly defined morphology with nc82 staining. However, the VC5 that Richard Benton has named (aka Ir41a ORNs) is relatively small and corresponds better to VC3m (Li Volkan 2016 refer to it with both names).

My lab has recently identified a drive that identifies a previously unstudied 4th ac1 ORN and this ORN targets the "classic" VM6, which by morphology, position and size matches the glomerulus you are calling VC5. GCaMP imaging shows that these neurons have a different response pattern than the Ir41a VC5/Vm3m ORNs. Several papers studying ORN lineages using MARCM and other clonal analysis have found that the VM6 ORN develops from the same lineage as the three previously known ac1 ORNs, which makes sense since all four are in the same sensilla and presumably come form the same SOP (Endo Hama Nat Neuro 2005, Li Volkan Plos Genetics 2016, Chai Benton Nat Comm 2019).

For consistency in the literature, I would think the following make sense based on morphology, clonal analysis, and historical references:

Or35a ORNs- target either VC3 (Couto 2005, Grabe 2015/2016, Silbering 2011) or VC3l (Fishilevich 2005, Li 2016)

Ir41a ORNs- target either VC5 (Grabe 2016, Silbering 2011, Li 2016) or VC3m (Li 2016)

4th ac1 ORNs (our driver- that we can share)- target VM6

Happy to discuss further if you'd like!

On 2020-12-01 20:43:45, user Guangmei Liu wrote:

Introduction<br /> We are university students taking an upper-level neurobiology course that centers on understanding neural circuits and modern research techniques through in-depth discussions of recent literature. To fully immerse ourselves in current scientific discourse, we have written this review of the manuscript from Park et al. posted on biorxiv.org (version: November 12, 2020).<br /> Jamie Dela Cruz 1, Angélica Gaona 1, John Axiotakis 1, Guangmei Liu 2<br /> 1 Senior undergraduate in Neurobiology, Boston University. 2 First-year PhD student in Neurobiology, Boston University.

Summary<br /> There is a growing body of literature examining the effects of social deprivation during the critical developmental period and how it affects later social function. In particular, Park et al. are interested in studying social recognition, or the ability of an animal to distinguish a novel conspecific from a familiar one. To uncover what neural circuits may underlie this, the authors used juvenile social isolation (jSI) and pharmacogenetic manipulation to study the effects of early isolation in mice. They first raised singly housed (SH) mice and group housed (GH) mice. SH mice lived alone for 8 weeks immediately after weaning, whereas GH mice lived together in those 8 weeks. Afterwards, SH and GH mice were re-socialized for 4 weeks. The authors then used a variety of behavioral tests to examine the social behaviors of SH and GH mice. Next, they inhibited nucleus accumbens shell (NAcSh)-projecting IL neurons in GH mice to see if the pathway is required for social recognition. Lastly, to see if the social recognition deficits in SH mice could be reversed, the researchers selectively activated NAcSh-projecting IL neurons in SH mice. They found that jSI impairs social recognition through decreased excitability of the mPFC IL-NAcSh pathway and that pharmacogenetic manipulation of this population also selectively affects social recognition. Therefore, this paper presents a novel brain circuit required for social recognition and adds to the literature implicating the mPFC and NAcSh in early social development. Overall, we recommend that the authors consider different statistical tests for certain figures, as the distribution of their data appears to be bimodal at times. We also suggest that the authors run another cohort of SH and GH mice through the experiments, this time performing tests both before and after resocialization to distinguish between the effects of jSI and resocialization. We see an opportunity to provide more evidence for the effects of resocialization by adding a parallel cohort of SH and GH mice who were never resocialized. Additionally, our review discusses portions of the paper where the authors could provide more explanation for certain methods and tweak the figures for improved clarity. <br /> In Figure 1, they investigate what social phenotypes are affected by early social isolation. They used the 3-chamber test to see if either mouse type showed social preference (spending more time exploring a conspecific rather than an object) and social recognition (spending more time interacting with a novel conspecific than a familiar one) (Figure 1C, 1D). There was no significant difference between SH and GH mice in the social preference test, but SH mice did show a significant social recognition deficit. To see if this was caused by a general recognition memory deficit or hippocampus-dependent memory deficit in SH mice, both mouse types underwent the novel object recognition test and the object place recognition test (Figure 1E, 1F). However, there were no significant differences. In Extended Data Figure 1, the researchers looked at whether the SH mice were physiologically or emotionally different from GH mice. Researchers compared the body mass, basal locomotor activity, and anxiety levels between the two, also finding no significant differences.<br /> Extended Data Figure 2 looks at whether different durations of social isolation and resocialization will result in different behavioral phenotypes. First, they decreased the isolation time by singly housing mice for 2 weeks after weaning and resocializing for 4 weeks. In this case, SH mice showed no significant differences in social behaviors compared to GH mice. They then singly housed mice for 8 weeks after weaning and regrouped for 8 weeks to increase the resocialization time. Despite this increase, SH mice in this treatment showed the same social recognition deficit as mice in the original SH treatment.<br /> In Figure 2, the authors injected a retrograde virus into the NAcSh for GFP labelling to see what regions of the mPFC were sending the most inputs. Neurons in the ventral mPFC regions were heavily labelled, with the most labelling at the infralimbic cortex (IL), though there were some at the prelimbic (PL) as well (Figure 2A-B). They then used ex vivo brain slice whole-cell patch clamp recordings to see the excitability of both the IL and the PL, finding that neuronal excitability was reduced in NAcSH-projecting IL neurons but not PL neurons (Figure 2C-D). Extended Data Figure 4 digs into the electrophysiological properties of these IL neurons in both SH and GH mice, finding no significant differences.<br /> Figure 3 answers two main questions, the first being: does this social recognition deficit still appear in SH mice in a different behavioral paradigm? To investigate this, they habituate both SH mice and GH mice to a target mouse on day 1. On day 2, they allow the SH or GH mouse to explore either an empty cup, a novel conspecific, or the familiar conspecific target. Once again, SH mouse explored the novel and conspecific mice equally, showing an impairment in social recognition (Figure 3A-C). The second question answered by this figure is: Are the NAcSh-projecting mPFC IL neurons differentially activated by distinct social stimuli (familiar versus novel conspecific)? The researchers used c-Fos immunohistochemistry and eGFP to examine co-labelled neurons in the IL after exposing mice to either a familiar or novel conspecific (Figure 3D-E). They found that GH mice had more c-Fos and eGFP co-labelled neurons after interacting with a familiar conspecific than GH mice that interacted with a novel conspecific, suggesting that NAcSh-projecting IL neurons are activated as a result of interacting with familiar conspecifics (Figure 3F).<br /> In Figure 4, Park et al. look at whether the NAcSh-projecting IL neurons are required for social recognition. In GH mice, they injected hM4Di receptors into NAcSh-projecting IL neurons and intraperitoneally injected them with CNO, reducing the excitability of these IL neurons (Figure 4A-B, D). These GH mice then underwent the social preference test and social recognition tests (Figure 4C). With their NAcSh-projecting IL neurons inhibited, GH mice showed social recognition deficits similar to that of the SH mice in Figure 1. Extended Data Figure 5 checks whether inhibiting the NAcSh-projecting IL neurons affected the GH mice in other physiological or psychological ways. However, the GH mice showed normal performance in the novel object recognition test, object place recognition test, open field test, elevated plus maze, and forced swim test. Extended Data Figure 6 looks at whether inhibiting these IL neurons affect sociability itself. The researchers found that inhibited GH mice did not distinguish a novel mouse from its cagemate, but this did not affect the reciprocal social interaction with a novel conspecific.<br /> Lastly, Figure 5 answers: Does increasing NAcSh-projecting IL neuronal activity rescue the social recognition deficit in SH mice? To test this, they expressed the hM3Dq receptor in NAcSh-projecting IL neurons within SH mice and injected CNO 40 minutes before undergoing the social behavior tests (Figure 5A-D). The authors found that social recognition was successfully rescued in these SH mice (Figure 5E-F).<br /> In the conclusion, they tie in their findings with similar ones regarding the hippocampus’s connections to the mPFC and NAcSh and their impact on social memory. They also discuss research about the impact of social isolation on impaired motivation and drug-seeking behavior. They wrap up with a discussion of when they believe the critical period of social recognition is and how their results can contribute to the understanding of disorders like ASD.

Major Criticisms<br /> In Figure 1, we thought that there were a few places that could use improvement or clarification. To go into detail, we would like clarification on why isolation occurred only after weaning and not pre-weaning. Previous literature has been known to isolate mice pre-weaning, and we wanted more justification on why post-weaning isolation was done instead. In addition, we also feel as 8 weeks of social isolation is too long of a period and would like to see additional evidence on why the period could not have been shorter. We also wonder why there was no behavioral testing done before and after resocialization. If there was, we would like to see the data included in the paper. Otherwise, we would suggest that you run the same behavioral experiment on a separate cohort and carry out tests before and after resocialization. Perhaps then results of the behavioral tests run on unsocialized mice can then be depicted in panels C and D for comparison. Another criticism we would like to note is that the distribution found in panels D, E, and F emulates a bimodal distribution instead of a Gaussian distribution. If possible we would like to see a different statistical analysis run that is better fitting of the data. The same can be said for Figure 5 panel E and F. Another major issue noted is the assumption that resocialization is rewarding for the mice. In some instances, one could argue that resocialization is not rewarding as the mouse could be faced with aggressive counterparts. A measurement of anxiety levels during resocialization would help aid in your argument depending on the results. We think that one way you can approach this is by measuring cortisol levels in mice before and after they have been reintroduced. You could also quantify aggression levels before the mouse was reintroduced and once the mouse has been added back into the group. Lastly, for panels E, F, and B we are looking for a bit more clarification on what characteristics delegated a familiar and novel object, position, and mouse. For example, we were wondering if the target mouse was an age and sex match.<br /> Figure 2 looks at NAcSh-projecting IL neurons in the deep layer of the mPFC. However, we suggest that the authors clarify which layer it is. Additionally, to avoid criticisms about possible discrepancies between the number of cells counted and the slice image, we suggest that the researchers provide a high-magnification image of DAPI staining and eGFP to show that each green dot shows a nucleus.<br /> The social habituation/recognition tasks in Figure 3 were performed after 4-week regrouping. It is a good control to keep all behavioral tests after the 8-week group housing or single housing and 4-week regrouping paradigm. However, to more directly confirm the social deficit in the SH mice, we suggest the social habituation/recognition tasks also performed in parallel without regrouping.

Minor Criticisms<br /> In Figure 1 panels C and D, we would like a bit more clarification on where the objects were located in relation to the mouse. The heat maps suggest their locations; however, it is not directly stated in the writing or the figure. In addition, a legend distinguishing between GH and SH in the Social Preference, Social Recognition, Novel Object Recognition, and Object Place Recognition bar graphs would be helpful as it is only indicated in panel A. In addition, we wondered if the chamber placement of the familiar or novel object/mouse were counterbalanced so that they were not always placed on the same side of the mouse. We speculate if there was no counterbalancing done that the mouse may have preferred a certain chamber instead of a particular mouse or object. One last thing we would like to see is the exact age range in which the mice participated in the behavioral tests since it is not made completely clear in the Methods section. <br /> The Results section that discusses Figure 2 begins with an explanation of why the authors focused on mPFC-NAcSh connections in their study. However, we suggest that this is explained in the Introduction instead since it left us wondering why the authors focused on mPFC-NAcSh connections in their study; it was unclear whether there was literature supporting this decision. <br /> In Figure 3 panel B, we think it is an interesting finding that SH mice also showed significantly decreased interacting time with the conspecifics in the habituation session as GH mice did, given that these SH mice would later do poorly in social recognition tests. Thus, it would be better to notify the readers that it is an unexpected or interesting finding, and also propose the hypothesis of this phenomenon. For the panel E and F, you did a good quantification of neuronal activity in the NAcSh-projecting IL neurons by calculating the percentage of c-Fos and eGFP co-labeled neurons among total eGFP labeled neurons, because the number of NAcSh-projecting IL neurons may change in SH mice compared to GH mice. We would like to know whether the neural circuitry from IL to NAcSh is altered by social isolation. For this purpose, we suggest you inject an equal amount of AAVrg-eGFP-Cre in both GH and SH mice, and quantify the number of eGFP-labeled neurons in them. <br /> For Figure 4, the data is generally well organized and the experimental protocol was summarized well in the schematic. However, for Figure 4D (the comparison between spiking in baseline and in the presence of CNO), it would be valuable to show the effect of the control saline vehicle on spiking for both the eGFP mice as well as the hM4Di mice to illustrate that the presence of the IP injection or saline has no effect if it indeed had none. The preference index had also proved difficult to read; the way the lines overlapped made the connections between the data points on each bar hard to discern. Perhaps color coding them or using different shapes instead of uniform dots would be beneficial. <br /> Overall, Figure 5 seemed clear and straightforward. However, we did want a bit more clarification as to why 1mg/kg CNO was used for vehicle injection even though previously in Figure 4 there was 3mg/kg used. We suspect this may be due to an increase in sensitivity pertaining to excitation but would like to see that confirmed within the literature if it is the case. Another point to be made is that 4B and 5B appear to be inconsistent and like to see a bit more clarification or a comment on why that may be.

Merits<br /> For Figure 1 panel A, the addition of the schematic was helpful in understanding the timeline of the study for both GH and SH mice. The same can be said for panels B,E, and F. The results and tests done of the mice seemed appropriate to further aid in the understanding of social recognition and preference. All in all, the authors used every panel in the figure to justify how they came to their conclusion regarding the social preference and recognition test GH and SH mice. <br /> Figure 4 is paramount in illustrating the nuanced effect of this circuit on social behavior—namely, the impairment of social recognition while retaining nominal social preference in mice which was derived from the clearly reported results of the inhibitive manipulation. This connection is no more salient in the paper than here.<br /> Figure 5 was imperative for our understanding in rescuing social recognition. Hand in hand with Figure 4, it clearly defines how social recognition is affected by the loss and regain of the NAcSh-projection IL neurons. In particular, the middle graphs in E and F do an excellent job in highlighting the effect of IL-NAc shell neurons activation in social preference and recognition tests for both GH and SH mice.

Future Directions <br /> The findings of this paper prove to have important impacts pertaining to acquisition of social familiarity. Although it was noted in the paper that future direction includes investigation of animal models of ASD, it would be also beneficial to look at animal models of schizophrenia. In specific, revaluation of what was found in Piskorowski et al. in comparison to this paper pertaining to the critical period. The discrepancy, that is 2 weeks compared to 11 weeks, seems way too large and should be further investigated to better understand why the critical period may be one or the other. As an alternative, it may be found that it may be neither and that there is another time period that better represents the critical time period for normal social recognition.<br /> It would also be interesting to look into why the excitability of NAcSh-projecting IL neurons had decreased. Because the neurons in SH mice showed no significant electrophysiological differences from those in GH mice, the decreased excitability is likely a result of morphological changes. Indeed, Silva-Gómez et al. (2003) found that a similar social isolation protocol in rats results in decreased dendritic spine density within the mPFC.<br /> It is interesting and surprising that both GH and SH mice showed significantly decreased interacting time with the conspecifics in the habituation session in Figure 3B, but the social recognition was impaired in SH mice only. It might be because the SH mice could not remember the familiar mice and recognized them as all novel ones, which would indicate that the processes of memory consolidation and memory retrieval were impaired in SH mice. Thus, we think it would be interesting to investigate social recognition with a perspective of memory in the future.

Works Cited:<br /> Silva-Gómez, A.B., Rojas, D., Juárez, I., & Flores, G. (2003). Decreased dendritic spine density on prefrontal cortical and hippocampal pyramidal neurons in postweaning social isolation rats. Brain Research, 983(1), 128-136.

Piskorowski RA, et al. (2016)Age-Dependent Specific Changes in Area CA2 of the Hippocampus and Social Memory Deficit in a Mouse Model of the 22q11.2 Deletion Syndrome. Neuron 89, 163–176.

On 2020-12-01 15:19:49, user Guangmei Liu wrote:

Introduction<br /> We are university students taking an upper-level neurobiology course that centers on understanding neural circuits and modern research techniques through in-depth discussions of recent literature. To fully immerse ourselves in current scientific discourse, we have written this review of the manuscript from Park et al. posted on biorxiv.org (version: November 12, 2020).<br /> Jamie Dela Cruz1, Angélica Gaona1, Guangmei Liu2, John Axiotakis1<br /> 1 Undergraduate in Neurobiology, Boston University. 2 First-year PhD student in Neurobiology, Boston University.

Summary<br /> There is a growing body of literature examining the effects of social deprivation during the critical developmental period and how it affects later social function. In particular, Park et al. are interested in studying social recognition, or the ability of an animal to distinguish a novel conspecific from a familiar one. To uncover what neural circuits may underlie this, the authors used juvenile social isolation (jSI) and pharmacogenetic manipulation to study the effects of early isolation in mice. They first raised singly housed (SH) mice and group housed (GH) mice. SH mice lived alone for 8 weeks immediately after weaning, whereas GH mice lived together in those 8 weeks. Afterwards, SH and GH mice were re-socialized for 4 weeks. The authors then used a variety of behavioral tests to examine the social behaviors of SH and GH mice. Next, they inhibited nucleus accumbens shell (NAcSh)-projecting IL neurons in GH mice to see if the pathway is required for social recognition. Lastly, to see if the social recognition deficits in SH mice could be reversed, the researchers selectively activated NAcSh-projecting IL neurons in SH mice. They found that jSI impairs social recognition through decreased excitability of the mPFC IL-NAcSh pathway and that pharmacogenetic manipulation of this population also selectively affects social recognition. Therefore, this paper presents a novel brain circuit required for social recognition and adds to the literature implicating the mPFC and NAcSh in early social development. Overall, we recommend that the authors consider different statistical tests for certain figures, as the distribution of their data appears to be bimodal at times. We also suggest that the authors run another cohort of SH and GH mice through the experiments, this time performing tests both before and after resocialization to distinguish between the effects of jSI and resocialization. We see an opportunity to provide more evidence for the effects of resocialization by adding a parallel cohort of SH and GH mice who were never resocialized. Additionally, our review discusses portions of the paper where the authors could provide more explanation for certain methods and tweak the figures for improved clarity. <br /> In Figure 1, they investigate what social phenotypes are affected by early social isolation. They used the 3-chamber test to see if either mouse type showed social preference (spending more time exploring a conspecific rather than an object) and social recognition (spending more time interacting with a novel conspecific than a familiar one) (Figure 1C, 1D). There was no significant difference between SH and GH mice in the social preference test, but SH mice did show a significant social recognition deficit. To see if this was caused by a general recognition memory deficit or hippocampus-dependent memory deficit in SH mice, both mouse types underwent the novel object recognition test and the object place recognition test (Figure 1E, 1F). However, there were no significant differences. In Extended Data Figure 1, the researchers looked at whether the SH mice were physiologically or emotionally different from GH mice. Researchers compared the body mass, basal locomotor activity, and anxiety levels between the two, also finding no significant differences.<br /> Extended Data Figure 2 looks at whether different durations of social isolation and resocialization will result in different behavioral phenotypes. First, they decreased the isolation time by singly housing mice for 2 weeks after weaning and resocializing for 4 weeks. In this case, SH mice showed no significant differences in social behaviors compared to GH mice. They then singly housed mice for 8 weeks after weaning and regrouped for 8 weeks to increase the resocialization time. Despite this increase, SH mice in this treatment showed the same social recognition deficit as mice in the original SH treatment.<br /> In Figure 2, the authors injected a retrograde virus into the NAcSh for GFP labelling to see what regions of the mPFC were sending the most inputs. Neurons in the ventral mPFC regions were heavily labelled, with the most labelling at the infralimbic cortex (IL), though there were some at the prelimbic (PL) as well (Figure 2A-B). They then used ex vivo brain slice whole-cell patch clamp recordings to see the excitability of both the IL and the PL, finding that neuronal excitability was reduced in NAcSH-projecting IL neurons but not PL neurons (Figure 2C-D). Extended Data Figure 4 digs into the electrophysiological properties of these IL neurons in both SH and GH mice, finding no significant differences.<br /> Figure 3 answers two main questions, the first being: does this social recognition deficit still appear in SH mice in a different behavioral paradigm? To investigate this, they habituate both SH mice and GH mice to a target mouse on day 1. On day 2, they allow the SH or GH mouse to explore either an empty cup, a novel conspecific, or the familiar conspecific target. Once again, SH mouse explored the novel and conspecific mice equally, showing an impairment in social recognition (Figure 3A-C). The second question answered by this figure is: Are the NAcSh-projecting mPFC IL neurons differentially activated by distinct social stimuli (familiar versus novel conspecific)? The researchers used c-Fos immunohistochemistry and eGFP to examine co-labelled neurons in the IL after exposing mice to either a familiar or novel conspecific (Figure 3D-E). They found that GH mice had more c-Fos and eGFP co-labelled neurons after interacting with a familiar conspecific than GH mice that interacted with a novel conspecific, suggesting that NAcSh-projecting IL neurons are activated as a result of interacting with familiar conspecifics (Figure 3F).<br /> In Figure 4, Park et al. look at whether the NAcSh-projecting IL neurons are required for social recognition. In GH mice, they injected hM4Di receptors into NAcSh-projecting IL neurons and intraperitoneally injected them with CNO, reducing the excitability of these IL neurons (Figure 4A-B, D). These GH mice then underwent the social preference test and social recognition tests (Figure 4C). With their NAcSh-projecting IL neurons inhibited, GH mice showed social recognition deficits similar to that of the SH mice in Figure 1. Extended Data Figure 5 checks whether inhibiting the NAcSh-projecting IL neurons affected the GH mice in other physiological or psychological ways. However, the GH mice showed normal performance in the novel object recognition test, object place recognition test, open field test, elevated plus maze, and forced swim test. Extended Data Figure 6 looks at whether inhibiting these IL neurons affect sociability itself. The researchers found that inhibited GH mice did not distinguish a novel mouse from its cagemate, but this did not affect the reciprocal social interaction with a novel conspecific.<br /> Lastly, Figure 5 answers: Does increasing NAcSh-projecting IL neuronal activity rescue the social recognition deficit in SH mice? To test this, they expressed the hM3Dq receptor in NAcSh-projecting IL neurons within SH mice and injected CNO 40 minutes before undergoing the social behavior tests (Figure 5A-D). The authors found that social recognition was successfully rescued in these SH mice (Figure 5E-F).<br /> In the conclusion, they tie in their findings with similar ones regarding the hippocampus’s connections to the mPFC and NAcSh and their impact on social memory. They also discuss research about the impact of social isolation on impaired motivation and drug-seeking behavior. They wrap up with a discussion of when they believe the critical period of social recognition is and how their results can contribute to the understanding of disorders like ASD.

Major Criticisms<br /> In Figure 1, we thought that there were a few places that could use improvement or clarification. To go into detail, we would like clarification on why isolation occurred only after weaning and not pre-weaning. Previous literature has been known to isolate mice pre-weaning, and we wanted more justification on why post-weaning isolation was done instead. In addition, we also feel as 8 weeks of social isolation is too long of a period and would like to see additional evidence on why the period could not have been shorter. We also wonder why there was no behavioral testing done before and after resocialization. If there was, we would like to see the data included in the paper. Otherwise, we would suggest that you run the same behavioral experiment on a separate cohort and carry out tests before and after resocialization. Perhaps then results of the behavioral tests run on unsocialized mice can then be depicted in panels C and D for comparison. Another criticism we would like to note is that the distribution found in panels D, E, and F emulates a bimodal distribution instead of a Gaussian distribution. If possible we would like to see a different statistical analysis run that is better fitting of the data. The same can be said for Figure 5 panel E and F. Another major issue noted is the assumption that resocialization is rewarding for the mice. In some instances, one could argue that resocialization is not rewarding as the mouse could be faced with aggressive counterparts. A measurement of anxiety levels during resocialization would help aid in your argument depending on the results. We think that one way you can approach this is by measuring cortisol levels in mice before and after they have been reintroduced. You could also quantify aggression levels before the mouse was reintroduced and once the mouse has been added back into the group. Lastly, for panels E, F, and B we are looking for a bit more clarification on what characteristics delegated a familiar and novel object, position, and mouse. For example, we were wondering if the target mouse was an age and sex match.<br /> Figure 2 looks at NAcSh-projecting IL neurons in the deep layer of the mPFC. However, we suggest that the authors clarify which layer it is. Additionally, to avoid criticisms about possible discrepancies between the number of cells counted and the slice image, we suggest that the researchers provide a high-magnification image of DAPI staining and eGFP to show that each green dot shows a nucleus.<br /> The social habituation/recognition tasks in Figure 3 were performed after 4-week regrouping. It is a good control to keep all behavioral tests after the 8-week group housing or single housing and 4-week regrouping paradigm. However, to more directly confirm the social deficit in the SH mice, we suggest the social habituation/recognition tasks also performed in parallel without regrouping.

Minor Criticisms<br /> In Figure 1 panels C and D, we would like a bit more clarification on where the objects were located in relation to the mouse. The heat maps suggest their locations; however, it is not directly stated in the writing or the figure. In addition, a legend distinguishing between GH and SH in the Social Preference, Social Recognition, Novel Object Recognition, and Object Place Recognition bar graphs would be helpful as it is only indicated in panel A. In addition, we wondered if the chamber placement of the familiar or novel object/mouse were counterbalanced so that they were not always placed on the same side of the mouse. We speculate if there was no counterbalancing done that the mouse may have preferred a certain chamber instead of a particular mouse or object. One last thing we would like to see is the exact age range in which the mice participated in the behavioral tests since it is not made completely clear in the Methods section. <br /> The Results section that discusses Figure 2 begins with an explanation of why the authors focused on mPFC-NAcSh connections in their study. However, we suggest that this is explained in the Introduction instead since it left us wondering why the authors focused on mPFC-NAcSh connections in their study; it was unclear whether there was literature supporting this decision. <br /> In Figure 3 panel B, we think it is an interesting finding that SH mice also showed significantly decreased interacting time with the conspecifics in the habituation session as GH mice did, given that these SH mice would later do poorly in social recognition tests. Thus, it would be better to notify the readers that it is an unexpected or interesting finding, and also propose the hypothesis of this phenomenon. For the panel E and F, you did a good quantification of neuronal activity in the NAcSh-projecting IL neurons by calculating the percentage of c-Fos and eGFP co-labeled neurons among total eGFP labeled neurons, because the number of NAcSh-projecting IL neurons may change in SH mice compared to GH mice. We would like to know whether the neural circuitry from IL to NAcSh is altered by social isolation. For this purpose, we suggest you inject an equal amount of AAVrg-eGFP-Cre in both GH and SH mice, and quantify the number of eGFP-labeled neurons in them. <br /> For Figure 4, the data is generally well organized and the experimental protocol was summarized well in the schematic. However, for Figure 4D (the comparison between spiking in baseline and in the presence of CNO), it would be valuable to show the effect of the control saline vehicle on spiking for both the eGFP mice as well as the hM4Di mice to illustrate that the presence of the IP injection or saline has no effect if it indeed had none. The preference index had also proved difficult to read; the way the lines overlapped made the connections between the data points on each bar hard to discern. Perhaps color coding them or using different shapes instead of uniform dots would be beneficial. <br /> Overall, Figure 5 seemed clear and straightforward. However, we did want a bit more clarification as to why 1mg/kg CNO was used for vehicle injection even though previously in Figure 4 there was 3mg/kg used. We suspect this may be due to an increase in sensitivity pertaining to excitation but would like to see that confirmed within the literature if it is the case. Another point to be made is that 4B and 5B appear to be inconsistent and like to see a bit more clarification or a comment on why that may be.

Merits<br /> For Figure 1 panel A, the addition of the schematic was helpful in understanding the timeline of the study for both GH and SH mice. The same can be said for panels B,E, and F. The results and tests done of the mice seemed appropriate to further aid in the understanding of social recognition and preference. All in all, the authors used every panel in the figure to justify how they came to their conclusion regarding the social preference and recognition test GH and SH mice. <br /> Figure 4 is paramount in illustrating the nuanced effect of this circuit on social behavior—namely, the impairment of social recognition while retaining nominal social preference in mice which was derived from the clearly reported results of the inhibitive manipulation. This connection is no more salient in the paper than here.<br /> Figure 5 was imperative for our understanding in rescuing social recognition. Hand in hand with Figure 4, it clearly defines how social recognition is affected by the loss and regain of the NAcSh-projection IL neurons. In particular, the middle graphs in E and F do an excellent job in highlighting the effect of IL-NAc shell neurons activation in social preference and recognition tests for both GH and SH mice.

Future Directions <br /> The findings of this paper prove to have important impacts pertaining to acquisition of social familiarity. Although it was noted in the paper that future direction includes investigation of animal models of ASD, it would be also beneficial to look at animal models of schizophrenia. In specific, revaluation of what was found in Piskorowski et al. in comparison to this paper pertaining to the critical period. The discrepancy, that is 2 weeks compared to 11 weeks, seems way too large and should be further investigated to better understand why the critical period may be one or the other. As an alternative, it may be found that it may be neither and that there is another time period that better represents the critical time period for normal social recognition.<br /> It would also be interesting to look into why the excitability of NAcSh-projecting IL neurons had decreased. Because the neurons in SH mice showed no significant electrophysiological differences from those in GH mice, the decreased excitability is likely a result of morphological changes. Indeed, Silva-Gómez et al. (2003) found that a similar social isolation protocol in rats results in decreased dendritic spine density within the mPFC.<br /> It is interesting and surprising that both GH and SH mice showed significantly decreased interacting time with the conspecifics in the habituation session in Figure 3B, but the social recognition was impaired in SH mice only. It might be because the SH mice could not remember the familiar mice and recognized them as all novel ones, which would indicate that the processes of memory consolidation and memory retrieval were impaired in SH mice. Thus, we think it would be interesting to investigate social recognition with a perspective of memory in the future.

Works Cited:<br /> Silva-Gómez, A.B., Rojas, D., Juárez, I., & Flores, G. (2003). Decreased dendritic spine density on prefrontal cortical and hippocampal pyramidal neurons in postweaning social isolation rats. Brain Research, 983(1), 128-136.

Piskorowski RA, et al. (2016)Age-Dependent Specific Changes in Area CA2 of the Hippocampus and Social Memory Deficit in a Mouse Model of the 22q11.2 Deletion Syndrome. Neuron 89, 163–176.

On 2020-03-31 15:20:48, user Søren Grubb wrote:

Dear David A. Hartmann and the Shih lab,

I want to congratulate you on a beautiful work. I know how thorough and careful you are, and this subject of whether pericytes are contractile or not, is very important – and controversial. So, I read your paper with great interest, and I am very surprised to see that<br /> you observe capillary lumen decrease when optogenetically stimulating true pericytes. I have a lot of questions and comments, so I hope you don’t mind!

I agree with your finding (or confirmation) that smooth muscle actin expression drops<br /> after (up to) 4th order capillary, as we have also found in our recent Nature communications paper: https://www.nature.com/arti.... You cite the Alarcon-Martinez et al paper to claim that there may be SMA that is not detected. I would like to make you aware that in that paper, they have a different numbering for the blood vessels, which means our 1st order capillary would correspond to their 3rd order blood vessel. Which<br /> means that when they improve their SMA stainings from 4th to 6th order vessels using their fixation procedures, it would correspond to from 2nd to 4th order capillary with our numbering. So, my conclusion is that retina might be more difficult to fixate than brain, and we do not necessarily miss out on any SMA. But I may be wrong, I often am.

I see that you have mentioned a “sphincter” in supplementary movie 5. I am not sure what<br /> your purpose of mentioning that sphincter is, I just want to let you know that that is not a typical precapillary sphincter. A typical precapillary sphincter and bulb are visible just next to the penetrating arteriole around 21 seconds into your Supplementary movie 7 where the tissue moves a little bit in the z-direction. For more info on precapillary sphincters see our paper: https://www.nature.com/arti...

For our paper we adopted your nomenclature for ensheathing pericytes on the first order capillary (which you call precapillary) because I feel that is a good description. However, your drawing of ensheathing pericytes indicated to me that they were a continuous sheet<br /> surrounding the capillary, which I found confusing until I did the confocal microscopy<br /> myself and saw that it was just because the pericyte processes are so tightly positioned<br /> around the capillary that they look like a continuous structure. I have tried to draw detailed ensheathing pericytes on Figure 1e in our NatComms paper (see link above). Maybe we all should do an effort to make more precise drawings of the mural cell morphology, like Zimmermann did beautifully in his paper: https://link.springer.com/a....

I would like to also make you aware that the smooth muscle “hybrids” as we have called<br /> the smooth muscle cells on far the most of the penetrating arterioles (with average<br /> lumen diameter around 12µm), often have a slightly bulbous nucleus, and 2-3 processes<br /> in each direction around the arteriole. So, they look significantly different from the “true” smooth muscle cells that exist on larger arterioles and arteries, which have spindle shape and an elongated nucleus.

I have never understood the reason that only the true pericyte soma should be contractile, so I’m glad to see that you address that on page 3 line 25-29. My concern has been, that because the pericyte soma protrudes it can somehow push close the capillary lumen at that exact spot if the tissue around it swells or if the capillary is somehow pulled in direction of the arteriole (by strong arteriole contraction) – and thereby false positively be interpreted as contraction.

You write that the localized two-photon optical manipulations “disentangles their local<br /> influence on capillary diameter from the influence of flow in upstream vessels”, but pericytes have gap junctions that connect them to endothelial cells, so how can you be sure if you only stimulate and observe locally? Have you tried to uncouple them with gap junction blockers?

If one capillary branch has increased RBC flux by optogenetic stimulation, does that<br /> mean the other branch has decreased flux (indicating a local effect) or does the other branch also have increased flux (indicating an upstream effect)?

Have you ever seen any indication that the blebbing you see also happens on the luminal<br /> side of the pericyte, which could push the endothelial cell towards the lumen? Are<br /> these “contractions” and blebbing by depolarization pericyte specific or would<br /> you find similar blebbing in other cells you depolarize optogenetically, for example astrocytes? Do you think the blebbing is caused by an increase in intracellular<br /> Ca2+?

You write that the blebbing might be caused by “excessive mechanical tension” when<br /> pericytes are stimulated to “supraphysiologic levels”. If the stimulation you use is not physiologically relevant but necessary for effect (in contrast to the Hill paper, that saw no effect), under what conditions do you think true pericytes contract?

If the actin cytoskeleton should be able to create a force, I guess most of the actin<br /> cytoskeleton should be organized to pull in the same direction, have you seen any indication of that?

The idea to ablate bridging pericytes is very elegant. When you ablate a pericyte, I assume<br /> it will go into apoptosis and the first thing it does is retrieve its processes and round up. Could the increased capillary lumen diameter be explained by the extra volume around the endothelial cell that a retraction of the pericyte processes leaves behind?

Thanks for a really interesting paper, it was a pleasure reading it. I really hope you find<br /> time to answer my questions.

Best regards

Søren Grubb

Lauritzen<br /> lab, Department of Neuroscience, University of Copenhagen

On 2019-12-17 16:36:21, user Johan S. Martinez-Fuentes wrote:

NE 598 Group 3<br /> IntroductionWe are university students enrolled in a course focused on understanding neural circuits, including factors important for their development and control of animal physiology. In an effort to promote constructive discourse of current research in this field, and to gain experience in the process of peer-review, we provide the following critique of the currently unpublished manuscript from Wallace et al. posted on biorxiv.org (version: July 25, 2019).

Summary:There has been a growing appreciation for the role microglia play in regulating synaptic connectivity during brain development; however, how microglia regulate the circuit integration of neurons in neurogenesis in the healthy adult brain remains unclear. Wallace et al. focus on the effects of microglia on adult-born granule cells (abGCs) as part of the mechanisms underlying a previously reported increase in activity of principle neurons of the olfactory bulb (OB) after microglia ablation. Their general approach consists of combining genetic labeling methods with in vivo live-cell imaging of microglia and abGCs (both constitutive labeling and GCaMP indicator of activity-related calcium influx) under conditions of odor presentation and microglial ablation using the CSF-1R antagonist PLX-5622. Overall, the authors found evidence for specific microglial interaction with adult-born abGC spines, that the population-level dendritic GCaMP response of OB abGCs was significantly decreased, and that the excitatory input into the abGCs were selectively decreased with no change to their inhibitory input. These results further support the notion that microglia play an important role in sculpting the circuit connections of nascent/developing neurons in the context of adult neurogenesis, with new descriptions of potential molecular mechanisms that may be at play. Overall, we recommend more consistency with respect to experimental time courses to strengthen the overall conclusions, more consistent definitions of threshold values for the classification of evoked responses, and clearly articulated cohort numbers and ages. We recommend improving the labelling of figures in terms of defining the control and experimental groups using keys, and the sizes of the two groups should be more balanced. Further, we recommend consistency between written text, legends and the figures themselves, particularly in cases where the number of odorants stated and displayed do not match. The authors may elaborate on these points in-text for improved understanding of their findings.<br /> In Figure 1, to explore the nature of microglia interactions with abGCs, the authors employ viral-genetic labeling to target both cell populations and examine them under in vivo two-photon imaging. The authors confirmed the highly motile nature of microglial processes, as microglial interactions with abGC "mushroom" and "filopodial" spines were quantified by spatial overlap of the cell markers. While overlapping of both types of spines with microglial processes were not significantly greater than expected by chance ("offset" image analysis), there was an increase in the number of microglial interactions with mushroom spines with about two-fold increase in interaction time than expected by chance. This was not seen with microglial interactions with filopodia, thus showing preference for mushroom/potentially active spines.<br /> In an effort to investigate how microglia ablation effects odor-evoked responses of abGCs, Wallace et al used two-photon imaging to observe abGC calcium activity over the entire time course of abGC development in anesthetized mice on PLX5622 (PLX) chow. Compared to controls, abGC neurons in PLX-treated mice were less responsive to odors as quantified in 2F by cumulative distribution plot. Additionally, figure 2H features a raincloud plot that quantifies a decrease in the median lifetime sparseness of the abGC dendrites in OB of PLX-mice. Moreover, figure 2I quantifies median response amplitude across all dendrites, showing significant decrease in median amplitude across dendrites of treated anesthetized mice. These results suggest a decrease in their dendrites’ temporal selectivity and likely reflects the developing abGC’s decreased odor responsiveness. Another set of experiments testing these effects in awake mice were performed (Figure 3). cumulative distribution of dendrite responses in figure 3B affirms suppressed calcium transients under odor exposure in PLX-treated awake mice. There were not significant decreases in median number of responsive odors (Fig. 3C), nor lifetime median sparseness of dendrites.<br /> In Figure 4 the investigators explore whether effects of microglial ablation were specific to developing versus mature abGCs. After following the experimental protocol shown in Figure 1a, the cumulative distribution of the responses are unchanged after PLX administration, and noise is not significant (Figure 4c). Cumulative distribution of the number of effective odor (exceeding an ROC threshold of 0.53) also shown not to be significant (Figure s4d). Finally, this figure also includes a Raincloud plot of lifetime sparseness, with control and PLX groups largely overlapped, and kernel density estimates underneath with box plots showed insignificant differences (Figure 4d). Thus, the ablation of microglia did not significantly change the evoked responses of developed abGCs, highlighting the importance of microglial during abGC development.<br /> In contrast in figure 4.1, there is no administration of PLX chow. The abGCs are imaged twice at the 3 month post-injection, and three weeks later alongside control group imaging (Figure 4.1a). Dendrite-odor pair response comparisons in the images Before 1 and Before 2 as seen in the timeline garnered similar results with an R2 value of 0.73 (Figure 4.1b). There are also distribution plots show no significant difference between groups (Figure 4.1c-e). Overall, this suggests abGC cells do not display significant differences in their responses three weeks after the injection. Similar results are shown in Figure 4.2 with 9 weeks after the first imaging set (Figure 4.2a).<br /> In Figure 5, possible PLX-mediated structural changes to abGC spines in the EPL were assessed by quantification of spine number and volume in two-photon acquired images. The authors measured spine density per abGC after four weeks with or without drug treatment during abGC development and found no significant difference resulting from microglial ablation. When considering total population of spine volumes, the PLX-treated condition revealed spines were significantly smaller compared to those in control. However, this effect was not observed when cell-averaged spine volumes were compared between conditions.<br /> In figure 6, the authors looked at electrophysiological correlates in the previously observed spine head sizes during abGC development. To do this they simultaneously recorded in vitro spontaneous excitatory postsynaptic currents (sEPSCs) using patch clamping and in vivo imaging (Figure 6a). They report that there are no differences in frequency of sEPSCs from control to PLX-treated mice, but observed reduced amplitude (Figure 6c-d). They then report their finding of the membrane properties as being the same across all mice, control and treated (Supplemental 1). To test potential changes to spontaneous inhibitory postsynaptic currents (IPSC), the authors repeated the same experiment but tracing the IPSCs and found no difference between the control mice and the PLX-treated mice(Figure 6e-g). These results show changes in abGC functional responses is due to the weaker excitatory inputs. Using the timeline in Fig. 4, the authors also tested electrophysiological effects of microglial ablation on matured abGCs (Fig. 7), and found that ablation after development has no effect on synaptic input, either excitatory or inhibitory.

Major Issues:We believe there is a general lack of explicitly tracking the age of mice used in this study, which may potentially affect the significance of the findings. The authors list the age of mice used as 8-12 weeks from the beginning of experiments. This may be too large of a range given the lack of knowledge in the field regarding how factors regulating neurogenesis change with age (Kase et al., 2019). One suggestion is to explicitly list the n associated with the age of mouse used, and perhaps in supplementary figures color code certain quantified data points by age to show how measures may or may not be different. Figure 1 uses a low number of mice (n=3), and so it is unclear whether the significant increased time of microglia-abGC interactions may be more related to earlier or later ages at this adult brain stage. The issue here may be summarized by the question, do developmentally perturbed abGCs recover activity after 12+ weeks? We invite the authors to consider addressing this timing discrepancy.<br /> In Figure 2, the timeline for development of abCGs could be improved upon because there doesn't seem to be a fixed time point to anchor the data set, we are unsure to what extent the authors can be confident in their comparisons. Moreover, there is no mention of the timeline that the authors used in Figure 3. Additionally, the cumulative distribution plots used in figures 2 and 3 do not do an adequate job of showing the discrepancy between the PLX and control groups. We suggest using another form of statistical analysis to depict the disparities between these two groups more effectively (e.g., consider general histogram depicting counts per bin of response level). There are some more integral criticisms that can be made for Figure 4 even though it is useful and well-done. In the figure legend, 16 compounds are discussed; however, the figure itself only shows the combination of the compound, heatmap, and trace for 15 substances. Furthermore, while each set of experiments looks at a different aspect of the effects of microglial ablation, the different timelines that are used over the course of the experiment and the changes to it as seen in figure 4 specifically, can be problematic when trying to make assertions when trying to make comments on the findings of the paper as a whole. Additionally, the age of the animals themselves in not mentioned. Furthermore, the ROC threshold indicated for treating evoked responses as effective is inconsistent between the primary figure, where it is listed as 0.53, the supplementary figure 4.1 where it is listed as 0.39, and the supplementary figure 4.2 where it is listed as 0.78. The use of supplementary figures and experiments was useful on its own right; however, changing the threshold values between the sets of experiments at their analogous counterpoints is problematic when trying to consider the outcomes of the parts in unison since all of the portions are using the ROC threshold value in the same way. <br /> There are two main issues to address in Figure 5. One is the abrupt change in the timing of lentiviral labeling of abGCs and PLX feeding. Here, the two were simultaneous, such that experimental migrating abGCs are expected to interact with microglia not present in other developmental ablation experiments. This particular timing would make the experimental condition more similar to control where microglia are intact. Thus, the synaptic findings in Figure 5 are not strictly transferable to functional deficits seen in Figure 2. This also means that the authors may expect a more robust synaptic phenotype if they revert to the experimental timeline used in Figure 2. The second issue is the oversampling conducted in the experimental condition: there was an average of ~61 spines sampled from each control abGC, and ~101 spines from each PLX-treated abGC. The authors may consider quantifying more control spine volumes to make a more balanced/fair comparison.<br /> A significant issue with Figure 7 is that the authors decide to use an experimental timeline different from that of Figure 4 where the time from lentiviral labeling is shortened by one month, but their choice behind this change in timeline is not explained. Besides the change in timeline, the recordings are completed after a month after injection, whereby the difference in age of abGCs from shorter experimental timelines makes it unclear what sort of broader conclusions can be drawn.

Minor Issues:In Figure 1B, the insets showing percent coverage are insightful for understanding microglial-abGC interaction dynamics; however, it suffers from a lack of x-axis labeling that affects ease of reading. We suggest either moving all insets to its own panel with explicit time labeling, or make the x-axis reference clearer in sub-panels. Regarding spine selection, it may be important to address how/whether other spines not well-described by the two classifications were considered (i.e., were stubby and cup-shaped spines considered/observed?). It would also be interesting to see whether there were any differences across the quantified measures as a function of time (1-4 weeks post-injection).<br /> It would be interesting if the authors addressed their rationale for picking the odors that they did in both figures 2 and 3. Panels 2D and 3A would benefit from providing the common names of the scents corresponding to each odor. Figure 3 in general could also be improved by distinguishing the PLX and control groups more effectively. This could be accomplished by adding clearer labels on each of the figure insets. We would also suggest increasing the overall number of experimental mice for this particular experiment to see if the data that is currently trending towards significance can be bolstered above threshold. <br /> While overall Figure 4 is quite well-done, there are some minor errors and possible areas of improvement. In the timeline in part 4a it would have been useful to label the Before (control) as a control imaging session because looking at the figure at first glance it is not entirely clear that the control is not another group of mice and rather is the same mice imaged twice. With the consideration that a timeline is used (which was a good idea) mentioning first imaging and second imaging session directly on it could be useful. It may be helpful to the reader if the names of the odorant compounds were included. Furthermore, while one can eventually piece together that the control group is in purple and the PLX group is in orange, they are unable to do so from the figure alone. In figure 4.2d there is a key on the figure that indicates these groups are specified by these colors, but this cannot be well determined in the primary figure; while a small thing to fix, this is integral to comprehending the results accurately. Furthermore, only three mice are used in the primary experiment. It may have been useful to look in more mice for the purposes of the experiments.<br /> In reporting the results for Figure 5, it is not intuitive why cell-averaged spine volume is not significant between control and experimental conditions, but it is the opposite when analyzing individual spine populations. A short description to reconcile this conflicting finding is needed. We suspect this suggests that a relatively small population of PLX-treated abGCs harbor most of the spine volume changes. Furthermore, it is unclear in the discussion how well the authors may speak to a trend in increase in spine density when there seems to be two data points that may be driving a lot of the PLX population average.<br /> In Figure 6C-G, the figures are all comparing control to PLX-treated mice.These graphs all have two different colored sets of data, and in 6A there is a demonstration of what these two colors correspond to. However, in the rest of the figure there is no clarification of which set of data corresponds to which color. We suggest the authors include which data set if for which condition on each of the graphs or add a legend near these graphs to be clearer to the readers.

Merits:In Figure 1, the authors highlight evidence of cellular interactions that lay proper motivation for examining the effects that microglia may have on abGC functional development. The data acquisition and method of analysis are generally well-described in their respective report sections, and the conservative nature of quantifying microglia-spine interactions lends to more confident data. The comparison of real data to its offset counterpart across many quantified measures is also a clever way to argue for microglial preferential interaction with mushroom spines.<br /> Figure 2 provides excellent histological confirmation of microglial ablation. In figure 2 and 3, the authors showed the processed data for the GCaMP6s traces in panels 3A, 2D, and 2E in an easily interpretable manner. Moreover, the decision to use a raincloud plot for panel 2H and a bar graph in 2F showed significance more effectively than the cumulative distribution plots. <br /> There are several parts of the experiments associated with Figure 4 that are highly useful. The use of a timeline is highly conducive the set up of the experiment highly understandable and creates a visual image that is easier to comprehend than the worded explanation. Furthermore, it is useful that the experimenters have chosen to include the actual chemical structures of those used in the experiments. The raincloud plot shows expertly how the data compares between the groups very directly. The kernel plot gives a sense of the individual data points, and the box plots give important information on statistical measures of the data. Additionally, the concept of including an experiment on discussing the relevance of the ablation of microglia in the context of whether developed abGCs are affected strengthens the overall argument and credibility of the paper as a whole. Finally, including a supplemental section which had experiments both on looking at simply long time post injection in comparison to the three month mark (Figure 4.1) and one that looked at an increased period of time with the PLX administration (Figure 4.2) was also very useful in bolstering the results.<br /> Figure 5 is a valuable addition to the article as it brings a cell biological mechanism into discussion for the observed functional phenotypes in microglial ablation. We commend the authors for reporting different single-spine and single-cell perspectives of analysis on the same data set in Fig. 5D even though the two analyses lay out a complex and seemingly conflicting picture. But combined with the rigor in the authors’ approach, this motivates the reader to ponder future experiments to explain the data.

Future DirectionsWith respect to Figure 1, future experiments may further partition the subtypes of mushroom spines with which microglia interact based on different post-synaptic markers. For instance, microglia may preferentially interact with spines expressing certain receptors. It is also unclear how activity in the olfactory bulb may direct microglial interactions with abGC spines. Increasing olfactory activity in mice by housing in an environment with prolonged exposure to stimulatory odors, and subsequently tracking microglial interactions, may result in more robust phenotype and better reveal microglial attraction to certain spines.<br /> Concerning Figures 2 and 3, we suggest that future experiments should attempt to refine the timeline by providing a fixed time point for the development period of abGCs. We also suggest that more experimental mice be added to the cohort in figure 3 to probe the validity of the non-significance of their statistical analyses. <br /> As in many other sets of experiments seen in this paper, in Figure 4 a number of different odorants was used to evoke responses. We think it would be interesting to take a closer look at the chemical composition of the compounds and look at the differential effects on the responses of the abGCs. Additionally, regarding the fourth set of experiments in particular it may have been interesting to look at the before period being even further along in the life of the microglia. Microglia live for a couple years in mice, it may be interesting to look at the effects of the PLX administration in microglia that were not only fully mature, but also as they are reaching the end of their life.<br /> An intriguing idea stemming from the data in Figure 5 is that there is a subpopulation of abGCs that is particularly susceptible to microglia-dependent spine volume enlargement. Given the relatively low number of abGCs sampled per group, this may be a rather large subpopulation, perhaps representing dedicated GCs or periglomerular cells, both of which should be labeled non-discriminantly here. Thus, using a cell-type resource of the olfactory bulb, such as that created by Tepe et al. (2018), to find a lead for molecular markers to target susceptible adult-born neuron subpopulations may push our understanding of the phenotypes reported here.<br /> With regards to future experiments from the EPSC experiments (Figures 6, 7), it may be interesting to investigate potential changes in mini-EPSCs or -IPSCs to flesh out a fuller picture of the state of synaptic activity. The approach would effectively be the same only with acute introduction of tetrodotoxin at the site of recording. These minis may behave differently depending on the ablation and can have an effect on the EPSC frequency and amplitudes. This difference could be a notable change that leads to what appears to be either no change or a change in amplitude.

Works Cited:Kase Y, Otsu K, Shimazaki T, Okano H. (2019). Involvement of p38 in Age-Related Decline in Adult Neurogenesis via Modulation of Wnt Signaling. Stem Cell Reports.;12(6):1313-1328.<br /> Tepe, B., Hill, M. C., Pekarek, B. T., Hunt, P. J., Martin, T. J., Martin, J. F., & Arenkiel, B. R. (2018). Single-Cell RNA-Seq of Mouse Olfactory Bulb Reveals Cellular Heterogeneity and Activity-Dependent Molecular Census of Adult-Born Neurons. Cell reports, 25(10), 2689–2703.e3. doi:10.1016/j.celrep.2018.11.034.

On 2019-11-05 15:11:52, user Johan S. Martinez-Fuentes wrote:

NE598 GROUP 3<br /> We are students at Boston University focused on learning about neural circuits and how their structure and function relate to animal behavior. In an effort to promote constructive discourse of current research in this field, and to gain experience in the process of peer-review, we provide the following critique of the currently unpublished manuscript from Hammond et al. posted on biorxiv.org (version: September 05, 2019).

Summary: Multiple sclerosis (MS) is a neurodegenerative disease characterized by loss of white and grey matter leading to motor and cognitive disability. It remains unknown exactly what role the components of the immune system, including microglia and molecular complement factors (e.g., C3, C1q), play in disease progression of grey matter in MS. Hammond et al. use a mouse model of MS called experimental autoimmune encephalomyelitis (EAE) in combination with molecular, genetic, and immunohistochemical approaches to find that C3/C1q and microglial activation are implicated in different aspects of grey matter pathology in EAE. These results argue for complement signaling, and associated microglial activation, as important players in MS-related grey matter degeneration and disease severity. This research has promise of being impactful as it contributes to our general lack of knowledge surrounding lesions of MS independent of demyelination (Mandolesi et al., 2015), and potentially highlights new avenues for therapeutic treatments. Overall, we recommend improving the usage and presentation of some of the data as well as addressing complexities of cellular phenotypes, which appear to be understated.<br /> Figure 1 explored the potential functional relationship between the complement production, specifically that of C1q and C3 protein, and the EAE model. The authors used western blot to analyze C1q and C3 expression in hippocampal lysates comparing the sham and EAE mice and found an increase in both the levels of C1q and C3, 2.6-fold and 1.9-fold respectively as compared to the increase in the sham controls (Figure 1A). They normalized the band densities to the sham controls and quantified the C1q and C3 results (Figure 1B). Further, they explored mRNA expression in hippocampal tissue by isolating RNA from the sham and EAE (n=10 each) mice and analyzed using qPCR and quantified the fold change of C1qa and C3, with 2.1 fold and 8.4 fold above sham controls respectively which implicated a potential connection between local gene expression and increased protein production in the model (Figure 1C). Additionally, the group used qPCR to analyze sham and EAE (n=5 each) hippocampal CD11b+ microglia/myeloid cells and their C1qa and C3 gene expression finding no significant difference in the expression of C1qa in the EAE mice as compared to the control, but there was 54.5-fold increase for C3 (Figure 1D).<br /> Figure 2 provides visual affirmation of the upregulation of C3/C1q in the hippocampi of EAE-mice compared to sham controls. Immunohistochemsitry was used to shed light on the differential spatial patterns of C3/C1q expression across regionalized sections of the hippocampal formation. Specifically, EAE-mice showed an increase in C1q across the entire hippocampus and in some cases showed co-localization with PSD95 suggesting it may affect synaptic functionality. This phenomena extended to C3/C3d expression in the CA1 stratum-radiatum region of the hippocampus. <br /> In the third figure, the investigators display the results of an experiment developed to determine the effects of C1q or C3 loss on the motor impairment in EAE mice by comparing pathology in EAE immunized WT, C1qa KO, and C3 KO mice (n=24, 17, and 7 respectively) on a clinical scale over the course of approximately one-month post immunization. They found nearly identical results between the C1qa and WT mice groups, but lower clinical scores indicating less severe EAE related deficits in the C3 KO group. Notably, the timeline of symptom onset was consistent across the groups. To display the results, they used a graph of Days Post Immunization versus Clinical Score displaying all three of the groups’ mean scores (Figure 3).<br /> Because the authors had previously found a significant amount of synapse elimination in the CA1-stratum, in Figure 4 they looked further into the role of complement proteins in grey matter loss, specifically in Homer1 and PSD95+ puncta in the Figure 4. Using immunohistology the puncta were quantified using the “find spots” algorithm setting a threshold of brightness for the PDS95+. Compared to the WT EAE, which had a 13% decrease in Homer1 puncta, the C1qa KO EAE showed only a 7% decrease in puncta compared to the sham control. However, both C3 and C1qa showed no significant difference to the sham control. All data were normalized to the sham control and each measure was taken from an average of 6 image stacks per mouse. This could suggest that the alternate pathways of C3 is more important for grey matter pathogenesis due to increased protection from synapse elimination in C3-KO compared to wild type and C1q-KO.<br /> In Figure 5, to assess the role of C1q and C3 for activated microglia in EAE, the authors conducted morphometric quantitative image analysis of IBA1 immunostain signal in the hippocampus across control and KO animals. Activated microglia show shorter, thicker skeletal processes. Thus, an increase in activated microglia was measured through segmentation algorithm in Volocity by (i) increased IBA1 expression, (ii) increased IBA1 volume, and (iii) a decrease in the ratio of either IBA1+ skeletal length or surface area to volume compared to sham control. In both EAE WT and EAE C1q-KO conditions the authors observed a significant increase in the level of activated microglia across all measures, but no significant difference was seen in EAE C3-KO. Thus, C3-dependent activity appears to be important for EAE-related microglia activation, and taken with the previous results, this may suggest why synaptic protection in C1q-KO is insufficient for improvement in clinical score. This set of results is highly intriguing as it suggests microglia as a target for therapeutic intervention in order to potentially improve grey matter health and patient outcomes.

Major Issues:<br /> While Figure 1 supports the implication of the complement protein C1q and C3 expression in the deficits that characterize the EAE model fairly well, there are a few critical issues. Firstly, it includes both male and female mice, and it is well-known that MS has a higher prevalence among females and this could be a potential issue with the EAE model. The investigators claim that there is no sex difference, but their n of 7 and 11 is too small to confidently make this claim. They should include more mice and run the proper statistical tests or comment on this confluence. Further, they perform an experiment looking at hippocampal CD11b+ microglia/myeloid C1qa and C3 gene expression, but only use one marker. Figure 1 introduces the issue of isolating resident-brain macrophages (microglia) rather than those that pass cross the blood brain barrier, whereby CD11b+ is insufficient to distinguish because it is expressed across a variety of immune cell in adhesion-related associations. In Figure 5, the use of IBA1 is not strictly restricted to microglia but also includes monocyte-derived macrophages that may be crossing the blood-brain barrier, which poses issues in isolating a microglial phenotype (Satoh et al., 2016). For example, if the C3-KO condition results in increased numbers of IBA1+ macrophages then relying solely on IBA1 may mask a microglial phenotype. The authors may consider using a co-marker exclusive to microglia (e.g., TMEM119). Authors may consider analyzing protein expression in microglia.<br /> Regarding the issue of having insufficient n for comparison, the authors must seriously consider the risk of oversampling certain conditions so as to bias or skew results. Instances of this can be seen in Figures 3, 4, and 5. Generally in these figures, the WT n ~20, while C1q conditions have n ~ 15, and lastly C3 conditions are <10. The authors may consider increasing sampling in undersampled conditions, or re-run statistical analyses of subsets of oversampled groups to see if results are still significant.<br /> In Figure 2, although the sparse colocalization of C1q and PSD95 in figure 2 E-D somewhat implies that C1q is upregulated at synapses and thereby dendrites, the images do not provide the resolution necessary to resolve this colocalization or actual synapse itself. This criticism extends to 2I-J for the same reasons, and the issue of rigorously defining synapses is also apparent in Figure 4. The punctas that are being marked are post-synaptic, but there is no confirmation of association with dendrites or any other part of the neurons creating these synapses. The authors may consider sparsely labeling neurons with virally introduced, promoter-driven expression of fluorescent protein to visualize spine morphologies. Returning to Figure 2, there is no bar-graph quantifying the findings for these last panels. We acknowledge that 2F adequately resolves C1q expression and thereby confirms their antibodies’ efficacy, but this panel would benefit from providing a DAPI-stain that confirms the structural integrity of their mouse-model’s cytoarchitecture. In 2G, we feel that the images are not easily interpretable and could be improved by using a unique immunohistological marker to tag blood vessels and by normalizing the signal so that we can more clearly resolve the upregulation of C3/C3d puncta. The reader would also benefit from low-magnification insets to images 2D-J to confirm proper sub-region comparison.<br /> Conceptually, the major criticism of the experiment outlined in Figure 3 would be its inconsistency of focus compared to the rest of the study. While the vast majority of the experiments work to implicate the complement pathway in hippocampal degeneration, the clinical test that is chosen is a motor test. It may have been more useful to this study in particular to use a cognitive behavioral test for memory. Furthermore, they include no comparison with a sham mouse which is not suitable as there is no control point of reference for the clinical score.<br /> For Figure 4, the analysis could be done more in depth with a much clearer explanation of which sections are being studied and compared.The data is being normalized, but it is unclear from which sections exactly. Because of the way that the data is presented there is no way to check if there is just a concentrated population of these punctas in a certain section/hippocampal subregion, or if the spread of punctas is truly as uniform as the normalized data suggests it is.<br /> An essential piece of evidence missing from Figure 5 is a positive control for microglial activation in C3-KO mice. Are the microglia, under EAE conditions, capable of exhibiting activation characteristics? It is possible that there is large-scale defect on inflammatory processes related to the germline loss of C3, and not directly related to the functions of C3 itself. Considering the onset of motor symptoms across all mice is similar, one simple way to address this is to check if they all also share an activated microglial phenotype around day 6 and/or day 14 post-immunization. Another way may be direct intracerebroventricular (ICV) injection of LPS (here, the authors may also see if EAE is correspondingly accelerated).

Minor Issues:<br /> In Figure 1, it would be more conducive to show all the data points on the bar graphs so that a better representation of the spread of the data can be visualized. It would also be useful for the group to include what percentage of mice had an increase in C1q and C3. Furthermore, it would be useful for the group to include more on the condition of the animals and whether they used all the data they collected in the analysis or whether some was thrown away.<br /> The age of the mice should be presented in figure legends (see Fig. 2, 4, 5) to build upon the narrative established in Figure 1. Moreover, although the authors attempt to show the aforementioned co-localization of C1q and PSD95 we think figure 2 could be vastly improved by including an inset in 2D-E to contextualize where we are looking with respect to the hippocampal formation. <br /> Overall, the display of Figure 3 is well crafted and the legend does well at explaining the facts of import; however, there could be some potential corrections. On the graph two of the groups are in the same color, the readability may increase by choosing different colors for each of the mice groups—especially if a sham control is added as earlier recommended. Further, it may be useful to include more background, possibly in the results portion for this figure, of the clinical test utilized and what different scores indicate relatively in terms of severity of symptoms.<br /> In Figure 4, the authors should be more detailed in adding magnification and the scale bar scale to the images of the IHC, and they should explain why the different images use different or the same colors. While green is generally thought to be a more visible color, the authors must keep the presentation consistent across conditions, otherwise they risk biasing the perception and interpretation of their data. <br /> Please correct the following typos:’value’ to ‘area’ in “Similar results were obtained for the surface value/volume ratio…” (Page 16); ‘Qioptiq’ instead of ‘Quioptic’ in “IHC sections were imaged… with Quioptic Optigrid optical sectioning hardware” (Page 10).

Merits:<br /> In Figure 1, The group effectively uses the data presented in the first figure to begin the argument for the rest of their study. They are able to implicate the C1q and C3 proteins as having a relationship with EAE pathway. Furthermore, as it is well-known the relationship between protein production and mRNA is not 1:1 it was a good notion to include data on both. This figure also has a high level of readability, it is labelled well, and comprehensibility.<br /> Figure 2 successfully verifies the antibodies’ fidelity in visualizing C1q, PSD95, and C3/C3d in the mouse hippocampus. Importantly, this serves as a proof of principle figure because it validates the efficacy of their experimental mouse model and confirms that their antibodies function properly. Moreover, their approach is clever because it affords them with an opportunity to resolve region-specific expression of the aforementioned molecules of interest. <br /> The concept of integrating a behavioral experiment into this largely molecularly based study as seen in Figure 3 is commendable and certainly enhances this study’s findings by implicating the functionality of the complement pathway to the actual symptomology of the disease model course. It also allows for a look at the effects of the disease in a very readable and visual manner over the course of the progression.<br /> In Figure 4, the explanation of the way the data was collected and how it was analysed was quite clear. Using the same region as had been previously found to be affected by the changes done by this study is commendable. Notable in Figure 5, the measures for microglial activation shown here abide by the standards established in the field.

Future Directions<br /> From Figure 1, to more definitively determine whether the C1qa and C3 KO’s show other inflammatory responses rather than simply the deletion of the complement proteins the group could do separate inflammation tests for the complements. Perhaps the group could build off of their experiments in the first figure by utilizing an assay to isolate the microglia of the mice and characterize the movement with pro-inflammatory markers such as TNFa, IL-2, or IL-6 by testing in WT, C1q KO and C3 KO with and without inflammation. They could also consider running qPCR. Additionally, the group could consider running this experiment with a behavioral component, such as a cognitive deficit test concerning memory. <br /> From Figure 2, concerning future directions, we think these figure panels would benefit from higher resolution images; however, if the authors do not have access to super resolution microscopy or EM we suggest performing synaptosome enrichment to quantify differential protein expression between sham and EAE populations. We also think that the colocalization results would be bolstered by recapitulating these experiments using other synaptic markers than just PSD95.<br /> It could be a very interesting future study to look at the role of the complement system in regards to motor function on a molecular level given the clinically oriented results they obtained in Figure 3. Furthermore, it would be interesting if the group carried out a cognitive deficit behavioral with the respective groups that would align more with the rest of the given study. Further, it may be interesting to look at a knockdown of the complement pathway elements analyzed and to compare the progression of symptomology in that case.<br /> Based on the findings in Figure 4, it would be interesting to see what is the spatial distribution of populations of puncta that are, as well as aren't, being reduced. It is unknown whether the elimination is uniform or specific to a single layer or to a certain projection pathway of the hippocampus. Further analyzing the data that has already been collected and analyzing it as intact stack of images rather than simply averaging many layers together. In addition to this, it would be useful to see the synapses with synaptic markers such as CaMKII using an AAV to trace them and use a retrograde.<br /> Branching from the work in Figure 5, to further explore the importance of activated microglia in EAE, future experiments perturbing the population of microglia across different stages of EAE may be conducted to see whether this is sufficient to improve clinical scores. The CSF1 receptor inhibitor, PLX3397, has been previously used to efficiently eliminate microglia, with ~50% reduction by three days (Elmore et al., 2014); this drug may be incorporated into the EAE timing to examine the effects of microglia loss. As an alternative, antisense oligonucleotides (ASOs) against C3 or CSF1 for pan-microglia may also be considered, especially since some ASO drugs are already FDA approved.

Works CitedElmore, M. R., Najafi, A. R., Koike, M. A., Dagher, N. N., Spangenberg, E. E., Rice, R. A., … Green, K. N. (2014). Colony-stimulating factor 1 receptor signaling is necessary for microglia viability, unmasking a microglia progenitor cell in the adult brain. Neuron, 82(2), 380–397. doi:10.1016/j.neuron.2014.02.040

Mandolesi G, Gentile A, Musella A, Fresegna D, De Vito F, Bullitta S, Sepman H, Marfia GA, Centonze D. Synaptopathy connects inflammation and neurodegeneration in multiple sclerosis. Nat Rev Neurol. 2015 Dec;11(12):711-24. doi: 10.1038/nrneurol.2015.222.

Satoh J, Kino Y, Asahina N, Takitani M, Miyoshi J, Ishida T, Saito Y. TMEM119 marks a subset of microglia in the human brain. Neuropathology. 2016 Feb;36(1):39-49. doi: 10.1111/neup.12235.

On 2019-04-23 12:47:59, user Brian Levine wrote:

In this study, the researchers assessed concurrent validity of questionnaires against established measures in a sample of 217 participants. There is a strong motivation for this kind of study, which provides useful information for researchers assessing memory, imagery/scene construction, navigation, and future thinking. The researchers are commended for a comprehensive study reflecting many hours of effort in order to execute these measures. My comments will be largely focused on the measures of autobiographical memory (AM), some of which were developed by my group. This comment grew out of a discussion with my trainees who also read the article, including Nick Diamond, Carina Fan, Raluca Petrican, Stephanie Simpson, and Lynn Zhu. I thank the authors for posting this preprint, open to community commentary.

A major contribution of this paper is an emphasis on subjective experience, which, although impossible to assess directly, is important to the consideration of episodic memory. This paper supports the view that subjective and objective instruments do not assess the same thing. As stated by the authors, the use of these instruments depends on the goals of the study. Where we disagree is the premise that seems to be implied in the title, which is that questionnaires (and to some extent, the objective tests) are measuring something different than what they purport to measure.

My main critique of the approach is that it lacks nuance in terms of levels of analysis within AM, which is itself a multifaceted construct. The authors took a strictly univariate approach in which each criterion measure is treated as a unitary measure of a latent construct. Normally, multiple measures would be deployed in a latent construct approach because no single measure is process-pure.

A main finding of the present study is that overall, subjective ratings (either on questionnaires or self-/other ratings of laboratory test performance) correlate with each other to a greater degree than the subjective/objective comparison. This is interesting though not surprising given that subjective measures do not measure the same thing as objective measures, and that they share measurement error bias. This is also the case for the scene construction measure which is held as objective, but in fact takes subjective ratings into consideration in the scoring.

In the Autobiographical Interview (AI), internal details are treated as a measure of a person’s capacity to recover contextual information from past events; external details reflect content not specifically related to the defined event and are therefore considered to be inversely related to cognitive control over memory retrieval. A recovered detail is neutral with respect to subjective/conscious experience. Patient M.L., who had a specific impairment in conscious re-experiencing of the past due to frontotemporal disconnection, showed only marginal reductions in internal detail production, even though his “remember” ratings for the same events suggested a profoundly reduced conscious experience (Levine, Svoboda, Turner, Mandic, & Mackey, 2009). He also showed reduced activation of the AM network when presented with rich retrieval cues for these events. Even more to the point, patients with severe medial temporal lobe amnesia, including H.M. (Steinvorth, Levine, & Corkin, 2005) have produced events with substantial internal details (see also Cermak & O'Connor, 1983).

The SAM episodic subscale, on the other hand, was developed specifically to probe the subjective experience of recollection at the trait level. As noted by the authors, we found that these were unrelated in our original SAM paper in healthy young adults (Palombo, Williams, Abdi, & Levine, 2013; see also Hebscher, Levine, & Gilboa, 2018 for a similar finding), nor were people with Severely Deficient Autobiographical Memory (SDAM) impaired on AM for recent events using the AI. Considering these findings, the above-described patient findings, and the more general findings of dissociation between subjective recollection and recognition performance, as illustrated in the Remember/Know technique, a strong relationship between these two measures should not be expected.

Nonetheless, some relationship between recovered details and self-reported episodic autobiographical re-experiencing at the trait level could be expected. I believe the lack of relationship is owing to the fact that the AI was designed to elicit the richest possible event descriptions from participants. As the authors note, internal details are scored liberally for the sake of reliability (i.e. the “benefit of the doubt” rule where any detail that could reasonable be considered internal was classified as such). However, there was another purpose in eliciting rich episodic autobiographical memories, which was to avoid a false positive classification of memory impairment based on incidental factors, such as misunderstanding instructions, which is of particular importance in studies of aging and clinical samples. Accordingly, under the most commonly used administration method, the subject selects an event for each time period that is highly accessible and likely well-rehearsed. The resulting score therefore reflects the participant’s best possible narrative production. This is why M.L. and H.M. could produce seemingly normal autobiographical narratives.

The SAM, on the other hand, is explicitly designed as a measure of trait mnemonics, not cognitive function as assessed by performance on a given test. The instructions for the episodic questions are “When answering, don’t think about just one event; rather, think about your general ability to remember specific events.” Even assuming that the SAM and the AI are designed to assess the same construct (which as I argue above is not the case) there is a difference between asking how one performs in general versus assessing how they perform when asked to give their best possible narrative by the examiner. By analogy, an introverted person may appear extroverted if required in certain social situations. There is no requirement to cue 5 lifetime period events as originally specified in our 2002 aging study. The AI scoring system has been applied to memories cued in different ways. Harvesting unrehearsed events from significant others may be a more effective way to estimate one’s typical retrieval abilities as opposed to their best possible performance.

The present paper used a sample of young adults. The AI as implemented in our 2002 study was developed for use in older adults and in patients. The internal detail measure is very sensitive to medial temporal lobe integrity. While this has been demonstrated in neuroimaging studies of healthy young adult samples (Hebscher et al., 2018; Palombo et al., 2018), its sensitivity to individual differences in a homogeneous sample of young adults is limited relative to individuals with compromised medial temporal lobe function, especially at the behavioral level. Nonetheless, the proportion of internal/total details or internal details/word count should be examined rather than the raw count of internal details, as the latter is confounded with verbosity. A comprehensive test of this relationship should also examine detail subcategories and time period effects. Given the foregoing I do not expect that this would change the results substantially, but it should be done for completeness.

It is intriguing that the parallel analysis on subjective vs. objective measures of spatial memory yielded significant relationships. This speaks to the complexity of AM relative to spatial memory. In navigation, the criteria for success are clearer than for AM. If someone arrives at the correct location (or gets lost), their subjective and objective experience are consonant. But if someone recalls an episode, it is unclear if the correct criterion is subjective experience or imagery or quantity of detail. As noted above, I agree with the authors that there is a distinction between subjective and objective measures, and that one’s selection of measures should be governed by the goals of the study. I would not agree that the present findings call into question whether or not internal details “is actually a good measure of recall ability” given that this measure (or its variants) has been used in over 170 studies (for table of studies, see AutobiographicalInterview.com), with good evidence for the validity of the internal/external distinction, including associations to brain structure and function. I also disagree that the findings of this study justify the use of vividness ratings alone as proxies for memory recall ability, especially in patients, who may show greater variability and less reliability in their introspective ratings than healthy adults. In any case, generalization to aging or clinical samples from a homogenous sample of younger adults is not justified.

There is great richness to these data that could be exploited in a multivariate data-driven approach. I recognize that this was not the goal of this study, but a multivariate approach such as Canonical Correlation Analysis (CCA) would allow the researchers to detect latent variables and patterns of association across these measures opaque to a series of bivariate correlations and linear regressions. This feels like a lost opportunity in favor of an assumption-laden approach that results in a flat, protracted series of individual analyses that is difficult to follow. In fact, much of the analyses here are already exploratory in that they assess the ability of questionnaires to predict performance on constructs other than the one they were hypothesized to measure. Data driven multivariate approaches are well-suited for such goals.

Finally, I had difficulty understanding the justification for proposing a single sentence test of any psychological construct. Classical test theory dictates that the reliability of a composite is better than the reliability of a single item. While single items may be useful as a screening technique, for pathognomonic signs, or when doing mass testing, they should not be used for assessment of complex traits, where interpretations of individual items may vary across individuals. A brief questionnaire for each construct would be more stable and does not pose an undue burden on participants. There are no psychometric data presented here to support the use of a single item measure aside from the fact that they showed sensitivity in this sample of healthy adults. These overfitted coefficients will shrink if tested in a separate sample. The composite test of all 15 single items could be subjected to psychometric analysis, but it is unclear if this is of interest.

Cermak, L. S., & O'Connor, M. (1983). The anterograde and retrograde retrieval ability of a patient with amnesia due to encephalitis. Neuropsychologia, 21(3), 213-234.

Hebscher, M., Levine, B., & Gilboa, A. (2018). The precuneus and hippocampus contribute to individual differences in the unfolding of spatial representations during episodic autobiographical memory. Neuropsychologia, 110, 123-133. doi:10.1016/j.neuropsychologia.2017.03.029

Levine, B., Svoboda, E., Turner, G. R., Mandic, M., & Mackey, A. (2009). Behavioral and functional neuroanatomical correlates of anterograde autobiographical memory in isolated retrograde amnesic patient M.L. Neuropsychologia, 47(11), 2188-2196.

Palombo, D. J., Bacopulos, A., Amaral, R. S. C., Olsen, R. K., Todd, R. M., Anderson, A. K., & Levine, B. (2018). Episodic autobiographical memory is associated with variation in the size of hippocampal subregions. Hippocampus, 28(2), 69-75. doi:10.1002/hipo.22818

Palombo, D. J., Williams, L. J., Abdi, H., & Levine, B. (2013). The survey of autobiographical memory (SAM): a novel measure of trait mnemonics in everyday life. Cortex, 49(6), 1526-1540. doi:10.1016/j.cortex.2012.08.023

Steinvorth, S., Levine, B., & Corkin, S. (2005). Medial temporal lobe structures are needed to re-experience remote autobiographical memories: evidence from H.M. and W.R. Neuropsychologia, 43(4), 479-496.

On 2019-02-27 11:54:52, user Laurentius Huber wrote:

This version of the manuscript is based on the following reviewer comments and responses:

Please find a formatted version of this response letter with figures here: https://goo.gl/3czXWG

Response Letter:<br /> We thank the referees for reviewing our manuscript entitled “Sub-millimeter fMRI reveals multiple topographical digit representations that form action maps in human motor cortex”. The critical reading of this manuscript is highly appreciated, and we believe that the comments have helped to improve the manuscript and clarify the interpretation of the presented results. The manuscript has been modified according to the reviewers’ suggestions.<br /> All points raised by the reviewers have been addressed in detail below.

Reviewer #1:<br /> R1.1 <br /> This is a very interesting study investigating the spatial organization of hand movement representations in M1. Certainly the hand representation in M1 is likely complex and therefore requires advanced methods to probe. Both imaging and neurophysiological evidence clearly suggests that M1 is not so much concerned with the representation of fingers, but rather of complex hand movements. The use of a winner-take-all map for fingers is therefore likely a less effective way of gaining a deeper understanding of the organization of M1.

We thank the reviewer for his/her expert assessment and for appreciating the necessity of advance methodology to investigate the complex representations in M1.

We would like to comment on the reviewer’s statement that “imaging and neurophysiological evidence clearly suggests that M1 is not so much concerned with the representation of fingers, but rather of complex hand movements”. We agree that there is imaging and electrophysiological evidence that parts of M1 can represent complex hand movements. However, we take issue that it would be established that the entire M1 must behave like this. We believe this is only part of the entire picture. <br /> In fact, physiological support of the control of the mentioned “complex hand movement” and muscle and movement synergies comes from investigations of cortico-motoneuronal (CM) cells, (CM cells are the ones with motor neurons innervating shoulder, elbow, and finger muscles). Note, however, that these representations and these cells are confined to the caudal part of M1 (also known as the “new” M1 or Brodmann area BA4p). This is the evolutionary younger part of M1 that is located deep in the central sulcus. In this part of M1, individual body parts are largely overlapping (probably to facilitate complex hand movement) and a finger dominance maps might be misleading (as the reviewer suggested).

However, we would like to note that there are no such CM cells in the rostal M1 (Rathelot and Strick, 2006, 2009). As pointed out in Fig. S9 of or manuscript, the new finding of mirrored finger representations are solely visible in the rostal M1 (a.k.a. “old” M1 or BA4a). In this evolutinary old part of M1, body part movements (e.g. hand, elbow, shoulder) have locally distinct domains with less overlap compared to BA4p.<br /> Thus, we respectfully disagree with the reviewer about the effectiveness of finger dominance maps. These maps are extensively used in imaging and electrophysiology and have efficiently lead to important findings throughout the last century (Woolsey 1979; Hlustik 2001; Idovina 2001; Sanes 1995; Penfield 1937; Schieber 1993; Schellekens 2018; Olman 2012; Siero 2014). We don’t want to discredit this large body of literature of body part maps. And we would also like to use the tool of finger dominance maps, when appropriate.

We would also like to point out that at no point in this analysis, we are estimating “winner-takes-all maps”. We are aware of the shortcoming of winner-takes all maps and thus, the finger-dominance maps that we are depicting in many figures, are not binary. Instead, our finger-dominance maps are shown with a continuous color scale. Every voxel has a relative regime (from 0 to 1) of how much it is dominated from that finger. This analysis retains the fact that multiple fingers can be represented in the same voxel.<br /> For even more quantitative interpretations, (e.g. to avoid that the color of one fingers covers the color of another fingers that is more weakly represented) we included Fig. 3B that shows the mirrored representation in column profiles.

The methods presented in this paper are carefully applied and well documented. In fact the authors have made the tools and data available in an open repository, for which they are to be commended. I really have no quibbles with the processing or VASO approach, both of which have extensive prior publication history.

We thank the reviewer for recognizing the importance of investigating the organization of M1 and we are delighted that the reviewer considers out methods adequate.

R1.2 <br /> The paper is clearly written and illustrated. However the crux of the problem lies in the extent of the novelty of the imaging sequence versus the lack of novelty in the neuroscience findings. Certainly practioners of VASO have made a convincing argument for its superiority over GE-EPI BOLD for the localization of function at the mesoscopic scale and I certainly am convinced of that. Nonetheless researchers around the globe have used GE-EPI to look at various columnar structures in animal and human brain with some degree of success. While the results in this paper are the amongst the clearest, the spatial resolution doesn't really go beyond what Cheng et al. used in their Neuron paper in 2001. So while VASO is certainly a viable and perhaps better alternative to BOLD, this manuscript doesn't really advance the MRI side of the equation much beyond what these authors and others have already shown.

We thank the reviewer for appreciating the clarity of the manuscript and for appreciating the value of VASO in high-resolution fMRI.<br /> Given the reviewer’s doubts about the novelty, we would like to explicitly point out the methodological advancements we achieved and novel neuroscience finding that we found.

Methodological Novelty:<br /> We agree with reviewer, that previous studies could already achieve sub-millimeter in-plane resolutions. Note, however that previous papers (including the Cheng paper) relied on flat portions of cortices and collapsed the third dimension along 3-4mm thick MR-slices. This means that precious MRI methods to investigate “columnar” alignment where not applicable across people and certainly not across the entire precentral M1-gray matter bank with its characteristic Omega-like folding pattern. VASO has never before proven its applicability for sub-millimeter “columnar” imaging. And certainly not for along the curved cortex. This is a novel achievement. <br /> We agree with the reviewer that we could previously already show indications of layer results (with submillimeter in-plane resolution). Please note however, that our previous methodology was limited to a very small FOV of less than 3cm in read direction and less than 2cm in slice direction, resulting in a coverage that could only capture 0.8% of the cortex. In previous studies, this was sufficient to address research questions about individual chunks of the cortex. However, it is not sufficient for topographical mapping of “columnar” organization. One fundamental achievement of this study is that we developed a fundamentally new acquisition approach that allows us to achieve 22% of brain coverage. This was achieved with the novel development of advanced readout strategies. As such, we invested two years of development for the inclusion of advanced GRAPPA reconstruction, asymmetric echoes, and corresponding reconstruction to image space. Compared to our previous methods, the resulting coverage is more than an order of magnitude bigger. This is fundamentally novel and enabled the present study in the first place. <br /> In this study we developed a fundamentally new analysis methodology. The corresponding LAYNII software package used here allows columnar and laminar signal pooling in the voxel space of the native EPI space. There is no other analysis method that can achieve this. While there are previous automatic software packages (e.g. FreeSurfer, CBS-Tools etc.) that allow similar analysis steps, they are not suitable to detect ‘columnar’ structures that are smaller than 1mm (5 digits in 3mm) within the curved cortex. These methods require closed surfaces (not possible with, partial brain coverage), alignment with ‘anatomical’ data (which requires spatial resampling=blurring). Previous methods work in vertex space (not voxel space) and thus are associated with resolution loss during spatial resampling, which makes the neighboring finger representations merge and disappear. The mirrored finger results are only as clearly visible with all the above analysis advancements. And thus, we consider these advancements as a fundamental methodological novelty. <br /> Other methodological analysis novelties developed here are the columnar smoothing without signal leakage across sulci, laminar Point-spread function estimation (Fig. S3, S8), layering in 3D with isotropic voxels (not only 2D as previously), cortical unfolding in voxel space.

Biological novelty<br /> With respect to the referenced study from Cheng et al., we would like to point out that they showed patterns that resembled the expected shape and size as columns but never established such structure and organization. There is no expected ground truth of ocular dominance columns alignment (e.g. where to find which columns). This is different for our study. We can differentiate between any random columnar pattern compared to a meaningful somatotopic organization, with neighbouring fingers being represented in neighbouring columns. This form of meaningful columnar mapping at submillimeter scale is novel compared to Cheng et al.<br /> As opposed to previous columnar fMRI studies, we do not simply try to depict known structures with known shape and size as proof-of-principle for a method as previous studies. Instead here, we are finding previously unknown organization principles of sub-millimeter representations in M1. This is a fundamentally new approach and a paradigm shift for the field of “columnar” and “laminar” fMRI. <br /> We report fundamentally new neuroscientific insights about how the previously described action representations in the microscopic regime are integrated into previously described body-part representations in the macroscopic regime This was not described until now and is a fundamental novelty of this study.<br /> We agree with the reviewer that previous studies (including Ejaz et al.,) found deviations of the homunculus model. It is not clear until now, however, how these deviations (multiple representations and fractionalizations) are coming about. Are these deviation of the linear body-part alignments just randomly aligned? Or do the deviations follow a specific geometric order? If yes, which one? According to which order are the movement actions aligned? In this study we find -for the first time- mirrored representations of individual digits in the primary motor cortex that are differently engages for different actions. This is novel and has not been described previously.

In the revised version of the manuscript, we tried to stress the novelty of the study.

R1.2 <br /> So we are left with the importance of the neuroscientific findings, and here I have some more serious issues. The organization of M1 and S1 along an action-axis is well known and certainly not as mysterious as the authors would represent.

We agree with the reviewer that there are previous accounts of action representations in the motor cortex. We are describing them as part of our introduction and discussion section. We did not intend to describe them as ‘mysterious’ by any means. The point that we are trying to make is that these action representations are partly in conflict with somatotopic organization principles that are found in most of the high-resolution imaging literature (e.g. Schellekens 2018; Olman 2012; Siero 2014).

In the revised version of the manuscript, we emphasize the [Ejaz et al., 2015] even more in a dedicated paragraph about it.

R1.3 <br /> Furthermore, they have dismissed a paper that shows a similar result using MRI by misrepresenting the findings of that paper as I understand them (Ejaz et al., 2015, Nature Neurosci). <br /> Specifically, in reference to that paper, Huber et al. state that 1) the work argues for a simple topographic arrangement of single finger representations in S1, and 2) that the overlap between finger activation patterns is "due to noise". In that work (Ejaz et al., 2015), they used BOLD fMRI to measure the activity patterns evoked by single- and multi-finger movements in M1 and S1. The spatial arrangements of these patterns in both regions were stable within each participant (compared across different scanning sessions), but highly variable across participants. These finger patterns are shown in Fig. 1 of that paper. Close visual inspection of the patterns reveals they do not follow a clear linear arrangement in either S1 or M1, and perhaps some evidence of digit "mirroring" can be observed - definitely there are parts of the cortex activated for the thumb at the dorsal end of the hand region.

They then calculate the dissimilarity between all pairs of finger patterns for M1 and S1, separately. Importantly, the relative dissimilarity between any pair of activity patterns (within a participant) was highly stable across participants. This is notable given the spatial arrangements of these patterns was highly variable across individuals. One stable characteristic was that the thumb pattern was more similar to the little finger than to the ring finger. This finding clearly shows - contrary to what Huber et al. claim it shows - that a simple linear somatotopic arrangement cannot account for the digit representations in M1 or S1.

1.) Our justification for the statements in the previous version of the paper:<br /> We assume the reviewer refers to the citation on page 5 of the original manuscript:

“In the primary somatosensory cortex, we find no clear deviations from the homunculus model as shown previously in humans (Ejaz 2015; Schluppeck 2017; Olman 2012; Kolasinski 2016; Shellekens 2018).”

This statement in our manuscript was based on the following paragraph in [Ejaz et al., 2015] from page 1034:

“There was some consistency: when averaging activity patterns across participants (Fig. 1), a blurry somatotopic arrangement became visible with the thumb activating more ventral and the other fingers more dorsal areas of the motor strip.”

Figure caption: adapted screenshot from Fig. 1 of Ejaz et al. Subject average activation maps show rough features of linear somatotopic arrangement (with secondary deviations). Thumb representations peaks at the bottom (pink arrow) and the remaining fingers are linearly aligned with the little finger representation peaking at the top (red arrow).<br /> We also noticed indications of a secondary thumb representation in Fig. 1 of [Ejaz et al., 2015] next to the index finger. We discussed these double-thumb indications in the Ejaz et al. figures extensively among ourselves and eventually decided not elaborate on them in our manuscript for the following reasons:<br /> In our own pilot studies, we noticed that for some kinds of thumb movement tasks, the thumb-movement can come along with unwanted secondary wrist movement. This was not the case for index/middle/ring/pinky-finger movements. Since the wrist movement representations are expected to be located next to the pinky-finger, we were sceptical that the secondary thumb representation form Ejaz might actually refer to unwanted wrist movement?<br /> In our own BOLD data, we find some cases of signal leakage from S1 to M1 (across the central sulcus), which might introduce artifactual double representation in M1. Since, Ejaz et al., also used BOLD sequences, we speculate that this might have been the case in those data too? <br /> The text of the paper [Ejaz et al., 2015] does not discuss the secondary blob at all. Neither does it mention it in the context of a potential double-representations or mirrored representation. Thus we are hesitant to include it as a reference for this feature. If would be more appropriate for us to give the authors of [Ejaz et al., 2015] full credit for the discovery of mirrored representations, if they would have described it and discussed it consistently across people.

It is further to note that the above statement in our preprint referred to the sensory cortex, not the motor cortex.

Revision to avoid future misunderstandings:<br /> We think this misunderstanding can be resolved by removing the [Ejaz et al. 2015] citation on page 5. Instead we discuss the paper in more depth on page 7.

R1.4 <br /> Furthermore, they (Ejaz et al.) go on to show that the stable structure of overlap of finger representations in M1 and S1 can be accounted for by the statistics of everyday hand movement. They did not interpret the spatial variability of these patterns as "noise due to inter-individual variability in every day hand movements". On the contrary, the statistics of hand use they showed is stable across individuals (also see Ingram et al., 2008, Exp. Brain Res.), as is the organizing principle underlying the spatial organization of activity patterns in M1 and S1.

1.) Justification for our statements in the previous version of the paper:<br /> We assume the comment from the reviewer refers to the following section of our manuscript on page 6:

“Previous studies by Sane et al. (1995) and by Ejaz et al. (2015) already identified deviations from linear organizations for finger representations in the human motor cortex with GE-BOLD at 2.5 mm and 1.4 mm resolutions, respectively. However, without the localization specificity, a consistent spatial layout principle, such as the mirrored finger representation alignment, was not found. Instead, the exact pattern of overlapping and segregated representations was interpreted as noise due to inter-individual variability in every day hand movements (Ejaz 2015).”

We included this interpretation of Ejatz’ results based on the first few sentences of the discussion section in [Ejaz et al., 2015] on page 1039:

“The relative similarities between activity patterns were preserved across individuals, despite the substantial spatial inter-subject variability of the activity patterns themselves. The representational structure remained invariant even when the shared somatotopic arrangement of the digits was removed from the data. This suggests an organizing mechanism that shapes the overlap between patterns without enforcing a regular spatial layout. The representational structure could be predicted by the natural statistics of hand use.“

If we understand the highlighted section correctly, Ejaz et al. found that there are deviations from a simple somatotopic organization. And the patterns of these deviations have a considerable variability across people. It is not clear, however, according to which consistent organization principle this variability comes about.

In our view, we thus (mis-)described the phrase “inter-individual variability without given structure” with the term “noise due to inter-individual variability”.

Revision to avoid future misunderstandings:<br /> We agree that the term “noise due to inter-individual variability” might be misleading to describe “inter-individual variability”. In the revised version of the manuscript, the corresponding section is revised as follows:<br /> A previous study by Ejaz et al. (2015) already identified deviations from linear organizations for finger representations in the human motor cortex with GE-BOLD at 2.5 mm and 1.4 mm resolutions, respectively. These data already showed some indications of multiple finger representations (e.g. Fig. 1 in (Ejaz et al. 2015)). However, these data were not discussed with respect to an alternative geometric somatotopic organization principle such as a mirrored representation.

R1.5 <br /> I definitely agree with the authors that M1 organization is more complex arrangement than simple linear finger organization. Whether the organization really is best described by two discrete finger maps with phase reversal, however, really has to await a more rigorous experimental and statistical evaluation than even what is presented in Huber et al. Whatever the answer may be, however, I do think that the improved specificity of VASO sequence may play an important role in uncovering such representations in the future, but I don't feel that what has been shown goes much beyond what is known from the literature already.

We are glad that the reviewer agrees with our work showing that the M1 representations can be complex. We agree that the literature needs to be augmented with more rigorous studies.<br /> In fact, with the manuscript at hand we intent to do just that: providing a more rigorous experimental evaluation. We aim to move beyond the position of Ejaz et al. Namely, we aim to go beyond the conclusion “that the motor cortex is more complicated than individual finger representations”, . and describe how it is different, how these differences are geometrically organized, and whether they are stable across people.<br /> Accounting also the large bulk of electrophysiological and micro-stimulation evidence about the body-part sub-divisions in M1 we opt to see how these representation are in agreement with the results from Ejaz.<br /> In previous imaging studies (including Ejaz et al.,) it was common to view M1 as one large chunk of cortex that would follow the same architectonic principle. There is a large body of invasive literature, however, that suggests that this is not correct, neither functionally (Rathelot and Strick, 2006, 2009) nor anatomically (Geyer 1996). Thus, we intend to describe the body-part representations with a more rigorous fine-scale evaluation. To get there, we developed the advanced methodology as described here. And we start to describe the simplest movement principle of the literature (finger tapping) in the simplest part of M1, namely the evolutionary “old” M1 that has been described as body part representations. <br /> Thus, we feel that our findings go beyond what it known form the literature already.

Reviewer #3: <br /> General Comments: <br /> This paper uses the vascular space occupancy (VASO) method of measuring cerebral blood volume (fMRI) to explore the somatotopy of the finger representation at a sub-millimeter resolution in M1 and S1 of humans. This is an important problem as prior fMRI papers exploring this issue did not have sufficient resolution to adequately address a fine grained topography for fingers. This paper appears to have adequate resolution (~0.8mm) to make a major contribution to understanding the topography of the hand in M1 as well as S1. As such, this paper is primarily one of anatomical location and fMRI reconstruction. In addition, it addresses the issue of whether a given body part representation is always active when that body part is moved. The answer is that there is functional specialization within each M1finger representation. The figures are complex and it is paramount that their display is straightforward, consistent and simple to understand.

R3.1. The stated goal of this paper is to"non-invasively investigate the functional organization topography across columnar and laminar structures in humans", particularly M1 and S1. To understand the topography of the fingers in M1, the entire extent of the finger representations in M1 must be accurately mapped. Such maps are shown in Figs. 6S and 10S. These maps, for each participant, could form the core of an important paper, but they belong in the main body of the paper. They also need to be shown systematically for each participant. The data showing the columnar organization of M1 and S1 seem like important validating information for the reconstruction of the central sulcus. Some of this could be moved to the Supplementary information. What is currently displayed in Figs. 1-5 is just a small sample from the entire extent of slices through M1. Although the concept of mirror hand representations derived from single slices is appealing, it is only represents a small fraction of the entire map of the central sulcus. Furthermore, the single fMRI slices totally ignore the finger representations present in the depth of the central sulcus.

We would like to clarify our goal of this study. We feel the quoted section was taken out of context. As mentioned in the abstract, it was not our goal to ‘investigate the complete topographical organization of the motor cortex at its entirety’. Instead, the quoted section comes from an introductory sentence that states that our goal actually was to ‘develop imaging and analysis methodology, which -in principle- allows us to investigate topographical features’. In a next step we then use the M1/S1 system as a test bed to investigate the neuroscientific usefulness of that methodology. Given that we find -previously not described- neuroscience findings of the mirrored digit representation, we think that the neuroscientific usefulness it confirmed. In this sense, we see our manuscript to lie along a fine line between a methods paper and neuroscience paper.

We agree with the reviewer that every figure in the Manuscript and the Supplementary information is “tuned” to a specific message that we want to bring across. We further agree that Figs. 1-5 in the main manuscript are just a small sample of the main story and there is much more information to be seen. We don’t see this as a weakness of the manuscript. But as a means to follow the comment R3.14, namely selectively showing figures that have a specific message, which comes across as intuitive as possible.

In order to discuss the mirrored pattern of digit representations, we find it most natural to zoom into the hand area (Fig. 1). Correspondingly, when it comes to showing the inter-participant consistently of this feature (Fig. 2), we find it advantageous to use the same imaging procedure across all people as in Fig. 1. However, when it comes to explaining where these features are located across the dimensions of the central sulcus, we show additional unzoomed images. <br /> We agree with the reviewer that entire maps of the unflattened sensory-motor-system would give a more comprehensive view. However, it would distract the reader from the feature of interest. Those entire maps would mostly contain nothing (e.g. all the non-stimulated body parts, trunk, face, feet, etc.) and the 3-8mm of interest would be tiny (e.g. See Fig. S6). <br /> To address the reviewers comment, we included the full maps of the central sulcus into the manuscript main body (new figure 3), additional to the zoomed images.<br /> Furthermore, we included additional IMAGIRO maps (as requested) of for more participants with zoomed and unzoomed sections to guide the reader which part of the superior part of M1 it refers to (See new Fig. S6E).

The of laminar and columnar fMRI is still emerging. Thus, not all potential sources of analysis artifacts are fully described and understood. To minimize potential misinterpretation it has been suggested to depict the final results as close to the raw data as possible (Polimeni 2017; Kay 2019). Thus we try to show the activation maps in the raw EPI space (Fig. 1,2,4), when possible. This way, it can be easily be directly appreciated that the mirrored finger pattern is not an artifact of a flawed infolding artifact. Furthermore, the activity maps in EPI space best depict the spatial scale of columnar size with respect to the cortical thickness and location at the hand knob. Flattened maps are produced by several additional steps and are presented in an very abstract space where, these reference dimensions are lost. Thus, we are hesitant to remove the activation maps on the folded cortex from the manuscript. However, we included additional unfolded flattened maps in the supplementary material.

Please note that we are also required to following the Journal’s Guidelines to only include material that is central to the narrative. In doing so, we follow the rule of not having more than double of supplementary figures as figures in the main text. Thus, is included the some of additional maps as figure-panels, not as additional stand-alone figures.

We revised the manuscript to account for the reviewer’s comment. Specifically, we rephrased the abstract and introduction section to make our goals clearer. We also tried to make it clearer what the message is for each figure, in the figure captions respectively.

Kay, K., Jamison, K., Vizioli, L., Zhang, R., Margalit, E., & Ugurbil, K. (2019). A critical assessment of data quality and venous effects in sub-millimeter fMRI. NeuroImage, 189, 847–869. http://doi.org/10.1016/j.ne... <br /> Polimeni, J. R., Renvall, V., Zaretskaya, N., & Fischl, B. (2017). NeuroImage Analysis strategies for high-resolution UHF-fMRI data. NeuroImage, (April), 1–25. http://doi.org/10.1016/j.ne...

R3.2. The orientation of brain images and reconstructions should be the same in every figure. For example, Fig. 1A and 1E seem to have the right side of the brain image toward the right whereas Fig. 1B-D has it to the left. In Fig. 6S, the orientation of the CS appears to be opposite to that shown in Fig. 10S. Continually forcing the reader to flip the images creates unnecessary confusion. Since this paper shows the right hemisphere, left/medial should be on page left and right/lateral should be on page right. The terms medial and lateral are preferable to left and right. In Figs. 6S, 10S, the actual location of the medial wall/sagittal fissure should be indicated. Without this marker, the CS just floats in space with no anchor to the actual brain image. A calibration should be included on each image.

We agree that the orientation is confusing. This comes from the fact that the convention of MRI images is to view them as they would look like from the experimenter perspective. E.g. looking at an axial cut from the perspective of the participants feet. The right motor cortex of the person is then depicting on the left. This is contradicting to the 3D-head-models from viewing from above. Thus, the 3D-views and the 2D-views were confusing.<br /> Based on the reviewers comments, we tried to make it more consistent in Fig. 1, S6 and S10. This means however, that the 3D-head-models are mirrored representations compared to their real-live pendants. <br /> We included additional calibration markers and the landmarks of the medial wall in multiple figures. E.g. Fig. S6, S9, S3.

R3.3. The term 'multiple' is used incorrectly throughout the manuscript. Multiple means 'more than 2'.

We respectfully disagree with the reviewer on this point. In our understanding, the term ‘multiple’ refers to ‘more than one’ (source: https://en.oxforddictionari.... We chose this term deliberately vague. We find only two mirrored representation consistently across all participants. However, we cannot exclude the possibility that there are more representation hidden below the detection threshold. Since absence of evidence is not the same as evidence of absence, we would like to refrain from calling it “double” representation. This excludes the possibility of a third or fourth representation. <br /> In one participant, with a large tilting angle, and with a very low threshold, we see indications of a third representation. However, since its not reproducible across participants, its discussion is subject to future experiments with more sensitive imaging methodology only.

R3.4. It is unclear how the images in Fig. 1E were developed. What do the colors mean? Why is this representation shown here when it is not used until Figs. 3S, 6S.

Fig. 1 was intended as a figure describing the methods applied in this study. Thus, we included the coordinate system of layers and columns in 3D-grids as they are used for the directional smoothing. We agree with the reviewer that it can be confusing, we thus removed the panel E from the figure in the revised version of the manuscript.

R3.5. Discussion- <br /> The requested revisions in the data presentation will require revision of comparisons to other fMRI papers. <br /> The Discussion would be improved by a more extensive comparison to studies in monkeys where most of the mapping of M1 has occurred. An excellent brief summary of the monkey literature may be found in the section written by Paul Cheney in Omrani et al, 2017. The discussion should address two issues. <br /> First, a comparison of the organization of human M1 to the anatomical and physiological explorations of this region in the monkey. Second, the issue of specialization (separate regions of grasping and retraction) has its basis in monkey data that indicates specialization of M1 neurons for specific tasks.

We agree with the reviewer that the summary from Cheney provides a nice summary about representations in the motor cortex learned from monkey experiments. Based on this summary, we included an additional paragraph into the discussion section that should address the two issues.

Most of the knowledge on the functional representation of movements in the primary motor cortex has been obtained from countless experiments in monkeys over the last century. The current state of consensus in the field is nicely summarized by Paul Cheney in (Omrani 2017; see also referenced therein); Overall, corticomotoneuronal cells in the primary motor encode muscle-related parameters of movement such as muscle activity and muscle force. Although some corticomotoneuronal cells in the primary motor cortex (particularly those involved with finger movements) have their terminations confined to motoneurons of single muscles, a large amount of corticomotoneuronal cells are not rigidly coupled to the activity of its target muscles but show specialization for particular movements or categories of muscle activity. Namely, almost half of the corticomotoneuronal cells facilitate muscles involving at least one distal and one proximal joint and are specialized for specific muscle synergies, E.g. for reach-to-grasp movements. With respect to action representations shown in Fig. 2B, it is important to note that Cheney and Fetz (1985) had previously identified the muscle fields of neighboring corticomotoneuronal cells. They showed that neighboring corticomotoneuronal had muscle fields that were very similar. Hence, the notion of cortical patches that are preferentially activated for grasping and retraction actions (Fig. 2B) has its basis in previous monkey data and could refer to these previously described muscle fields.

Specific Comments:

R3.6. The first sentence of the Significance statement is incomprehensible. In general, the significance of this study is not well explained.

Since the significance statement is removed from the revised version of the manuscript.

R3.7. Introduction- Sanes et al., 1995 did not study monkeys.

We agree with the reviewer. The Sanes reference is moved to a different section now.

R3.8. "However, the organizational principle of smaller body parts such as individual digits could not be resolved due to the lack of localization specificity of conventional GE-BOLD fMRI and the sparse sampling of invasive electrophysiological recordings." This may be true for fMRI but the electrophysiological stimulation in monkeys (Kwan et al.l 1978; Strick and Preston, 1982 [up to 16 penetrations per 1mm2]) and Park et al. 2001) can hardly be described as sparse.

We agree with the reviewer that the term “sparse” might be misleading and does not give those experiments’ justice. The point we were trying to make is, that fMRI is inherently a continuous mapping technique that continuously samples the entire cortical sheath without any holes between electrodes. Which is true even at low resolutions. To address the reviewers comment, we revised the paragraph in the introduction section.

R3.9. Lin et al 2011 is often used as evidence that VASO accurately measures CBV. However, close examination of Fig. 1 in Lin et al reveals that the VASO and Gd-DTPA blood volume measurements often do not occupy the same voxels. That is, many VASO voxels with significant activation have no significant Gd-DTPA activation and many Gd-DTPA voxels with significant activation have no VASO activation. This observation suggests that VASO does not accurately represent CBV when voxel to voxel comparisons are made by the two different methods of measuring CBV. What other evidence, other than theoretical, indicates that VASO accurately measures CBV? (Lin AL, Lu H, Fox PT, Duong TQ. Cerebral blood volume measurements- Gd-DTPA vs. VASO - and their relationship with cerebral blood flow in activated human visual cortex. Open Neuroimag. J. 2011; 5: 90-95.)

We share the reviewer’s concerns whether VASO is a good measure for CBV. For this reason, we validated our SS-SI-VASO variant with gold-standard methods in multiple setups across the last 5 years. Ranging from concomitant VASO imaging with optical imaging spectroscopy in rats, up to validations of layer-dependent VASO signal with MION/Ferraheme imaging in rats and monkeys.

While we agree that Fig. 1 in Lin et al., shows deviations of VASO and Gd-DTPA, we would like to refrain from speculating what might be the reason for this. Reasons could range from acquisition challenges up to analysis inconsistencies. See the following reference:

Huber, L., et al (2015). Micro- and macrovascular contributions to layer-dependent blood blood volume fMRI: A multi-modal, multi-species comparison. ISMRM. doi: http://dx.doi.org/10.7490/f... ).

Note that our validation studies are quantitative in physical units of ml. This is in contrast to significance maps in Lin et al., that might be prone to biases in different noise characteristics post-injection of GD. <br /> Also note that our validations are carried out across columnar structures (B) and laminar structures (C).

See figures from:<br /> Huber, L., Goense, J.B.M., Kennerley, A.J., Guidi, M., Trampel, R., Turner, R., and Möller, H.E. (2015). Micro- and macrovascular contributions to layer-dependent blood blood volume fMRI: A multi-modal, multi-species comparison. In Proceedings of the International Society of Magnetic Resonance in Medicine, p. 2114. Doi: http://dx.doi.org/10.7490/f...<br /> Huber, L., Goense, J.B.M., Kennerley, A.J., Trampel, R., Guidi, M., Ivanov, D., Gauthier, C.J., Turner, R., Möller, H.E., Reimer, E., et al. (2015). Cortical lamina-dependent blood volume changes in human brain at 7T. Neuroimage 107, 23–33.<br /> Huber, L. (2015). Mapping human brain activity by functional magnetic resonance imaging of blood volume. University of Leipzig. https://fim.nimh.nih.gov/fi... <br /> Kennerley, A.J., Huber, L., Mildner, T., Mayhew, J.E., Turner, R., Möller, H.E., and Berwick, J. (2013). Does VASO contrast really allow measurement of CBV at high field (7 T)? An in-vivo quantification using concurrent optical imaging spectroscopy. In Proceedings of the International Society of Magnetic Resonance in Medicine, p. 0757.

In the revised version of the manuscript, we included the following additional paragraph into the discussion section:

Note that the CBV weighting in VASO has been extensively validated by comparisons with gold-standard methods in rats and monkeys across layer and columns (Huber et al., 2015a-c; Kennerley et al., 2013).

R3.10. The voxel size is listed as 0.89mm x 0.99mm on page 2 versus 0.79mmx0.79mmx 0.99mm on page 1. Which is correct?

The correction resolution is 0.79 mm. This typo is corrected in the revised version of the manuscript.

R3.11. Was the smoothing across layers a directional smoothing?

The reviewer is correct. The layer-smoothing was applied in specific directions only. It was only applied in the direction that is parallel to the column. There was no smoothing perpendicular to this direction. <br /> Note that this way of “directional” smoothing refers to cortical directions. The smoothing was independent of the direction in the laboratory frame of reference. As such, the smoothing is applied independent of the orientation of read-direction, slice-direction and phase direction. The LAYNII program LN_DIRECT_SMOOTH was not applied in this study. <br /> An additional sentence about this is included in the revised version of the manuscript.

R3.12. Page 13- "...primary motor cortex is 4 mm (Fischl and Dale 2000), the resolution of 0.79 mm used here allows us to obtain 5-7 independent data points across the 20 layers. The number of 20 layers is chosen based on previous experience in finding a compromise". This description is hard to understand. Suggest something like- The cortical thickness of the primary motor cortex is 4 mm (Fischl and Dale 2000). With our resolution of 0.79 mm, we obtained 5-7 independent data points across the thickness of the cortex. These data points were upsampled to create 20 layers across the thickness of the cortex. Twenty layers was chosen based on previous experience in finding a compromise... These 20 layers were smoothed and extracted (tell me what you did here) in sheets to produce a reconstruction of the face of the anterior bank of the central sulcus (Figs. 3S, 6S, 10S).

Based on the reviewer’s suggestion, we tried provide a more detailed description of the underlying assumptions and the necessity of using so many layers in a recent blog post: https://layerfmri.com/2019/... <br /> In the revised version of the manuscript, we the included the following summarizing statement:

The cortical thickness of the primary motor cortex is 4 mm (Fischl and Dale 2000). With our resolution of 0.79 mm, we obtained 5-7 independent data points across the thickness of the cortex. Across these data points, we created 20 layers across the thickness of the cortex on a 4-fold finer grid than the effective resolution. The number of twenty layers was chosen based on previous experience in finding a compromise data size and smoothness (see Fig. S6 in (Huber 2018)). Columnar profiles in Fig. 3 and Fig. S4 are generated from unsmoothed data. For Figs. S3 and S6, the functional signal was smoothed with 0.5 mm within columns and extracted in sheets to produce a reconstruction of the face of the anterior bank of the central sulcus. No smoothing was applied across columns.

R3.13. Fig. 2B- For participant 5, the copper and turquoise outlines are reversed. Hue of copper and turquoise colors are not consistent in each panel. <br /> In last panel of 2B, first line- there is a hand in this panel. What is its purpose? If the purpose is to be a key for finger color, the thumb should be magenta.

The reviewer is right, the copper and turquoise patch seems reversed in participant 5. Note, however that this is not a presentation error in the preparation of the images. We find that the grasping-extension patches do not follow a the same organization principle along the medial-lateral direction across participants. It is highly dependent on the position of the axial projection chosen. E.g. it can be seen in Fig. S6 (and previous version of Fig. S9) that, dependent on the depth of the central sulcus, the copper and turquoise patches are either on the medial or lateral side. Please also note that participant 5 is not an outlier here; in fact, participant 1 (in the same figure) has the same copper-turquoise alignment as participant 5. Please also note, that the sensory cortex consistently shows a grasping preference, across all participants.

The additional hand pictogram had been included as a figure key to remind the reader, which color refers to which finger. Based in the reviewers comments, it is excluded in the revised version of the manuscript. It is already shown in panel A) anyway.

R3.14. Fig. S3C- Several features of this figure make it hard to decipher and undermine the explanation of the reconstruction method. I am assuming that the little squares in panel B are equivalent to columns. This should be stated explicitly. If the colors correspond to the fingers, then the mirror representation of the hand shown in Figs. 1-3 is nowhere to be found. This is confounding. It may be useful to show the location of the slice in panel D. Panel D is reversed from panel A, creating needless confusion. In panel C, the laminar thickness of the cortex is greater than the depth of the central sulcus. Calibrations would help but why not make the laminar thickness accurate? State explicitly that the IMAGIRO reconstruction consists of 20 layers, each like the one in B. Spelling- Columnar 'distance' <br /> It took me a long time to understand what you were doing. The descriptions of the reconstruction needs to be simple, clear and intuitive or very few will comprehend them. It all makes sense but the reader should not have to go to the blog (which I did) to understand them.

We thank the reviewer for the suggestions to make this figure clearer. We also applaud the reviewers level of commitment to check the description on our blog.<br /> -> The little squares indeed refer to the columnar dimension. Additional comments are included in the caption.<br /> -> The colors do not refer to finger dominance, but to the medial-lateral position. This is included in the caption now.<br /> -> The location colors are now included in panel C, as suggested.<br /> -> Panels C and D are now switched, as suggested.<br /> -> If, the laminar thickness could be accurately depicted, all 20 layers would be 2-3 mm apart in the figure. If we would depict it in the right geometry, the layers could not be separated with the naked eye. Scale bars are included as suggested, which points out how they are distorted.<br /> -> An explicit reference about 20 layers is included.<br /> -> The typo is corrected in “distance”

Updated Fig. 3:

We agree, that an intuitive image is helpful. Here, we tried to find a compromise of simple intuitive figures that are representing the complexity of the analysis without making the supplementary material too long. The reviewer’s comments are appreciated to achieve this.

R3.15. Fig. 4S part B- Should note that this is upsampled to produce 20 layers.

The revised version of the manuscript has an additional statement included:

Note that the size of layer and column structures are smaller than the effective resolution of 0.79 mm. They are estimated in an upscaled space.

R3.16. Fig. 9S- Why is the background of the VASO view of the anterior bank of the CS entirely red? This implies that the entire CS is related to the 5th finger. How is that possible? Why are there yellow and green patches distributed all along the CS? This arrangement is different from any of the other figures. There does not seem to be a double mirror representation in this participant. <br /> In the bottom panels, why is the view limited to just part of M1 instead of the whole of M1? In general, this figure is quite confusing and really difficult to interpret. The organization of the grasping and retraction patches is an important issue. A better explanation (illustration?) of what you are trying convey in this figure is necessary.

We agree with the reviewer that previous Figure S9 could be confusing. We tried to show too many features in one Figure. Our goal of this figure was to show the consistency of the finger representations across the different tasks and also to show the position of the mirrored representation along the depth of the central sulcus. Based on the reviewer’s comments, we decided to remove Fig. S9. From the manuscript. We believe that these to messages already come across from Fig. S5, S6, S9 (new).

To answer the reviewer’s questions (for the sake of his/her curiosity): <br /> -> The top-right figure was included for the sake of orientation. It was not included to suggest the significance of the mirrored pattern. Thus, we did not threshold the finger dominances at all. In areas outside the hand-knob, therefore, the finger-preference measure for all fingers is close to 0. The red color outside the hand knob does not mean that this finger is represented there. It only means that all the other fingers are even noisier. E.g. that the finger preference for the index finger is 0.0014 compared to other fingers with a finger preference of 0.0005. For reference, in the hand knob, the finger preferences are in the regime 0.3-1 (please, see Fig. 3B about the absolute selectivity strengths in an outside the hand knob). The previous figure S9 corresponds to the line graph in Fig. 3B from above. <br /> -> We believe that there is, in fact, a mirrored pattern visible in this figure. Within the Brodman area subsection BA4A, the color pattern is reversed.

R3.17. Fig. 10S- in the right panel, the orientation seems to be incorrect. That is, left is lateral and right is medial which means the left ear arrow should be pointing to the right.

We agree, the arrow description now says “right” ear.

R3.18. I suggest alphabetizing the reference list.

In the updated reference list “S” is after “O”.

R3.19. The correct citation is- Meier JD, Aflalo TN, Kastner S, Graziano MS. Complex organization of human primary motor cortex: a high-resolution fMRI study. J Neurophysiol. 2008 Oct;100(4):1800-12. doi: 10.1152/jn.90531.2008. Epub 2008 Aug 6

The reference is updated

On 2019-02-26 13:10:37, user Laurentius Huber wrote:

Please find a formatted version of this response letter with figures here: https://goo.gl/3czXWG

Response Letter:<br /> We thank the referees for reviewing our manuscript entitled “Sub-millimeter fMRI reveals multiple topographical digit representations that form action maps in human motor cortex”. The critical reading of this manuscript is highly appreciated, and we believe that the comments have helped to improve the manuscript and clarify the interpretation of the presented results. The manuscript has been modified according to the reviewers’ suggestions.<br /> All points raised by the reviewers have been addressed in detail below.

Reviewer #1:<br /> R1.1 <br /> This is a very interesting study investigating the spatial organization of hand movement representations in M1. Certainly the hand representation in M1 is likely complex and therefore requires advanced methods to probe. Both imaging and neurophysiological evidence clearly suggests that M1 is not so much concerned with the representation of fingers, but rather of complex hand movements. The use of a winner-take-all map for fingers is therefore likely a less effective way of gaining a deeper understanding of the organization of M1.

We thank the reviewer for his/her expert assessment and for appreciating the necessity of advance methodology to investigate the complex representations in M1.

We would like to comment on the reviewer’s statement that “imaging and neurophysiological evidence clearly suggests that M1 is not so much concerned with the representation of fingers, but rather of complex hand movements”. We agree that there is imaging and electrophysiological evidence that parts of M1 can represent complex hand movements. However, we take issue that it would be established that the entire M1 must behave like this. We believe this is only part of the entire picture. <br /> In fact, physiological support of the control of the mentioned “complex hand movement” and muscle and movement synergies comes from investigations of cortico-motoneuronal (CM) cells, (CM cells are the ones with motor neurons innervating shoulder, elbow, and finger muscles). Note, however, that these representations and these cells are confined to the caudal part of M1 (also known as the “new” M1 or Brodmann area BA4p). This is the evolutionary younger part of M1 that is located deep in the central sulcus. In this part of M1, individual body parts are largely overlapping (probably to facilitate complex hand movement) and a finger dominance maps might be misleading (as the reviewer suggested).

However, we would like to note that there are no such CM cells in the rostal M1 (Rathelot and Strick, 2006, 2009). As pointed out in Fig. S9 of or manuscript, the new finding of mirrored finger representations are solely visible in the rostal M1 (a.k.a. “old” M1 or BA4a). In this evolutinary old part of M1, body part movements (e.g. hand, elbow, shoulder) have locally distinct domains with less overlap compared to BA4p.<br /> Thus, we respectfully disagree with the reviewer about the effectiveness of finger dominance maps. These maps are extensively used in imaging and electrophysiology and have efficiently lead to important findings throughout the last century (Woolsey 1979; Hlustik 2001; Idovina 2001; Sanes 1995; Penfield 1937; Schieber 1993; Schellekens 2018; Olman 2012; Siero 2014). We don’t want to discredit this large body of literature of body part maps. And we would also like to use the tool of finger dominance maps, when appropriate.

We would also like to point out that at no point in this analysis, we are estimating “winner-takes-all maps”. We are aware of the shortcoming of winner-takes all maps and thus, the finger-dominance maps that we are depicting in many figures, are not binary. Instead, our finger-dominance maps are shown with a continuous color scale. Every voxel has a relative regime (from 0 to 1) of how much it is dominated from that finger. This analysis retains the fact that multiple fingers can be represented in the same voxel.<br /> For even more quantitative interpretations, (e.g. to avoid that the color of one fingers covers the color of another fingers that is more weakly represented) we included Fig. 3B that shows the mirrored representation in column profiles.

The methods presented in this paper are carefully applied and well documented. In fact the authors have made the tools and data available in an open repository, for which they are to be commended. I really have no quibbles with the processing or VASO approach, both of which have extensive prior publication history.

We thank the reviewer for recognizing the importance of investigating the organization of M1 and we are delighted that the reviewer considers out methods adequate.

R1.2 <br /> The paper is clearly written and illustrated. However the crux of the problem lies in the extent of the novelty of the imaging sequence versus the lack of novelty in the neuroscience findings. Certainly practioners of VASO have made a convincing argument for its superiority over GE-EPI BOLD for the localization of function at the mesoscopic scale and I certainly am convinced of that. Nonetheless researchers around the globe have used GE-EPI to look at various columnar structures in animal and human brain with some degree of success. While the results in this paper are the amongst the clearest, the spatial resolution doesn't really go beyond what Cheng et al. used in their Neuron paper in 2001. So while VASO is certainly a viable and perhaps better alternative to BOLD, this manuscript doesn't really advance the MRI side of the equation much beyond what these authors and others have already shown.

We thank the reviewer for appreciating the clarity of the manuscript and for appreciating the value of VASO in high-resolution fMRI.<br /> Given the reviewer’s doubts about the novelty, we would like to explicitly point out the methodological advancements we achieved and novel neuroscience finding that we found.

Methodological Novelty:<br /> We agree with reviewer, that previous studies could already achieve sub-millimeter in-plane resolutions. Note, however that previous papers (including the Cheng paper) relied on flat portions of cortices and collapsed the third dimension along 3-4mm thick MR-slices. This means that precious MRI methods to investigate “columnar” alignment where not applicable across people and certainly not across the entire precentral M1-gray matter bank with its characteristic Omega-like folding pattern. VASO has never before proven its applicability for sub-millimeter “columnar” imaging. And certainly not for along the curved cortex. This is a novel achievement. <br /> We agree with the reviewer that we could previously already show indications of layer results (with submillimeter in-plane resolution). Please note however, that our previous methodology was limited to a very small FOV of less than 3cm in read direction and less than 2cm in slice direction, resulting in a coverage that could only capture 0.8% of the cortex. In previous studies, this was sufficient to address research questions about individual chunks of the cortex. However, it is not sufficient for topographical mapping of “columnar” organization. One fundamental achievement of this study is that we developed a fundamentally new acquisition approach that allows us to achieve 22% of brain coverage. This was achieved with the novel development of advanced readout strategies. As such, we invested two years of development for the inclusion of advanced GRAPPA reconstruction, asymmetric echoes, and corresponding reconstruction to image space. Compared to our previous methods, the resulting coverage is more than an order of magnitude bigger. This is fundamentally novel and enabled the present study in the first place. <br /> In this study we developed a fundamentally new analysis methodology. The corresponding LAYNII software package used here allows columnar and laminar signal pooling in the voxel space of the native EPI space. There is no other analysis method that can achieve this. While there are previous automatic software packages (e.g. FreeSurfer, CBS-Tools etc.) that allow similar analysis steps, they are not suitable to detect ‘columnar’ structures that are smaller than 1mm (5 digits in 3mm) within the curved cortex. These methods require closed surfaces (not possible with, partial brain coverage), alignment with ‘anatomical’ data (which requires spatial resampling=blurring). Previous methods work in vertex space (not voxel space) and thus are associated with resolution loss during spatial resampling, which makes the neighboring finger representations merge and disappear. The mirrored finger results are only as clearly visible with all the above analysis advancements. And thus, we consider these advancements as a fundamental methodological novelty. <br /> Other methodological analysis novelties developed here are the columnar smoothing without signal leakage across sulci, laminar Point-spread function estimation (Fig. S3, S8), layering in 3D with isotropic voxels (not only 2D as previously), cortical unfolding in voxel space.

Biological novelty<br /> With respect to the referenced study from Cheng et al., we would like to point out that they showed patterns that resembled the expected shape and size as columns but never established such structure and organization. There is no expected ground truth of ocular dominance columns alignment (e.g. where to find which columns). This is different for our study. We can differentiate between any random columnar pattern compared to a meaningful somatotopic organization, with neighbouring fingers being represented in neighbouring columns. This form of meaningful columnar mapping at submillimeter scale is novel compared to Cheng et al.<br /> As opposed to previous columnar fMRI studies, we do not simply try to depict known structures with known shape and size as proof-of-principle for a method as previous studies. Instead here, we are finding previously unknown organization principles of sub-millimeter representations in M1. This is a fundamentally new approach and a paradigm shift for the field of “columnar” and “laminar” fMRI. <br /> We report fundamentally new neuroscientific insights about how the previously described action representations in the microscopic regime are integrated into previously described body-part representations in the macroscopic regime This was not described until now and is a fundamental novelty of this study.<br /> We agree with the reviewer that previous studies (including Ejaz et al.,) found deviations of the homunculus model. It is not clear until now, however, how these deviations (multiple representations and fractionalizations) are coming about. Are these deviation of the linear body-part alignments just randomly aligned? Or do the deviations follow a specific geometric order? If yes, which one? According to which order are the movement actions aligned? In this study we find -for the first time- mirrored representations of individual digits in the primary motor cortex that are differently engages for different actions. This is novel and has not been described previously.

In the revised version of the manuscript, we tried to stress the novelty of the study.

R1.2 <br /> So we are left with the importance of the neuroscientific findings, and here I have some more serious issues. The organization of M1 and S1 along an action-axis is well known and certainly not as mysterious as the authors would represent.

We agree with the reviewer that there are previous accounts of action representations in the motor cortex. We are describing them as part of our introduction and discussion section. We did not intend to describe them as ‘mysterious’ by any means. The point that we are trying to make is that these action representations are partly in conflict with somatotopic organization principles that are found in most of the high-resolution imaging literature (e.g. Schellekens 2018; Olman 2012; Siero 2014).

In the revised version of the manuscript, we emphasize the [Ejaz et al., 2015] even more in a dedicated paragraph about it.

R1.3 <br /> Furthermore, they have dismissed a paper that shows a similar result using MRI by misrepresenting the findings of that paper as I understand them (Ejaz et al., 2015, Nature Neurosci). <br /> Specifically, in reference to that paper, Huber et al. state that 1) the work argues for a simple topographic arrangement of single finger representations in S1, and 2) that the overlap between finger activation patterns is "due to noise". In that work (Ejaz et al., 2015), they used BOLD fMRI to measure the activity patterns evoked by single- and multi-finger movements in M1 and S1. The spatial arrangements of these patterns in both regions were stable within each participant (compared across different scanning sessions), but highly variable across participants. These finger patterns are shown in Fig. 1 of that paper. Close visual inspection of the patterns reveals they do not follow a clear linear arrangement in either S1 or M1, and perhaps some evidence of digit "mirroring" can be observed - definitely there are parts of the cortex activated for the thumb at the dorsal end of the hand region.

They then calculate the dissimilarity between all pairs of finger patterns for M1 and S1, separately. Importantly, the relative dissimilarity between any pair of activity patterns (within a participant) was highly stable across participants. This is notable given the spatial arrangements of these patterns was highly variable across individuals. One stable characteristic was that the thumb pattern was more similar to the little finger than to the ring finger. This finding clearly shows - contrary to what Huber et al. claim it shows - that a simple linear somatotopic arrangement cannot account for the digit representations in M1 or S1.

1.) Our justification for the statements in the previous version of the paper:<br /> We assume the reviewer refers to the citation on page 5 of the original manuscript:

“In the primary somatosensory cortex, we find no clear deviations from the homunculus model as shown previously in humans (Ejaz 2015; Schluppeck 2017; Olman 2012; Kolasinski 2016; Shellekens 2018).”

This statement in our manuscript was based on the following paragraph in [Ejaz et al., 2015] from page 1034:

“There was some consistency: when averaging activity patterns across participants (Fig. 1), a blurry somatotopic arrangement became visible with the thumb activating more ventral and the other fingers more dorsal areas of the motor strip.”

Figure caption: adapted screenshot from Fig. 1 of Ejaz et al. Subject average activation maps show rough features of linear somatotopic arrangement (with secondary deviations). Thumb representations peaks at the bottom (pink arrow) and the remaining fingers are linearly aligned with the little finger representation peaking at the top (red arrow).<br /> We also noticed indications of a secondary thumb representation in Fig. 1 of [Ejaz et al., 2015] next to the index finger. We discussed these double-thumb indications in the Ejaz et al. figures extensively among ourselves and eventually decided not elaborate on them in our manuscript for the following reasons:<br /> In our own pilot studies, we noticed that for some kinds of thumb movement tasks, the thumb-movement can come along with unwanted secondary wrist movement. This was not the case for index/middle/ring/pinky-finger movements. Since the wrist movement representations are expected to be located next to the pinky-finger, we were sceptical that the secondary thumb representation form Ejaz might actually refer to unwanted wrist movement?<br /> In our own BOLD data, we find some cases of signal leakage from S1 to M1 (across the central sulcus), which might introduce artifactual double representation in M1. Since, Ejaz et al., also used BOLD sequences, we speculate that this might have been the case in those data too? <br /> The text of the paper [Ejaz et al., 2015] does not discuss the secondary blob at all. Neither does it mention it in the context of a potential double-representations or mirrored representation. Thus we are hesitant to include it as a reference for this feature. If would be more appropriate for us to give the authors of [Ejaz et al., 2015] full credit for the discovery of mirrored representations, if they would have described it and discussed it consistently across people.

It is further to note that the above statement in our preprint referred to the sensory cortex, not the motor cortex.

Revision to avoid future misunderstandings:<br /> We think this misunderstanding can be resolved by removing the [Ejaz et al. 2015] citation on page 5. Instead we discuss the paper in more depth on page 7.

R1.4 <br /> Furthermore, they (Ejaz et al.) go on to show that the stable structure of overlap of finger representations in M1 and S1 can be accounted for by the statistics of everyday hand movement. They did not interpret the spatial variability of these patterns as "noise due to inter-individual variability in every day hand movements". On the contrary, the statistics of hand use they showed is stable across individuals (also see Ingram et al., 2008, Exp. Brain Res.), as is the organizing principle underlying the spatial organization of activity patterns in M1 and S1.

1.) Justification for our statements in the previous version of the paper:<br /> We assume the comment from the reviewer refers to the following section of our manuscript on page 6:

“Previous studies by Sane et al. (1995) and by Ejaz et al. (2015) already identified deviations from linear organizations for finger representations in the human motor cortex with GE-BOLD at 2.5 mm and 1.4 mm resolutions, respectively. However, without the localization specificity, a consistent spatial layout principle, such as the mirrored finger representation alignment, was not found. Instead, the exact pattern of overlapping and segregated representations was interpreted as noise due to inter-individual variability in every day hand movements (Ejaz 2015).”

We included this interpretation of Ejatz’ results based on the first few sentences of the discussion section in [Ejaz et al., 2015] on page 1039:

“The relative similarities between activity patterns were preserved across individuals, despite the substantial spatial inter-subject variability of the activity patterns themselves. The representational structure remained invariant even when the shared somatotopic arrangement of the digits was removed from the data. This suggests an organizing mechanism that shapes the overlap between patterns without enforcing a regular spatial layout. The representational structure could be predicted by the natural statistics of hand use.“

If we understand the highlighted section correctly, Ejaz et al. found that there are deviations from a simple somatotopic organization. And the patterns of these deviations have a considerable variability across people. It is not clear, however, according to which consistent organization principle this variability comes about.

In our view, we thus (mis-)described the phrase “inter-individual variability without given structure” with the term “noise due to inter-individual variability”.

Revision to avoid future misunderstandings:<br /> We agree that the term “noise due to inter-individual variability” might be misleading to describe “inter-individual variability”. In the revised version of the manuscript, the corresponding section is revised as follows:<br /> A previous study by Ejaz et al. (2015) already identified deviations from linear organizations for finger representations in the human motor cortex with GE-BOLD at 2.5 mm and 1.4 mm resolutions, respectively. These data already showed some indications of multiple finger representations (e.g. Fig. 1 in (Ejaz et al. 2015)). However, these data were not discussed with respect to an alternative geometric somatotopic organization principle such as a mirrored representation.

R1.5 <br /> I definitely agree with the authors that M1 organization is more complex arrangement than simple linear finger organization. Whether the organization really is best described by two discrete finger maps with phase reversal, however, really has to await a more rigorous experimental and statistical evaluation than even what is presented in Huber et al. Whatever the answer may be, however, I do think that the improved specificity of VASO sequence may play an important role in uncovering such representations in the future, but I don't feel that what has been shown goes much beyond what is known from the literature already.

We are glad that the reviewer agrees with our work showing that the M1 representations can be complex. We agree that the literature needs to be augmented with more rigorous studies.<br /> In fact, with the manuscript at hand we intent to do just that: providing a more rigorous experimental evaluation. We aim to move beyond the position of Ejaz et al. Namely, we aim to go beyond the conclusion “that the motor cortex is more complicated than individual finger representations”, . and describe how it is different, how these differences are geometrically organized, and whether they are stable across people.<br /> Accounting also the large bulk of electrophysiological and micro-stimulation evidence about the body-part sub-divisions in M1 we opt to see how these representation are in agreement with the results from Ejaz.<br /> In previous imaging studies (including Ejaz et al.,) it was common to view M1 as one large chunk of cortex that would follow the same architectonic principle. There is a large body of invasive literature, however, that suggests that this is not correct, neither functionally (Rathelot and Strick, 2006, 2009) nor anatomically (Geyer 1996). Thus, we intend to describe the body-part representations with a more rigorous fine-scale evaluation. To get there, we developed the advanced methodology as described here. And we start to describe the simplest movement principle of the literature (finger tapping) in the simplest part of M1, namely the evolutionary “old” M1 that has been described as body part representations. <br /> Thus, we feel that our findings go beyond what it known form the literature already.

Reviewer #3: <br /> General Comments: <br /> This paper uses the vascular space occupancy (VASO) method of measuring cerebral blood volume (fMRI) to explore the somatotopy of the finger representation at a sub-millimeter resolution in M1 and S1 of humans. This is an important problem as prior fMRI papers exploring this issue did not have sufficient resolution to adequately address a fine grained topography for fingers. This paper appears to have adequate resolution (~0.8mm) to make a major contribution to understanding the topography of the hand in M1 as well as S1. As such, this paper is primarily one of anatomical location and fMRI reconstruction. In addition, it addresses the issue of whether a given body part representation is always active when that body part is moved. The answer is that there is functional specialization within each M1finger representation. The figures are complex and it is paramount that their display is straightforward, consistent and simple to understand.

R3.1. The stated goal of this paper is to"non-invasively investigate the functional organization topography across columnar and laminar structures in humans", particularly M1 and S1. To understand the topography of the fingers in M1, the entire extent of the finger representations in M1 must be accurately mapped. Such maps are shown in Figs. 6S and 10S. These maps, for each participant, could form the core of an important paper, but they belong in the main body of the paper. They also need to be shown systematically for each participant. The data showing the columnar organization of M1 and S1 seem like important validating information for the reconstruction of the central sulcus. Some of this could be moved to the Supplementary information. What is currently displayed in Figs. 1-5 is just a small sample from the entire extent of slices through M1. Although the concept of mirror hand representations derived from single slices is appealing, it is only represents a small fraction of the entire map of the central sulcus. Furthermore, the single fMRI slices totally ignore the finger representations present in the depth of the central sulcus.

We would like to clarify our goal of this study. We feel the quoted section was taken out of context. As mentioned in the abstract, it was not our goal to ‘investigate the complete topographical organization of the motor cortex at its entirety’. Instead, the quoted section comes from an introductory sentence that states that our goal actually was to ‘develop imaging and analysis methodology, which -in principle- allows us to investigate topographical features’. In a next step we then use the M1/S1 system as a test bed to investigate the neuroscientific usefulness of that methodology. Given that we find -previously not described- neuroscience findings of the mirrored digit representation, we think that the neuroscientific usefulness it confirmed. In this sense, we see our manuscript to lie along a fine line between a methods paper and neuroscience paper.

We agree with the reviewer that every figure in the Manuscript and the Supplementary information is “tuned” to a specific message that we want to bring across. We further agree that Figs. 1-5 in the main manuscript are just a small sample of the main story and there is much more information to be seen. We don’t see this as a weakness of the manuscript. But as a means to follow the comment R3.14, namely selectively showing figures that have a specific message, which comes across as intuitive as possible.

In order to discuss the mirrored pattern of digit representations, we find it most natural to zoom into the hand area (Fig. 1). Correspondingly, when it comes to showing the inter-participant consistently of this feature (Fig. 2), we find it advantageous to use the same imaging procedure across all people as in Fig. 1. However, when it comes to explaining where these features are located across the dimensions of the central sulcus, we show additional unzoomed images. <br /> We agree with the reviewer that entire maps of the unflattened sensory-motor-system would give a more comprehensive view. However, it would distract the reader from the feature of interest. Those entire maps would mostly contain nothing (e.g. all the non-stimulated body parts, trunk, face, feet, etc.) and the 3-8mm of interest would be tiny (e.g. See Fig. S6). <br /> To address the reviewers comment, we included the full maps of the central sulcus into the manuscript main body (new figure 3), additional to the zoomed images.<br /> Furthermore, we included additional IMAGIRO maps (as requested) of for more participants with zoomed and unzoomed sections to guide the reader which part of the superior part of M1 it refers to (See new Fig. S6E).

The of laminar and columnar fMRI is still emerging. Thus, not all potential sources of analysis artifacts are fully described and understood. To minimize potential misinterpretation it has been suggested to depict the final results as close to the raw data as possible (Polimeni 2017; Kay 2019). Thus we try to show the activation maps in the raw EPI space (Fig. 1,2,4), when possible. This way, it can be easily be directly appreciated that the mirrored finger pattern is not an artifact of a flawed infolding artifact. Furthermore, the activity maps in EPI space best depict the spatial scale of columnar size with respect to the cortical thickness and location at the hand knob. Flattened maps are produced by several additional steps and are presented in an very abstract space where, these reference dimensions are lost. Thus, we are hesitant to remove the activation maps on the folded cortex from the manuscript. However, we included additional unfolded flattened maps in the supplementary material.

Please note that we are also required to following the Journal’s Guidelines to only include material that is central to the narrative. In doing so, we follow the rule of not having more than double of supplementary figures as figures in the main text. Thus, is included the some of additional maps as figure-panels, not as additional stand-alone figures.

We revised the manuscript to account for the reviewer’s comment. Specifically, we rephrased the abstract and introduction section to make our goals clearer. We also tried to make it clearer what the message is for each figure, in the figure captions respectively.

Kay, K., Jamison, K., Vizioli, L., Zhang, R., Margalit, E., & Ugurbil, K. (2019). A critical assessment of data quality and venous effects in sub-millimeter fMRI. NeuroImage, 189, 847–869. http://doi.org/10.1016/j.ne... <br /> Polimeni, J. R., Renvall, V., Zaretskaya, N., & Fischl, B. (2017). NeuroImage Analysis strategies for high-resolution UHF-fMRI data. NeuroImage, (April), 1–25. http://doi.org/10.1016/j.ne...

R3.2. The orientation of brain images and reconstructions should be the same in every figure. For example, Fig. 1A and 1E seem to have the right side of the brain image toward the right whereas Fig. 1B-D has it to the left. In Fig. 6S, the orientation of the CS appears to be opposite to that shown in Fig. 10S. Continually forcing the reader to flip the images creates unnecessary confusion. Since this paper shows the right hemisphere, left/medial should be on page left and right/lateral should be on page right. The terms medial and lateral are preferable to left and right. In Figs. 6S, 10S, the actual location of the medial wall/sagittal fissure should be indicated. Without this marker, the CS just floats in space with no anchor to the actual brain image. A calibration should be included on each image.

We agree that the orientation is confusing. This comes from the fact that the convention of MRI images is to view them as they would look like from the experimenter perspective. E.g. looking at an axial cut from the perspective of the participants feet. The right motor cortex of the person is then depicting on the left. This is contradicting to the 3D-head-models from viewing from above. Thus, the 3D-views and the 2D-views were confusing.<br /> Based on the reviewers comments, we tried to make it more consistent in Fig. 1, S6 and S10. This means however, that the 3D-head-models are mirrored representations compared to their real-live pendants. <br /> We included additional calibration markers and the landmarks of the medial wall in multiple figures. E.g. Fig. S6, S9, S3.

R3.3. The term 'multiple' is used incorrectly throughout the manuscript. Multiple means 'more than 2'.

We respectfully disagree with the reviewer on this point. In our understanding, the term ‘multiple’ refers to ‘more than one’ (source: https://en.oxforddictionari... "https://en.oxforddictionaries.com/definition/us/multi-)"). We chose this term deliberately vague. We find only two mirrored representation consistently across all participants. However, we cannot exclude the possibility that there are more representation hidden below the detection threshold. Since absence of evidence is not the same as evidence of absence, we would like to refrain from calling it “double” representation. This excludes the possibility of a third or fourth representation. <br /> In one participant, with a large tilting angle, and with a very low threshold, we see indications of a third representation. However, since its not reproducible across participants, its discussion is subject to future experiments with more sensitive imaging methodology only.

R3.4. It is unclear how the images in Fig. 1E were developed. What do the colors mean? Why is this representation shown here when it is not used until Figs. 3S, 6S.

Fig. 1 was intended as a figure describing the methods applied in this study. Thus, we included the coordinate system of layers and columns in 3D-grids as they are used for the directional smoothing. We agree with the reviewer that it can be confusing, we thus removed the panel E from the figure in the revised version of the manuscript.

R3.5. Discussion- <br /> The requested revisions in the data presentation will require revision of comparisons to other fMRI papers. <br /> The Discussion would be improved by a more extensive comparison to studies in monkeys where most of the mapping of M1 has occurred. An excellent brief summary of the monkey literature may be found in the section written by Paul Cheney in Omrani et al, 2017. The discussion should address two issues. <br /> First, a comparison of the organization of human M1 to the anatomical and physiological explorations of this region in the monkey. Second, the issue of specialization (separate regions of grasping and retraction) has its basis in monkey data that indicates specialization of M1 neurons for specific tasks.

We agree with the reviewer that the summary from Cheney provides a nice summary about representations in the motor cortex learned from monkey experiments. Based on this summary, we included an additional paragraph into the discussion section that should address the two issues.

Most of the knowledge on the functional representation of movements in the primary motor cortex has been obtained from countless experiments in monkeys over the last century. The current state of consensus in the field is nicely summarized by Paul Cheney in (Omrani 2017; see also referenced therein); Overall, corticomotoneuronal cells in the primary motor encode muscle-related parameters of movement such as muscle activity and muscle force. Although some corticomotoneuronal cells in the primary motor cortex (particularly those involved with finger movements) have their terminations confined to motoneurons of single muscles, a large amount of corticomotoneuronal cells are not rigidly coupled to the activity of its target muscles but show specialization for particular movements or categories of muscle activity. Namely, almost half of the corticomotoneuronal cells facilitate muscles involving at least one distal and one proximal joint and are specialized for specific muscle synergies, E.g. for reach-to-grasp movements. With respect to action representations shown in Fig. 2B, it is important to note that Cheney and Fetz (1985) had previously identified the muscle fields of neighboring corticomotoneuronal cells. They showed that neighboring corticomotoneuronal had muscle fields that were very similar. Hence, the notion of cortical patches that are preferentially activated for grasping and retraction actions (Fig. 2B) has its basis in previous monkey data and could refer to these previously described muscle fields.

Specific Comments:

R3.6. The first sentence of the Significance statement is incomprehensible. In general, the significance of this study is not well explained.

Since the significance statement is removed from the revised version of the manuscript.

R3.7. Introduction- Sanes et al., 1995 did not study monkeys.

We agree with the reviewer. The Sanes reference is moved to a different section now.

R3.8. "However, the organizational principle of smaller body parts such as individual digits could not be resolved due to the lack of localization specificity of conventional GE-BOLD fMRI and the sparse sampling of invasive electrophysiological recordings." This may be true for fMRI but the electrophysiological stimulation in monkeys (Kwan et al.l 1978; Strick and Preston, 1982 [up to 16 penetrations per 1mm2]) and Park et al. 2001) can hardly be described as sparse.

We agree with the reviewer that the term “sparse” might be misleading and does not give those experiments’ justice. The point we were trying to make is, that fMRI is inherently a continuous mapping technique that continuously samples the entire cortical sheath without any holes between electrodes. Which is true even at low resolutions. To address the reviewers comment, we revised the paragraph in the introduction section.

R3.9. Lin et al 2011 is often used as evidence that VASO accurately measures CBV. However, close examination of Fig. 1 in Lin et al reveals that the VASO and Gd-DTPA blood volume measurements often do not occupy the same voxels. That is, many VASO voxels with significant activation have no significant Gd-DTPA activation and many Gd-DTPA voxels with significant activation have no VASO activation. This observation suggests that VASO does not accurately represent CBV when voxel to voxel comparisons are made by the two different methods of measuring CBV. What other evidence, other than theoretical, indicates that VASO accurately measures CBV? (Lin AL, Lu H, Fox PT, Duong TQ. Cerebral blood volume measurements- Gd-DTPA vs. VASO - and their relationship with cerebral blood flow in activated human visual cortex. Open Neuroimag. J. 2011; 5: 90-95.)

We share the reviewer’s concerns whether VASO is a good measure for CBV. For this reason, we validated our SS-SI-VASO variant with gold-standard methods in multiple setups across the last 5 years. Ranging from concomitant VASO imaging with optical imaging spectroscopy in rats, up to validations of layer-dependent VASO signal with MION/Ferraheme imaging in rats and monkeys.

While we agree that Fig. 1 in Lin et al., shows deviations of VASO and Gd-DTPA, we would like to refrain from speculating what might be the reason for this. Reasons could range from acquisition challenges up to analysis inconsistencies. See the following reference:

Huber, L., et al (2015). Micro- and macrovascular contributions to layer-dependent blood blood volume fMRI: A multi-modal, multi-species comparison. ISMRM. doi: http://dx.doi.org/10.7490/f... ).

Note that our validation studies are quantitative in physical units of ml. This is in contrast to significance maps in Lin et al., that might be prone to biases in different noise characteristics post-injection of GD. <br /> Also note that our validations are carried out across columnar structures (B) and laminar structures (C).

See figures from:<br /> Huber, L., Goense, J.B.M., Kennerley, A.J., Guidi, M., Trampel, R., Turner, R., and Möller, H.E. (2015). Micro- and macrovascular contributions to layer-dependent blood blood volume fMRI: A multi-modal, multi-species comparison. In Proceedings of the International Society of Magnetic Resonance in Medicine, p. 2114. Doi: http://dx.doi.org/10.7490/f...<br /> Huber, L., Goense, J.B.M., Kennerley, A.J., Trampel, R., Guidi, M., Ivanov, D., Gauthier, C.J., Turner, R., Möller, H.E., Reimer, E., et al. (2015). Cortical lamina-dependent blood volume changes in human brain at 7T. Neuroimage 107, 23–33.<br /> Huber, L. (2015). Mapping human brain activity by functional magnetic resonance imaging of blood volume. University of Leipzig. https://fim.nimh.nih.gov/fi... <br /> Kennerley, A.J., Huber, L., Mildner, T., Mayhew, J.E., Turner, R., Möller, H.E., and Berwick, J. (2013). Does VASO contrast really allow measurement of CBV at high field (7 T)? An in-vivo quantification using concurrent optical imaging spectroscopy. In Proceedings of the International Society of Magnetic Resonance in Medicine, p. 0757.

In the revised version of the manuscript, we included the following additional paragraph into the discussion section:

Note that the CBV weighting in VASO has been extensively validated by comparisons with gold-standard methods in rats and monkeys across layer and columns (Huber et al., 2015a-c; Kennerley et al., 2013).

R3.10. The voxel size is listed as 0.89mm x 0.99mm on page 2 versus 0.79mmx0.79mmx 0.99mm on page 1. Which is correct?

The correction resolution is 0.79 mm. This typo is corrected in the revised version of the manuscript.

R3.11. Was the smoothing across layers a directional smoothing?

The reviewer is correct. The layer-smoothing was applied in specific directions only. It was only applied in the direction that is parallel to the column. There was no smoothing perpendicular to this direction. <br /> Note that this way of “directional” smoothing refers to cortical directions. The smoothing was independent of the direction in the laboratory frame of reference. As such, the smoothing is applied independent of the orientation of read-direction, slice-direction and phase direction. The LAYNII program LN_DIRECT_SMOOTH was not applied in this study. <br /> An additional sentence about this is included in the revised version of the manuscript.

R3.12. Page 13- "...primary motor cortex is 4 mm (Fischl and Dale 2000), the resolution of 0.79 mm used here allows us to obtain 5-7 independent data points across the 20 layers. The number of 20 layers is chosen based on previous experience in finding a compromise". This description is hard to understand. Suggest something like- The cortical thickness of the primary motor cortex is 4 mm (Fischl and Dale 2000). With our resolution of 0.79 mm, we obtained 5-7 independent data points across the thickness of the cortex. These data points were upsampled to create 20 layers across the thickness of the cortex. Twenty layers was chosen based on previous experience in finding a compromise... These 20 layers were smoothed and extracted (tell me what you did here) in sheets to produce a reconstruction of the face of the anterior bank of the central sulcus (Figs. 3S, 6S, 10S).

Based on the reviewer’s suggestion, we tried provide a more detailed description of the underlying assumptions and the necessity of using so many layers in a recent blog post: https://layerfmri.com/2019/... <br /> In the revised version of the manuscript, we the included the following summarizing statement:

The cortical thickness of the primary motor cortex is 4 mm (Fischl and Dale 2000). With our resolution of 0.79 mm, we obtained 5-7 independent data points across the thickness of the cortex. Across these data points, we created 20 layers across the thickness of the cortex on a 4-fold finer grid than the effective resolution. The number of twenty layers was chosen based on previous experience in finding a compromise data size and smoothness (see Fig. S6 in (Huber 2018)). Columnar profiles in Fig. 3 and Fig. S4 are generated from unsmoothed data. For Figs. S3 and S6, the functional signal was smoothed with 0.5 mm within columns and extracted in sheets to produce a reconstruction of the face of the anterior bank of the central sulcus. No smoothing was applied across columns.

R3.13. Fig. 2B- For participant 5, the copper and turquoise outlines are reversed. Hue of copper and turquoise colors are not consistent in each panel. <br /> In last panel of 2B, first line- there is a hand in this panel. What is its purpose? If the purpose is to be a key for finger color, the thumb should be magenta.

The reviewer is right, the copper and turquoise patch seems reversed in participant 5. Note, however that this is not a presentation error in the preparation of the images. We find that the grasping-extension patches do not follow a the same organization principle along the medial-lateral direction across participants. It is highly dependent on the position of the axial projection chosen. E.g. it can be seen in Fig. S6 (and previous version of Fig. S9) that, dependent on the depth of the central sulcus, the copper and turquoise patches are either on the medial or lateral side. Please also note that participant 5 is not an outlier here; in fact, participant 1 (in the same figure) has the same copper-turquoise alignment as participant 5. Please also note, that the sensory cortex consistently shows a grasping preference, across all participants.

The additional hand pictogram had been included as a figure key to remind the reader, which color refers to which finger. Based in the reviewers comments, it is excluded in the revised version of the manuscript. It is already shown in panel A) anyway.

R3.14. Fig. S3C- Several features of this figure make it hard to decipher and undermine the explanation of the reconstruction method. I am assuming that the little squares in panel B are equivalent to columns. This should be stated explicitly. If the colors correspond to the fingers, then the mirror representation of the hand shown in Figs. 1-3 is nowhere to be found. This is confounding. It may be useful to show the location of the slice in panel D. Panel D is reversed from panel A, creating needless confusion. In panel C, the laminar thickness of the cortex is greater than the depth of the central sulcus. Calibrations would help but why not make the laminar thickness accurate? State explicitly that the IMAGIRO reconstruction consists of 20 layers, each like the one in B. Spelling- Columnar 'distance' <br /> It took me a long time to understand what you were doing. The descriptions of the reconstruction needs to be simple, clear and intuitive or very few will comprehend them. It all makes sense but the reader should not have to go to the blog (which I did) to understand them.

We thank the reviewer for the suggestions to make this figure clearer. We also applaud the reviewers level of commitment to check the description on our blog.<br /> -> The little squares indeed refer to the columnar dimension. Additional comments are included in the caption.<br /> -> The colors do not refer to finger dominance, but to the medial-lateral position. This is included in the caption now.<br /> -> The location colors are now included in panel C, as suggested.<br /> -> Panels C and D are now switched, as suggested.<br /> -> If, the laminar thickness could be accurately depicted, all 20 layers would be 2-3 mm apart in the figure. If we would depict it in the right geometry, the layers could not be separated with the naked eye. Scale bars are included as suggested, which points out how they are distorted.<br /> -> An explicit reference about 20 layers is included.<br /> -> The typo is corrected in “distance”

Updated Fig. 3:

We agree, that an intuitive image is helpful. Here, we tried to find a compromise of simple intuitive figures that are representing the complexity of the analysis without making the supplementary material too long. The reviewer’s comments are appreciated to achieve this.

R3.15. Fig. 4S part B- Should note that this is upsampled to produce 20 layers.

The revised version of the manuscript has an additional statement included:

Note that the size of layer and column structures are smaller than the effective resolution of 0.79 mm. They are estimated in an upscaled space.

R3.16. Fig. 9S- Why is the background of the VASO view of the anterior bank of the CS entirely red? This implies that the entire CS is related to the 5th finger. How is that possible? Why are there yellow and green patches distributed all along the CS? This arrangement is different from any of the other figures. There does not seem to be a double mirror representation in this participant. <br /> In the bottom panels, why is the view limited to just part of M1 instead of the whole of M1? In general, this figure is quite confusing and really difficult to interpret. The organization of the grasping and retraction patches is an important issue. A better explanation (illustration?) of what you are trying convey in this figure is necessary.

We agree with the reviewer that previous Figure S9 could be confusing. We tried to show too many features in one Figure. Our goal of this figure was to show the consistency of the finger representations across the different tasks and also to show the position of the mirrored representation along the depth of the central sulcus. Based on the reviewer’s comments, we decided to remove Fig. S9. From the manuscript. We believe that these to messages already come across from Fig. S5, S6, S9 (new).

To answer the reviewer’s questions (for the sake of his/her curiosity): <br /> -> The top-right figure was included for the sake of orientation. It was not included to suggest the significance of the mirrored pattern. Thus, we did not threshold the finger dominances at all. In areas outside the hand-knob, therefore, the finger-preference measure for all fingers is close to 0. The red color outside the hand knob does not mean that this finger is represented there. It only means that all the other fingers are even noisier. E.g. that the finger preference for the index finger is 0.0014 compared to other fingers with a finger preference of 0.0005. For reference, in the hand knob, the finger preferences are in the regime 0.3-1 (please, see Fig. 3B about the absolute selectivity strengths in an outside the hand knob). The previous figure S9 corresponds to the line graph in Fig. 3B from above. <br /> -> We believe that there is, in fact, a mirrored pattern visible in this figure. Within the Brodman area subsection BA4A, the color pattern is reversed.

R3.17. Fig. 10S- in the right panel, the orientation seems to be incorrect. That is, left is lateral and right is medial which means the left ear arrow should be pointing to the right.

We agree, the arrow description now says “right” ear.

R3.18. I suggest alphabetizing the reference list.

In the updated reference list “S” is after “O”.

R3.19. The correct citation is- Meier JD, Aflalo TN, Kastner S, Graziano MS. Complex organization of human primary motor cortex: a high-resolution fMRI study. J Neurophysiol. 2008 Oct;100(4):1800-12. doi: 10.1152/jn.90531.2008. Epub 2008 Aug 6

The reference is updated.

On 2018-11-19 20:53:04, user Diedrichsen_lab wrote:

This is a very interesting study investigating the spatial organization of hand movement representations in M1. We agree with the authors that the hand representation in M1 is likely complex and therefore requires advanced methods to probe. We would like to point out, however, that the authors’ reference to a previous paper from our lab (Ejaz et al., 2015, NatNeuro) contains a number of misunderstandings. Specifically, we take issue with the authors stating that 1) our work argues for a simple topographic arrangement of single finger representations in S1, and 2) that the overlap between finger activation patterns is “due to noise”.

In our work (Ejaz et al., 2015), we used BOLD fMRI to measure the activity patterns evoked by single- and multi-finger movements in M1 and S1. The spatial arrangements of these patterns in both regions were stable within each participant (compared across different scanning sessions), but highly variable across participants. These finger patterns are shown in figure 1 of our paper. Close visual inspection of the patterns reveals they do not follow a clear linear arrangement in either S1 or M1, and perhaps some evidence of digit “mirroring” can be observed – definitely there are parts of the cortex activated for the thumb at the dorsal end of the hand region.

We then calculate the dissimilarity between all pairs of finger patterns for M1 and S1, separately. Importantly, the relative dissimilarity between any pair of activity patterns (within a participant) was highly stable across participants. This is notable given the spatial arrangements of these patterns was highly variable across individuals. One stable characteristic was that the thumb pattern was more similar to the little finger than to the ring finger. This finding clearly shows – contrary to what our paper is cited for - that a simple linear somatotopic arrangement cannot account for the digit representations in M1 or S1.

We then show that the stable structure of overlap of finger representations in M1 and S1 can be accounted for by the statistics of everyday hand movement. Thus, we did not interpret the spatial variability of these patterns “noise due to inter-individual variability in every day hand movements”. On the contrary, the statistics of hand use is stable across individuals (Ingram et al., 2008, Exp. Brain Res.), as is the organizing principle underlying the spatial organization of activity patterns in M1 and S1.

Overall, both imaging and neurophysiological evidence clearly suggests that M1 is not so much concerned with the representation of fingers, but rather of complex hand movements. The use of a winner-take-all map for fingers is therefore a less effective way of gaining a deeper understanding of the organization of M1. We do agree with the authors that M1 organization is more complicated than a simple linear finger organization. Whether the organization really is best described by two discrete finger maps with phase reversal, however, really has to await a more rigorous experimental and statistical evaluation. Whatever the answer may be, however, we do think that the improved specificity of the VASO sequence may play an important role in uncovering such representations in the future, and we are excited to see these new developments.

On 2018-11-08 13:53:42, user Ting-Yat Wong wrote:

Review of "Association of a lincRNA postmortem with suicide by violent means and in vivo with aggressive phenotypes?"

Dear Dr. Punzi,

We recently came across your manuscript, which you submitted to bioRxiv. As part of the “International Research Training Group (IRTG) 2150 – The Neuroscience of Modulating Aggression and Impulsivity in Psychopathology” (www.irtg2150.rwth-aachen.de/) "www.irtg2150.rwth-aachen.de/)"), we offer students a comprehensive and unique qualification program. One of our students came across your manuscript while searching for appropriate material to discuss in our monthly journal club. In this part of the qualification program, students are asked to put themselves in the shoes of future reviewers and formulate constructive criticism. We really enjoyed reading your excellent manuscript and agreed that it contains important new findings. It is impressive that the authors revealed the impact of non-coding RNA on aggressive phenotypes with a relative large postmortem brain sample and further provided evidence that the non-coding RNA may link to emotion regulation and impulsiveness in an independent in vivo sample via fMRI. Below, you will find a list of our comments and suggestions, which we hope to help you to further improve your manuscript and publish it successfully.

1. We can see the importance of testing the expression of LINC01268 in the region of DLPFC. However, we are also interested in whether you have tested other brain regions, such as anterior cingulate cortex.

2. Your prior study was mentioned a few times in the preprint manuscript but its details are lacking. Given that the importance of this study, it might be better to give some more details (e.g. a brief description).

3. Adding the samples from your prior study can add power to your analysis. However, we do not see the meaning of it. We deem that an independent sample as a replication is good enough.

4. We concern about the priority of main texts in the method section. It might be less important to stress too much on the describing suicide cases and how you categorize them. We found that the Table 1 is already good enough to capture the overall picture of your samples. The audience may also need more information about the method you used. Therefore, you might consider rearrange the priority of the texts in your method section.

5. We also concerned about the consent from your participants. It might be important to disclose this piece of information.

6. Some figures have an external border containing the boxplots (e.g. figure 2A/B). It looks like screen captured figures. We recommend that you should use better quality figures.

7. Uses of abbreviations should be careful. Otherwise, the audience is confused if some abbreviations popped up suddenly. For example, in the abstract the last sentence of the result section, using WGCNA is confusing and the unbiased audiences cannot understand what this refers to.

8. Although WGCNA provided important information of the biological meaning of LINC01268, its results actually make the whole discussion more confusing. A bit more effort should be paid to link its biological meaning to aggressive phenotypes.

Overall, we think that your manuscript is well-written, your experiment is well-designed and your study provides important and novel results. We hope our comments help you to improve the current version of your manuscript. In case you have any questions, please feel free to contact us (www.irtg2150.rwth-aachen.de/) "www.irtg2150.rwth-aachen.de/)").

Best regards from Aachen, Germany<br /> The IRTG students

On 2018-10-26 19:39:06, user Dorian Pustina wrote:

Hi Kaori,

I think you have done a great work here to achieve a comparison that is of high interest to the community. Congratulations. The most curious aspect was that you could run such a complex study on an i5 processor.

About the results, I am not surprised that LINDA missed many subcortical/brainstem lesions. On the contrary, I was surprised that it got some of those lesions. The reason is simple: LINDA was designed and tested on large lesions, while ATLAS is composed of many cases with small lesions. In fact, I checked the ATLAS dataset a few months ago and the median lesion size was very low, around ~5ml.xt

Brainstem lesions in particular would be very hard to detect with LINDA simply because LINDA is trained to expect some signal at its low resolution step, which probably is not there for small lesions. On top of this, I don't even think LINDA is considering the brainstem in the registration steps, it might mask it out completely.

This said, I still think your work is very valuable. I have three minor suggestions:<br /> 1. Please describe the lesion properties in better detail, particularly lesion size,, and put this in perspective with the lesion sizes used in each of the studies that developed the respective methods.<br /> 2. In the conclusion paragraph, you state: "We observed that testing on multi-site data resulted in decreased segmentation accuracy." This sounds like the problem is the multi-site nature of the test dataset, which may discourage people from running multi-site studies. The drop in accuracy has more simply to do with the nature of lesion accepted in a dataset, their size and location. I don't see multisite studies to be a problem per se.<br /> 3. Looks like ASSD values in Table 4 do not match the values described in the manuscript.

DISCLAIMER: I did not perform a thorough review of the paper. Any opinion expressed here is based on a quick superficial reading and should not be taken taken as proof of approval or disapproval.

On 2018-01-11 23:16:17, user Leslie Vosshall wrote:

We received some great questions and feedback from Christopher Potter at Johns Hopkins. Emily Dennis's replies are interleaved below:

We just read your C elegans pre-print paper for our lab’s journal club. It was very interesting! I really liked the mutant screen. Very cool. We had a couple question/comments to send on (which I hope is OK?).

1. The work’s impact might be greater if you could test more thoroughly if str-217 was indeed a GPCR that responds to DEET. The HEK heterologous expression didn’t work, but can you instead express str-217 in another worm chemosensory neuron that doesn’t respond to DEET and see if that now confers a response? I’m not a C.elegans person, but it seems like this should be fairly easy to do (especially with the Bargeman lab nearby).

RESPONSE: I'm very excited about this experiment! We're doing our best to get clean signal/expression in a completely DEET-insensitive neuron (the first few neurons we looked at are affected by DEET in some way even without the str-217 receptor) -- we don't have this yet but those data will definitely make it into the revision(s) when we have them.

1. For the experiments testing if DEET could act as an odorant (Figure 1C), DEET appeared not to do much. But given your later results that DEET responses, and ADL neuron activity, lead to changed in search (?) behaviors, I’m wondering if maybe its worth taking a closer look? Maybe I read it wrong, but it sounds like a paralytic is added close to the odor source to make it easier to count worms that made an odor choice. But this might hide a DEET response? Can you instead track the behavior of worms as they get closer to the DEET source? It could be the DEET-in-agarose worked because they just needed a higher local concentration of DEET, meaning that you might only see an olfactory effect when they get quiet close to a DEET source.

RESPONSE: I totally agree it's hard to say DEET does nothing. We have had a really hard time coming up with a perfect experiment that separates the effects of method of delivery, time/duration of exposure, proximity, and concentration in these population chemotaxis assays. I did try a few things that didn't make it into the final paper that may be of interest. First, I added DEET to the lid of the dish and didn't see any effect of DEET (though we didn't include those data in the paper as the assay itself is non standard and a little messy since DEET can chemically interact with/'melt' plastic). I also did do some population chemotaxis experiments without the paralytic, and they look very similar to the results in our pre-print. Another related anecdote: in experiments with isoamyl alcohol and DEET as point stimuli, I often saw animals on the DEET spot (!) and the odor spots, but it would be fun to see if changing the distances between DEET/odor spots would change this, or if adding a DEET spot to a 'random' place on the plate would reveal any avoidance of that spot. In an experiment somewhat indirectly related to this idea of delivery/distance being important, I am also currently exploring how duration and strength of stimulation of ADL neurons specifically alters behavior (using optogenetics).

My intuition from observing these experiments is that DEET alone has very little effect as an olfactory/point stimulus in this assay. However, I definitely do not think we've fully explored all contexts that volatile DEET could interact with, so it would be interesting to go through, say, a larger panel of odor stimuli and co-present with DEET to see if there's any change or to add volatile/point sources of DEET to other assays and see what happens.

1. It wasn’t mentioned, but did the other mutants you identified also work in the same neuron, or perhaps implicate a shared signaling pathway?

RESPONSE: We only were able to map one other strain, which mapped to the gene nstp-3. Our early attempts to do cell ID and figure out where this is expressed weren't informative so we don't know if it's the same or different cells. My guess is there are lots of genes and lots of neurons required for complete DEET-sensitivity, so there's lots more to do & explore! I would love to see someone do a sensitized screen in the str-217 mutant strain to see if we can get even higher chemotaxis...

Nice work! Fingers crossed for a painless journal review.

RESPONSE: Thanks again, this was a lovely email to receive.

On 2017-12-13 16:36:30, user Md Nurul Islam wrote:

I think there is a different in the approaches spatially tuned cells needs to be dealt with. In our lab we prefer detecting with empty eyes and then going into computation to do further verification and characterization. This way we reduce False positive rates that may arise from doing shuffling on spatial units. Again, the whole point of shuffling the spike times is that we want to see if the results that we see (place cell, grid cell, hd cell) are random and the generation of spiking activity is particular variable dependent. Now, when it comes to grid cell, given that it has multiple firing fields, there is always a big chance that animal will be closer to or at one of the firing fields and the shuffled spike will be associated to that location mimicking the grid-like pattern and giving a 95% gridness score closer to the original spiking activity, so there may have a chance of False negative as well (I have not tested it). But when it comes to False positive, I do not see a reason not to look into the geometric locations of the autocorrelation peaks and only looking into gridness as a 'verification' tool for the grid cells. And the entire idea of 'detecting' or 'determining' or 'verifying' grid cells based on shuffling analysis, and considering it as an standard, does not need to have a proof of high false positive rate when it fundamentally may not be acceptable to do so.

On 2017-03-16 13:03:39, user Róbert Bódizs wrote:

Dear Colleagues!<br /> The issue of slow and fast sleep spindle frequencies, as well as the problem of the individual- and derivation-specific amplitude criteria is the main focus of our research group since 2004 (http://dx.doi.org/10.1111/j... ). After recognizing the empirical and theoretical importance of the issue we created a new conceptual framework and a new methodology in order to formalize the phenomenon of individual-specificity of sleep spindles (J Neurosci Methods. 2009 Mar 30;178(1):205-13. doi: 10.1016/j.jneumeth.2008.11.006). Our conceptual proposals and empirical findings were published in several scientific papers. Journal of Sleep Research, Journal of Neuroscience, Scientific Reports, Frontiers in Human Neuroscience, Developmental Psychology are among the journals publishing these findings and considerations. It is unfortunate that authors of the present report completely dismiss these parts of the scientific literature. Several problems and issues reported in the manuscript of Cox et al, were already addressed, carefully reviewed and considered elsewhere. This neglect is however, even more embarrassing if one considers that 3 out of 4 authors of the present paper were listening to a keynote presentation on the issue of individual specificity in sleep spindling the last year (The 1st International Conference on Sleep Spindling, May 12-14, Budapest: http://static.akcongress.co... ). In this presentation I reviewed and critically considered the problem of universal, ad-hoc frequency and amplitude criteria in sleep spindle detection. The introductory part of the Cox et al paper is a reflecting on the same issue. We are also the first proponents of the idea that human sleep spindles have to be individualized in the broader frequency range of 9-16 Hz. The same values appear in the Cox et al paper. Last but not least, we empirically tested the best match between frequency criteria of fix frequency methods and individualized frequency methods. Results were particularly interesting as the 12 Hz (or 12.5 Hz) demarcation was found to be the optimal for dissociating slow and fast sleep spindles in healthy human adults in contrast to the widely acknowledged 13 Hz value (Front. Hum. Neurosci., 17 February 2015 | https://doi.org/10.3389/fnh... "https://doi.org/10.3389/fnhum.2015.00052)"). It happens that the 12 Hz value is considered as being optimal - again without mentioning the outcomes of our analyses resulting in the same value. An analysis which was performed on 161 healthy volunteers.<br /> I hope that the authors are willing to acknowledge the above mentioned reports as parts of the common knowledge of our scientific community.<br /> It is strange that - for sem reason - my previous comment was deleted from this site. I am just wondering why this happened, as I do not think that my sentences have to be moderated. <br /> Sincerely yours,<br /> Róbert Bódizs

On 2016-12-22 20:18:01, user mauromanassi wrote:

Dear Will and Peter,

Congratulations on your new paper! We have read it with great interest. We listed below our concerns and comments on it. We hope you will find these comments useful, we wrote them with a very constructive spirit hoping to improve the manuscript.

General comments:

1. You mentioned that three general classes of mechanism have been advanced to account for crowding (positional uncertainty, feature averaging and source confusion). How do you consider grouping? Another mechanism? When do you think it occurs? Any assumption would have strong constraints on the way the model is built.

2. Lines 172-176. It is not clear why mixture modeling based on maximum likelihood would fail to predict the underlying distribution of a data set. This technique has been widely used in the visual short term memory literature as the author properly cited. Some of us have also been using it for explaining visual masking and its interaction with spatial attention (Agaoglu, Agaoglu, Breitmeyer, & Ogmen, 2015; Agaoglu, Breitmeyer, & Ogmen, 2016).

3. Categorizing errors based on their distance to the nearest model prediction is technically equivalent to mixture modeling with three circular Gaussians, each sitting at the error predicted by each model (averaging, substitution etc.). So the method used here is qualitatively similar but quantitatively seems rather arbitrary. The current way of analysis implicitly assumes that the best way to account for crowded responses is a mixture model with (at least) three components, and then goes onto quantifying the weight of each component as a function of target-flanker spacing.

Minor comments:

The novel contribution of this study is a bit unclear to us. If it is to show that a population code of orientation selectivity can generate all types of errors, what is exactly the difference between your previous paper (CB 2015) and this manuscript?

Poder & Wageman 2007 study is highly relevant to this work. Also Ester and colleagues' studies used a similar approach, and the differences in model parameters between similar and dissimilar flankers in Ester et al. (2015) and the differences between one-gap flanker and two-gap flanker conditions in this study would be very interesting to compare.

In a recent study using the stimulus paradigm that you used previously (Agaoglu & Chung, 2016), we have shown that this particular stimulus paradigm is prone to eccentricity confounds. Perceptual errors are highly affected by the absolute orientation of the target and flankers, not just relative to each other. It is unclear how this affects the results reported here.

Line 34. It is fair to ask to cite our relevant work (Agaoglu, Chung, & Ogmen, 2016) where you described previous work on crowding and eye movements, since we presented a different point of view. The same holds for Pachai, Doering & Herzog 2016 (you cited only the reply to the reply). As scientists, we can agree to disagree, we hope.

Line 143. Except for N1, perceptual error does not seem to follow a linear trend. For A2 there is an increase in perceptual error only for the smallest flanker size. You may want to revise that sentence.

Line 270. We have a supporting evidence for this sentence. The role of masking is indeed increasing random guessing and slightly decreasing stimulus encoding precision (Agaoglu, Agaoglu, Breitmeyer, & Ogmen, 2015). However, ruling out metacontrast masking only because of this seems weak. Since the stimulus duration was 500 ms, we don't think there is any masking at all. You might also want to mention that to support the claim made in this sentence.

Mauro Manassi<br /> Mehmet Agaoglu<br /> Michael Herzog<br /> Susana Chung

On 2016-08-24 20:55:25, user Tal Yarkoni wrote:

This is an innovative and very thought-provoking paper that will hopefully be widely read by researchers working with fMRI. I have two general comments with respect to the authors' main thesis:

1. As far as I can tell, the authors don't motivate the decision to focus exclusively on sub-voxel representations. They point out that non-smooth sub-voxel representations would be impossible to detect with fMRI, which is an important observation. But surely non-smooth *supra-voxel* representations would still be easily detectable with fMRI. A priori, there doesn't seem to be a good reason to rule out this kind of representation in the brain. As far as I can tell, representational similarity analyses would still work successfully if the brain were composed of hundreds of functionally discrete tiles that were non-smooth at both the sub-voxel and supra-voxel levels. This doesn't seem like a far-fetched possibility; for example, suppose that when people think about penguins, they're somewhat more likely to think about the unusual climate in which penguins live. Representations of climate may be non-smooth, yet reside in fundamentally different brain circuits from representations of physical shape, size, etc. One consequence would be that neural representations of robins would almost certainly more closely resemble those of sparrows than those of penguins even if there were no spatially graded sub-voxel representations at all in the human brain--simply in virtue of sharing a larger number of salient properties with the former than the latter. Of course, I'm not suggesting that there _aren't_ smooth sub-voxel representations in the brain, but simply that the authors conclusion that "the neural code must be smooth, both at the subvoxel and functional levels" doesn't necessarily follow.

2. Even if one assumes that the signal detected by fMRI is in fact driven entirely by smooth sub-voxel representations, it still wouldn't follow that the neural code must be smooth at the sub-voxel level. All we would be able to conclude is that there is at least *some* component of the signal that is smooth. This would not preclude other neural codes from existing, and in fact, we already have abundant evidence of non-smooth sub-voxel representations. For example, ocular dominance columns clearly exist, and if fMRI is unable to detect them, that reflects a limitation of fMRI, not a generalizable claim about the way the brain represents information. While I'm not a systems neuroscientist, I would imagine that there are any number of examples in the systems neuroscience literature of non-smooth, but highly structured sub-voxel representations that would probably be completely undetectable with fMRI. So I think the authors may want to be more circumspect about the conclusions they draw. Their results don't really show that only a subset of neural coding schemes are plausible; rather they suggest that whatever neural representations fMRI is capable of detecting are likely to stem from either (a) smooth representations (either sub- or supra-voxel) or (b) non-smooth supra-voxel representations. This leaves open the possibility (and it seems like a very real one) that the vast majority of information represented in the brain is not represented in a way that is amenable to detection with fMRI.

Setting these concerns aside, I think this is still a paper that should be of great interest to most cognitive neuroscientists. One point that is made very elegantly here is that the nature of neural representations does not have to be (and probably isn't) uniform across the brain. In particular, the authors put forward a compelling argument for the possibility that brain regions higher in the processing stream--and that are more likely to represent very abstract, multidimensional information--may not be amenable to imaging at all. This point should give many fMRI researchers pause when considering studying, e.g., the representational structure of prefrontal cortex. At the very least, the manuscript raises a number of important questions that should spur further discussion within the neuroimaging community.

On 2016-06-23 17:12:34, user Justyna Hobot wrote:

"@anilkseth: TMS to prefrontal (or parietal) cortex does NOT impair visual metacognition, new @sacklercentreled by @DanielBor https://t.co/LnHE3DRtL5."

Dear Authors, how would you rate your awareness that the quoted sentence is just a catchy overstatement? I allow myself to post some comments on the paper, I hope this might be helpful.

1. "An advantage of TMS, besides its non-invasive nature, is that TMS-induced changes are limited to short time periods so that plasticity is unlikely to affect performance."

Didn’t you apply TMS in order to induce the plasticity-like changes that affect cognitive performance?

1. "First, continuous theta burst TMS (cTBS) was used instead of repetitive TMS."

Continuous Theta Burst Stimulation (cTBS) is an example of repetitive TMS. Repetitive TMS simply means it has a precise temporal pattern of pulses, and cTBS has the precise temporal pattern of pulses (see e.g. Bergmann 2016 or Oberman 2011).

Bergmann, T. O., Karabanov, A., Hartwigsen, G., Thielscher, A., & Siebner, H. R. (n.d.). Combining non-invasive transcranial brain stimulation with neuroimaging and electrophysiology: Current approaches and future perspectives. NeuroImage. http://doi.org/10.1016/j.ne...<br /> Oberman, L., Edwards, D., Eldaief, M., & Pascual-Leone, A. (2011). Safety of Theta Burst Transcranial Magnetic Stimulation: A systematic review of the literature. Journal of Clinical Neurophysiology, 28(1), 67–74. http://doi.org/10.1097/WNP....

1. "This technique involves a very rapid sequence of TMS pulses, typically for 40 s, and is thought to suppress cortical excitability for up to 20 minutes (ref. 19)"

"thought to suppress cortical excitability" – the 40 s cTBS may suppress M1 excitability, as long as it is applied correctly and the basal state of the brain allows such changes to occur, but e.g. the change of current direction can reverse inhibition to facilitation (see e.g. Jacobs 2012), and the short version of cTBS (like the one used by you) may actually increase M1 excitability, if there is no prior voluntary motor activation (see e.g. Gentler 2008).

"for up to 20 minutes" – you referred to Huang 2005, where the motor cortical excitability after the 40 s of cTBS was suppressed for 60 min. The after-effects lasting up to 20 minutes were also reported, but after 20 s (not 40 s) of the cTBS. Therefore, there is no need to confuse the reader by writing: "TMS pulses, typically for 40 s, and is thought to suppress cortical excitability for up to 20 minutes".

Jacobs, M. F., Zapallow, C. M., Tsang, P., Lee, K. G. H., Asmussen, M. J., & Nelson, A. J. (2012). Current direction specificity of continuous ?-burst stimulation in modulating human motor cortex excitability when applied to somatosensory cortex. Neuroreport, 23(16), 927–931. http://doi.org/10.1097/WNR....<br /> Gentner, R., Wankerl, K., Reinsberger, C., Zeller, D., & Classen, J. (2008). Depression of human corticospinal excitability induced by magnetic theta-burst stimulation: evidence of rapid polarity-reversing metaplasticity. Cerebral Cortex (New York, N.Y.: 1991), 18(9), 2046–2053. http://doi.org/10.1093/cerc...<br /> Huang, Y.-Z., Edwards, M. J., Rounis, E., Bhatia, K. P., & Rothwell, J. C. (2005). Theta burst stimulation of the human motor cortex. Neuron, 45(2), 201–206. http://doi.org/10.1016/j.ne...

1. "In this way, TMS administration can be entirely separated from the behavioural task, and therefore will not distract the participants from it."

It may be worth to note that what happens just after applying cTBS may reverse its after-effects (see e.g. Huang 2008), which means the first minutes of performing the post-TBS block may influence the effects observed on the following part. Did you try to check, how consistent the task performance was, by comparing the first 150 trials with the second half of the block?

Huang, Y.-Z., Rothwell, J. C., Edwards, M. J., & Chen, R.-S. (2008). Effect of physiological activity on an NMDA-dependent form of cortical plasticity in human. Cerebral Cortex (New York, N.Y.: 1991), 18(3), 563–570. http://doi.org/10.1093/cerc...

1. "In addition, a small (n=7) patient lesion study showed that the anterior prefrontal cortex (i.e. a region neighbouring the DLPFC) selectively impaired perceptual metacognition, though not memory-based metacognition, compared with patients who had temporal lobe lesions (27)."

You may check Del Cul 2009 paper, which also indicated the involvement of aPFC in perceptual metacognition, and the study was conducted on a bigger group of patients (n=15) than the one you refer to. Moreover, McCurdy 2013 showed that variation in visual metacognitive efficiency in his study was correlated with volume of frontal polar regions, while the variation in memory metacognitive efficiency with volume of the precuneus. However, I wonder, how this should support the use of DLPFC, instead of aPFC? Only because it is a neighbouring region?

Cul, A. D., Dehaene, S., Reyes, P., Bravo, E., & Slachevsky, A. (2009). Causal role of prefrontal cortex in the threshold for access to consciousness. Brain, 132(9), 2531–2540. http://doi.org/10.1093/brai...<br /> McCurdy, L. Y., Maniscalco, B., Metcalfe, J., Liu, K. Y., Lange, F. P. de, & Lau, H. (2013). Anatomical Coupling between Distinct Metacognitive Systems for Memory and Visual Perception. The Journal of Neuroscience, 33(5), 1897–1906. http://doi.org/10.1523/JNEU...

1. "In experiment 1 we therefore sought to replicate the Rounis study, as well as extend it to the posterior parietal cortex, since this region in neuroimaging studies is very commonly co-activated with DLPFC".

What do you mean when saying "this region"? PPC is an area, big enough to be consisted of subregions that have a different cytoarchitectonics, a different pattern of structural connectivity, and the activity of these subregions may correlate in a different way with the activity in different subregions of DLPFC (e.g. Leech 2011). The same of course applies to DLPFC (see e.g. Optiz 2016 for comparison of distinct DLPFC stimulation zones with respect to functional networks).

Leech, R., Kamourieh, S., Beckmann, C. F., & Sharp, D. J. (2011). Fractionating the Default Mode Network: Distinct Contributions of the Ventral and Dorsal Posterior Cingulate Cortex to Cognitive Control. The Journal of Neuroscience, 31(9), 3217–3224. http://doi.org/10.1523/JNEU...<br /> Opitz, A., Fox, M. D., Craddock, R. C., Colcombe, S., & Milham, M. P. (2016). An integrated framework for targeting functional networks via transcranial magnetic stimulation. NeuroImage, 127, 86–96. http://doi.org/10.1016/j.ne...

1. "Furthermore, we attempted to enhance the original Rounis design, by including an active TMS control (vertex), rather than sham stimulation."

Is there any reason to assume that by applying 2 times the same protocol to the same site (600 pulses to the vertex) you control for the effects of applying the same protocol to two different sites (300 pulses to each site)?

1. "We were concerned that managing the relative frequency of subjective ratings of "clear" and "unclear" labels across an experiment may have placed additional working memory demands on participants, since they would need to keep a rough recent tally of each rating in order to balance them out. In addition, these labels were difficult to interpret psychologically on account of their relative nature. We therefore opted instead for the labels "[completely] random [guess]" and "[at least some] confidence." Using confidence instead of clarity labels is a common practice, consistent with other recent metacognition studies (24, 25)."

What do you think about a possibility that by replacing the introspective report with a different kind of metacognitive report you investigated a different phenomenon/underlying processes than Rounis 2010 did (see e.g. Overgaard and Sandberg 2012)? In the papers of Fleming you refer to, metacognitive assessment always follows the behavioural response, which means it relies on processes such as e.g. error monitoring (see e.g. Young and Summerfield 2012), and in your paradigm the behavioural response is combined with the metacognitive rating, so it may be difficult to conceive it as a metacognitive measure of the confidence in choice ("Most notably, confidence in choice was used instead of visibility to determine metacognitive judgement.").

Overgaard, M., & Sandberg, K. (2012). Kinds of access: different methods for report reveal different kinds of metacognitive access. Philosophical Transactions of the Royal Society B: Biological Sciences, 367(1594), 1287–1296. http://doi.org/10.1098/rstb...<br /> Yeung, N., & Summerfield, C. (2012). Metacognition in human decision-making: confidence and error monitoring. Phil. Trans. R. Soc. B, 367(1594), 1310–1321. http://doi.org/10.1098/rstb...

1. "The AMT was defined as the lowest intensity that elicited at least 3 consecutive twitches, stimulated over the motor hot spot, while the participant was maintaining a voluntary contralateral finger-thumb contraction."

There is no consistency in the literature in what is understood as AMT, the main differences are present in: the amount of pulses required, the amplitude of MEP required, the level of muscular contraction. By looking at this paper the reader cannot know what method was used, even if it was the same as Rounis 2010 it still says nothing, as she does not provide this information either.

1. "cTBS was delivered with the handle pointing posteriorly and the coil placed tangentially to the scalp"

What was the current direction used? If you did not change the current direction to the reversed (AP-PA in the brain), then the current flow (PA-AP) was the opposite to the optimal (AP-PA), that presumably resulted in higher motor thresholds compared to ones that are obtained by using the optimal method.

1. "The standard cTBS pattern used, as with the Rounis 2010 study, was a burst of three pulses at 50 Hz given in 200 ms intervals, repeated for 300 pulses (or 100 bursts) for 20 s."

It may be good to mention the pulses (if they) were biphasic. Also "given in 200 ms intervals" may confuse the reader, because she may not be sure whether the inter trial interval (the time period between the last pulse in the first train to the first pulse in the next train) was 160 ms (as it should be) or 200 ms.

1. You have performed a lot of stimulations, have you forgotten that PPC was stimulated as well? There is no information in the paper on how PPC was determined; neither about the region of interest (within PPC) nor about the method used to target this region. Also, you may want to change PPN to PPC on the charts.

2. Surprisingly, there are quite big differences in metacognitive sensitivity in the pre-TBS blocks of the experiment 1, which makes it impossible to compare the effects resulting from stimulation to the different sites. Even more surprisingly, you do not address this issue in the discussion.

3. "In this way, we could rigorously explore the within subject likelihood of both a metacognitive impairment (or enhancement) following DLPFC cTBS and no metacognitive change following vertex cTBS, with a potential single subject replication of this pattern."

Doesn’t the lack of counterbalancing across the simulation sites indicate this was not a "rigorous exploration" (e.g. an influence of the behavioural learning)?

1. "The remaining 17 participants are summarised in table 5. Ten of these participants had no meta d’ changes on the first DLPFC session, and thus were not asked to return for subsequent sessions."

Does it mean that if you got the intended effect (by rejection of >50% of the participants), you would conclude that cTBS influences metacognitive sensitivity? I assume that you would not, therefore it may be difficult to follow the idea behind the rejection of participants who do not confirm the expectations of the researchers.

1. "Of the remaining 7 participants, 3 showed the expected impairment, while 4 showed a clear metacognitive enhancement following DLPFC cTBS. 6 of these 7 participants also showed a clear metacognitive change for the vertex control session, and thus were not asked to return for the 3rd session (2nd DLPFC)."

Still quite difficult to follow. The possibility of obtaining some significant effects caused by stimulation to the control site, in my opinion, represents the goal of the active control stimulation (performed in order to evaluate whether the potential significant effect of stimulation is site-specific). Also it probably shouldn’t be surprising to observe some effects in your control condition, as the vertex stimulation may influence the activity in DMN (e.g. Jung 2016).

Jung, J., Bungert, A., Bowtell, R., & Jackson, S. R. (2016). Vertex Stimulation as a Control Site for Transcranial Magnetic Stimulation: A Concurrent TMS/fMRI Study. Brain Stimulation, 9(1), 58–64. http://doi.org/10.1016/j.br...

1. "We have therefore not only failed to replicate the Rounis result, but provided evidence from our own experiments that on this paradigm there is no modulatory effect of theta-burst TMS to DLPFC on metacognition."

This evidence is not a scientific evidence, this explanation is as likely as the one that you did't apply the stimulation protocol properly (e.g. because it may work only when the current flow is perpendicular to the stimulated structure). The generalisations such as "no modulatory effect of theta-burst TMS" may not be accurate, especially in the case when one uses only the short version of one type of TBS protocols (300 pulses of cTBS), or "DLPFC" – this is just the general term, that is related to multiple subregions, and the stimulation in your study was (probably) applied just to one of them.

1. "First, it may well be that cTBS of cortex, at the medically safe stimulation thresholds commonly employed (80% of active motor threshold) is just not intense enough to induce a subtle cognitive effect, such as a reduction in metacognitive sensitivity."

Is there any way to verify this explanation? For example, by providing the reader with the information about the average MSO, the current direction used, the method used to determine AMT?

1. "To our knowledge, only one published paper to date, besides that of Rounis and colleagues, has demonstrated the general efficacy of DLPFC cTBS in modulating cognitive performance (38)."

What about, e.g.: cTBS applied to the left DLPFC impairs MCST performance (Ko 2008); DLPFC stimulation changes subjective evaluation of percepts, i.e. metacogniton (Chiang 2014); cTBS over the left DLPFC decreases medium load working memory performance (Schicktanz 2015). Moreover, Rahnev 2016 reported that both: cTBS applied to right aPFC and cTBS applied to right DLPFC affected metacognition. Is there any reason to ignore the results that are not consistent with the view presented in the discussion?

Ko, J. H., Monchi, O., Ptito, A., Bloomfield, P., Houle, S., & Strafella, A. P. (2008). Theta burst stimulation-induced inhibition of dorsolateral prefrontal cortex reveals hemispheric asymmetry in striatal dopamine release during a set-shifting task – a TMS–[11C]raclopride PET study. European Journal of Neuroscience, 28(10), 2147–2155. http://doi.org/10.1111/j.146<br /> Schicktanz, N., Fastenrath, M., Milnik, A., Spalek, K., Auschra, B., Nyffeler, T., … Schwegler, K. (2015). Continuous Theta Burst Stimulation over the Left Dorsolateral Prefrontal Cortex Decreases Medium Load Working Memory Performance in Healthy Humans. PLoS ONE, 10(3). http://doi.org/10.1371/jour...<br /> Chiang, T.-C., Lu, R.-B., Hsieh, S., Chang, Y.-H., & Yang, Y.-K. (2014). Stimulation in the Dorsolateral Prefrontal Cortex Changes Subjective Evaluation of Percepts. PLOS ONE, 9(9), e106943. http://doi.org/10.1371/jour...<br /> Rahnev, D., Nee, D. E., Riddle, J., Larson, A. S., & D’Esposito, M. (n.d.). Causal evidence for frontal cortex organization for perceptual decision making.

1. "Following a 1 minute interval, this was repeated at a different site for a further 20s (or again on the vertex in the control condition), determined by which group the participant was assigned to. The five groups were: i) bilateral DLPFC, ii) bilateral PPC, iii) left DLPFC and PPC, iv) right DLPFC and PPC, and v) VERTEX (control)."

Did you counterbalance the starting sites of the stimulation?

1. "However, the fact that we did not observe metacognitive impairment reliably in any subject in experiment two speaks against interpreting our null results simply in terms of missing the DLPFC during cTBS."

Does it? Following this way of reasoning one may conclude you missed the DLPFC in the first experiment, as you observed the effect just for some of the participants.

1. "... our results nevertheless indicate that the cTBS approach is not sensitive enough to establish a causal link between DLPFC and metacognitive processes."

Can it stem from the fact you used a short version of the protocol (300 pulses), and a probability the conventional cTBS (600 pulses) is excitatory in the first half and switches to inhibition only after the full length protocol (see e.g. Gamboa 2010), so application of 300 cTBS pulses may result either in no change or in small inhibitory/excitatory effects? Or, can it rather result from a possibility that the site within DLPFC you were targeting may have nothing to do with metacognitive processes?

Gamboa, O. L., Antal, A., Moliadze, V., & Paulus, W. (2010). Simply longer is not better: reversal of theta burst after-effect with prolonged stimulation. Experimental Brain Research, 204(2), 181–187. http://doi.org/10.1007/s002...

On 2014-06-10 13:49:57, user Authors of the manuscript wrote:

Dear Mike X Cohen,

this kind of personal commenting is much more helpful and constructive for the authors than the anonymous peer-review process and we thank you for taking your time to write this comment. We respond to some of your points in the following:

MXC: “It is not always clear whether the authors are criticizing the biophysical interpretation of CFC analyses, or the mathematical foundations of CFC methods. Perhaps it would be useful for the authors to define the situations under which CFC could be validly interpreted, and what exactly the neurobiologically meaningful interpretation would be.<br /> Concerning the former, the authors accurately state that relatively little is understood about the neural mechanisms that could produce CFC, and this may impede interpretations of empirical findings (the same criticism applies to most macroscopic measures of brain activity, including ERPs, time-frequency power, most measures of functional connectivity, the FMRI BOLD response, etc.).”

Authors:

We agree with this comment in the sense that indeed many measures in Neuroscience depend on an interpretational step. However, in contrast to the current handling of CFC, these aspects are well acknowledged for measures like BOLD and ERP. In addition there have been intense efforts to disentangle various generating mechanisms of BOLD signals and ERPs. (For the origin of the BOLD signal, the role of astrocytes, lactate, and calcium see for example: Niessing et al, Science, 2005; Logothetis et al., Nature, 2001; Barros, TINS, 2013; Petzold&Murthy, Neuron, 2011; Iadecola&Nedergaard, Nat Neurosci, 2007 . For generating principles of the ERP see for example: Mazaheri & Jensen, J Neurosci, 2008; Turi et al. NeuroImage, 2012; Telenczuk et al, J Neurophysiol, 2010, and references therein).

In these fields, the variety of generating mechanisms is typically discussed and wording is carefully chosen. With respect to the interpretation of CFC measures, this care is often lacking. Moreover, the mathematical methods of CFC are more involved compared to standard BOLD-fMRI or ERP analyses. Therefore, plain technical errors in published work occur more frequently than in either ERP or BOLD fMRI studies.<br /> _____

MXC: “Their suggestion for researchers to label their CFC analyses as relatively exploratory vs. confirmatory and as a marker vs. biophysical understanding (figure 5) is also sensible (this suggestion also could be applied to most or perhaps all measures of brain activity). The reliance on DCM should be cautioned against the over-parameterization and opaqueness of DCM models used in practice.”

Authors:

We agree with this comment insofar as the mathematics involved in DCMs is necessarily much more involved than that in the current standard CFC analyses. In our opinion however, this is outweighed by the advantage to be able to state the relative odds for and against the presence of a CFC mechanism in the data. Moreover, we also agree that the mathematical complexity of model specification indeed results in a certain opaqueness, especially to the lay.

We disagree with the criticism of over-parametrization, as models selected by Bayesian model comparison need two properties: (1) the ability to explain the data well, and (2) generalizability. The latter is ensured by automatically favoring models that explain the data well without using an excessive number of parameters, thus implementing Occam's razor. However, it is indeed necessary to carefully specify models for comparison, that are plausible a priori, based on existing knowledge (Lohmann et al, NeuroImage, 2013; comments by Friston et al, NeuroImage, 2013; Breakspear, NeuroImage, 2013; reply by Lohmann, NeuroImage, 2013). This requirement may mean that DCMs of CFC will have to wait until the mechanisms underlying CFC are spelled out more explicitly using interventions.<br /> ____

MXC: “the general point is that methods for assessing CFC are not necessarily confounded just because their results can be difficult to interpret from a neurophysiological perspective. Let me explain this by analogy: Imagine comparing ten randomly selected negative numbers with ten randomly selected positive numbers. A t-test would indicate statistical significance, but this significance is uninterpretable. However, the reason that the result is uninterpretable is not due to a confound of the t-test, but rather, due to the assumptions underlying the data collection. Imagine you received the same numbers but were told that they reflected measurements of relative alpha-band power in conditions A and B. Now the same result would be interpretable.”

Authors:

Indeed, in some sense the whole first part of our paper illustrates the variety of different but equally plausible reasons behind a CFC signature, or different possible interpretations if you wish. So, why do we call them "methodological confounds"?

Taking an analogy with the t-test might help us here, though we think that the analogy provided by MXC is slightly misleading and prefer a different version of the analogy. Namely, when you make a t-test, the un-interpretability is not only about the "origin of the data" (as in the example of MXC), but also (and actually even more) about the "nature of the data".

T-test makes specific assumptions on the underlying probability distribution (e.g. normality) and when these assumptions do not hold, the p-value obtained might very well just reflect the fact that the underlying distribution did not match well.

This is similar to CFC - we do not claim that the CFC measures are wrong, but in some sense show that the underlying assumption that there is real coupling in the data might well be doubted (for several reasons explained in the text). We show how alternative assumptions (i.e. non-linearity, common drive etc) could as well account for high CFC values. I.e. the CFC measure describes the amount of coupling only if we already assume the existence of this coupling, and the absence of the other mechanisms, or their constancy over experimental conditions.

Maybe "methodological confounds" sounds more appropriate if one keeps also this analogy in mind - if the methodology is applied in case of doubt with assumptions, the results are not interpretable. It is the same with the T-test - applying it to any distribution, one is not able to draw conclusions. This is not a fault of the T-test. However we would end up with a possible confound if we DID not know what the underlying distribution is, but still applied the T-test. In the case of CFC analysis we do not have a good understanding of underlying biophysics, but still apply the CFC measure and try to interpret it.

It might be useful to compare two different possibilities of expanding the acronym CFC - either Cross-Frequency Correlation or Cross-Frequency Coupling. The latter indicates biophysical interaction and even causality and is the one used now in the literature. Our article discusses at length why in fact we should rather hold to Cross-Frequency Correlation. Moreover, we explain that even in this case it is important to try to partial out the effects that could diminish the specificity of CFC as a marker.<br /> ______

MXC: “Their first example is the van der Pol oscillator. The authors claim that CFC here reflects a confound, because (page 3) “there is no simple physical interpretation for the different frequency components of the oscillator.” The interpretation depends entirely on the assumptions of the signal. If this were a neural signal, one might interpret that certain phases of the lower frequency oscillation regulate the variability of faster activity (as an aside, the lack of band-limited activity in Figure S1 is a classic situation of when *not* to interpret results as reflecting an oscillation; this has been discussed since the 1990’s by, among other researchers, Singer, Tallon-Baudry, Pfurtscheller, Miller). This is readily apparent by plotting the van der Pol signal along with its rectified derivative, which can be obtained with the Matlab code below:

ode = @(t,y)

vanderpoldemo(t,y,1);

[t,y] = ode45(ode,[0 20],[2 0]);

plot(t,y(:,1)), hold on

plot(t(1:end-1),abs(diff(y(:,1)))*8,'r')

The problem here is not with the measure of CFC. In fact, I do not see a problem at all; the authors simply tested a method on simulated data and got a result, much like a t-test on signed random numbers would produce a result. Here is another, even more striking, example:

t=0:1/1000:1;

plot(t,sin(2*pi*40*t) .*sin(2*pi*t))

As with the van der Pol illustration, one can say that CFC here is uninterpretable because there is no interaction amongst subsystems; there is simply a 40-Hz sine wave multiplied by a 1-Hz sine wave (this could occur from two independent systems with wave cancelation at the recording electrode). Again, the problem is not with the CFC measure, but that the simulated data do not lend themselves to a neurobiological interpretation of CFC.”

Authors:

Indeed, “the simulated data do not lend themselves to a neurobiological interpretation of CFC”, and neither do the neurobiological data at the moment. This is one of the main points of the manuscript.

The problem is that for now, the neurobiological measurements might not lend themselves to the “coupling” interpretation of CFC. The CFC analysis has been adopted and is used with a certain aim and interpretation. Thus it seems fair to say that if the methodology does not provide answers and interpretations it should, we deal with "methodological confounds".

The examples brought up show that without further assumptions and knowledge of the underlying neurobiology, current methodology is unable to discriminate between various basic but very different interpretations. In analogy with the T-test example above, similar other toy examples treated with a T-test would illustrate what could happen if the underlying distribution did not match the assumptions (i.e. normality) - and why a T-test is not applicable without checking its assumptions first.

As we mention in several places, this is not a problem when one tries to use the CFC measure only as a MARKER, however the problem comes when one goes one step further in the interpretation, trying to give a particular (physiological) meaning to CFC (“high frequency oscillations modulated by low frequency phase” or something along these lines).

Also, notice that your second example (modulated sinusoids) does tell you something about which parameters (in terms of bandwidth) should be used so that the CFC measure would be closer to its desired interpretation.<br /> ____

MXC: “Their other examples are also not compelling as identifying any confounds with CFC measures. Prime numbers are nonrandom sequences with a periodic structure (http://xxx.lanl.gov/pdf/cond-m... and anyway, true random sequences can appear non-random at small N. A more serious concern is that the authors are interpreting CFC in random data or in ECoG data with non-linearity introduced (Figure S6) without performing any statistics to justify the interpretation of CFC. Analogously, a t-statistic on random numbers is unlikely to be exactly 0; it is only through evaluation of that t-statistic with respect to a null hypothesis distribution that a t-value of, say, 1.5 can be interpreted.”

Authors:

Interestingly enough, prime-numbers, when one partials out the fact that there is only one even prime number, one prime number that is divisible by three etc, seem to be best described as what are called pseudo-random numbers. (See for example any of Terence Tao’s blog posts or presentations on “primes and pseudorandomness”.) So at least for now, to our knowledge, there seems to be no reason to believe that there is cross-frequency coupling behind any process we might expect to generate prime numbers. ;) But of course this is just an illustration of how hard it is to conclude anything about mechanistic processes by just using a CFC measure. As a side note, one should also not forget that still some care is needed when interpreting such statistics, i.e. recall the numerical information on the change of sign between \pi(x) and li(x) and Skewes’ numbers. ;) But probably none of us is an expert on primes and knows exactly why they give rise to a high CFC index. We reason in the article that even in the case of the CFC measured from the brain, this “why” still continues to have a multitude of possible answers.

Now, more seriously, in the ECoG or random data we use the exactly same procedure as is usual in the CFC analysis. Indeed, we used the code provided by Tort for the modulation index, and the code provided by Canolty et al. from their Science paper and hence, their respective surrogate analysis (and in our text it was indicated that the results were significant). In addition, for the non-linearity case we even provided a simple example (supplementary material) where we derived analytically that quadratic non-linearities lead to CFC. <br /> ____

MXC: “Another issue identified by the authors is the potential confound of co-occurring but independent low-frequency phase and high-frequency power dynamics. This is a potential confound (discussed in Cohen, 2014, Analyzing Neural Time Series Data; figure 30.7) but is fairly easy to identify and address (including: avoiding interpreting CFC from immediate post-stimulus periods, removing the phase-locked time-domain signal before computing CFC, and inspecting whether the time-course of CFC differs from the time-course of phase clustering). Perhaps the authors have additional suggestions?”

Authors:

As we note in our manuscript “if a brain area under a recording electrode receives time-varying input from any other brain area, this input might generate similar dependencies across frequency components (Figure 4A). The problem is that usually one has no control over the timing of the internal input to the examined brain area (Figure 4B). Thus, phase-amplitude coupling measured anywhere in the brain can be potentially explained by common influence on the phase and amplitude, without the phase of a low frequency oscillation modulating the power of high frequency activity.” The improvements mentioned in your commentary do not help to identify and address the problems with INTERNAL input, where we have no idea about the onset time (see Figure 4). <br /> ____

MXC: “Later, they write (pages 9-10 and figure 4) "If a brain area under a recording electrode receives time-varying input from any other brain area, this input might generate similar dependencies across frequency components." This does not seem to be a confound, but rather, a description of CFC: low-frequency oscillations from a distal brain region modulate local activity, as manifest in higher frequency oscillations. Perhaps if the authors would identify a mechanism/consequence of CFC for neural activity it would be easier to understand whether/how this is a confound.”

Authors:

There is a misunderstanding here. We would not NOT agree with the interpretation that “low-frequency oscillations from a distal brain region modulate local activity, as manifest in higher frequency oscillations”. Instead we clearly write in our manuscript that “non-stationary input to a given area simultaneously affects the phase of a low frequency component and increases high-frequency activity (common drive to frequency components of the same signal).” This means that the low frequency phase is modulated and the high frequency component is influenced by the same common drive to the area. As we conclude: “In this case, high-frequency amplitude increases occur preferentially for certain phases of slow oscillations even without any need of interaction between the two rhythms.” (See also Figure 3). Again, we would agree on this point if CFC would stand for Cross-Frequency Correlation rather than Cross-Frequency Coupling, as the latter indicates interaction or causality.

____

MXC: “On page 6, the authors write “The main conclusion is – not that surprisingly - that a clear peak in the power spectrum of the low frequency component is a prerequisite for a meaningful interpretation of any CFC pattern.” The justification does not follow. If one is interested in *phase* dynamics, why does there need to be a peak in *power*? Assuming that phase reflects the timing of neural populations while power reflects their spatial coherence at the LFP level, why is spatial coherence considered a prerequisite for investigating timing? In real EEG data, power and phase dynamics are often independent of each other.”

Authors:

It is here not at all necessary to think about which neural processes the phase or power variable could reflect. The reason for why a peak in the power spectrum is a prerequisite for a meaningful interpretation of phase (as an index that is a parameter of an oscillation) is well known in the physics/electrical engineering community and simply comes from the signal processing perspective: phase can be meaningfully defined only for narrow-band (and slowly frequency-varying) oscillatory signals for which the phase grows monotonically (please see page 35 of the manuscript: Supplementary discussion - conditions for a meaningful phase). Note that although narrow-band filtering a signal enhances smooth dynamics of its phase, it does not improve its physical interpretability.

____

MCX: “A related discussion is potential differences in power across conditions. CFC methods generally measure the relationship between power and phase, not the magnitude of power. Appropriate permutation-based statistical corrections will account for differences in the magnitude of power (Cohen, 2014, chapter 30).”

Authors:

Yes, we agree that this is something that one indeed can control for and just point out that this is not always done in the literature. (See literature review).<br /> ____

MCX: “The potential confound of low power for estimating phase (Muthukumaraswamy & Singh, 2011) applies only for very low SNR; in real EEG data, power and phase dynamics are often easily disambiguated and unrelated to each other.”

Authors:

The level of SNR for EEG is dependent on the frequency band considered and stimulation elicited by the experimental protocol. Here the main point is that many studies compare CFC between conditions that elicit very different power in a given band (e.g. peak vs no peak). Thus there is straight away a bias in the reliability of the phase estimation and therefore of the phase-amplitude coupling. How big this effect is should be assessed for each dataset. In addition, the amplitude and phase defined by the analytical signal approach (using Hilbert transforms) are not fully independent and even a nominal change in one of them induces a perturbation in the other (Supplementary Figure 7B).

____

MXC: “Table 1 should include citations of the papers surveyed; otherwise independent verification is not possible.”

Authors:

we feel that the description preceding the literature review enables anyone to find the respective papers (as the years, journals and search criteria have been mentioned, a simple PUBMED search can provide the explicit list of papers considered). The magic paper is the one we added manually, which we indeed can identify here - Saalmann et al., 2012 in Science. The literature review covers papers up to January 2014 (included).

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giag031), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 1:

The authors assembled the genomes of three Cobitis species native to Eurasia in an attempt to investigate the effects of structural variants on hybrid meiotic failure. This is certainly an interesting topic given the advances in our abilities to study hybridization that have been enabled by modern genomic sequencing methods, and the evolutionary consequences of asexually-reproducing species that result from rare instances of these hybrid events.

Major comments: The introduction of the manuscript is well-written and focused on the topic at hand. Language was mostly clear throughout the manuscript. However, the paper overall is very lengthy and would benefit from extensive revision. Personally, I think the assembly and annotation of the three genomes is worthy of being a paper (genome report) on its own. Extraction of this material into a separate manuscript would allow the authors to hone the remainder of the paper into a much more concise and focused manuscript. Some aspects of the methods section related to genome assembly and annotation could be clarified and/or bolstered. Presentation of methods is mostly clear, but the description of genome annotation methods is a bit tough to follow. This procedure included many complicated steps and may benefit from a flow chart, even if included only as a supplemental figure.

Several important quality control steps pertaining to genome assembly and DNA/RNA sequence processing were not mentioned. Authors do not report methods used for quality filtering or trimming. They do not report any process for removal of sequencing adapters. Additionally, they do not report screening of the genome assemblies for contamination from other species. These are critical steps in producing high-quality genome assemblies that need to be addressed.

Presentation of statistics describing genome assembly quality, contiguity, and completeness could be improved. Authors might want to take some inspiration from statistics required for reporting in genome reports published by other journals, such as G3 or Genome Biology and Evolution. Sequencing depth is not reported in any context for the initial assemblies. Only log-transformed values are available in a single figure. Throughout the manuscript, authors conflate sequencing coverage (the proportion of a genome or genomic region that has been sequenced) with sequencing depth (the number of times a base or genomic region has been sequenced).

For the sex-linked primers designed by the authors - I would recommend development of an internal positive control that would be expected to amplify in both sexes and be easily distinguishable from the sex-linked locus by size or fluorescent label. This allows the users to distinguish between failed PCRs and identification of the homogametic sex. This is especially important because the fish selected for marker development were collected from a relatively small portion of the species' distributions (Figure 1) so there could be population-specific differences that affect reliability of these markers for identifying sex. This is a problem I regularly encounter in my own work for wide-ranging species.

I was also surprised that the authors did not conduct a GWAS analysis. That seems to be a fairly typical analysis included in studies of this type to elucidate sex-linked SNPs. It would add to an already extensive manuscript; however, this could add an additional argument for splitting this manuscript in two. It would provide more space to include it in a more focused manuscript.

The results section contains many statements that would be more appropriate in the Methods section, or could be deleted entirely because they are redundant with statements already present in the Methods section. Additionally, there are some sentences that are more appropriate for inclusion in the Discussion section because they are interpretive. I have included examples under the 'Minor comments' section of this review. Some of the material presented as results in the Supplementary tables is presented in a confusing manner, and appears to contain errors (see examples in 'Minor comments' section below).

The first several paragraphs of the Discussion section either repeat material already covered in the Results section, or go on tangents that are not directly related to the main purpose of the paper. However, some of it could be more appropriate to include in a genome report if the authors split the manuscript in two.

Given the above issues, I find that the paper needs extensive editing and possibly more analytical work (if some of the methodological deficiencies were overlooked in the analysis phase as well as the writing phase of this project). It is unlikely this work could be accomplished in the normal window for a revision. Therefore, I regrettably suggest rejection of the manuscript.

Finally, I have no meaningful experience with FISH probes or chromosomal painting so unfortunately, I can't provide much comment on those portions of the paper.

Minor comments: Line 291: please provide specific version number for Hisat2 Line 319: version numbers for D-Genies and SyRI missing Line 331: version number for NGenomeSyn missing Line 439-440: Authors provide N50 values, but the paper would benefit from providing some additional metrics, such as N90 and L90, to help readers gauge the contiguity of these genomes. Line 442 - 443: I'm having a hard time understanding how the authors are calling these 'chromosome-level' assemblies when nearly a third (>30%) of the genome of two species (C. tanaitica and C. elongatoides) could not be assembled into chromosomal scaffolds. Line 457 - 458: Either the term 'topologically associated domains' is missing, or the authors need to remove the parentheses from around TADs if it was defined earlier in the manuscript. Line 470: change 'less' to 'fewer' Line 483 - 486: The statements that observed patterns of repeat families 'suggest' something are interpretive and should be moved to the discussion. Line 499 - 500: This sentence repeats content of the methods section. I suggest deleting it. Line 540 - 564: If I am understanding correctly, the discussion of 'coverage' here would be more accurately described as 'depth' since the authors seem to be talking about average sequencing depth in different areas of the genome. Furthermore, authors never provide untransformed measures of sequencing depth in any context (the initial genome assemblies, pool-seq data, re-sequenced individuals, etc.). Therefore, it is difficult to determine if the differences being discussed here are derived from data with enough statistical power to measure differences in sequencing depth between male and female fish. Lines 614 - 619: This could be explored with GWAS Lines 635 - 641: Much of this paragraph is a description of methods and belongs in the Methods section. Lines 664 - 667: Much of this is interpretive - more appropriate for the discussion. Lines 700 - 711: This paragraph has little or no relevance to the main topic of this paper (hybrid meiotic failure). Line 745: remove "loci's" Line 813 - 815: PMER was already defined earlier in the paper. Line 854: I suggest removal of "the first of their kind in an asexually reproducing vertebrate," because such statements rarely age well, and the concept behind the paper is interesting enough to stand on its own without pointing out the novelty of it being the 'first' time it was detected. References section: Capitalization of article titles varies from one reference to the next. Scientific names are sometimes italicized; other times they are not. Table 2: 'L50' and 'Number of Chromosomes' are always going to be integers. Why are there two significant digits to the right of the decimal point? Supplementary Figure S2: 'Cobitis' should be italicized. Supplementary Table S7: This table presents pre- and post-HiC values in a confusing manner that is nonsensical and probably erroneous. For example, the N50 values seem problematic. How do you have a 154 Kbp pre-HiC N50 contig value for C. elongatoides, but a 154 Mbp post-HiC N50 contig value for the same species? This is longer than the longest reported chromosome for any species (C. taenia) in Supplementary Table S8 (99 Mbp). Supplementary Table S10: I don't know what the percentages in line 33 refer to?

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data. Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(i) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(ii) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping, across the whole genome, to ensure full understanding and clarity.

In the revised manuscript, the authors have improved the presentation and analysis of their data, expanding the description of SNS-seq mapping across the genome, and more clearly assessing to what extent there is correlation between SNS-seq signal and previous mapping approaches to predict origins (by MFA-seq and ChiP-chip of ORC1/CDC6). With regard the correlation between SNS-seq and ORC/1CDC6 ChIP-chip, it should be noted that two datasets were generated in distinct strains of T. brucei (Lister 427 and TREU927, respectively), and it is unclear if the latter dataset can be accurately mapped to the strain used here. Notwithstanding this concern, these improvements clarify a number of aspects of the SNS-seq mapping: (1) the signal is more prevalent in the transcribed core of the genome than in the largely transcriptionally silent subtelomeres; and (2) whereas previous work revealed strong correlation between ORC1/CDC6 localisation and MFA-seq peaks at the ends of multigene transcription units, neither of these data show significant overlap with SNS-seq signal, which is not seen at transcription start or stop sites ('SSRs'; supplementary Fig.8D) and shows marked depletion at predicted ORC1/CDC6 sites (supplementary Fig.8C). To the authors' credit, they acknowledge this lack of correlation in the discussion.

The authors have not provided any new data to substantiate their assertion that SNS-seq accurately detects origins in T. brucei, and therefore the work rests on a single experimental approach, without validation. As a result, the suggestion of abundant, previously undetected origins in the intergenic regions of multigene transcription remains a prediction. One key untested limitation of the work lies in the observation that the very large majority of SNS-seq signal overlaps with previously RNA-DNA hybrids; without an experimental test, the suggestion that the authors have 'disclosed for the first time a strong link between RNANA hybrid formation and DNA replication initiation' remains conjecture.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of origins of replications. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Between the initial submission and this revision, the raised major concerns have not been resolved, and no additional validation has been provided.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript is concluded with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) There are substantial discrepancies between the origins identified here and those reported in previous studies. Given that the other studies precede this manuscript, it is the authors' duty to investigate these differences. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

We agree that orthogonally validation of origins detected by stranded SNS-seq is necessary and we are working on it.

(2) I am concerned that up to 96% percent of all SNS-seq peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Upon request, the authors have performed a control, where randomly placed peaks were run through the same filtering process. Only approximately twice as many experimental peaks passed filtering compared to random peaks. While the authors emphasize reproducibility between replicates, technical artifacts from the protocol would also be reproducible. Moreover, in other SNS-seq studies, for example, Pratto et al. Cell 2021, Fig. 1B, + and − strand peaks always appear closely paired. This pattern contrasts strongly with Fig. 2A in this manuscript.

The size and overlap of peaks depend on the length of the SNS. In our study, the width of the peaks corresponds to the size of the short nascent strands (0.5–2.5 kb) chosen as the starting material, whereas the width of the peaks in Pratto et al., Cell, 2021 are much larger (few kb). This could be due to the longer SNS used in the Pratto et al. study. Consequently, the overlap of the longer SNS is more pronounced since the SNS fibres elongate in both directions: at the 3′ end by DNA polymerase and at the 5′ end by ligation of Okazaki fragments. Additionally, the genomic regions displayed in our Figure 2A and in Pratto et al, Figure 1B are presented at substantially different resolutions, with a roughly ten‑fold difference in scale.

Further, I have some minor concerns that do not affect the main conclusions of the manuscript:

- Fig 2C: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions. This data would be better presented with all regions stretched to the same size. This has not been addressed in the revision.

As the reviewer suggested, we have produced scaled plots of the stranded SNS-seq origins over genic and intergenic regions (see Figure 3, which is attached along with the Reviewer #2 (Recommendations for the authors)). However, we would prefer to keep the unscaled versions in the manuscript and add a note in the text as part of the Version of Record, explaining that the origins are evenly distributed throughout intergenic regions rather than being centred within them.

- Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length. This has not been addressed in the revision.

This observation is correct. By applying filtering and setting the maximum distance between the positive and negative peaks, we are most likely affecting the average length by excluding potentially wider origins.

We'll modify the text as part of the Version of Record.

Are claims well substantiated?:

The identification of origins via SNS-seq appears to be incompletely supported to me.<br /> All downstream analyses depend on the reliability of origin identification.<br /> Impact:

This study has the potential to be valuable for two fields: In research focused on T. brucei as a disease agent, where essential processes that function differently than in mammals are excellent drug targets. Further, this study would impact basic research analyzing DNA replication over the evolutionary tree, where T. brucei can be used as an early-divergent eucaryotic model organism.

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

eLife Assessment

The authors use sequencing of nascent DNA (DNA linked to an RNA primer, "SNS-Seq") to localise DNA replication origins in Trypanosoma brucei, so this work will be of interest to those studying either Kinetoplastids or DNA replication. The paper presents the SNS-seq results for only part of the genome, and there are significant discrepancies between the SNS-Seq results and those from other, previously-published results obtained using other origin mapping methods. The reasons for the differences are unknown and from the data available, it is not possible to assess which origin-mapping method is most suitable for origin mapping in T. brucei. Thus at present, the evidence that origins are distributed as the authors claim - and not where previously mapped - is inadequate.

We would like to clarify a few points regarding our study. Our primary objective was to characterise the topology and genome-wide distribution of short nascent-strand (SNS) enrichments. The stranded SNS-seq approach provides the high strand-specific resolution required to analyse origins. The observation that SNS-seq peaks (potential origins) are most frequently found in intergenic regions is not an artefact of analysing only part of the genome; rather, it is a result of analysing the entire genome.

We agree that orthogonal validation is necessary. However, neither MFA-seq nor TbORC1/CDC6 ChIP-on-chip has yet been experimentally validated as definitive markers of origin activity in T. brucei, nor do they validate each other.

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data.

Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(1) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(2) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping across the whole genome to ensure full understanding and clarity.

Regarding comparisons with previous work:

- Two other attempts to identify origins in T. brucei - ORC1/CDC6 binding sites (ChIP-on-chip, PMID: 22840408) and MFA-seq (PMID: 22840408, 27228154) - were both produced by the McCulloch group. These methods do not validate each other; in fact, MFA-seq origins overlap with only 4.4% of the 953 ORC1/CDC6 sites (PMID: 29491738). Therefore, low overlap between SNS-seq peaks and ORC1/CDC6 sites cannot disqualify our findings. Similar low overlaps are observed in other parasites (PMID: 38441981, PMID: 38038269, PMID: 36808528) and in human cells (PMID: 38567819).

- We also would like to emphasize that the ORC1/CDC6 dataset originally published (PMID: 22840408) is no longer available; only a re-analysis by TritrypDB exists, which differs significantly from the published version (personal communication from Richard McCulloch). While the McCulloch group reported a predominant localization of ORC1/CDC6 sites within SSRs at transcription start and termination regions, our re-analysis indicates that only 10.3% of TbORC1/CDC6-12Myc sites overlapped with 41.8% of SSRs.

- MFA-seq does not map individual origins, it rather detects replicated genomic regions by comparing DNA copy number between S- and G1-phases of the cell cycle (PMID: 36640769; PMID: 37469113; PMID: 36455525). The broad replicated regions (0.1–0.5 Mbp) identified by MFA-seq in T. brucei are likely to contain multiple origins, rather than just one. In that sense we disagree with the McCulloch's group who claimed that there is a single origin per broad peak. Our analysis shows that up to 50% of the origins detected by stranded SNS-seq locate within broad MFA-seq regions. The methodology used by McCulloch’s group to infer single origins from MFA-seq regions has not been published or made available, as well as the precise position of these regions, making direct comparison difficult.

Finally, the genomic features we describe—poly(dA/dT) stretches, G4 structures and nucleosome occupancy patterns—are consistent with origin topology described in other organisms.

On the concern that SNS-seq may map RNA-DNA hybrids rather than replication origins: Isolation and sequencing of short nascent strands (SNS) is a well-established and widely used technique for high-resolution origin mapping. This technique has been employed for decades in various laboratories, with numerous publications documenting its use. We followed the published protocol for SNS isolation (Cayrou et al., Methods, 2012, PMID: 22796403). RNA-DNA hybrids cannot persist through the multiple denaturation steps in our workflow, as they melt at 95°C (Roberts and Crothers, Science, 1992; PMID: 1279808). Even in the unlikely event that some hybrids remained, they would not be incorporated into libraries prepared using a single-stranded DNA protocol and therefore would not be sequenced (see Figure 1B and Methods).

Furthermore, our analysis shows that only a small proportion (1.7%) of previously reported RNA-DNA hybrids overlap with SNS-seq origins. It is important to note that RNA-primed nascent strands naturally form RNA-DNA hybrids during replication initiation, meaning the enrichment of RNA-DNA hybrids near origins is both expected and biologically relevant.

On the claim that our analysis focuses narrowly on inter-CDS regions and ignores other genomic compartments: this is incorrect. We mapped and analyzed stranded SNS-seq data across the entire genome of T. brucei 427 wild-type strain (Müller et al., Nature, 2018; PMID: 30333624), including both core and subtelomeric regions. Our findings indicate that most origins are located in intergenic regions, but all analyses were performed using the full set of detected origins, regardless of location.

We did not ignore transcription start and stop sites (TSS/TTS). The manuscript already includes origin distribution across genomic compartments as defined by TriTrypDB (Fig. 2C) and addresses overlap with TSS, TTS and HT in the section “Spatial coordination between the activity of the origin and transcription”. While this overlap is minimal, we have included metaplots in the revised manuscript for clarity.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of the origins of replication. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript concludes with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

We sincerely thank you for this positive feedback.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

Thank you very much for this remark.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Thank you for appreciating our discussion.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) I do not understand why SNS-seq would create peaks. Replication should originate in one locus, then move outward in both directions until the replication fork moving outward from another origin is encountered. Hence, in an asynchronous population average measurement, I would expect SNS data to be broad regions of + and -, which, taken together, cover the whole genome. Why are there so many regions not covered at all by reads, and why are there such narrow peaks?

Thank you for asking these questions. As you correctly point out, replication forks progress in both directions from their origins and ultimately converge at termination sites. However, the SNS-seq method specifically isolates short nascent strands (SNSs) of 0.5–2.5 kb using a sucrose gradient. These short fragments are generated immediately after origin firing and mark the sites of replication initiation, rather than the entire replicated regions. Consequently: (i) SNS-seq does not capture long replication forks or termination regions, only the immediate vicinity of origins. (ii) The narrow peaks indicate the size of selected SNSs (0.5–2.5 kb) and the fact that many cells initiate replication at the same genomic sites, leading to localized enrichment. (iii) Regions without coverage refer to genomic areas that do not serve as efficient origins in the analyzed cell population. Thus, SNS-seq is designed to map origin positions, but not the entire replicated regions.

(2) I am concerned that up to 96% percent of all peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Specifically, if the authors placed the same number of peaks as was measured randomly in intergenic regions, would 4% of these peaks pass the filtering process by chance?

Maintaining the strandness of the sequenced DNA fibres enabled us to filter the peaks, thereby increasing the probability that the filtered peak pairs corresponded to origins. Two SNS peaks must be oriented in a way that reflects the topology of the SNS strands within an active origin: the upstream peak must be on the minus strand and followed by the downstream peak on the plus strand.

As suggested by the reviewer, we tested whether randomly placed plus and minus peaks could reproduce the number of filter-passing peaks using the same bioinformatics workflow. Only 1–6% of random peaks passed the filters, compared with 4–12% in our experimental data, resulting in about 50% fewer selected regions (origins). Moreover, the “origins” from random peaks showed 0% reproducibility across replicates, whereas the experimental data showed 7–64% reproducibility. These results indicate that the retainee peaks are highly unlikely to arise by chance and support the specificity of our approach. Thank you for this suggestion.

(3) There are 3 previous studies that map origins of replication in T. brucei. Devlin et al. 2016, Tiengwe et al. 2012, and Krasiļņikova et al. 2025 (https://doi.org/10.1038/s41467-025-56087-3), all with a different technique: MFA-seq. All three previous studies mostly agree on the locations and number of origins. The authors compared their results to the first two, but not the last study; they found that their results are vastly different from the previous studies (see Supplementary Figure 8A). In their discussion, the authors defend this discrepancy mostly by stating that the discrepancy between these methods has been observed in other organisms. I believe that, given the situation that the other studies precede this manuscript, it is the authors' duty to investigate the differences more than by merely pointing to other organisms. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

The MFA-seq data for T. brucei were published in two studies by McCulloch’s group: Tiengwe et al. (2012) using TREU927 PCF cells, and Devlin et al. (2016) using PCF and BSF Lister427 cells. In Krasilnikova et al. (2025), previously published MFA-seq data from Devlin et al. were remapped to a new genome assembly without generating new MFA-seq data, which explains why we did not include that comparison.

Clarifying the differences between MFA-seq and our stranded SNS-seq data is essential. MFA-seq and SNS-seq interrogate different aspects of replication. SNS-seq is a widely used, high-resolution method for mapping individual replication origins, whereas MFA-seq detects replicated regions by comparing DNA copy number between S and G1 phases. MFA-seq identified broad replicated regions (0.1–0.5 Mb) that were interpreted by McCulloch’s group as containing a single origin. We disagree with this interpretation and consider that there are multiple origins in each broad peaks; theoretical considerations of replication timing indicate that far more origins are required for complete genome duplication during the short S-phase. Once this assumption is reconsidered, MFA-seq and SNS-seq results become complementary: MFA-seq identifies replicated regions, while SNS-seq pinpoints individual origins within those regions. Our analysis revealed that up to 50% of the origins detected by stranded SNS-seq were located within the broad MFA peaks. This pattern—broad MFA-seq regions containing multiple initiation sites—has also recently been found in Leishmania by McCulloch’s team using nanopore sequencing (PMID: 26481451). Nanopore sequencing showed numerous initiation sites within MFA-seq regions and additional numerous sites outside these regions in asynchronous cells, consistent with what we observed using stranded SNS-seq in T. brucei. We will expand our discussion and conclude that the discrepancy arises from methodological differences and interpretation. The two approaches provide complementary insights into replication dynamics, rather than ‘vastly different’ results.

We recognize the importance of validating our results in future using an alternative mapping method and functional assays. However, it is important to emphasize that stranded SNS-seq is an origin mapping technique with a very high level of resolution. This technique can detect regions between two divergent SNS peaks, which should represent regions of DNA replication initiation. At present, no alternative technique has been developed that can match this level of resolution.

(4) Some patterns that were identified to be associated with origins of replication, such as G-quadruplexes and nucleosomes phasing, are known to be biases of SNS-seq (see Foulk et al. Characterizing and controlling intrinsic biases of lambda exonuclease in nascent strand sequencing reveals phasing between nucleosomes and G-quadruplex motifs around a subset of human replication origins. Genome Res. 2015;25(5):725-735. doi:10.1101/gr.183848.114).

It is important to note that the conditions used in our study differ significantly from those applied in the Foulk et al. Genome Res. 2015. We used SNS isolation and enzymatic treatments as described in previous reports (Cayrou, C. et al. Genome Res, 2015 and Cayrou, C et al. Methods, 2012). Here, we enriched the SNS by size on a sucrose gradient and then treated this SNS-enriched fraction with high amounts of repeated λ-exonuclease treatments (100u for 16h at 37oC - see Methods). In contrast, Foulk et al. used sonicated total genomic DNA for origin mapping, without enrichment of SNS on a sucrose gradient as we did, and then they performed a λ-exonuclease treatment. A previous study (Cayrou, C. et al. Genome Res, 2015, Figure S2, which can be found at https://genome.cshlp.org/content/25/12/1873/suppl/DC1) has shown that complete digestion of G4-rich DNA sequences is achieved under the conditions we used.

Furthermore, the SNS depleted control (without RNA) was included in our experimental approach. This control represents all molecules that are difficult to digest with lambda exonuclease, including G4 structures. Peak calling was performed against this background control, with the aim of removing false positive peaks resulting from undigested DNA structures. We explained better this step in the revised manuscript.

The key benefit of our study is that the orientation of the enrichments (peaks) remains consistent throughout the sequencing process. We identified an enrichment of two divergent strands synthesised on complementary strands containing G4s. These two divergent strands themselves do not, however, contain G4s (see Fig. 8 for the model). Therefore, the enriched molecules detected in our study do not contain G4s. They are complementary to the strands enriched with G4s. This means that the observed enrichment of

G4s cannot be an artefact of the enzymatic treatments used in this study. We added this part in the discussion of the revised manuscript.

We also performed an additional control which is not mentioned in the manuscript. In parallel with replicating cells, we isolated the DNA from the stationary phase of growth, which primarily contains non-replicating cells. Following the three λ-exonuclease treatments, there was insufficient DNA remaining from the stationary phase cells to prepare the libraries for sequencing. This control strongly indicated that there was little to no contaminating DNA present with the SNS molecules after λ-exonuclease enrichment.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Four broad issues need to be addressed.

(1) The authors have attempted to test the overlap between ORC1/CDC6 (an ORC subunit) binding in the genome and SNS-seq. If there were an overlap, this would provide evidence that the SNS-seq signals represent origins. However, the analysis provided is inadequate: merely a statement that "we obtained an overlap of 4.2% between origins and ORC1/CDC6 binding sites within a window of {plus minus}2 kb and 6.2% in the window of {plus minus}3 kb". Nowhere are these data shown or properly discussed:

a) The authors need to provide a diagram showing where in the genome the very small amount of overlapping SNS-seq and ORC1/CDC6 binding occurs, and to clearly show and state how many of the intergenic SNS-seq peaks are sites of ORC1/CDC6 binding. In the absence of such analysis, a key question is unanswered: is there any evidence of ORC1/CDC6 (or ORC more broadly) binding at the SNS-seq signals within the polycistronic transcription units?

In the original version of the manuscript, these data were already presented as percentages in the text and as a metaplot (Supplementary Fig. 8C).

We based our analysis on the set of 350 TbORC1/CDC6 binding sites available on TriTrypDB at the time of analysis. This dataset was a filtered subset of the originally reported TbORC1/CDC6 ChIP‑on‑chip peaks (personal communication, TriTrypDB). Since then, the unfiltered dataset has been made available. We therefore re‑analyzed the overlap using this dataset, to which we applied a filtering that yielded 990 binding sites closely matching the 953 sites reported by the McCulloch group. We need to stress here that the original 953 sites reported by the McCulloch group (Tiengwe et al., 2012 PMID: 22840408), is not available anymore and that the authors:

- do not provide genomic coordinates for the 953 binding sites and

- do not release any scripts or methodology that would allow independent reproduction of the 953 sites.

A similar remark also applies to the MFA-seq data (see below).

To address the reviewer’s request, we have now:

(1) Recalculated the overlap using the updated TbORC1/CDC6 dataset (990 binding sites) from TriTrypDB.

(2) Added the absolute number of overlapping SNS‑seq origins and TbORC1/CDC6 binding sites in the Results section for clarity.

(3) Included the TbORC1/CDC6 binding sites in the chromosomal overview (newly added to Supplementary Fig. 8A), so that their genomic localization relative to SNS‑seq peaks is visually accessible.

(4) Revised the metaplots of TbORC1/CDC6 distribution around SNS‑seq origins using the updated dataset (Supplementary Fig. 8C).

With these improvements, we now find that:

- Within ±2 kb, 12.9% (253) of SNS‑seq origins overlap with 25.6% of TbORC1/CDC6 binding sites.

- Within ±3 kb, 18.8% (370) of SNS‑seq origins overlap with 37.4% of TbORC1/CDC6 binding sites.

The updated metaplot shows a clear depletion of TbORC1/CDC6 signal at the origin center, with modest enrichment ~5 kb upstream and downstream. The underlying reason for this pattern remains unknown, and we agree that additional studies will be needed to understand it.

b) Equally, the authors need to explain what they conclude from this analysis. They make a comparison with T. cruzi ORC1/CDC6 and SNS-seq overlap, which does not illuminate what the data tell us. For instance, if there is no or minimal overlap between ORC1/CDC6 binding and SNS-seq peaks within the polycistronic transcription units, do they conclude that the major SNS-seq signal they detail is evidence for ORC-independent DNA replication? If there is no overlap, what further evidence can they provide that these signals truly are origins?

First, we would like to clarify that, to date, there is no evidence supporting ORC‑independent DNA replication in T. brucei, and—importantly—no published data demonstrating that TbORC1/CDC6 is universally required for DNA replication initiation. Because of this, we consider that it would be inappropriate to conclude that regions lacking detectable TbORC1/CDC6 signal undergo ORC‑independent initiation. We would prefer not to speculate in the absence of supporting evidence and would gratefully consider any reference the reviewer wishes to provide on this subject.

Second, the low overlap between TbORC1/CDC6 binding sites and SNS‑seq origins does not, in our view, invalidate our mapping of replication initiation sites. Multiple factors contribute to this:

(1) Low overlap between ORC1/CDC6 and origin‑mapping techniques has been repeatedly reported across kinetoplastids. For instance, in T. cruzi, 88.2% of origins detected by DNAscent nanopore sequencing showed no overlap with TcORC1/CDC6–Ty1 ChIP signal within ±3 kb, and only 11.7% co‑localized. This is strikingly similar to our observations in T. brucei. Thus, our data are consistent with the broader pattern in trypanosomatids rather than an exception.

(2) The origin topology detected by stranded SNS‑seq is supported by several genomic characteristic found frequently in other eukaryotes, including:

- A highly specific and polarized poly(dA)/poly(dT) sequence environment.

- Strand‑specific G4 structures positioned around origin centers.

- A conserved nucleosome‑depleted region flanked by well‑positioned nucleosomes.

These features are absent from shuffled controls, appear at high significance, and recapitulate hallmark signatures of replication origins in other eukaryotes.

Together, these findings give us confidence that the SNS‑seq peaks represent genuine origins - despite the incomplete overlap with TbORC1/CDC6 binding.

Third, we fully agree with the reviewer that a definitive conclusion would require an additional, independent validation method.

Given the lack of complete ORC subunit datasets and the unusual biology of trypanosomatid replication complexes, we believe that the cautious interpretation above is the most appropriate.

c) The authors state (Discussion): "Validation of origins is generally a difficult task, particularly in trypanosomatids, where proteins involved in the initiation of DNA replication are difficult to determine. Few proteins have been described as potential ORC subunits (reviewed in 61), and none of them have been shown to be a specific marker that indicates the origins." There are two problems with the statement. First, most of the subunits of ORC have now been described in T. brucei; the authors should make this clear. Second, mapping of ORC1/CDC6 localisation, contrary to what the authors state here, shows precise correlation with the peaks of every MFA-seq signal described (see Tiengwe et al, Cell Reports, 2012); thus, ORC1/CDC6 binding provides evidence that MFA-seq is detecting origins, something that cannot be said for SNS-seq. The authors need to correct this misleading paragraph.

As suggested, we have removed the paragraph from the Discussion to avoid confusion. However, we disagree with the reviewer's assessment and clarify below our position regarding the issues raised.

First, we agree that five candidate ORC subunits have now been identified in T. brucei. Our intention was not to suggest the contrary, but rather to emphasize that, although candidate ORC components have been described, direct functional evidence for their roles in replication initiation is still limited. For this reason, we were cautious in referring to any ORC component as a definitive marker of replication origins.

Second, regarding the reviewer’s statement that TbORC1/CDC6 binding “shows precise correlation with the peaks of every MFA‑seq signal”, we respectfully disagree based on several observations:

(1) MFA‑seq does not identify individual origin centers, but rather broad replicated regions that often span hundreds of kilobases. By design, this method cannot define the number or position of discrete origins within each peak. For that reason, MFA-seq regions do not have the resolution required to validate TbORC1/CDC6 binding sites as individual origins.

(2) In the published datasets (Tiengwe et al., Devlin et al.), no metaplots or locus‑wide quantification of the overlap between MFA‑seq peaks and TbORC1/CDC6 binding were provided. The coordinates or the approach used to define the discrete regions that they define as the originsin the MFA‑seq broad peaks have never been described or made available, making it difficult to evaluate the claimed correspondence.

(3) Notably, McCulloch’s group later reported that only 4.4% of the 953 TbORC1/CDC6 sites overlapped with their 42 MFA‑seq “origins”, underscoring that the degree of correspondence is in fact limited (PMID: 29491738).

(4) Finally, as noted in our response to point (1b), low overlap between ORC1/CDC6 binding sites and origin‑mapping techniques is a consistent observation across kinetoplastids, including T. cruzi, where DNAscent‑mapped origins show only ~12% overlap with TcORC1/CDC6 ChIP signals. This suggests that the limited overlap we observe is not unique to our dataset.

For these reasons, we are not convinced that the TbORC1/CDC6 binding sites have been shown to align precisely with MFA seq peaks, nor that these datasets definitively validate origin mapping in T. brucei. Nevertheless, to avoid over‑interpretation and potential confusion, we have removed the paragraph from the Discussion as requested. We hope this clarifies our position and improves the accuracy and neutrality of the manuscript.

(2) Like for ORC1/CDC6 localisation, the authors' evaluation of the relationship between MFA-seq and SNS-seq mapping is inadequate, and the depth of the analysis and discussion needs to be improved:

a) The authors state: "We found 28-42% stranded SNS-seq origins overlapped with early and 43-55% overlapped with late S-phase MFA-seq replicated regions (Supplementary Figure 8B)." This seems important and provides (limited) validation of both datasets, but cannot be discerned from the supplied figure. Please provide a metaplot of the two datasets centred on the MFA-seq loci, including the SNS-seq peak amplitude.

We would like to emphasize that MFA‑seq is not a method designed to map individual origins, and this fundamentally limits the interpretability of metaplots centered on MFA-seq regions. MFA‑seq identifies broad replication‑enriched domains, typically spanning 100–500 kb, within which multiple origins may fire asynchronously across the cell population.

This concern is reinforced by the original MFA‑seq publications (Tiengwe et al., 2012; Devlin et al., 2016), which:

- do not provide positional data for the 42-47 MFA‑inferred origins,

- do not describe the computational method used to derive individual origin coordinates from the broad peaks, and

- do not release any scripts or methodology that would allow independent reproduction of the claimed origin positions.

Because of this, it is not possible to reconstruct or validate how the 42 MFA‑seq “origin” sites were defined, nor to use those coordinates as anchors for metaplot analyses.

Most importantly, we disagree with the underlying assumption that each MFA‑seq peak corresponds to exactly one origin. This assumption runs counter to the principle of the technique, which identifies regions of higher DNA content in replicating cells than in non-replicating cells; it is also contradicted by our stranded SNS‑seq data and by DNA combing measurements:

- SNS‑seq detects multiple discrete origins within the same genomic regions that produce a single broad MFA‑seq peak.

- DNA combing reveals inter‑origin distances of ~36–422 kb (median ~150 kb) (PMID: 26976742), which is far shorter than the ~400–600 kb replication domains identified by MFA‑seq.

- Furthermore, with only 42 origins detected by MFA-seq, it is not possible to achieve complete genome replication in T. brucei during S-phase. DNA combing has found that the average speed of replication forks in the procyclic forms is 1.9 Kb/min. (PMID: 26976742). Dividing the size of the Trypanosoma brucei brucei TREU927 genome (26.1 Mb) by 42 origins (PMID: 22840408) shows that 621 Kb must be replicated during the S phase. Using the calculated average replication speed of 1.9 Kb/min, we can estimate that the replication of 621 Kb would take 327 min (5.45 hours) (621 Kb/1.9 Kb/min = 327 min). However, this exceeds the estimated length of the S-phase in these parasites, which is 2.31 hours (138.6 minutes) (PMID: 32397111, 31811174, 28258618) or less, 1.36 hours (PMID: 2190996, 10574712) in Trypanosoma brucei procyclic forms. Therefore, more than 42 origins are necessary to complete replication during the short S phase.

This makes it unlikely that MFA-seq regions represent single functional origins. For these reasons, a metaplot centered on MFA‑seq “loci” may lead to misinterpretations and would not provide biologically meaningful information.

We hope that the expanded explanation clarifies our interpretation of the relationship between these two complementary, but fundamentally different, methods.

b) The authors state that "Our results showed that the origins are predominantly located in the intergenic regions within the PTUs (Figure 2C)'. This finding cannot be discerned from this figure, which does not show 'strand switch regions' (SSRs; transcription start/stop sites), where MFA-seq predicts all origins to localise. The authors need to acknowledge this difference and must show a comparison of SNS-seq data, including peak amplitude, around all SSRs (whether predicted by MFA-seq to act as origins or not, since all appear to bind ORC1/CDC6).

We have now provided the metaplots showing the overlap between stranded SNS-seq origins and SSRs (see Supplementary Figure 8D). This difference has been acknowledged and discussed in the revised manuscript.

c) Finally, the authors' interpretation that around 30-55% of SNS-seq peaks overlap with MFA-seq 'origins' is highly questionable. MFA-seq peaks are regions of increased DNA content in replicating cells relative to non-replicating cells, and so the entire region under the MFA-seq peak is not necessarily an origin, but is likely to be a more discrete locus (eg, the SSR, where ORC1/CDC6 mainly localises). They should correct the wording and discuss what significance they see in this overlap; for instance, do they think SNS-seq 'clusters' are more pronounced within the MFA-seq peaks and, if so, what might this mean, and why does it not correlate with ORC1/CDC6 localisation?

As the reviewer notes, ‘MFA‑seq peaks are regions of increased DNA content, and so the entire region under the MFA-seq peak is not necessarily an origin but is likely to be a more discrete locus’. This is exactly why MFA‑seq is inappropriate for identifying discrete/individual origins: within these replicated domains, multiple origins can fire, as revealed both by stranded SNS‑seq mapping.

Regarding the overlap between SNS‑seq origins and MFA‑seq peaks, we agree with the reviewer that this overlap should not be interpreted as validating MFA‑seq “origin positions.” Instead, we now describe it more accurately as the proportion of discrete SNS‑seq origins that fall within broader MFA‑seq replication domains. This is expected, because SNS‑seq identifies individual initiation events, whereas MFA‑seq identifies S‑phase replication domains averaged across a population. Our stranded SNS‑seq data do not show enhanced origin accumulation within MFA-seq regions, and we find no correlation with TbORC1/CDC6 positions. This is now discussed.

Regarding SSRs, we do not share the view that they should be considered privileged initiation sites. After remapping the TbORC1/CDC6 ChIP‑on‑chip dataset (see above) to the T. brucei Lister 427–2018 genome (Supplementary Fig. 8A), we observed that TbORC1/CDC6 binding is distributed throughout the chromosomes, not restricted to SSRs. To quantify this, we analyzed the overlap between TbORC1/CDC6 sites and all annotated SSR classes (dSSRs, cSSRs, and head‑to‑tail regions, as defined in Kim et al. 2009). The results show that:

Only 10% of TbORC1/CDC6 binding sites fall within 40% of all SSRs.

At the level of individual SSR types:

- TTS: 3.3% of TTS overlap with 0.3% of TbORC1/CDC6 sites.

- TSS: 67% of TSS overlap with 6.1% of TbORC1/CDC6 sites.

- Head‑to‑tail regions: 54.2% overlap with 3.6% of TbORC1/CDC6 sites.

These analyses demonstrate that most TbORC1/CDC6 sites are not located at SSRs, contradicting the idea that SSRs represent primary or exclusive origin sites.

Author response image 1.

Overlap between TbORC1/CDC6-12Myc binding sites (Tiengwe 2012, Cell Reports) and strand‑switch regions (SSRs). Venn diagram showing the overlap of 990TbORC1/CDC6-12Mycbinding sites (Retrieved from TritrypDB filtered at score 22 to achieve a number of binding sites similar to the one (953 binding sites) published in Tiengwe 2012, Cell Reports) and SSR sites in the genome (Kim 2018, NAR). The intersection shows that 10.3% of Orc1/CDC6 binding sites overlap with 41.8% SSRs. The intersection is subdivided into TSS (orange), TTS in (blue) and HT in (green).

(3) A key objection to the data presentation is the decision to limit SNS-seq mapping to the intergenic regions. In addition to overlooking the SSRs (see above, 2), so-called subtelomeres, which account for nearly 50% of the T. brucei genome and are largely untranscribed, are not shown or discussed at all. Providing this data will improve clarity and also provide a key test of one of the predictions that the authors make: "most origins are localized in actively transcribed regions, which could lead to collisions between DNA replication and the transcription machinery. This spatial coincidence implies that transcription and replication must occur in a highly ordered and cooperative manner in T. brucei."

We do not understand why this reviewer concluded that we took 'the decision to limit the mapping of SNS-seq to intergenic regions'. This is a factual error.

To be clearer,

(2) We now explicitly present the distribution of SNS‑seq origins across core and subtelomeric regions in the revised Figure 2D, making clear that origin mapping was performed genome‑wide.

(2) And that SNS‑seq origins are also present in subtelomeric regions. We have revised the manuscript to avoid any implication that origin firing is restricted only to actively transcribed regions. Our data show that most SNS‑seq origins lie within intergenic regions of PTUs, but a minority are found outside these regions—including subtelomeres and SSRs. The revised text reflects this nuance and highlights that the spatial relationship between transcription and replication is strong but not exclusive.

These additions undoubtedly ensure that the genomic-wide nature of SNS-seq analysis is transparent to the reader and should therefore remove this reviewer's “key objection”.

a) The authors must show SNS-seq mapping to the subtelomeres (in addition to around the SSRs; see comment (2). If no SNS-seq peaks are detected in the subtelomeres, what do the authors conclude about how the genome is duplicated? If SNS-seq peaks are detected in the subtelomeres, do they correspond with the ordered nucleosomes in this part of the genome described by Maree et al (PMID: 28344657); if so, might SNS-seq signal localisation not be directed by transcription but chromatin?

We have now presented the proportion of origins in subtelomeric regions (see Figure 2B).

As illustrated in the metaplots in Author response image 2, the distribution of nucleosomes around the subtelomeric origins is similar to the distribution shown for all origins in the manuscript. We do not see the pattern of nucleosomes as described by Maree et al (PMID: 28344657) over ORC1/CDC6 binding sites in this part of the genome.

Author response image 2.

Metaplots showing the mean nuclesome signal over centred SNS-seq origins in subtelomeric regions. Two replicates from Maree et al 2019 (PMID: 28344657).

We never claimed that transcription directs the localisation of the SNS-seq signal. We did not conduct experiments to address this issue. In contrast, we consider that the organisation of chromatin exerts a significant influence on the selection of active origins.

(4) The major conclusion of the manuscript is that the SNS-seq signal corresponds very precisely to the locations of RNA-DNA hybrids (R-loops). Given all the limitations discussed above, can the authors rule out the possibility that SNS-seq is merely mapping DNA-DNA hybrids and is not, in fact, detecting origins?

a) It is legitimate to speculate about the possibility that the very extensive overlap between SNS-seq and DRIP-seq signals within polycistronic transcription units (between ORFs) might suggest that DRIP-seq data detects nascent strands at replication origins, rather than R-loops at sites of pre-mRNA processing, as previously suggested by Briggs et al (PMID: 30304482). (eg, 'we disclosed for the first time a strong link between R-loop formation and DNA replication initiation'; 'The RNA:DNA hybrids are formed at initiation sites by RNA priming of SNS and Okazaki fragments'). However, the authors should acknowledge that alternative explanations for the localisation and potential functions of inter-CDS R-loops have been suggested,

We do not find extensive overlap between stranded SNS-seq and DRIP-seq signal. We have observed only a minor proportion (1.7%) of the previously reported DRIP-seq signal to overlap with the origins detected by stranded SNS-seq. The RNA-primed SNS must form RNA:DNA hybrids during the initiation of DNA replication, and that an enrichment of these hybrids around the origins is expected. Therefore, we legitimately speculated that this minor proportion of RNA:DNA hybrids enriched around origin centres could be due to the origin activation.

We agree that some of the DRIP-seq signals detected around the origins may be sites of pre-mRNA processing, as previously suggested by Briggs et al. (PMID: 30304482). Since there is no data proving implication of pre-mRNA processing into DNA replication initiation we prefer not to speculate about it.

b) More importantly, the authors should provide experimental evidence that tests such a mechanistic prediction of R-loops and origins: for instance, have they attempted to remove R-loops, eg, by treatment with RNase H, and checked that the SNS-seq signal is unaltered? In the absence of such data, they cannot exclude the possibility that their work has revealed an overlooked problem with SNS-seq (which may not be limited to T. brucei; are matched DRIP-seq and SNS-seq datasets available to correlate these signals in a range of organisms?).

We have not attempted RNase H treatment for a fundamental methodological reason: it seems highly improbable that RNA:DNA hybrids would persist through the multiple denaturation steps inherent to the SNS‑seq enrichment protocol. Published biophysical measurements show that RNA:DNA hybrids melt at ~95 °C (Roberts & Crothers, Science, 1992; PMID: 1279808), which is the temperature repeatedly applied during SNS isolation. Under these conditions, persistent RNA:DNA hybrids cannot remain intact and therefore cannot be responsible for the SNS‑seq peaks detected.

We do not interpret our findings as revealing an “overlooked problem with SNS‑seq.” Instead, we consider that the enrichment of RNA:DNA hybrids around origins observed in DRIP‑seq is biologically meaningful and expected, given that replication initiation involves RNA‑primed nascent strands and that DRIP‑seq detects such structures.

Reviewer #2 (Recommendations for the authors):

I have some minor concerns that do not affect the main conclusions of the manuscript:

(1) Figure 2B: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions.

That is correct. The regions displayed in the heatmaps are genic and intergenic region sorted by size. We did not want to convey with this metaplot that the origins are accumulating at the centres of the intergenic region but mainly that genic regions are mostly devoid of origins and the intergenic regions enriched in origins.

(2) Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length.

This observation is correct. By applying filtering and setting the maximum distance between the positive and negative peaks, we are most likely affecting the average length by excluding origins that are potentially wider. Nevertheless, the violin plot shows that the majority of origins are shorter than 500 nt. In the end, the size of regions detected as the origin is not important. What gives the resolution of stranded-SNS-seq is the ability to identify the centre of the origin between the minus and plus peaks.

(3) Data in the manuscript were sometimes not presented in an easy-to-read manner. In some cases, this was due to benign things, such as missing labels for the mean frequency plots (e.g., Figure 2B, blue and green) or very small fonts for axes (Figure 2B). Sometimes, due to the plot types that were chosen, such as pie-charts (Figure 2C, see https://medium.com/analytics-vidhya/dont-use-pie-charts-in-data-analysis-6c005723e657), stacked bar plots (Figure 6B), or showing cumulative distributions (Figure 5C, and Figure 2D) it makes it difficult to judge the actual distribution.

Wherever possible, the size of the small fonts was increased to the maximum. Missing labels were added to the mean frequency plots. We increased the font size for the axes in the frequency plots.

However, we found cumulative distributions useful. If you have a more specific proposal for replacing cumulative distributions, we would be very grateful to hear it. We also hope that magnifying the figures in TIFF format with a higher resolution will improve visibility.

(4) Figure 2B: This data would be better presented with all regions stretched to the same size (the reason is explained in the public review).

We performed the scaled plots for the stranded SNS-seq origins over the genic and intergenic regions as the reviewer suggested (see Author response image 3), but we prefer to keep the unscaled versions in the manuscript.

Author response image 3.

Distribution of mapped origins in scaled genic and intergenic regions. Scaled heatmaps present the distribution of the mapped origins and shuffled controls within scaled genic and intergenic regions (± 2 kb).

(5) Line 149: "The number of origins in both cells was 148 compared using normalised mapped reads": Supplementary Figure 2D mentions that conditions were subsampled to the same amount. I would mention that explicitly in the main text ("compared using normalized, subsampled mapped reads"), as 'normalizing' would not include 'subsampling' for me. Also, I could not find the methods section that the authors refer to here.

Thanks for the suggestion. We changed the text to make this point clearer. In the methods section, the subsampling process was referred to as 'PCF down-sampling', but we changed now the name to 'Read sub-sampling' to be more consistent in the edited version of the manuscript.

(6) Figure 2C: I struggled to understand what gDNA stands for. Maybe it could be replaced with something like distribution in genome?

Thanks for this suggestion. It is changed to ‘distribution in genomic sequence’.

(7) Figure 5C: I cannot see how a G4 30 kb from an origin could be relevant. This also does not fit the scale of the author's own model at all (Figure 8).

The main goal of Figure 5C was to demonstrate the differences between origins and the nearest G4s compared to the shuffled controls. The graph shows that 50% of the origins have a G4 within 2010 bp, whereas the median for the shuffled control is 4154 bp in the case of non-stabilised G4s. Our model is based on Figure 5D, which illustrates the enrichment of G4s and poly(dA) around the centre of origins.

(8) Figure 6B: could be made supplementary in my opinion. All relevant data is repeated in panel D.

It is true that Figures 6B and 6C contain some repetition. However, we would prefer to keep Figure 6B because it provides a quantification of the six indicated categories, along with the statistical tests. Figure 6B only presents the three categories that changed significantly. Figure 6D shows distribution but does not contain quantified data.

(9) Figure 6D: This plot is repeating a lot, within single figures (Figure 6A, top) but also between figures (e.g., Figure 5D, Figure 4B). I'd prefer it if the initial plots of each figure were expanded a bit (here Figure 6A, top) to include some information from the previous figures. Then all these summary plots could be combined into a single figure at the very end (maybe still as different panels to reduce the number of lines in a single plot). Otherwise, each summary plot repeats the tracks of the previous, which becomes very repetitive.

Our model is based on these summary plots, and we calculated the relative distances between the different elements using them. Two elements were repeated in each plot: the positions of poly(dA) and G4s. These two elements served as reference points to determine the relative positions of the other elements. Following your suggestion would result again in repetitive summary plots at the end, as one combined summary plot would be overloaded with lines and difficult to understand.

(10) Figure 6D & Figure 7C: Both show predicted G4s; however, on the plus strand, one prediction has a two-peaked shape, the other only a single peak. Is this a mistake?

The graphs for the predicted G4s do not have the same shape in the two plots as they were performed in different reference genomes for T. brucei. Figure 6C is in the 427-reference genome as the MNase-seq data set was analysed in this reference genome and we re-did the SNS-seq analysis and the G4 prediction in this reference genome to be able to compare them directly. In Figure 7C we are comparing origins DRIP-seq and predicted G4s, in this case all datasets could be compared in the 427-2018 reference genome.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study investigates the role of vascular mural cells, specifically pericytes and vascular smooth muscle cells (vSMCs), in maintaining blood-brain barrier (BBB) integrity and regulating vascular patterning. Analyzing zebrafish pdgfrb mutants that lack brain pericytes and vSMCs, they show that mural cell deficiency does not impair BBB establishment or maintenance during larval and early juvenile stages. However, mural cells seem to be crucial for preventing vascular aneurysms and hemorrhage in adulthood as focal leakage, basement membrane disruption, and increased caveolae formation are observed in adult zebrafish at aneurysm hotspots. The authors challenge the paradigm that mural cells are essential for BBB regulation in early development while highlighting their importance for long-term vascular stability.

Strengths:

Previous studies have established that the zebrafish BBB shares molecular and morphological homology with e.g. the mammalian BBB and therefore represents a suitable model. By examining mural cell roles across different life stages - from larval to adult zebrafish - the study provides an unprecedented comprehensive developmental analysis of brain vascular development and of how mural cells influence BBB integrity and vascular stability over time. The use of live imaging, whole-brain clearing, and electron microscopy offers high-resolution insights into cerebrovascular patterning, aneurysm development, and structural changes in endothelial cells and basement membranes. By analyzing "leakage hotspots" and their association with structural endothelial defects in adults the presented findings add novel insights into how mural cell loss may lead to vascular instability.

Weaknesses:

The study uses quantitative tracer assays with multiple molecular weight dyes to evaluate blood-brain barrier (BBB) permeability. The study normalizes the intensity of tracer signals (e.g., 10 kDa, 70 kDa dextrans) in the brain parenchyma to the vascular signal of a 2000 kDa dextran tracer (assumed to remain within vessels). Intensity normalization is used to control for variations in tracer injection efficiency or vascular density. This method doesn't directly assess the absolute amount of tracer present in the parenchyma, potentially underestimating leakage severity. As the lack of BBB impairment is a "negative" finding, more rigorous controls or other methods might be needed to corroborate it.

In response to these and comments from other reviewers, we have now performed further carefully controlled analysis to test leakage of tracers using molecular weights ranging from 1 to 2000 kDa. We have performed additional normalisation approaches (new data in Fig. 2a–d) imaging tracer extravasation together with vascular reporters (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916) and used this transgenic reporter for normalisation (as suggested by Reviewer #2). The results of these experiments all supported our initial conclusions (revised Extended Data Fig. 3a–d) further validating the reliability of our method. Furthermore, as suggested by the reviewer analysis of the raw tracer intensity amounts in the parenchyma were also performed with no normalization at all (see Author response image 1). This also supports our conclusion that the BBB is intact in young animals. Finally, we now use our methods to demonstrate that we can detect an immature leaky BBB at 3 dpf and a mature functional BBB at 7 dpf (Fig. 2e-f), a suitable positive control to show that our methods and analyses are reliable.

Author response image 1.

Raw intensity values from the parenchyma confirm findings in Figure 2 and Extended Data Figure 3.a–d, Raw mean fluorescence intensity values of extravasated tracers in the midbrain.(a–b) show unnormalized values corresponding to Extended Data Fig. 3a–d, and (c–d) show unnormalized values corresponding to Fig. 1a–d. Unpaired t-tests for 70 and 10 kDa at 14 dpf in (a–b), for 10 kD at 7 dpf, and for 70 kDa at 14 dpf in (c–d). Mann-Whitney tests for 70 and 10 kDa at 7 dpf in (a–b), for 70 kDa at 7 dpf, and for 10 kDa at 14 dpf (c–d), due to non-normal distribution. These data were all generated in genotype blind assays, display variance in signal that is generated between embryos due to injection differences and show no difference between the genotypes analysed in BBB integrity. Comparison of this to normalised data using 2000 kDa tracer or kdrl expression in endothelial cells (Fig. 2 and Extended Data Fig. 3) confirms that normalisation improves the analysis, effectively controlling for embryo-to-embryo differences in delivery of tracer and imaging.

Reviewer #2 (Public review):

Summary:

The authors generated a zebrafish mutant of the pdgfrb gene. The presented analyses and data confirm previous studies demonstrating that Pdgfrb signaling is necessary for mural cell development in zebrafish. In addition, the data support previously published studies in zebrafish showing that mural cell deficiency leads to hemorrhages later in life. The authors presented quantified data on vessel density and branching, assessed tracer extravasation, and investigated the vasculature of adult mice using electron microscopy.

Strengths:

The strength of this article is that it provides independent confirmation of the important role of Pdgfrb signaling for the development of mural cells in the zebrafish brain. In addition, it confirms previous literature on zebrafish that provides evidence that, in the absence of pericytes/VSMC, hemorrhages appear (Wang et al, 2014, PMID: 24306108 and Ando et al 2021, PMID: 3431092). The study by Ando et al, 2021 did not report experiments assessing BBB leakage in pdgfrb mutants but in the review article by Ando et al (PMID: 34685412) it is stated that "indicating that endothelial cells can produce basic barrier integrity without pericytes in zebrafish."

We thank the reviewer for their comments and pointing out literature that we had not cited (this has been corrected in our revised manuscript).

As noted by other reviewers, our study goes beyond simply confirming previous literature. The quoted section by the reviewer from Ando et al 2021 regarding intact barrier integrity in pdgfrb mutants is a conclusion based on apparent lack of haemorrhages in pdgfrb mutants[1]. Our work shows haemorrhages in older animals and as such is in line with these previously published results, but it also extends previous work, for the first time reporting detailed functional analysis to assess BBB integrity. Our study uses definitive tracer assays (now including extensive revisions) to identify intact the BBB in pdgfrb mutants in live animals. This has not been previously described and is important because it offers a new perspective on the evolutionary conservation (or otherwise) of pericyte control of BBB function. Furthermore, our study investigates the nature of hotspot leakage and haemorrhages in more detail than in previous work.

Weaknesses:

(1) The authors should avoid using violin plots, which show distribution. Instead, they should replace all violin plots in the figures with graphs showing individual data points and standard deviation. For Figure 2f specifically, the standard deviation in the analyzed cohort should be shown.

This is a good point and we have replaced the violin plots with individual data points and shown all data as mean±SEM.

(2) The authors have not shown the reduced PDGFRB protein or the effect of mutation on mRNA level in their zebrafish mutant.

Our pdgfrb^uq30bh mutant allele introduces a mutation predicted to generate a truncated protein very similar to previously validated alleles (see detail in revised Extended Data Fig. 1a and methods). Our pdgfrb^uq30bh mutant also phenocopies previous pdgfrb mutants (sa16389 and um148 alleles)[2,3], displaying mural cell loss with multiple markers (Fig. 1a, new data in Extended Data Fig. 1b–c, Fig. 3b–c; Extended Data Fig. 4c–d) and the same typical morphological defects and survival rates (new data in Extended Data Fig. 1d–f). Thus our mutant phenocopy gives confidence it is most likely a null allele, in line with previous papers studying presumed null alleles[1].

We believe this provides sufficient confidence in this allele of pdgfrb. Moreover, considering that our manuscript focusses on loss of mural cells and we show definitively that this mutant has robust loss of mural cells in the brain, our mutant is suitable for this study.

(3) Statistical data analysis: Did the authors perform analyses to investigate whether the data has a normal distribution (e.g., Figures 1d, e)?

We thank the reviewer for raising this and apologise for this oversight. All data have now been assessed for normality using Shapiro-Wilk test and further statistical analyses have been performed accordingly. The specific quantifications referred to by the reviewer in Extended Data Fig. 3a–d (previously Fig. 1d-e), have normal distribution except for quantification measuring 70 kDa extravasation at 7 dpf, therefore Mann-Whitney test has been used for this comparison. Further information can be found in figure legends and methods.

(4) Analysis of tracer extravasation. The use of 2000 kDa dextran intensity as an internal reference is problematic because the authors have not provided data demonstrating that the 2000 kDa dextran signal remains consistent across the entire vasculature. The authors have not provided data demonstrating that the 2000 kDa dextran signal in vessels exhibits acceptable variance across the vasculature to serve as a reliable internal reference. The variability of this signal within a single animal remains unknown. The presented data do not address this aspect.

We thank the reviewer for their comment and agree that analysis was needed for showing 2000 kDa dextran as a reliable normalization signal.

We now show the data in the following Figures that demonstrate the consistency of signal throughout the vasculature using this 2000-kDa tracer: Extended Data Fig. 2b, Extended Data Fig. 3a and c, Extended Data Fig. 5a, Extended Data Fig. 6. In fact, we observe that this 2000 kDa tracer provides a very reliable marker of large and small calibre vessels in larval, juvenile and adult animals, even in fixed and cleared whole tissues and animals (e.g. Extended Data Fig. 2d-e, Extended Data Fig. 5 and 6).

Our further experiments and analysis support the use of this tracer as an ideal way to normalise for variation between animals and coupled with improved masking of vessels using transgenic labels (e.g. Extended Data Fig. 2b) we can quantify across whole vascular networks to reduce the concern about variation within individual animals. We also find 2000 kDa shows negligible leakage through the brain vessels Extended Data Fig. 2b–c (new data) at 2 hours post-injection (hpi) and provided images in Extended Data Fig. 6b–b′′ showing detectable signals even at 6 hpi. Finally, results generated with this approach, normalisation to transgenic markers or even raw parenchymal values of tracer intensity, generate the same conclusions. In addition, we point the reviewer to a recent pre-print that further validates this method from our team[4].

Overall, we find the use of this tracer an ideal way to normalise for differences in injection volumes between animals and we recommend the use of this method to other groups assessing BBB leakage in zebrafish.

Additionally, it's intriguing that the signal intensity in the parenchyma of the tested tracers presents a substantial range, varying by 20-30% in the analysed cohort (Figure 1g, Extended Figure 1e). Such large variability raises the question of its origin. Could it be a consequence of the normalization to 2000 kDa dextran intensity which differs between different fish? Or is it due to the differences in the parenchymal signal intensity while the baseline 2000 kDa intensity is stable? Or is the situation mixed?

This is a good point raised by the reviewer.

To address this, we have used the following approaches:

(1) We provide additional experiments and normalisation methods that support the utility of our tracer studies (new data in Fig 2a–f and Extended Data Fig. 2b–c), discussed in detail below.

(2) We provide graphs of the raw parenchymal distribution of tracer not normalised at all (also requested by reviewer 1). This is provided in Author response image 1 and further supports all our conclusions, showing that our normalisation methods generate meaningful data.

Overall, the range of parenchymal intensity that we see after tracer injection and live imaging shows variations introduced during microinjection. However, these ranges are in-line with previous publications using similar methods (see studies by O’Brown et al 2019 and 2023)[5,6], allow reliable statistical comparisons to be drawn between control and mutants and allow us to detect both immature and functional BBB states during zebrafish development (new data in Fig. 2e-f).

Of note, the variability we see is likely introduced during the injection process into tiny larval blood vessels and is the reason why we perform normalization of parenchymal tracers to a vascular dextran signal that doesn’t leak from brain vessels. In our studies, 2000-kDa dextran has been co-injected with the smaller size tracers, therefore any potential differences in injection volumes as well as imaging conditions (however consistent) should be reduced by this method.

An alternative and potentially more effective approach would be to cross the pdgfrb mutant line with a line where endothelial cells are genetically labeled to define vessels (e.g. the line kdrl used in acquiring data presented in Figure 2a). Non-injected controls could then be used as a baseline to assess tracer extravasation into the parenchyma.

We thank the reviewer for this suggestion.

In response, we have performed new tracer leakage experiments at 7 and 14 dpf in siblings and pdgfrb mutants and quantified parenchymal tracer extravasation by normalizing to vascular reporters (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916). The results were in-line with the previously presented and independent experiments and showed indistinguishable phenotypes between siblings and pdgfrb mutants (new data, Fig. 2a–d). We also used uninjected controls to assess baseline and saw consistent values approaching zero in these images and did not include this in the revised paper.

Furthermore, we have also used this approach in wild-type larvae at 3 dpf (immature BBB) and 7 dpf (functional BBB)[5]. We detected significantly higher parenchymal extravasation of 10 and 70 kDa tracers at 3 dpf compared to 7dpf, demonstrating that our method can detect leakage (new data, Fig. 2e–f).

We believe that both normalization approaches have advantages (as discussed above), therefore showing the same results with these two different approaches has further strengthened our findings.

How is the data presented in Figure 3e generated? How was the dextran intensity calculated? It looks like the authors have used the kdrl line to define vessels. Was the 2000 kDa still used as in previous figures? If not, please describe this in the Materials and Methods section.

We have moved this data to Fig. 4e (previously Fig. 3e).

Previously, we had plotted raw data due to the nature of the experiment being conducted on a vibratome sectioned tissue. The 2000 kDa tracer was not used. In response to this query and to be consistent with the new approach suggested by the reviewer, we have revised the quantification by normalizing the 10 kDa tracer extravasation to Tg(kdrl:Hsa.HRAS-mCherry)^s916) for this and the new experiments on juveniles (Fig. 5h–i). Please see the corresponding figure legends or revised methods (lines 464–472).

(5) The authors state that both controls and mutants show extravasation of 1 kDa NHS-ester into the parenchyma. However, the presented images do not illustrate this; it is not obvious from these images (Extended Data Figure 1c). Additionally, the presented quantification data (Extended Data Figure 1e) do not show that, at 7 dpf, the vasculature is permeable to this tracer. Note that the range of signal intensity of the 1 kDa NHS-ester is similar to the 70 kDa dextran (Figure 1g and Extended Figure 1e). Would one expect an increase in the ratio in case of extravasation, considering that the 2000 kDa dextran has the same intensity in all experiments? Please explain.

We thank the reviewer for raising this important point.

To clarify, we have never claimed that “2000-kDa dextran has the same intensity in all experiments”. On the contrary, vascular 2000 kDa normalization has been used to account for potential differences caused by injection, as stated in the submitted supplementary materials and now made more clear in the revision.

In response to this query, we conducted more detailed analysis on tracer extravasation patterns based on molecular weight (new data, Extended Data Fig 2b–c). This analysis showed that 1- and 10-kDa tracers have much higher extravasation rate compared to 70- and 2000-kDa tracers. Interestingly, we did not find a significant difference between 1 and 10 kDa extravasation. Therefore, in the revised manuscript we used only 10 kDa in further experiments and have removed 1 kDa from the figures.

To assess the tracers individually (new data in Extended Data Fig. 2c), parenchymal extravasation of individual tracers was normalised to their own vascular signal (eg. Mean intensity of 10 kDa in midbrain/mean intensity of 10 kDa in vasculature), to account for potential differences in injection volume. This provides a suitable method to assess leakage in wild-type animals and is now in line with how previous studies have analysed such tracer injections[5,6]. Please see revised figure legends and supplementary materials for details.

(6) The study would be strengthened by a more detailed temporal analysis of the phenotype. When do the aneurysms appear? Is there an additional loss of VSMC?

We thank the reviewer for this suggestion, and we have now performed staged imaging of the pdgfrb mutants and siblings between 7 and 21 dpf using TgBAC(acta2:EGFP)^uq17bh transgene (new data, Fig. 3b-c; Extended Data Fig. 4a–d). Consistent with previous results, acta2:EGFP-positive cells surrounding the middle mesencephalic central arteries (MMCtA) were missing in pdgfrb mutants. At 21 dpf, we have also observed a mild dilation of these vessels, likely the earliest changes to generate aneurysms (new data, Fig. 3c).

To extend the number of stages analysed in this study, we have also performed new tracer leakage experiments in juveniles (30 dpf) and found that aneurysms can be detected at this age when the 10 kDa tracer is used (new data in Fig. 5b–b′). Consistent with the adult stage phenotype, aneurysms were limited to the larger calibre vessels (arteries) in the brain. We have also observed hotspots, and upon quantification, we found fewer numbers in juveniles compared to adults, suggesting that severity of aneurysms and hotspots increase with age.

Taken together, our results show that the aneurysms in pdgfrb mutants start appearing at late larval/early juvenile stages (~21 dpf) with observable dilations. By 30 dpf, aneurysms accompanied by small numbers of hotspots are observed, which exhibits significantly increased numbers by adulthood. This also correlates with reduced development and survival rate of pdgfrb mutants after 30 dpf (new data, Extended Data Fig. 1d–e).

(7) The authors intended to analyze the BBB at later stages (line 128), but there is not a significant time difference between 2 months (Figure 2) and 3 months (Figure 3) considering that zebrafish live on average 3 years. Therefore, the selection of only two time-points, 2 and 3 months, to analyze BBB changes does not provide a comprehensive overview of temporal changes throughout the zebrafish's lifespan. How long do the pdgfb mutants live?

Respectfully, zebrafish transition from juvenile stages to adulthood between 2 and 3 months and there are many significant differences in the physiology of this organism at these two ages. At 2 months, zebrafish are still juveniles undergoing metamorphosis with rapid growth and ongoing skeletal and vascular development. By 3 months, they are sexually mature adults and have much more developed cranioskeletal and vascular systems. Having said that, we take the reviewers important point that further temporal resolution would improve the study.

We have performed new experiments in 1-month-old animals and provided comprehensive analysis of the vascular phenotypes occurring in pdgfrb mutants. These were very informative experiments analysing leakage using 10-kDa tracer injections and have significantly improved the study. We had previously provided experiments at 5-month-old adults as well (previously Fig. 4a–b and Extended Data Fig. 4a) and so now the study includes larval stages (7, 14 dpf), juveniles at 1 and 2 months and adults at 3 and 5 months. While the additional timepoints did not offer up any new conclusions, they significantly enhanced the body of work overall.

Of further note, we provided survival data up to 90 dpf where survival of the pdgfrb mutants is significantly reduced compared to siblings (Extended Data Fig. 1e). We believe this is associated with the severity of the aneurysms and haemorrhages which probably lead to lethality in these mutants.

(8) Why is there a difference in tracer permeability between 2 and 3 months (Figures 2 and 3)? Are hemorrhages not detected in 2-month-old zebrafish?

In response to this and other queries, we have added new additional experiments that provide more detailed temporal analysis on tracer accumulation (new data in Fig. 5b–c, Fig. 5f–g).

In short, we do not see obvious haemorrhages in 1- or 2-month fish at a gross level during dissections (not shown). We find that using 10-kDa tracer, we can detect small hotspots at aneurysms as early as 1 month, likely representing the earliest loss of integrity. We do not see obvious hotspots in 2-month-old animals when we use the 70-kDa tracer, this suggests to us that it is less sensitive for hotspot detection (in line with new Extended Data Fig. 2c). Finally, we find that the number of hotspots increases dramatically from Juvenile to Adult stages in our datasets, which we take as indicative of a progressive phenotype.

Overall, tracer size matters for detecting hotspots and they become more apparent in older animals - we have added a note in the main text to cover these points (lines 200–205)

(9) Figure 3: The capillary bed should be presented in magnified images as it is not clearly visible. Figure 3e shows that in the pdgfb mutant the dextran intensity is higher also in regions 6-10. How do the authors explain this?

We thank the reviewer for raising this important point.

Firstly, we now include enlarged views of the capillary beds for this experiment (Fig. 4d′) and new experiments mentioned below.

Secondly, in relation to why there is higher tracer in lateral locations and not just medial sites of haemorrhage, we believe that this is most likely due to the progressive spread of tracer from the medial hotspots. To test if this is likely, we performed additional experiments and tested tracer accumulation at 2 different timepoints in brains collected at 0.5 or 6 hpi (new data in Fig. 5f–g, Extended Data Fig. 6a–b′′). Tracer accumulation at 0.5 hpi was very minimal and was primarily limited to hotspots and nearby regions new data in (Fig. 5h), whereas a higher tracer accumulation in brains was observed across medial to lateral regions at 6 hpi (new data in Fig. 5i) in pdgfrb mutants. Comparing the data in Figure 4 (2 hpi) and new data in Figure 5i (6 hpi), the 10 kDa-tracer appears to have spread to more lateral locations given the increased time allowed post injection.

We cannot formally exclude the possibility that tracer leakage does occur slower through capillaries than at major hotspots, which might fit with the proposed model of slow leakage via increased EC transcytosis[7-9]. However, considering that we cannot detect increased tracer accumulation in pdgfrb mutants that lack aneurysms and haemorrhages at 7 and 14 dpf, such a scenario would require capillary transcytosis to be active at later juvenile and adult stages but not in larval and late larval animals. Thus, we believe the most plausible explanation is that aneurysm/haemorrhage associated leakage is the primary cause of the vascular integrity defects in zebrafish pdgfrb mutants.

We have added discussions addressing this in the revised manuscript (lines 220–230, 300–302).

(10) In general, the manuscript would benefit from a more detailed description of the performed experiments. How long did the tracer circulate in the experiments presented in Figures 2, 3, and 4?

We thank the reviewer for this suggestion and have now ensured that this is clearly described for in figure legends and methods (lines 391–395).

(11) How do the authors explain the poor signal of the 70 kDa dextran from the vasculature of 5-month-old zebrafish presented in Extended Data Figure 3?

We agree that the dextran signal was reduced compared to the other experiments in that Figure. This is likely due to sample preparation and clearing causing reduced fluorescence. Upon consideration of the presented data and the additional experiments using 10 kDa tracers providing further validations for our claims, we decided to remove this data from the paper.

(12) The study would benefit from a clear separation of the phenotypes caused by the loss of VSMC. The title eludes that also capillaries present hemorrhages which is not the case. How do vascular mural cells differ from mural cells? Are there any other mural cells?

We take the reviewers point and have now updated the title as "Mural cells protect the adult brain from haemorrhage but do not control the blood-brain barrier in developing zebrafish."

(13) I have a few comments about how the authors have interpreted the literature and why, in my opinion, they should revise their strong statements (e.g., the last sentence in the abstract).

Scientists have their own insights and interpretations of data. However, when citing published data, it should be clearly indicated whether the statement is a direct quote from the original publication or an interpretation. In the current manuscript, the authors have not correctly cited the data presented in the two published papers (references 5 and 6). These papers do not propose a model where pericytes suppress "adsorptive transcytosis" (lines 73-76). While increased transcytosis is observed in pericyte-deficient mice, the specific type of vesicular transport that is increased or induced remains unknown.

Similarly, lines 151-152 refer to references 5 and 6 and use the term "adsorptive transcytosis," but the authors of both papers did not use this term. Attributing this term to the original authors is inaccurate. Additionally, lines 152-153 do not accurately represent the findings of references 5 and 6. These papers do not state that there is an induction of "caveolae" in endothelial cells in pericyte-deficient mice. In the absence of pericytes, many vesicles can be observed in endothelial cells, but these vesicles are relatively large. It is more likely that there is some form of uncontrolled transcytosis, perhaps micropinocytosis. Please refer to the original papers accurately.

We thank the reviewer for these comments. We take the point and have rewritten the manuscript carefully to improve accuracy and avoid misrepresenting any previous claims made in specific papers.

Also, the authors have missed the fact that in mice, the extent of pericyte loss correlates with the extent of BBB leakage. To a certain extent, the remaining pericytes, can compensate for the loss by making longer processes and so ensure the full longitudinal coverage of the endothelium. This was shown in the initial work of Armulik et al (reference 5) and later in other studies.

We certainly did not miss this important point (as we are also working with these mouse models) and we now include reference to this in our expanded discussion. Of note, we do think it would be worthwhile assessing if the extent of BBB leakage and pericyte coverage also correlates with the presence of microhaemorrhages in these hypomorphic mouse models, although this is more challenging to do in mice than in zebrafish.

The bold assertion on lines 183 -187 that a lack of specific BBB phenotype in pdgfrb zebrafish mutant invalidates mouse model findings is unfounded. Despite the notion that zebrafish endothelium possesses a BBB, I present a few examples highlighting the differences in brain vascular development and why the authors' expectation of a straightforward extrapolation of mouse BBB phenotypes to zebrafish is untenable.

In mice Pdgfrb knockout is lethal, but in zebrafish, this is not the case. In marked contrast to mice, however, zebrafish pdgfrb null mutants reach adulthood despite extensive cerebral vascular anomalies and hemorrhage. Following the authors' argumentation about the unlikely divergence of zebrafish and mice evolution, does it mean that the described mouse phenotype warrants a revisit and that the Pdgfrb knockout in mice perhaps is not lethal? Another example where the role of a gene product is not one-to-one, which relates to pericyte development, is Notch3. Notch3-null mice do not show significant changes in pericyte numbers or distribution, suggesting a less prominent role in pericyte development compared to zebrafish.

Although many aspects of development are conserved between species, there are significant differences during brain vascular development between zebrafish and mice. These differences could reveal why the BBB is not impaired in zebrafish pdgfrb mutants. There is a difference in the temporal aspect when various cellular players emerge. The timing of microglia colonization in the brain differs. In mice, microglia colonization starts before the first vessel sprouts enter the brain, while in zebrafish, microglia enter after. Additionally, microglia in zebrafish and mice have a different ontogeny. In mice, astrocytes specialize postnatally and form astrocyte endfeet postnatally. In zebrafish, radial glia/astrocytes form at 48 hpf, and as early as 3 dpf, gfap+ cells have a close relationship with blood vessels. Thus, these radial glia/astrocyte-like cells could play an important role in BBB induction in zebrafish. It's worth noting that in Drosophila, the blood-brain barrier is located in glial cells. While speculative, these cells might still play a role in zebrafish, while the role of pericytes does not seem to be crucial. Pericytes enter the brain and contact with developing vasculature (endothelium) relatively late in zebrafish (60 hpf). In mice, the situation is different, as there is no such lag between endothelium and pericyte entry into the brain. I suggest that the authors approach the observed data with curiosity and ask: Why are these differences present? Are all aspects of the BBB induced by neural tissue in zebrafish? What is the contribution of microglia and astrocytes?"

Another interesting aspect to consider is the endothelial-pericyte ratio and longitudinal coverage of pericytes in the zebrafish brain, and how this relates to what is observed in mice. How similar is the zebrafish vasculature to the mouse vasculature when it comes to the average length of pericytes in the zebrafish brain? Does the longitudinal coverage of pericytes in the zebrafish brain reach nearly 100%, as it does in mice?

Based on the preceding arguments, it is recommended that the authors present a balanced discussion that provides insightful discussion and situates their work within a broader framework.

Overall, we agree with most of the points made by the reviewer above. As we have now extended the format of this paper to be a full article, we have space to provide an extended discussion and introduction. We now try to capture many of the points made by the reviewer and we think that this has significantly improved the paper. We thank the reviewer for this contribution.

We do want to point out that we did not state that our findings using zebrafish pdgfrb mutants invalidate mouse model findings. We suggest that a deeper analysis to understand the nature of the hotspots in mural cell deficient mammalian models could be very interesting in light of the zebrafish observations. We hope that the revised discussion better reflects this.

Reviewer #3 (Public review):

This manuscript examines the role of pdgfrb-positive pericytes in the establishment and maintenance of the blood-brain barrier (BBB) in the zebrafish. Previous studies in PDGFB- or PDGFRB-deficient mice have suggested that loss of pericytes results in disruption of the BBB. The authors show that zebrafish pdgfrb mutant larvae have an intact BBB and that pdgfrb mutant adult fish show large vessel defects and hemorrhage but do not exhibit substantial leakage from brain capillaries, suggesting loss of pericytes is not sufficient to "open" the BBB. The authors use beautiful and compelling images and rigorous quantification to back up most of their conclusions. The imaging of the adult brain is particularly nice. The authors rigorously document the lack of BBB leakage in pdgfrbuq30bh mutant larvae and large vessel phenotypes (eg, enlargement and rupture) in pdgfrbuq30bh mutant adults. A few points would help the authors to further strengthen their findings contradicting the current dogma from rodent models.

We appreciate the reviewer's comments on the manuscript overall and agree that addressing the raised points was needed to strengthen our findings. We have addressed the main points below and believe that this revision greatly improves this study.

Major point:

The authors document pericyte loss using a single TgBAC(pdgfrb:egfp)ncv22 transgenic line driven by the promoter of the same gene mutated in their pdgfrbuq30bh mutants. Given their findings on the consequences of pericyte loss directly contradict current dogma from rodent studies, it would be useful to further validate the absence of brain pericytes in these mutants using one of several other transgenic lines marking pericytes currently available in the zebrafish. This could be done using pdgfrb crispants, which the authors show nicely phenocopy the germline mutants, at least in larvae. This would help nail down the absence of any currently identifiable pericyte population or sub-population in the loss of pdgfrb animals and substantially strengthen the authors' conclusions.

We thank the reviewer and agree that examination of pdgfrb^uq30bh mutants using another transgenic line labelling pericytes would further validate the absence of brain pericytes. We generated a transgenic line, TgBAC(abcc9:abcc9-T2A-mCherry)^uom139, to visualise pericytes and validated the absence of brain pericytes in the pdgfrb mutants (revised Extended Data Fig. 1b). The loss of brain pericytes matched our findings using TgBAC(pdgfrb:egfp)^uq15bh line as well as previously published data by Ando et al 2016-2021, where the brain pericytes except for metencephalic artery were missing[2,3].

Other issues:

The authors should provide more information about the pdgfrbuq30bh mutant and how it was generated (including a diagram in a supplemental figure would be useful).

We thank the reviewer for this suggestion. In addition to the explanations provided in supplementary materials, we have added a schematic, provided sanger sequencing results showing the mutation as well as predicted effect of the mutation on the protein domains (Extended Data Fig. 1a).

It would be helpful to show some data on whether mutants show morphological phenotypes or developmental delay at 7 and 14 dpf, to provide some context to better assess the reduced branching and vessel length vascular phenotypes (see Figures 1c-e).

We thank the reviewer for this suggestion. We have provided further details on body length and survival of the pdgfrb mutants until 90 dpf. As reported by Ando et al 2021, we did not observe any distinguishing feature until about 30 dpf[1,3]. The adult anatomy of our mutant allele matches that of previously described null mutants and is now shown (Extended Data Fig. 1f).

If available, it would be helpful to have a positive control for the tracer leakage experiments - a genetic manipulation that does cause disruption of the BBB and leakage at 2 hours post-tracer injection (see Figures 1f and g).

We thank the reviewer for this suggestion and agree that a positive control would validate reliability of our method. We have performed new experiments at 3 dpf when BBB integrity is not yet established and at 7 dpf when BBB is functional in zebrafish[5], testing both 10 and 70 kDa tracers (new data in Fig. 2e–f). We detected significantly higher tracer accumulation at 3 dpf, showing that our methods can detect tracer leakage in the brain.

Quantification of the findings in Figure 4c, d would be useful, as would the use of germline fish for these experiments if these are now available. If this is not possible, it would be helpful to document that the crispants used in these experiments lack pdgfrb:egfp pericytes at adult stages (this is only shown for 5 dpf larvae, in Extended Data Figure 4b).

We thank the reviewer for this comment. Using TgBAC(pdgfrb:egfp)^uq15bh line, we have imaged coronal brain sections collected from 10-week old pdgfrb crispants and uninjected siblings (age-matched animals used in Fig. 5d–e, previously Fig. 4c–d). We have now included data showing that adult pdgfrb crispants lack brain mural cells, phenocopying pdgfrb^uq30bh mutants (new data, Extended Data Fig. 6f). These particular crispants are very reliable in our hands and nicely reproduce stable mutant phenotypes, giving us confidence to use the faster F0 approach in this experiment.

Adult mutants clearly show less dye leakage in the more superficial capillary regions than WT siblings, but dextran intensity is a bit higher, although this could well be diffusion from more central brain regions where overt hemorrhage is occurring. Along similar lines though, the authors' TEM data in Extended Data Figure 4d hints that there may be more caveolae in mutant brain capillaries, although the N number was lower here than for the measurements from TEM of larger central vessels (Figure 4g). It would be useful to carry out additional measurements to increase the N number in Figure 4d to see whether the difference between wild-type sibling and mutant capillary caveolae numbers remains as not significant.

We thank the reviewer for these raising important points and suggestions.

Firstly, in relation to signal in capillary regions and likely diffusion from hotspots, please see the response to reviewer 3 point 9 above.

Secondly, we have imaged and analysed more capillaries in both pdgfrb mutants and siblings (Extended Data Fig. 7a–b, previously Extended Data Fig. 4d). The results showed no significant difference between these groups, suggesting that capillary EC transcytosis is unchanged in our pdgfrb mutants.

It might be helpful to include some orienting labels and/or additional descriptions in the figure legends to help readers who are not used to looking at zebrafish brain vessels have an easier time figuring out what they are looking at and where it is in the brain.

We thank the reviewer for this suggestion and agree that adding further information in the figure legends and illustrations about orientation would make it easier for readers. In addition to the information provided in the figure legends in the submitted version, we have added an illustration, more labels on the revised figures, extended the descriptions in figure legends, main text and methods.

We have added a schematic depicting the tracer leakage assay workflow, orientation of live imaging and analysed region of interest (Extended Data Fig. 1a–b).

All figure legends have been updated with the anatomical position and microscopy view.

Additional labels on figures have been added to understand the referenced vessel names (new data in Fig. 3c and Extended Data Fig. 4a–b′).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The study uses the intensity of tracer signals within the vessels to analyze BBB permeability, potentially underestimating leakage severity. The dye intensity is measured 2 hours after injection, however, other studies have already observed leakage after 30 Minutes, by imaging directly in the brain parenchyma. The overall intensity should also decrease through leakage from the other vessels of the body, e.g. in the trunk and tail. Probably the loss of intra-vascular dye intensity from leakage in barrier-free vessels is already so high (after 2 hours) that the smaller amount of leakage across the BBB cannot be observed.

We thank the reviewer for this comment and suggestion. We agree that small sized tracers leak from vasculature, particularly through fenestrated vessels in the trunk and tail. We have based our timing on previous studies and our own experience. In zebrafish, the study by O’Brown et al 2019 also used 2 hpi[5] for detection of leakage in mfsd2aa mutants, which also has been proposed to regulate BBB integrity by controlling EC transcytosis. Therefore, we believe that performing experiments at 2 hpi is appropriate to investigate roles of pericytes in BBB integrity. Our data would suggest that this timing works.

In response to this and other comments, we performed further experiments and analyses to test leakage of tracers testing molecular weights ranging from 1 to 2000 kDa individually. We showed that these tracers can reliably be detected in brain parenchyma and vasculature when imaged at 2 hpi. In another study, we showed that medium size tracers such as 40 kDa Dextran can be reliably detected in the vasculature in similar timepoints[10]. Considering we have performed experiments using 10 and 70 kDa tracers do detect parenchymal tracer accumulation and tracer still within the vessels, we believe this timepoint is appropriate for assessing BBB integrity in zebrafish.

In addition to these experiments, see our tracer leakage experiments in 1-month-old animals, at 0.5 and 6 hpi to test leakage pattern described above (Fig. 5 and Extended Data Fig. 6).

Therefore, the authors will need to validate their method of choice, showing an impairment of the BBB, caused by other agents (known to affect the BBB), and at 48hpf, when the BBB is not tightened yet. One example for BBB impairment can be found in O'Brown et al (2019), eLife 8e47326. doi: 10.7554/eLife.47326

We thank the reviewer for this suggestion. As shown by O’Brown et al 2019, we have performed experiments at 3 dpf when BBB integrity is not mature and at 7 dpf when BBB is functional[5], testing both 10 and 70 kDa tracers. We detected significantly higher tracer accumulation at 3 dpf, showing our new additional method (see below) can detect tracer leakage in the brain (new data in Fig. 2e–f).

Ideally, the authors would also supplement the method with additional approaches in the younger developmental stages to validate their findings.

The validation of the method and the findings is particularly important for the claims of lack of BBB impairment in the absence of mural cells, as this is a "negative" finding.

In response to this and comments from other reviewers, we performed additional tracer leakage experiments (new data in Fig. 2a–d) where we imaged 10 and 70 kDa tracers with a vascular reporter (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916) and used this reporter for normalisation. Both this approach as well as the experiments provided in the first submission (updated as Extended Data Fig. 3a–d) showed that pdgfrb mutants at 7 and 14 dpf have indistinguishable BBB integrity compared to siblings. See also Author response image 1 that further addresses this.

I also strongly suggest to rephrase and downtown the claim that vascular mural cells do not control the blood-brain barrier in developing zebrafish.

As a negative finding cannot be proven completely and lots of the previously shown effects on murine BBB impairment are rather weak (when caused by single agents such as Claudin5 deficiency or Sphingosine-phosphate receptor1 knockout), it might be important to only claim that in zebrafish no strong impairment (as observed in the mural cell-deficient mouse) could be observed. Or rephrase it to "no impairment as severe as/comparable to ... could be observed" and then provide an impairment control for the developmental stages.

We thank the reviewer for this comment and agree that negative findings are very challenging to prove. However, we find no evidence of leakage of the BBB in animals lacking mural cells at 7 and 14 dpf and believe that our data is robust on this point. As such, we believe we show that a vertebrate with a largely conserved EC BBB, can have intact barrier function in the absence of mural cells.

We have as suggested revised our claims throughout the manuscript to provide more further nuanced discussion of this, but we do not want to water down our claims too much as we believe they are important. We hope that the reviewer will appreciate our carefully worded and expanded discussion section.

Additional items of interest to the readers and therefore suggestions to improve the manuscript could be

(1) To include more molecular analysis: while the study identifies caveolae induction and basement membrane thickening as potential contributors to focal leakage, the exact molecular mechanisms linking mural cell loss to these structural changes are not deeply investigated.

(2) Also, the study primarily associates BBB disruption in the adult with aneurysms. Therefore other subtle or diffuse changes to BBB permeability that might occur even without overt vascular lesions are potentially underrepresented.

However, following up experimentally on these might exceed the scope of the manuscript.

We thank the reviewer for these suggestions and agree with both points. However, as stated by the reviewer, these experiments are beyond the scope of the manuscript and represent future directions for our lab and others.

Reviewer #2 (Recommendations for the authors):

(1) Mouse genes should be written as follows: Pdgfb, Pdgfrb and be in italics. See line line 70: it should be written "Pdgfb and Pdgfrb (italics)" and not "PdgfB and Pdgfrβ".

We have updated the text according to the reviewer’s suggestion.

(2) Please state the age of the fish analyzed in Figure 1f and 1g.

We have moved this data to Extended Fig. 3a–d (previously Fig. 1f-g) and have placed age information on the images and in the figure legends.

(3) Is the reduced vascular complexity in pdgfb mutant due to reduced angiogenesis or due to excessive pruning?

This is a good question, and we do not know at this stage. We have unpublished data that suggest pericytes secrete angiogenic growth factors, but this question warrants a thorough investigation that we believe is beyond the scope of this current study.

(4) Please check that the figure legends state the correct number of fish analysed. For example, Figure 1 d, e N=8 but there seem to be 9 data points per group - 14dpf.

We apologise for this mistake and thank the reviewer for raising this. We have updated the graphs and figure legends accordingly.

(5) Please indicate in the figures the genotypes (wt, het) of a sibling presented alongside a pdgfb mutant.

Wild-type and heterozygous mutants are commonly used together in zebrafish research as a collective control group termed siblings. Since we didn’t see any difference between wild-type and pdgfrbuq30bh/- groups in any experiments, we reported these groups together. This is now stated in the supplementary materials.

One exception to this was examination of the growth and survival rates where we show the genotypes separately (new data in Extended Data Fig. 1b-f).

(6) Please explain clearly what region is shown in Figure 2B. I do not understand the explanation "approximate location of dotted line". Is the image in the panel "a" top view of a brain?

We have moved this data to Fig. 3a′ (previously Fig. 2b) and replaced the dotted line in Figure 3a (previously Fig. 2a) with a white box indicating the location of the restricted region in the whole brain image.

We have revised the text as below:

“Subset of z-slices from the whole brain imaging in (a) and (b) (white boxes) indicating mural cell loss and abnormal capillary network patterning. 100-μm-thick maximum intensity projections (MIP) were generated using the continuation of the left middle mesencephalic central artery (MMCtA, arrow) as an anatomical landmark.”

In addition, we have updated all our figure legends clearly stating the view and anatomical position of the imaged sample.

(7) Figure 2e: Note that- the dotted areas do not correspond to the areas magnified. Please adjust.

We have moved this data to Extended Data Fig. 5a (previously Fig. 2e–e′) and updated the location of the white box in 5a shown in enlarged view in 5a′.

(8) Lines 112 and 114 - Should the indicated figure be Figure 2b-d and Figure 2c-d, respectively, and not Figure 1?

We thank the reviewer for pointing out this mistake. All the figure legends are now referred to appropriately in the revised manuscript.

(9) Data presented in Figure 2 and Figure 3 can be consolidated and presented as one Figure.

We thank the reviewer for this suggestion. After addition of new data and revising the manuscript we have decided to keep these data presented separately.

(10) Note that Figure 2a,b shows 5-month-old fish, not 2-month-old fish. Additionally, Extended Data Figure 3 shows 5-month-old fish, not 3-month-old fish.

The stages noted by the reviewer were correctly indicated.

(11) Figure 2d: Please clarify the definition of a "large vessel".

We have observed normal morphology in capillaries and noted aneurysms and hotspots in large calibre vessels such as arteries, which become more severe over time. We have revised this across the manuscript accordingly.

(12) Figure 4a, b: Please explain how the hotspots of leakage were defined based on the extravasated tracer.

Hotspots of leakage are scored when fluorescent tracer aggregates are clearly observed outside the vessels. Vessel borders were defined using the transgenic lines (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916). We have added a clear description in the methods section (lines 473–475).

Figure 4c: Why were Pdgfrb crispants used and not the mutant line?

They were used as pdgfrb crispants phenocopy the lack of brain mural cells (Extended Data Fig. 5e, previously Extended Data Fig. 4b) and mutant phenotype reliably and for practical reasons, because they allow faster experiments and reduce fish usage.

Figure 4e: The magnification of the electron microscopy images does not make it possible to clearly identify caveolae. What was the magnification of the collected images for caveolae analysis? How did the authors ensure that they quantified only caveolae and not other types of vesicles?

Respectfully, we disagree that the magnification is insufficient as our images were captured and analysed consistent with previous ultrastructural descriptions[11,12]. We based our quantification of caveolae on the size of vesicles observed and define them as circular profiles of less than 100 nm in diameter and were scored as luminal or abluminal based on proximity to each surface membrane (within 500 nm of each surface or in a thin-walled vessel the caveolae closest to each surface) (lines 398–409). Importantly, comparable analyses at similar magnifications have been independently validated in multiple caveola-deficient zebrafish genetic models[4,13]. Interestingly given the reviewers comments above, we do see increased vesicular structures that are larger than caveolae, but we only provide quantification of the caveolae here.

Reviewer #3 (Recommendations for the authors):

Congratulations to the authors on their really beautiful imaging and rigorous quantitative documentation of phenotypes - this is a really nicely done study, and could be very important to the field with just a few additional experiments to buttress the key conclusions.

We thank the reviewer for their kind comments.

In addition to the comments noted in the public review, I would only point out that there are two mislabeled call-outs in the text (Lines 112 and 114; says Figure 1, should say Figure 2).

We thank the reviewer for this point and have now revised the text accordingly.

(1) Ando, K., Ishii, T. & Fukuhara, S. Zebrafish Vascular Mural Cell Biology: Recent Advances, Development, and Functions. Life (Basel) 11 (2021). https://doi.org/10.3390/life11101041

(2) Ando, K. et al. Clarification of mural cell coverage of vascular endothelial cells by live imaging of zebrafish. Development 143, 1328-1339 (2016). https://doi.org/10.1242/dev.132654

(3) Ando, K. et al. Conserved and context-dependent roles for pdgfrb signaling during zebrafish vascular mural cell development. Dev Biol 479, 11-22 (2021). https://doi.org/10.1016/j.ydbio.2021.06.010

(4) Lim, Y. W. et al. Trans-Endothelial Trafficking in Zebrafish: Nanobio Interactions of Polyethylene Glycol-Based Nanoparticles in Live Vasculature. ACS Nano (2026). https://doi.org/10.1021/acsnano.5c21042

(5) O'Brown, N. M., Megason, S. G. & Gu, C. Suppression of transcytosis regulates zebrafish blood-brain barrier function. Elife 8 (2019). https://doi.org/10.7554/eLife.47326

(6) O'Brown, N. M. et al. The secreted neuronal signal Spock1 promotes blood-brain barrier development. Dev Cell 58, 1534-1547 e1536 (2023). https://doi.org/10.1016/j.devcel.2023.06.005

(7) Armulik, A. et al. Pericytes regulate the blood-brain barrier. Nature 468, 557-561 (2010). https://doi.org/10.1038/nature09522

(8) Daneman, R., Zhou, L., Kebede, A. A. & Barres, B. A. Pericytes are required for blood-brain barrier integrity during embryogenesis. Nature 468, 562-566 (2010). https://doi.org/10.1038/nature09513

(9) Mae, M. A. et al. Single-Cell Analysis of Blood-Brain Barrier Response to Pericyte Loss. Circ Res 128, e46-e62 (2021). https://doi.org/10.1161/CIRCRESAHA.120.317473

(10) Lim, Y.-W. et al. A Standardized Protocol to Investigate Trans- Endothelial Trafficking in Zebrafish: Nano-bio Interactions of PEG-based Nanoparticles in Live Vasculature. bioRxiv, 2025.2007.2023.666282 (2025). https://doi.org/10.1101/2025.07.23.666282

(11) Parton, R. G. & Simons, K. The multiple faces of caveolae. Nat Rev Mol Cell Biol 8, 185-194 (2007). https://doi.org/10.1038/nrm2122

(12) Parton, R. G. & del Pozo, M. A. Caveolae as plasma membrane sensors, protectors and organizers. Nat Rev Mol Cell Biol 14, 98-112 (2013). https://doi.org/10.1038/nrm3512

(13) Lim, Y. W. et al. Caveolae Protect Notochord Cells against Catastrophic Mechanical Failure during Development. Curr Biol 27, 1968-1981 e1967 (2017). https://doi.org/10.1016/j.cub.2017.05.06

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to investigate the mechanisms underlying Kupffer cell death in metabolic-associated steatotic liver disease (MASLD). The authors propose that KCs undergo massive cell death in MASLD and that glycolysis drives this process. However, there appears to be a discrepancy between the reported high rates of KC death and the apparent maintenance of KC homeostasis and replacement capacity.

Strengths:

This is an in vivo study.

Weaknesses:

There are discrepancies between the authors' observations and previous reports, as well as inconsistencies among their own findings.

Before presenting the percentage of CLEC4F⁺TUNEL⁺ cells, the authors should have first shown the number of CLEC4F⁺ cells per unit area in Figure 1. At 16 weeks of age, the proportion of TUNEL⁺ KCs is extremely high (~60%), yet the flow cytometry data indicate that nearly all F4/80⁺ KCs are TIMD4⁺, suggesting an embryonic origin. If such extensive KC death occurred, the proportion of embryonically derived TIMD4⁺ KCs would be expected to decrease substantially. Surprisingly, the proportion of TIMD4⁺ KCs is comparable between chow-fed and 16-week HFHC-fed animals. Thus, the immunostaining and flow cytometry data are inconsistent, making it difficult to explain how massive KC death does not lead to their replacement by monocyte-derived cells.

We thank the reviewer for the insightful comment and the opportunity to clarify this important point. To ensure consistency between our methodologies, we replaced Clec4f staining with TIM4 staining results as requested by the reviewer. We first showed the number of TIM4⁺ cells per unit area in Figure 1B. The results showed a significant and progressive loss of TIM4⁺ cells per unit area in the liver parenchyma, decreasing from approximately 60 cells/FOV at baseline (0w) to nearly 50 at 4w and further to about 30 at 16w post-HFHC diet. This finding is fully consistent with our flow cytometry data. The percentage of the embryonically derived KC population (CD11blow F4/80hi TIM4hi) among CD45⁺ cells dropped from 30.2% (0w) to 24.3% (4w) and 17.6% (16w) (Revised Figure 1C). The absolute number per gram of liver decreased from roughly 12 x 10⁵ (1w) to 9 x 10⁵ (4w) and 5 x 10⁵ (16w) (Revised Figure 1D).

These data suggest that despite the reported high rate of cell death among CLEC4F⁺TIMD4⁺ KCs, the population appears to self-maintain, with no evidence of monocyte-derived KC generation in this model, which contradicts several recent studies in the field.

We appreciate the reviewer’s insightful comment. We agree that our data show no substantial generation of monocyte-derived Kupffer cells (MoKCs) within the 16-week HFHC model. However, we do not believe the remaining embryonic KCs(EmKCs) are maintained through self-renewal, as the proportion of Ki67⁺TIM4⁺ cells remains low at all time points (Revised Figure S2D). Instead, our observations align with a phased replacement model: recruited monocytes first differentiate into monocyte-derived macrophages (MoMFs), which we see accumulate (Revised Figure S2B, S2C), and only later adopt a KC phenotype. Consistent with this, our 16-week model shows significant EmKC loss and MoMF expansion, but not yet the emergence of TIM4-MoKCs. This timing is supported by prior studies, where TIM4-KCs were observed at 24 weeks, but not at 16 weeks, on similar diets (Ref. 1,2). Therefore, we interpret our findings as capturing an earlier phase of MASLD progression, characterized by EmKC death and MoMF accumulation, prior to their full differentiation into MoKCs.

Moreover, there is no evidence that TIM4⁺CLEC4F⁺ KCs increase their proliferation rate to compensate for such extensive cell death. If approximately 60% of KCs are dying and no monocyte-derived KCs are recruited, one would expect a much greater decrease in total KC numbers than what is reported.

Thank you for raising this point, which allows for an important clarification. The interpretation that approximately 60% of KCs are dying is correct, but this refers to the proportion of the remaining KC population at 16 weeks that is TUNEL⁺, not to 60% of the original KC pool. Since our data show that over half of the EmKCs are lost by 16 weeks (Revised Figure 1B), the 60% of dying cells at this late time point corresponds roughly to only 25-30% of the total original KC population at baseline. This distinction reconciles the high rate of apoptosis observed late in disease with the overall progressive depletion of the EmKC pool.

It is also unexpected that the maximal rate of KC death occurs at early time points (8 weeks), when the mice have not yet gained substantial weight (Figure 1B). Previous studies have shown that longer feeding periods are typically required to observe the loss of embryo-derived KCs.

We appreciate the reviewer’s insightful observation. We think KC death is a continuous event during MASLD. To induce MASH, previous studies typically assess the loss of EmKCs after longer feeding periods, which might leave us an impression that longer feeding periods are required to observe substantive loss of embryonically derived KCs. In our HFHC model, the proportion of dying KCs was already elevated by 8 weeks, and this high rate was sustained through the 16-week endpoint. In a separate MCD dietary model characterized by rapid MASLD progression, a high rate of KC death was detectable as early as 6 weeks (Revised Figure 1F). Collectively, these data suggest that the onset of significant KC death is dependent on the pace of MASLD pathogenesis, more likely an early-initiated event that is through MASLD progression.

Furthermore, it is surprising that the HFD induces as much KC death as the HFHC and MCD diets. Earlier studies suggested that HFD alone is far less effective than MASH-inducing diets at promoting the replacement of embryonic KCs by monocyte-derived macrophages.

We appreciate the reviewer’s insightful comment. In our study, we observed significant KCs death under both HFD and HFHC feeding for 20, 16 weeks, respectively. Moreover, both HFHC and HFD induced similar stages of MASLD (characterized by significant lipid accumulation without fibrosis development) by these time points (Authir response image 1). Therefore, these data support that the onset of substantial KCs death may be an early MASLD event, before the progression to MASH. Additionally, this finding aligns with existing literature showing that 16 weeks of HFD feeding alone is sufficient to cause a marked reduction in the TIM4⁺KCs population (Ref. 1).

Author response image 1.

Detection of liver fibrosis in MASLD mouse models. Male wild-type C57BL/6J mice were fed a high-fat, high-cholesterol (HFHC) diet for 16 weeks or a high-fat diet (HFD) for 20 weeks to induce MASLD. Mice fed a normal chow diet (NCD) served as controls. (A) Sirius Red staining of liver sections was performed to assess collagen deposition and fibrosis during MASLD progression. Scale bar, 20 μm. (B) Western blot analysis of liver tissue lysates showing α-smooth muscle actin (α-SMA) expression as a marker of hepatic stellate cell activation and liver fibrosis.

In Figure 2D, TIMD4 staining appears extremely faint, making the results difficult to interpret. In contrast, the TUNEL signal is strikingly intense and encompasses a large proportion of liver cells (approximately 60% of KCs, 15% of hepatocytes, 20% of hepatic stellate cells, 30% of non-KC macrophages, and a proportion of endothelial cells is also likely affected). This pattern closely resembles that typically observed in mouse models of acute liver failure. Given this apparent extent of cell death, it is unexpected that ALT and AST levels remain low in MASH mice, which is highly unusual.

Thank you for this important feedback. To address concerns about the clarity of our imaging, we have provided high-resolution split-channel raw images for Figure 2D (Revised Figure 2D), which distinctly show the localization of TIM4, TUNEL, and GS. These confirm the progressive reduction of TIM4⁺KCs and the increase in TUNEL⁺ TIM4⁺cells over time. We agree that the high proportion of TUNEL⁺cells seems at odds with the modest ALT/AST elevation. This discrepancy might be explained by the distinct nature of cell death in MASLD. Unlike the acute necrosis with membrane rupture seen in acute liver failure—which causes massive, rapid enzyme release— obesity-related liver injury is a chronic process dominated by apoptosis (Ref. 4,5). Apoptosis preserves membrane integrity until late stages (Ref. 6), with dying cells packaged into apoptotic bodies for efficient phagocytic clearance by neighboring macrophages (Ref. 7,8). This controlled disposal system minimizes the leakage of intracellular enzymes. Therefore, the coexistence of widespread apoptosis (high TUNEL signal) with limited enzyme release (low ALT/AST) is a recognized feature of chronic MASLD pathogenesis.

No statistical analysis is provided for Figure 5D, and it is unclear which metabolites show statistically significant changes in Figure 5C.

We thank the reviewer for raising this statistical problem. We have now included statistical analysis in Revised Figure 5D.

In addition, there is no evaluation of liver pathology in Clec4f-Cre × Chil1flox/flox mice. It remains possible that the observed effects on KC death result from aggravated liver injury in these animals. There is also no evidence that Chil1 deficiency affects glucose metabolism in KCs in vivo.

We thank the reviewer for these important points. We previously characterized the liver pathology of Clec4f^ΔChil1 mice in detail (preprint: eLife 2025, DOI: 10.7554/eLife.107023.1, Fig. 2). On a normal chow diet, these mice showed no differences in body weight, hepatic lipid deposition, metabolic parameters, or glucose tolerance compared to controls. However, on an HFHC diet, Clec4f^ΔChil1 mice developed significantly worse metabolic and histological phenotypes. Crucially, our in vitro data demonstrate that recombinant Chi3l1 directly reduces KC death (preprint, Fig. 6E-F), indicating that the aggravated MASLD in knockout mice is a consequence of increased KC loss, not its cause.

Regarding glucose metabolism, we have previously shown that Chi3l1 deficiency leads to increased glucose uptake by KCs in vivo using the fluorescent glucose analog 2-NBDG. This effect was reversed by supplementing knockout mice with recombinant Chi3l1 (preprint Fig. 6G-H). This provides direct evidence that Chi3l1 modulates glucose uptake in KCs in vivo.

Finally, the authors should include a more direct experimental approach to modulate glycolysis in KCs and assess its causal role in KC death in MASH.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) in the HFHC-induced MASLD model (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for four weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity during active disease development. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data together with our complementary in vitro gain-of-function experiments, support a contributory role for excessive glycolytic activity in promoting KC apoptosis in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

Reviewer #2 (Public review):

Summary:

In this manuscript, He et al. set out to investigate the mechanisms behind Kupffer Cell death in MASLD. As has been previously shown, they demonstrate a loss of resident KCs in MASLD in different mouse models. They then go on to show that this correlates with alterations in genes/metabolites associated with glucose metabolism in KCs. To investigate the role of glucose metabolism further, they subject isolated KCs in vitro to different metabolic treatments and assess cleaved caspase 3 staining, demonstrating that KCs show increased Cl. Casp 3 staining upon stimulation of glycolysis. Finally, they use a genetic mouse model (Chil1KO) where they have previously reported that loss of this gene leads to increased glycolysis and validate this finding in BMDMs (KO). They then remove this gene specifically from KCs (Clec4fCre) and show that this leads to increased macrophage death compared with controls.

Strengths:

As we do not yet understand why KCs die in MASLD, this manuscript provides some explanation for this finding. The metabolomics is novel and provides insight into KC biology. It could also lead to further investigation; here, it will be important that the full dataset is made available.

Weaknesses:

Different diets are known to induce different amounts of KC loss, yet here, all models examined appear to result in 60% KC death. One small field of view of liver tissue is shown as representative to make these claims, but this is not sufficient, as anything can be claimed based on one field of view. Rather, a full tissue slice should be included to allow readers to really assess the level of death.

Thank you for raising this point regarding data presentation. We analyzed full tissue slices and found that including a view of the entire slice at a standard magnification makes individual KC difficult to resolve (Author response image 2). To clearly represent the extent and distribution of KCs death across the liver tissue slice, we now include lower-magnification images that provide a wider field of view, allowing readers to assess the pattern across a larger tissue area (Revised Figures 1, 2, 6F).

Author response image 2.

Assessment of KCs death on full liver tissue slice. (A) Immunofluorescence staining was performed to detect Kupffer cell (KC) death in liver sections from mice fed an MCD diet for 6 weeks. Cell death was assessed by TUNEL staining (green), and KCs were identified by TIM4 staining (red). Nuclei were counterstained with DAPI (blue). Representative whole-tissue view is shown. Scale bars, 1mm.

Additionally, there is no consistency between the markers used to define KCs and moMFs, with CLEC4F being used in microscopy, TIM4 in flow, while the authors themselves acknowledge that moKCs are CLEC4F+TIM4-. As moKCs are induced in MASLD, this limits interpretation. Additionally, Iba1 is referred to as a moMF marker but is also expressed by KCs, which again prevents an accurate interpretation of the data. Indeed, the authors show 60% of KCs are dying but only 30% of IBA1+ moMFs, as KCs are also IBA1+, this would mean that KCs die much more than moMFs, which would then limit the relevance of the BMDM studies performed if the phenotype is KC specific. Therefore, this needs to be clarified.

We thank the reviewer for the constructive comments. For consistency, we have standardized our KC marker to TIM4 for all immunostaining data, aligning it with our flow cytometry analysis (Revised Figures 1, 2D, 6F). We have also clarified that IBA1 is expressed by hepatic macrophages (both KCs and MoMFs)(Revised Figure 2C, Revised manuscript, page 5, lines 182-183). Moreover, we also included the clarification that 60% of TIM4⁺ KCs are TUNEL⁺ versus 30% of total IBA1⁺ cells further supports that KCs undergo death more readily than MoMFs (Revised manuscript, page 5, lines 186-189). We also acknowleged the limitation of BMDM studies in the Revised manuscript, page 8, line 332-340.

The claim that periportal KCs die preferentially is not supported, given that the majority of KCs are peri-portal. Rather, these results would need to be normalised to KC numbers in PP vs PC regions to make meaningful conclusions.

We thank the reviewer for this important point. We included the normalized data. At 8 weeks, the normalized death rate was significantly higher in periportal versus pericentral regions (p = 0.041), supporting increased periportal KC susceptibility during early MASLD. By 16 weeks, proportional death rates became comparable between zones (Revised Figure 2D, Revised manuscript, page 6, lines 194-201).

Additionally, KCs are known to be notoriously difficult to keep alive in vitro, and for these studies, the authors only examine cl. Casp 3 staining. To fully understand that data, a full analysis of the viability of the cells and whether they retain the KC phenotype in all conditions is required.

We appreciate the reviewer’s suggestions. To confirm the identity and health of isolated KCs in our in vitro studies, we showed that ~95% of primary isolated KCs are TIM4⁺ (Revised Figure S3A). Furthermore, Calcein-AM staining confirmed that the remaining KCs under our experimental conditions are viable and healthy (Revised Figure S4A).

Finally, in the Cre-driven KO model, there does not seem to be any death of KCs in the controls (rather numbers trend towards an increase with time on diet, Figure 6E), contrary to what had been claimed in the rest of the paper, again making it difficult to interpret the overall results.

We thank the reviewer for this comment. During our analysis, we indeed observed no reduction in KCs in the Clec4f cre control mice. This prompted us to consider that Cre insertion itself might influence KCs mainteinence. To investigate this, we performed TIM4/Ki67 co-staining, which revealed significantly higher numbers of proliferating KCs in Clec4f cre mice compared with C57BL/6J mice under NCD. Following HFHC feeding, KCs proliferation in Clec4f cre mice increased even further. These results indicate that Cre insertion enhanced KCs self-renewal in Clec4f cre mice，which contributes to maintenance of the KCs pool during MASLD (Revised Figures S8A and S8B). (Revised manuscript, page 9, line 363-370).

Additionally, there is no validation that the increased death observed in vivo in KCs is due to further promotion of glycolysis.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for five weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity in KCs. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data, together with our complementary in vitro gain-of-function experiments support a contributory role for excessive glycolytic activity in promoting KCs death in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

Reviewer #3 (Public review):

This manuscript provides novel insights into altered glucose metabolism and KC status during early MASLD. The authors propose that hyperactivated glycolysis drives a spatially patterned KC depletion that is more pronounced than the loss of hepatocytes or hepatic stellate cells. This concept significantly enhances our understanding of early MASLD progression and KC metabolic phenotype.

Through a combination of TUNEL staining and MS-based metabolomic analyses of KCs from HFHC-fed mice, the authors show increased KC apoptosis alongside dysregulation of glycolysis and the pentose phosphate pathway. Using in vitro culture systems and KC-specific ablation of Chil1, a regulator of glycolytic flux, they further show that elevated glycolysis can promote KC apoptosis.

However, it remains unclear whether the observed metabolic dysregulation directly causes KC death or whether secondary factors, such as low-grade inflammation or macrophage activation, also contribute significantly. Nonetheless, the results, particularly those derived from the Chil1-ablated model, point to a new potential target for the early prevention of KC death during MASLD progression.

The manuscript is clearly written and thoughtfully addresses key limitations in the field, especially the focus on glycolytic intermediates rather than fatty acid oxidation. The authors acknowledge the missing mechanistic link between increased glycolysis and KC death. Still, several interpretations require moderation to avoid overstatement, and certain experimental details, particularly those concerning flow cytometry and population gating, need further clarification.

Strengths:

(1) The study presents the novel observation of profound metabolic dysregulation in KCs during early MASLD and identifies these cells as undergoing apoptosis. The finding that Chil1 ablation aggravates this phenotype opens new avenues for exploring therapeutic strategies to mitigate or reverse MASLD progression.

(2) The authors provide a comprehensive metabolic profile of KCs following HFHC diet exposure, including quantification of individual metabolites. They further delineate alterations in glycolysis and the pentose phosphate pathway in Chil1-deficient cells, substantiating enhanced glycolytic flux through 13C-glucose tracing experiments.

(3) The data underscore the critical importance of maintaining balanced glucose metabolism in both in vitro and in vivo contexts to prevent KC apoptosis, emphasizing the high metabolic specialization of these cells.

(4) The observed increase in KC death in Chil1-deficient KCs demonstrates their dependence on tightly regulated glycolysis, particularly under pathological conditions such as early MASLD.

Weaknesses:

(1) The novelty is questionable. The presented work has considerable overlap with a study by the same lab, which is currently under review (citation 17), and it should be considered whether the data should not be presented in one paper.

We appreciate the reviewer for the opportunity to clarify the relationship between the two studies. In our previous work (citation 17), we focused on the transcriptional metabolic differences between Kupffer cells (KCs) and monocyte-derived macrophages (MoMFs) and identified Chi3l1 as a selective protective factor that limits glucose uptake and shields KCs from metabolic stress–induced cell death, with minimal effects on MoMFs. That study directly motivated the current work. The observation that KCs are uniquely protected from metabolic stress led us to hypothesize that excessive glycolytic activation itself may be a primary driver of KCs death, which forms the central question of the present study. Accordingly, the current manuscript shifts the focus from Chi3l1-mediated protection to the mechanistic role of hyperglycolysis in driving KCs mortality, using distinct experimental approaches and addressing a different biological question. Because the two studies address conceptually distinct aims—one defining a protective regulator of KCs survival and the other dissecting glycolysis-driven KCs death mechanisms—we believe they are best presented as separate manuscripts. Combining them into a single study would dilute the mechanistic depth and clarity of each story.

(2) The authors report that 60% of KCs are TUNEL-positive after 16 weeks of HFHC diet and confirm this by cleaved caspase-3 staining. Given that such marker positivity typically indicates imminent cell death within hours, it is unexpected that more extensive KC depletion or monocyte infiltration is not observed. Since Timd4 expression on monocyte-derived macrophages takes roughly one month to establish, the authors should consider whether these TUNEL-positive KCs persist in a pre-apoptotic state longer than anticipated. Alternatively, fate-mapping experiments could clarify the dynamics of KC death and replacement.

We thank the reviewer for this astute observation. As shown in revised Figure 2D, the proportion of TIM4⁺TUNEL⁺KCs peaks at 8 weeks after HFHC feeding and remains elevated at 16 weeks. However, examination of the corresponding single-channel TIM4 staining during this period reveals that the overall density of TIM4⁺ KCs does not undergo abrupt or synchronous depletion. This temporal dissociation between sustained TUNEL positivity and relatively gradual KCs loss suggests that TUNEL-positive KCs do not undergo immediate clearance. Based on these observations, we agree with the reviewer that a substantial fraction of TUNEL-positive KCs likely persists in a prolonged pre-apoptotic or stressed state rather than undergoing rapid cell death. This interpretation is consistent with the absence of extensive KCs depletion or compensatory monocyte infiltration at these time points. Importantly, previous studies (Ref. 1,2) indicate that KCs are eventually lost as MASLD progresses, supporting the notion that KC death is a gradual process that unfolds over an extended time frame rather than acutely.

(3) The mechanistic link between elevated glycolytic flux and KC death remains unclear.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for five weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity of KCs. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data, together with our complementary in vitro gain-of-function experiments, support a contributory role for excessive glycolytic activity in promoting KC apoptosis in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

(4) The study does not address the polarization or ontogeny of KCs during early MASLD. Given that pro-inflammatory macrophages preferentially utilize glycolysis, such data could provide valuable insight into the reason for increased KC death beyond the presented hyperreliance on glycolysis.

We thank the reviewer for this insightful comment. Regarding KCS ontogeny, flow cytometry analysis (Revised Figure 1C) shows that KCs remain uniformly TIM4^hi during early MASLD, indicating that monocyte-derived KCs (TIM4^low) have not yet emerged at these stages. To address KCs polarization, we assessed the expression of M1-type (pro-inflammatory) markers (Nos2, Cxcl9, CIITA, Cd86, Ccl3, and Ccl5) and M2-type (anti-inflammatory) markers (Chil3, Retnla, Arg1, and Mrc1) in KCs isolated from WT mice fed a HFHC diet for 0, 8, and 16 weeks. As shown in revised Figure S5A, M1 markers progressively increase over time, whereas M2 markers remain unchanged or slightly decrease. This polarization shift is consistent with the increased glycolytic activity observed in KCs during early MASLD. Together, these data indicate that embryonically derived KCs undergo a pro-inflammatory polarization accompanied by enhanced glycolytic metabolism during early MASLD, providing mechanistic context for their increased susceptibility to metabolic stress–induced cell death beyond hyperreliance on glycolysis alone (Revised manuscript, page 7-8, line 307-321).

(5) The gating strategy for monocyte-derived macrophages (moMFs) appears suboptimal and may include monocytes. A more rigorous characterization of myeloid populations by including additional markers would strengthen the study's conclusions.

We thank the reviewer for raising this important point. To improve the rigor of our analysis, we adopted gating strategies established in previous studies (PMID: 41131393; PMID: 32562600). Specifically, Kupffer cells were defined as CD45⁺CD11b⁺F4/80^hi TIM4^hi cells, while monocyte-derived macrophages (MoMFs) were defined as CD45⁺Ly6G^-CD11b⁺F4/80^low TIM4^low/− cells, thereby excluding contaminating neutrophils and minimizing inclusion of circulating monocytes. Using this refined gating strategy, we observed a progressive reduction of KCs accompanied by a corresponding increase in MoMFs in WT mice during HFHC feeding (Revised Figures 1C and S2B–C), (Revised manuscript, page 4, line 154-163).

(6) While BMDMs from Chil1 knockout mice are used to demonstrate enhanced glycolytic flux, it remains unclear whether Chil1 deficiency affects macrophage differentiation itself.

We thank the reviewer for this important question. To determine whether Chi3l1 deficiency affects macrophage differentiation, we analyzed the expression of M1-type (pro-inflammatory) markers (Nos2, Cxcl9, CIITA, Cd86, Ccl3, and Ccl5) and M2-type (anti-inflammatory) markers (Chil3, Retnla, Arg1, and Mrc1) in Kupffer cells isolated from WT and Chil1^-/- mice fed a HFHC diet for 0, 8, and 16 weeks. At baseline (0 weeks), Chi3l1 deficiency was associated with elevated expression of multiple M1 markers, whereas M2 marker expression was comparable between WT and Chil1^-/- KCs. During MASLD progression, the pro-inflammatory signature in Chil1^-/- KCs was further enhanced, while anti-inflammatory marker expression became dysregulated (revised Figure S5C). Together, these data indicate that Chi3l1 deficiency does not impair macrophage differentiation per se but biases KCs toward a partially pro-inflammatory, M1-like phenotype, providing additional context for the enhanced glycolytic flux observed in Chi3l1-deficient macrophages (Revised manuscript, page 7-8, line 307-321).

(7) The authors use the PDK activator PS48 and the ATP synthase inhibitor oligomycin to argue that increased glycolytic flux at the expense of OXPHOS promotes KC death. However, given the high energy demands of KCs and the fact that OXPHOS yields 15-16 times more ATP per glucose molecule than glycolysis, the increased apoptosis observed in Figure 4C-F could primarily reflect energy deprivation rather than a glycolysis-specific mechanism.

We thank the reviewer for highlighting this important point. We agree that KCs are highly metabolically active and that perturbations of OXPHOS can influence overall cellular energy balance. As noted in our response to comment #3, we further performed glycolysis inhibition assay by 2-DG in vivo, the protection of KCs observed following 2-DG in vivo (Revised Figure 4E-G) further provides evidence that increased glycolytic flux is not merely correlated with, but functionally contributes to KCs loss in

MASLD.

(8) In Figure 1C, KC numbers are significantly reduced after 4 and 16 weeks of HFHC diet in WT male mice, yet no comparable reduction is seen in Clec4Cre control mice, which should theoretically exhibit similar behavior under identical conditions.

We thank the reviewer for this comment. During our analysis, we indeed observed no reduction in KCs in the Clec4f cre control mice. This prompted us to consider that Cre insertion itself might influence KCs mainteinence. To investigate this, we performed TIM4/Ki67 co-staining, which revealed significantly higher numbers of proliferating KCs in Clec4f cre mice compared with C57BL/6J mice under NCD. Following HFHC feeding, KCs proliferation in Clec4f cre mice increased even further. These results indicate that Cre insertion enhanced KCs self-renewal in Clec4f cre mice，which contributes to maintenance of the KCs pool during MASLD (Revised Figures S8A and S8B). (Revised manuscript, page 9, line 363-370).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

To address the concerns raised in the public review, the authors should:

(1) Reassess their conclusions using the same panels in flow and microscopy, e.g., the combination of CLEC4F, TIM4, and IBA1. This will allow resKCs (CLEC4F+TIM4+IBA1+), moKCs (CLEC4F+TIM4-IBA1+), and moMFs (CLEC4F-TIM4-IBA1+) to be accurately defined and hence their viability and numbers correctly assessed.

We thank the reviewer for this insightful suggestion. In our flow cytometry analysis, we did not detect a CD45⁺CD11b^lowF4/80^hiTIM4^low population, indicating that monocyte-derived KCs (moKCs) have not emerged in our model at this stage. To more accurately quantify resident KCs (resKCs) in the current study, we replaced CLEC4F with TIM4 staining and enumerated TIM4⁺as well as TIM4⁺TUNEL⁺ cells. These data were highly consistent with CLEC4F⁺TUNEL⁺cell counts, confirming that moKCs are not involved in KCs death during early MASLD (Revised Figure 1A,B,E,F).

(2) Investigate why the number of KCs in controls and MASLD are so distinct between Figures 1 and 6.

We appreciate the reviewer’s suggestions. Like we explained above, Cre insertion promotes KCs self-renewal (Revised manuscript, Figure S8). This enhanced proliferative capacity likely accounts for the relative preservation of KCs numbers in Clec4f-Cre mice during HFHC feeding, explaining the apparent discrepancy with WT mice (Revised manuscript, Figure 6D-E).

(3) Normalise the tunel+ cells based on the number of KCs in PP vs PC regions.

After normalizing KCs death to KCs numbers in periportal (PP) versus pericentral (PC) regions, we found the proportion was significantly higher in PV regions compared to CV regions at 8 weeks of HFHC feeding. We have therefore revised our texts. (Revised manuscript, page 5, lines 194-201).

(4) Demonstrate the viability of KCs in vitro across conditions.

To confirm the identity and health of isolated KCs in our in vitro studies, we show that ~95% of primary isolated KCs are TIM4⁺ (Revised Figure S3A). Furthermore, Calcein-AM staining confirmed that the remaining KCs under our experimental conditions are viable and healthy (Revised Figure S4A).

(5) Confirm previous studies demonstrating different degrees of KC loss depending on the model of MASLD.

We thank the reviewer for highlighting this point. Consistent with previous studies, KCs loss has been reported to varying degrees depending on the MASLD model used, reflecting the heterogeneity of hepatic macrophages, marker choice, mouse husbandry, and diet regimen. For example, in a 6-week MCD feeding model, ~10% of CLEC4F⁺ KCs were TUNEL⁺ (Figure 4A, Ref. 9). Another 6-week MCD study reported a drop from 66% to 26% TIM4⁺ KCs (Figure 2A, Ref. 12). In an HFD model, TIM4⁺ KCs decreased by ~20% after 16 weeks (Figure 1G, Ref. 1). In a Western diet model, TIM4⁺KCs decreased by >50% at 36 weeks (Figures 1J and 2C, Ref. 2). Together, these studies underscore the model-dependent nature of KCs loss and highlight the importance of experimental context and marker selection when assessing KCs dynamics in MASLD. We have included these studies in our discussion section (Revised manuscript, page 9-10, line 393-402)

(6) Demonstrate in vivo that loss of CHIL1 drives further glycolysis in KCs.

In Figure 6G-H of our previous study, we showed that Chi3l1 deficiency leads to more glucose uptake by KCs in vivo whereas suppelementing KO mice with recombinant Chi3l1 will significantly reduced glucose uptake by KCs through treating mice with a fluorescent glucose analog 2-NBDG. We included the related figure here as Author response image 3.

Author response image 3.

Chi3l1 limits glucose uptake by Kupffer cells in vivo. (A) Measurement of 2-NBDG (a fluorescent glucose analog) uptake by KCs in vivo. WT and Chil1^-/- mice, either untreated or supplemented with rChi3l1, were injected intraperitoneally with 12 mg/kg 2-NBDG. After 45mins, KCs were isolated and glucose uptake assessed by spectrophotometry. (B) Representative immunofluorescence images of liver sections stained for TIM4 (red) and 2-NBDG uptake (green) to visualize glucose uptake by KCs in situ. Scale bar = 10 µm (zoom). Quantification is shown as the percentage of TIM4⁺ cells that are also 2-NBDG⁺. Representative images were shown in B. One-way ANOVA was performed in A, B. P value is as indicated.

(7) There is no mention of the publication of the metabolomics dataset; this should be released with the manuscript.

We included the raw metabolomics dataset as Table S1 and S2 now.

Reviewer #3 (Recommendations for the authors):

(1) Methods: Reconsider which methods are described in the main text versus the Supplementary Information to improve readability and consistency.

Thank you for your valuable suggestion. We have reevaluated and adjusted the placement of the methods section between the main text and the supplementary materials.

(2) Line 34: Check for grammar issues.

L34 has been revised as follows : Additionally, using Chi3l1-deficient mice, we further demonstrated that increased glucose utilization accelerates KCs death in vivo.

(3) Lines 101, 110: Explicitly reference the corresponding Supplementary Methods sections.

We have included the references for these two methods sections (Revised supplementary materials and methods, Line 30, 65, respectively).

(4) Figure 2: Iba1 marks all macrophages, not only monocyte-derived macrophages; both figure and text (line 205) require correction.

We have corrected Iba1 represent hepatic macrophages including both KCs and MoMFs (Revised Figure 2C, manuscript page 5, line 182).

(5) Line 218-219: Avoid overinterpretation, as only KCs, hepatocytes, and hepatic stellate cells were assessed - not all hepatic populations.

We appreciate the reviewer’s valuable suggestion and rephrased our description accordingly (Revised manuscript, page 5, line 186-189).

(6) Line 262: Use abbreviations consistently throughout the manuscript.

We have gone through the whole manuscript and double checked the abbreviations.

(7) Line 264: Include the palmitic acid (PA) concentration used.

We included 800 µM PA in the revised manuscript (Revised manuscript, page 6, line 250).”

(8) Lines 316-317: Check for grammar errors.

Grammar errors are checked (Revised manuscript, page 8, line 340-341).

(9) Line 337-338: See comment above on gating strategy.

We updated gating strategy accordingly (Revised manuscript, page 9, line 361-362).

(10) Line 343-344: Note that Chi3l1 is not exclusively expressed by KCs.

We rephrased our words accordingly (Revised manuscript, page 9, line 374-378).

(11) Lines 355-358: The statement that "sustained glycolytic hyperactivation culminates not in sustained activation, but in apoptotic cell death" is unsupported by data or literature, as macrophage polarization was not analyzed in this study.

We removed the statement from the revised manuscript.

(12) Lines 375-379: Rephrase to clarify that while KCs are metabolically active and glucose-demanding, excessive glycolytic flux accelerates apoptosis.

We have rephrased to clarify (Revised Manuscript, page 10, lines 405-407).

(13) Lines 375-385 & 387-397: Consolidate overlapping statements for conciseness and coherence.

We have consolidate the overlapping statements (Revised manuscript, page 10, lines 405-425).

Reference

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Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors aimed to identify the molecular target and mechanism by which α-Mangostin, a xanthone from Garcinia mangostana, produces vasorelaxation that could explain the antihypertensive effects. Building on prior reports of vascular relaxation and ion channel modulation, the authors convincingly show that large-conductance potassium BK channels are the primary site of action. Using electrophysiological, pharmacological, and computational evidence, the authors achieved their aims and showed that BK channels are the critical molecular determinant of mangostin's vasodilatory effects, even though the vascular studies are quite preliminary in nature.

Strengths:

(1) The broad pharmacological profiling of mangostin across potassium channel families, revealing BK channels - and the vascular BK-alpha/beta1 complex - as the potently activated target in a concentration-dependent manner.

(2) Detailed gating analyses showing large negative shifts in voltage-dependence of activation and altered activation and deactivation kinetics.

(3) High-quality single-channel recordings for open probability and dwell times.

(4) Convincing activation in reconstituted BKα/β1-Ca_v nanodomains mimicking physiological conditions and functional proof-of-concept validation in mouse aortic rings.

We thank the reviewer for acknowledging the strength of the different aspects investigated in our study.

Weaknesses are minor:

(1) Some mutagenesis data (e.g., partial loss at L312A) could benefit from complementary structural validation.

In the attempt to improve structural insight for the presented mutagenesis data, we have used Alphafold3 (AF3; Abramson et al., 2024) to generate models of the I308A, L312M and A316P substitutions and repeated the docking for each (Fig. R1). According to these predictive models,

The I308A substitution considerably straightens the S6 helix starting at this residue. Hence, all residues are displaced relative to the WT: C_a of L312, F315, and A316 are displaced by 2.8 Å, 4.2 Å, and 4.6 Å, respectively, widening the bottom of the binding pocket. However, the prediction confidence is rated lower as in the other AF3 models for all helices (70 > plDDT > 50). In the docking, poses in the binding pocket comparable to these observed in the WT (i.e. involving I308A, L312 and A316) and with the same molecule orientation have higher binding energies (-7.13 to -6.66 kcal mol^-1). Additionally, poses without contact to I308A arise that have a more vertical position, indicating that the structural change affects the binding region.

The changes induced by L312M are localized to residues 313-323, where S6 bends towards S5. Binding energies are lower especially in the best 2 poses that are also most comparable to the WT docking (-9.88 kcal mol^-1), but clustering overall is poor and poses are more heterogeneous. Interactions with L312M are completely abolished, while interactions with I308 (in 11/20 poses), F315 (in all poses), and A316 (in 5/20 poses) persist. Because of the rather small structural alteration induced by the substitution and the variable poses one could speculate that the reduced V_½ shift is due to the observed loss in binding to L312M; however, retained interactions to the other residues would still allow α-Mangostin to activate.

A316P induces a displacement of the S6 helix compared to the WT while the other pore helices are not affected. S6 shows an enhanced outward bending around A316, which results in displacements of residues where a-Mangostin would bind, i.e., the C_a of F315 and L312M are displaced by 2.4 Å and 2.8 Å (I308 is not affected). Residues below are moved in a more rotational way, resulting in a C_a displacement of 3.1 Å for Y318 and even 5.7 Å for V319, before displacements decrease again towards the intracellular helix end. While interactions with A316P are present in 10/20 analyzed poses, the helix displacement seems to hinder I308 and L312 interactions, as the best docked a-Mangostin pose (-8.41 kcal mol^-1) is predicted to only contact F315 and Y318, and overall, any I308 or L312 contacts only occurred in 3/20 and 7/20 poses (wildtype: 17/20 and 20/20 poses). This may hint at a mechanism where A316P probably has a substantial allosteric share in reducing the V_½ shift induced by a-Mangostin and underlines the exceptional effect of this mutation (i.e., complete loss of a V_½ shift).

Author response image 1.

Alphafold3 models of BK I308A, L312M, and A316P with α-Mangostin docked to the mutant structures. The upper row shows an overview of the mutant pore helices (AF3 models) used for molecular docking. The lower row shows the binding region with the wildtype structure overlaid in gray. Only 3 helices are shown for clarity.

Although these results provide interesting tentative explanations for the effect of the mutations and conclusions from AF3 models become increasingly robust, we think that definitive statements of their mechanistic contributions would require experimental studies of mutant channels, i.e., cryo-EM or crystallography, that are beyond our means. Therefore, we have decided not to include this data in the manuscript; however, it is accessible for the interested reader within the public review. Hopefully, as cryo-EM structures have been obtained for the wildtype channel, there will be studies on mutations of this gating-relevant S6 segment in the future.

(2) While Cav-BK nanodomains were reconstituted, direct measurement of calcium signals after mangostin application onto native smooth muscle could be valuable.

We are not sure if a global elevation of cellular calcium concentration would be informative. We rather expect that the relevant local Ca²⁺ elevation would occur as sparks in the BK-Ca_v nanodomains, close to the membrane. We would anticipate a change in spark duration, as the Ca²⁺ inward current would be stopped faster by the enhanced repolarization via a-Mangostin activated BKα/β1 channels. This would require fast Ca²⁺ imaging acquisition speed to capture spark activity. We concur that this would be an informative experiment to investigate a more native situation. However, we would have to accomplish such methodologically challenging measurements in a separate project, which could fruitfully be combined with a more extensive characterization of aortic contraction as also suggested in the following remark (3).

(3) The work has an impact on ion channel physiology and pharmacology, providing a mechanistic link between a natural product and vasodilation. Datasets include electrophysiology traces, mutagenesis scans, docking analyses, and aortic tension recordings. The latter, however, are preliminary in nature.

We completely agree with the reviewer that there is ample room for further studies that could characterize different tissues important in blood pressure regulation (such as resistance arteries), elucidate even more physiological detail (such as modulatory effects of the endothelium), or look deeper into the pharmacology using chemically altered Mangostin derivatives. While we very much like this to happen in future projects, in this study we focused on the functional aspects of a-Mangostin in BK channel gating. We present our tension recordings as a proof-of-concept to underline the activity of a-Mangostin in native tissues, and we clearly show the importance of the BK channel by using iberiotoxin as a specific inhibitor which impressively abolished relaxation.

References:

Abramson, J. et al. (2024) “Accurate structure prediction of biomolecular interactions with AlphaFold 3,” Nature, 630(8016), pp. 493–500. Available at: https://doi.org/10.1038/s41586-024-07487-w.

Reviewer #2 (Public review):

Summary:

In the present manuscript, Cordeiro et al. show that α-mangostin, a xanthone obtained from the fruit of the Garcinia mangostana tree, behaves as an agonist of the BK channels. The authors arrive at this conclusion through the effect of mangostin on macroscopic and single-channel currents elicited by BK channels formed by the α subunit and α + β1 sununits, as well as αβ1 channels coexpressed with voltage-dependent Ca2+ (CaV1,2) channels. The single-channel experiments show that α-mangostin produces a robust increase in the probability of opening without affecting the single-channel conductance. The authors contend that α-mangostin activation of the BK channel is state-independent and molecular docking and mutagenesis suggest that α-mangostin binds to a site in the internal cavity. Importantly, α-mangostin (10 μM) alleviates the contracture promoted by noradrenaline. Mangostin is ineffective if the contracted muscles are pretreated with the BK toxin iberiotoxin.

Strengths:

The set of results combining electrophysiological measurements, mutagenesis, and molecular docking reveals α-mangostin as a potent activator of BK channels and the putative location of the α-mangostin binding site. Moreover, experiments conducted on aortic preparations from mice suggest that α-mangostin can aid in developing drugs to treat a myriad of diverse diseases involving the BK channel.

We thank the reviewer for pointing out the significance of our study.

Weaknesses:

Major:

(1) Although the results indicate that α-mangostin is modifying the closed-open equilibrium, the conclusion that this can be due to a stabilization of the voltage sensor in its active configuration may prove to be wrong. It is more probable that, as has been demonstrated for other activators, the α-mangostin is increasing the equilibrium constant that defines the closed-open reaction (L in the Horrigan, Aldrich allosteric gating model for BK). The paper will gain much if the authors determine the probability of opening in a wide range of voltages, to determine how the drug is affecting (or not), the channel voltage dependence, the coupling between the voltage sensor and the pore, and the closed-open equilibrium (L).

We would like to take the opportunity to clarify this potential misunderstanding. In our manuscript, we have discussed three mechanistic explanations for the Mangostin activation: (1) an electrostatic effect at the selectivity filter, (2) structural and electrostatic changes of S6 that facilitate the opening of a putative lower gate, and (3) hydrophobic gating, i.e., counteracting dewetting of the pore. All possibilities would impact S6 and lower the free energy for pore opening, and we concur that therefore Mangostin most likely affects the closed-open equilibrium (L) of the BKα channel.

The sentence at the original lines 470-471, “(…) caused by an enhanced shift of the closed-open equilibrium toward the open state, such as the stabilization of the voltage sensor in an active conformation” refers to the observation that the presence of the β1 subunit enhances this closed-open shift. The stabilization of the voltage sensor domain was mentioned as one example of how it achieves this. We recognize that this example was an unfortunate choice, as β1 rather facilitates Ca²⁺-dependent allosteric pore opening unrelated to the discussed mechanisms of Mangostin. We have therefore removed this statement.

As to the suggestion to dissect the effect of Mangostin on C, D, and L, we agree with the reviewer that this would surely add to a full biophysical characterization. However, in our project, we strove towards including more experiments showing the physiological implications of Mangostin activation to emphasize the implication for vasodilation. We hope the reviewer understands that, with limited resources, this came at the expense of a full investigation of the different gating components, which could pose a separate project by itself.

(2) Apparently, the molecular docking was performed using the truncated structure of the human BK channel. However, it is unclear which one, since the PDB ID given in the Methods (6vg3), according to what I could find, corresponds to the unliganded, inactive PTK7 kinase domain. Be as it may, the apo and Ca2+ bound structures show that there is a rotation and a displacement of the S6 transmembrane domain. Therefore, the positions of the residues I308, L312, and A316 in the closed and open configurations of the BK channel are not the same. Hence, it is expected that the strength of binding will be different whether the channel is closed or open. This point needs to be discussed.

We apologize for the typing error and thank the reviewer for indicating this erroneous PDB ID. (“6vg3”). It should have read PDB ID 6v3g as in the legend to Fig. 4B. The reviewer appropriately points out that there are differences in the S6 segment addressed in our study between the two available cryo-EM structures obtained in the presence (PDB ID 6v38) and absence of Ca²⁺ (PDB ID 6v3g) (Tao and MacKinnon, 2019).

We had actually performed the docking with both structures, but chosen to show the Ca²⁺-free structure to better visualize the I308 position. a-Mangostin is found in the same S6 region in both, not obstructing the K⁺ conduction pathway. The binding energies of the favored poses are very similar; the binding energy in the best-ranking conformational cluster in the Ca²⁺-bound structure even was slightly lower (-8.64 kcal mol^-1) than in the docking with the Ca²⁺-free channel (-8.58 kcal mol^-1; Fig. 4B), which may not be a relevant difference.

We compared the residue interactions in both dockings (Author response table 1). S317 and Y318, which did not reduce the shift in V_½ upon substitution, were not predicted to contact a-Mangostin in either structure. In both structures, L312 and F315 were predicted to interact in virtually all poses analyzed. In the docking to the Ca²⁺-free state, also I308 was predicted to interact in 17/20 poses, while contacts to A316 occurred in 5/20 poses. In the Ca²⁺-bound state, predicted interactions shifted from I308 (which is expected as it is buried in the protein) to A316, and the isoprenyl moiety close to I308 rotated downwards. This could indicate that a-Mangostin adopts a more horizontal position following the upward reorientation of S6 in the Ca²⁺-bound state when the channel moves from one to the other conformation (Fig. S4).

Author response table 1.

Number of interactions of S6 residues in 20 analyzed α-Mangostin poses in the molecular dockings to the Ca2+-free and Ca2

These docking results are consistent with our functional measurements. Recent structures of the BK/γ1 complex showed that the VSD and Ca²⁺-bowl are stabilized in an active-like conformation that corresponds to the conformation seen in the Ca²⁺-bound state (Kallure et al., 2023; Yamanouchi et al., 2023; Redhardt, Raunser and Raisch, 2024), indicating that very likely the Ca²⁺-bound and Ca²⁺-free structures indeed represent open and closed conformations of the channel. We observed that α-Mangostin can bind to both of these states to activate the channel (Fig. 3C, D), showing the presence of a binding site in both conformations. Further, α-Mangostin induced a left-shift in V_½ also in higher Ca²⁺ concentration (Fig. 2D), indicating that it still binds to and activates the channel after the conformational change in S6. As we could not determine affinity for the mutants due to limited solubility, we have no information on the nature of the contribution of the substitutions, i.e., reduced binding or allosteric effect. As I308 is buried in the Ca²⁺-bound state, its contribution is likely mostly allosteric. We have also proposed dewetting as possible activation mechanism, which we expect to be less sensitive to the exact pose of a molecule (as shown for NS11021, Nordquist et al., 2024). Therefore, α-Mangostin could, e.g., change solvent accessibility of the I308 sidechain, energetically favoring the buried (open) state.

We have now included both dockings and Author response table 1 in Fig. S4, and we have added passages to the results section (starting at line 373) and discussion section (starting at lines 544, 588).

Minor:

(1) From Figure 3A, it is apparent that the increase in Po is at the expense of the long periods (seconds) that the channel remains closed. One might suggest that α-mangostin increases the burst periods. It would be beneficial if the authors measured both closed and open dwell times to test whether α-mangostin primarily affects the burst periods.

We thank the reviewer for this valuable suggestion, which we have implemented. In our single channel measurements shown in our original Fig. 3 we have not observed burst behavior of the BKɑ channels. This can be explained by the fact that we measured in resting condition (100 nM free Ca_i</sup>2+</sup>) and with rather mild depolarisation (+40 mV) where Po was very low. We have therefore analyzed measurements in 5 µM free a_i</sup>2+</sup> where we recorded sufficient burst activity also in the basal state.

The burst analysis showed that ɑ-Mangostin indeed prolongs bursts and shortens the interburst closures. Within bursts, both closed times and open times were increased, and we recorded a higher number of opening events per burst. We conclude that ɑ-Mangostin acts in both the closed and the open state, where it slows open-closed transitions resulting in less flicker, and stabilizes the open state via longer open times and a higher probability for closed-open transitions.

We now show this data in Fig. 3D-F and Table S8, and have accordingly added passages to the results section (starting at line 285), the discussion (line 510), and the methods section (starting at line 746).

(2) In several places, the authors make similarities in the mode of action of other BK activators and α-mangostin; however, the work of Gessner et al. PNAS 2012 indicates that NS1619 and Cym04 interact with the S6/RCK linker, and Webb et al. demonstrated that GoSlo-SR-5-6 agonist activity is abolished when residues in the S4/S5 linker and in the S6C region are mutated. These findings indicate that binding of the agonist is not near the selectivity filter, as the authors' results suggest that α-mangostin binds.

We will gladly clarify our ideas concerning the binding sites of other activators and ɑ-Mangostin. We first hypothesized that ɑ-Mangostin may share characteristics and mode of action with the class of negatively charged activators (NCA) that we have described before (Schewe et al., 2019). NCA were found to occupy a common fenestration site that is located close to the selectivity filter in TREK K2P channels, and in this manuscript we have shown by THexA competition and mutagenesis experiments that ɑ-Mangostin also binds in this fenestration region in TREK-1 channels (Fig. S3).

The existence of this common NCA binding site was also proposed for BK channels, as a docking placed the NCA NS11021 in an equivalent binding region, and, among others, NS11021 and GoSlo-SR-5-6 competed with THexA for binding in the pore (Schewe et al., 2019). These results were indeed not fully in agreement with the proposed binding site of GoSlo-SR-5-6 in Webb et al. (2015), although the most effective (double) mutants were located at S317 and I323, at the intracellular end of the cleft between neighboring S6 segments. In this manuscript, we have shown that α-Mangostin is present in the pore of BK channels by molecular docking, a THexA competition assay, and two mutations that reduced the shift in V_½ induced not only by ɑ-Mangostin but also by GoSlo-SR-5-6 (Fig. 4). While the docking was rather a starting point, both functional tests argue against a binding site in the S4/5 linker/S6C region; however, allosteric mechanisms could still reduce activation also in mutants in the S4/5 linker/S6C region far from the pore binding region proposed by us in the 2019 study and the present manuscript.

To summarize, we did not mean to imply that all BK activators should bind to this site, especially if they are not part of the NCA class (as NS1619, Cym4, as well as BC5, whose different binding site enabled us to use it as a control in our THexA competition assay). However, the cleft close to gating relevant S6 residues may well pose a region especially susceptible to modulator binding (as BL-1249, GoSlo-SR-5-6, and ɑ-Mangostin). We have moved, respectively separated, the initial GoSlo references from the reference to the pore binding site in the paragraph (lines329, 358) to improve clarity.

(3) The sentence starting in line 452 states that there is a pronounced allosteric coupling between the voltage sensors and Ca2+ binding. If the authors are referring to the coupling factor E in the Horrigan-Aldrich gating model, the references cited, in particular, Sun and Horrigan, concluded that the coupling between those sensors is weak.

We are grateful for the opportunity to improve this passage. We intended to express that observed effects (in this case the shift in V_½) are pronounced around 1 µM Ca²⁺. As the reviewer states, the coupling factor between the voltage and calcium sensors (E; 2.4) is weak compared to the coupling of Ca²⁺ (C; 8) and voltage (D; 25) to the pore in the Horrigan-Aldrich model. However, the shape of the Ca²⁺-dependence of V_½ cannot be completely described when E is neglected, with the highest difference around 1-2 µM Ca²⁺ (Horrigan and Aldrich, 2002). Deletion of the gating ring underlines the allosteric sensor coupling (Clay, 2017). This together with the steep Ca²⁺-dependence in this concentration range (meaning high Po changes upon occupancy increase; Cui, Cox and Aldrich, 1997) explains the higher apparent activation, visible as the higher shift in V_½ observed at the 1 µM Ca²⁺. Speaking with the model of Sun and Horrigan (2022), the suppressing “molecular logic gate” is already relieved by the presence of intermediate Ca²⁺, and the direct “gating lever” pathway via voltage acts synergistically and achieves the observed higher V_½ shift upon depolarization. We have adapted the sentence and separated the citations for better understanding (lines 503-507).

References:

Clay, J.R. (2017) “Novel description of the large conductance Ca2+-modulated K+ channel current, BK, during an action potential from suprachiasmatic nucleus neurons,” Physiological Reports, 5(20), p. e13473. Available at: https://doi.org/10.14814/phy2.13473.

Cui, J., Cox, D.H. and Aldrich, R.W. (1997) “Intrinsic Voltage Dependence and Ca2+ Regulation of mslo Large Conductance Ca-activated K+ Channels,” Journal of General Physiology, 109(5), pp. 647–673. Available at: https://doi.org/10.1085/jgp.109.5.647.

Horrigan, F.T. and Aldrich, R.W. (2002) “Coupling between voltage sensor activation, Ca2+ binding and channel opening in large conductance (BK) potassium channels,” The Journal of General Physiology, 120(3), pp. 267–305. Available at: https://doi.org/10.1085/jgp.20028605.

Kallure, G.S. et al. (2023) “High-resolution structures illuminate key principles underlying voltage and LRRC26 regulation of Slo1 channels.” bioRxiv, p. 2023.12.20.572542. Available at: https://doi.org/10.1101/2023.12.20.572542.

Nordquist, E.B., Jia, Z., Chen, J., 2024. “Small Molecule NS11021 Promotes BK Channel Activation by Increasing Inner Pore Hydration.” J. Chem. Inf. Model. 64, 7616–7625. https://doi.org/10.1021/acs.jcim.4c01012

Redhardt, M., Raunser, S. and Raisch, T. (2024) “Cryo-EM structure of the Slo1 potassium channel with the auxiliary γ1 subunit suggests a mechanism for depolarization-independent activation,” FEBS Letters, 598(8), pp. 875–888. Available at: https://doi.org/10.1002/1873-3468.14863.

Schewe, M. et al. (2019) “A pharmacological master key mechanism that unlocks the selectivity filter gate in K + channels.,” Science, 363(6429), pp. 875–880. Available at: https://doi.org/10.1126/science.aav0569.

Sun, L. and Horrigan, F.T. (2022) “A gating lever and molecular logic gate that couple voltage and calcium sensor activation to opening in BK potassium channels,” Science Advances, 8(50), p. eabq5772. Available at: https://doi.org/10.1126/sciadv.abq5772.

Tao, X. and MacKinnon, R. (2019) “Molecular structures of the human Slo1 K+ channel in complex with β4,” eLife 8, p. e51409. Available at: https://doi.org/10.7554/eLife.51409.

Webb, T.I. et al. (2015) “Molecular mechanisms underlying the effect of the novel BK channel opener GoSlo: Involvement of the S4/S5 linker and the S6 segment,” Proceedings of the National Academy of Sciences, 112(7), pp. 2064–2069. Available at: https://doi.org/10.1073/pnas.1400555112.

Yamanouchi, D. et al. (2023) “Dual allosteric modulation of voltage and calcium sensitivities of the Slo1-LRRC channel complex,” Molecular Cell, 83(24), pp. 4555-4569.e4. Available at: https://doi.org/10.1016/j.molcel.2023.11.005.

Reviewer #3 (Public review):

Summary:

This research shows that a-mangostin, a proposed nutraceutical, with cardiovascular protective properties, could act through the activation of large conductance potassium permeable channels (BK). The authors provide convincing electrophysiological evidence that the compound binds to BK channels and induces a potent activation, increasing the magnitude of potassium currents. Since these channels are important modulators of the membrane potential of smooth muscle in vascular tissue, this activation leads to muscle relaxation, possibly explaining cardiovascular protective effects.

Strengths:

The authors present evidence based on several lines of experiments that a-mangostin is a potent activator of BK channels. The quality of the experiments and the analysis is high and represents an appropriate level of analysis. This research is timely and provides a basis to understand the physiological effects of natural compounds with proposed cardio-protective effects.

We sincerely thank the reviewer for appraising the achievements of our study.

Weaknesses:

The identification of the binding site is not the strongest point of the manuscript. The authors show that the binding site is probably located in the hydrophobic cavity of the pore and show that point mutations reduce the magnitude of the negative voltage shift of activation produced by a-mangostin. However, these experiments do not demonstrate binding to these sites, and could be explained by allosteric effects on gating induced by the mutations themselves.

We are aware that our functional data are unfortunately not sufficient to clearly distinguish between effects due to affinity loss or due to allosteric mechanisms. Our attempts to generate complete dose–response curves for the mutants to determine accurate apparent IC₅₀ values were unfortunately limited by the solubility of the compound. Consequently, we have avoided making claims about affinity loss in the mutant analysis, and have instead only reported the reduction in potency, expressed as the shift in V_½. To reduce confounding effects from the mutations themselves, we selected substitutions that preserved the most wildtype-like GV-relationships, based on the extensive mutagenesis work of (Chen, Yan and Aldrich, 2014). We address this matter also in our answer to Recommendation (6) below, and we have replaced the word “binding” in the title of the manuscript. Nevertheless, we consider the proposed binding region to be well supported by the THexA competition experiments in combination with molecular docking, even though the specific mechanistic contributions of individual residues cannot yet be resolved.

Reviewer #3 (Recommendations for the authors):

(1) Natural xanthones as α-Mangostin induce vasorelaxation via binding to key gating residues in the S6 domain of BK channels.

(2) If α-Mangostin occupies a similar binding site to quaternary ammoniums, what is the explanation for not observing a reduction in the single-channel current (fast blocking effect)? The α-Mangostin site proposed here is in a region of the channel that should occlude ion permeation. The authors should discuss possible explanations for this apparently contradictory observation.

As the reviewer states, we indeed have not observed a reduced single channel amplitude in any measurement. The THexA competition assay showed that ɑ-Mangostin is present in the pore cavity and interferes with THexA access to its binding site. However, we do not think that their binding sites are similar, as QA ions bind directly below the filter entrance to block permeation, while our studies suggest that ɑ-Mangostin binds in the upper portion of the cleft between S6 helices. In this position, it would clearly overlap with the QA binding site and hinder access, but not block permeation. We would therefore not expect to see an amplitude reduction by intermittent α-Mangostin block. Consistently, all binding poses in our dockings were close to the cavity wall, without interfering with the central ion conduction pathway. To better illustrate this, we have added updated intracellular views of the dockings in the Ca²⁺-free and Ca²⁺-bound state (which we have also now included as suggested by another reviewer) to the supplementary information (Fig. S4A).

(3) In Figure 2D, it is difficult to appreciate the differences between the symbols representing the G-V relationships of BKa channels at different intracellular Ca concentrations, before and after activation with 10 μM a-Mangostin. A clearer distinction between the curves would help to interpret the data more easily.

We thank the reviewer for the suggestion to improve figure accessibility. We have changed the line appearance for better discrimination of the overlying portions.

(4) Both THexA and TPA block BK channels through voltage and state-dependent mechanisms. Therefore, their apparent affinity could change if a-Mangostin simply increases open probability or alters dwell times rather than physically blocking access to the binding site.

The reviewer addresses valid limitations that can affect the meaningfulness of competition experiments under certain conditions. However, we think that this does not apply to our results:

Previous studies have shown that the voltage dependence of quaternary ammonium blockers up to C₁₀ is rather weak in BK channels, and only a slight increase in block is present in the voltage range +30 mV to +100 mV (Li and Aldrich, 2004; Thompson and Begenisich, 2012). Hence, THexA voltage dependence has already reached a plateau in the competition assay (at +40 mV), and its voltage dependence would have little effect on our results.

Controversy exists about the nature of the state dependence of different quaternary ammonium blockers, but TBA is often recognized as an open channel blocker of BK channels, which probably also applies to THexA (Wilkens and Aldrich, 2006; Tang, Zeng and Lingle, 2009; Thompson and Begenisich, 2012; Posson, McCoy and Nimigean, 2013). Assuming such an open-channel block, apparent IC₅₀ values would be inversely proportional to Po. The THexA IC₅₀ was about 80 nM in the basal state, when Po is very low (0.024 at +40 mV as derived from the GV-relationship); an increase of open dwell times, respectively Po, in the presence of α-Mangostin to, e.g., 0.3 would therefore lead to a ≈10-fold decrease in apparent IC₅₀. However, the apparent THexA IC₅₀ strongly increased rather than decreased (more than 20-fold to around 1.6 µM). This cannot arise from Po change and must reflect the altered access of THexA to its binding site caused by α-Mangostin. Assuming a pure closed channel block where apparent IC₅₀ would correlate with the closed times, an increase of about 1.4-fold is expected. However, we recorded a much stronger 20-fold increase. Therefore, we are convinced that we have conclusively shown that α-Mangostin is present in the BK pore irrespective of the state dependence of THexA block.

(5) The pH dependence of the V1/2 shift supports the idea that α-Mangostin becomes more negatively charged at higher pH (enhancing its effect.) However, although the data are consistent with this interpretation, additional controls such as using a non-ionizable analog or assessing solubility changes with pH would be needed to confirm that the shift is caused specifically by ionization of α-Mangostin and not by indirect pH effects on channel gating.

We agree with the reviewer that the pH experiment by itself is not sufficient to clearly tie the existence of a charge to a possible activation mechanism. We still think that this is an interesting observation and should be made known, as we have investigated the mechanism of negatively charged activators in different K⁺ channel families before (Schewe et al., 2019). Unfortunately, we do not have access to uncharged derivatives mimicking the 3D conformation. From the commercially available substances, the bare xanthone backbone is completely insoluble in water. We have therefore tested the derivative 3-hydroxyxanthone as example with a minimal number of hydroxyl substituents (Author response image 2, Author response table 2 ). The 3-hydroxyxanthone indeed shows reduced activation compared to α-Mangostin. The shift in V_½ induced by 10 µM 3-hydroxyxanthone was only 14.99 ± 5.67 mV (≈50 mV for α-Mangostin). This supports that the presence of several (potentially) charged substituents is important for the activation mechanism. However, we have no knowledge about the efficacy of the compound or the local pK_a of the different hydroxyl groups. As the reviewer stated, systematic chemical modifications would be necessary to elucidate the importance of the charged substituent number and positions, which is not within our capabilities.

Author response image 2.

Activation of BKα by 3-hydroxyxanthone. (A) GV-relationship before and after application of 10 µM 3-hydroxyxanthone. (B) V_½ before and after application of 10 µM 3-hydroxyxanthone compared to α-Mangostin and the resulting difference in V_½ (ΔV_½). Measurements were conducted as described in the main manuscript with 100 nM free Ca_i²⁺.

Author response table 2.

Comparison of the V_½ ± SEM and ΔV_½ ± SEM before and after activation by 10 µM α-Mangostin or 10 µM 3-hydroxyxanthone in BKα channels. Unpaired t-test, two-tailed P values (α=0.05)

(6) The reduced V1/2 shifts observed in the I308A, L312M, and A316PP mutants may result from intrinsic gating alterations rather than a true loss of a-Mangostin binding. The GoSlo-SR-5-6 control is informative, but the persistence of activation in A316P does not fully resolve this. A more convincing test would be employing double or triple mutants.

As stated above, we acknowledge that our functional data do not allow us to definitively separate effects arising from a true loss of binding affinity from those due to potential allosteric effects. We tried to minimize intrinsic gating alteration brought by substitutions by not conducting a pure alanine or cysteine scanning mutagenesis. Instead, substitutions were chosen to be closest to the wildtype GV-relationship in (Chen, Yan and Aldrich, 2014) where possible. While L312M was virtually identical to the wildtype, A316P showed a change in slope in high Ca²⁺ concentrations, which could indicate a changed voltage sensitivity. Additionally, A316P completely abolished α-mangostin activation. We therefore also used A316G to ensure that the channel is functional and retains voltage sensitivity, even if its V_½ was shifted stronger. As we have conducted paired measurements and assessed the V_½ before and after activation, we are confident that we can attribute a reduced shift to the reduced action of α-mangostin.

Following the reviewer’s suggestion, we have generated and measured the double mutants I308A/L312M, I308A/A316G, and L312M/A316G (the triple mutant I308A/L312M/A316G did not produce measurable currents). The mutants I308A/L312M and I308A/A316G showed a moderate energy-additive effect and reduced the shift in V_½ by further ≈7 mV compared to the single mutation with the stronger shift. The combination L312M/A316G, however, did not further reduce the shift seen in the single mutations and did not even produce the shift induced by A316G alone.

Author response image 3.

Double Mutants I308A/L312M, I308A/A316G and L312M/A316G compared to the single mutations in the main manuscript. The V½ before and after activation with 10 µM α-Mangostin, the resulting shift in V½, and the GV-relationships are shown (n=6-7), measurements were made as in Fig. 4.

Author response table 3.

Summary of the V_½ before and after Mangostin activation and the resulting shifts in V_½ for the double mutants compared to the single mutants shown in the main manuscript.

Following a suggestion by another reviewer, we have generated Alphafold3 (AF3) models for I308A, L312M and A316P and repeated the Mangostin docking. We learned that the mutations are all predicted to substantially impact the structure of the S6 helix, therefore altering the binding region, and A316P especially impacted the nature of residue interactions. This could be an explanation why the double mutants do not show a clear and consistent additive effect.

Unfortunately, this outcome is not conclusive and the double mutants do not reveal further information compared to the single mutants. We have therefore decided not to include these measurements in the manuscript.

As we do not know if our answers will be sent to all reviewers, we repeat the relevant part about the AF3 models here:

(…) According to these predictive models,

The I308A substitution considerably straightens the S6 helix starting at this residue. Hence, all residues are displaced relative to the WT: C_a of L312, F315, and A316 are displaced by 2.8 Å, 4.2 Å, and 4.6 Å, respectively, widening the bottom of the binding pocket. However, the prediction confidence is rated lower as in the other AF3 models for all helices (70 > plDDT > 50). In the docking, poses in the binding pocket comparable to these observed in the WT (i.e. involving I308A, L312 and A316) and with the same molecule orientation have higher binding energies (-7.13 to -6.66 kcal mol^-1). Additionally, poses without contact to I308A arise that have a more vertical position, indicating that the structural change affects the binding region.

The changes induced by L312M are localized to residues 313-323, where S6 bends towards S5. Binding energies are lower especially in the best 2 poses that are also most comparable to the WT docking (-9.88 kcal mol^-1), but clustering overall is poor and poses are more heterogeneous. Interactions with L312M are completely abolished, while interactions with I308 (in 11/20 poses), F315 (in all poses), and A316 (in 5/20 poses) persist. Because of the rather small structural alteration induced by the substitution and the variable poses one could speculate that the reduced V_½ shift is due to the observed loss in binding to L312M; however, retained interactions to the other residues would still allow α-Mangostin to activate.

A316P induces a displacement of the S6 helix compared to the WT while the other pore helices are not affected. S6 shows an enhanced outward bending around A316, which results in displacements of residues where a-Mangostin would bind, i.e., the C_a of F315 and L312M are displaced by 2.4 Å and 2.8 Å (I308 is not affected). Residues below are moved in a more rotational way, resulting in a C_a displacement of 3.1 Å for Y318 and even 5.7 Å for V319, before displacements decrease again towards the intracellular helix end. While interactions with A316P are present in 10/20 analyzed poses, the helix displacement seems to hinder I308 and L312 interactions, as the best docked a-Mangostin pose (-8.41 kcal mol^-1) is predicted to only contact F315 and Y318, and overall, any I308 or L312 contacts only occurred in 3/20 and 7/20 poses (wildtype: 17/20 and 20/20 poses). This may hint at a mechanism where A316P probably has a substantial allosteric share in reducing the V_½ shift induced by a-Mangostin and underlines the exceptional effect of this mutation (i.e., complete loss of a V_½ shift). (…)

(7) The subtraction approach used to isolate BK currents (difference before and after a-Mangostin) assumes that the compound affects only BK channels. However, a-Mangostin could also modulate Cav currents directly, as reported for other polyphenolic compounds. No vehicle (DMSO) control is shown.

We agree with the reviewer that α-Mangostin could also modulate Ca_v currents; however, this would not interfere with the conclusions drawn from this nanodomain experiment. We intended to show the overall current modulation by ɑ-Mangostin in the voltage range relevant for Ca_v-BK coupling, as this would be the determinant for the membrane potential mediating the vasoactive effect. In native tissue, BK and Ca_v channels (among others) would likewise contribute to the net membrane conductance, with BK channels being a major contributor when activated. In fact, a concomitant inhibition of Ca_v channels could act synergistically in favor of vasodilation. This could therefore be a subject for the further investigation of potential ɑ-Mangostin targets. However, the fact that iberiotoxin prevented relaxation in aortic preparations conclusively showed that BK channels are the major player in native tissue.

We have reformulated some sentences to prevent misunderstandings that we refer to isolated BK currents instead of α-Mangostin activated currents.

DMSO controls were conducted and did not impact BK or Ca_v1.2 currents or the aortic tissue contraction. We have added representative measurements as Fig. S6 and stated the DMSO concentration in the Methods section (line 655).

(8) Most kinetic fits were obtained at strong depolarizations (around +100 mV), which limits how well these results can be extrapolated to physiological voltages. Although the BK-Cav experiments show facilitation between -50 and +50 mV, providing plots for activation and deactivation in that range would strengthen the physiological relevance.

We thank the reviewer for this valuable suggestion. We now additionally show that the impact of ɑ-Mangostin on activation is high at lower depolarisation, indeed underlining its physiological relevance. To address the activation time course in a more physiological voltage range, we have used our measurements of BKɑ channels in 10 µM Ca_i</sup>2+</sup> (where the V_½ shift induced by ɑ-Mangostin is equal to 100 nM ca_i²⁺+; Fig. 2D). The outward currents already present in the lower voltage range under these conditions allowed us to fit a monoexponential function to the traces of 0 mV to 100 mV prepulses. The τ of activation decreased from 29.6 ± 3.1 ms at 0 mV to 2.4 ± 2 ms at +100 mV. After ɑ-Mangostin activation, the time course was accelerated, with a τ of activation of 9.5 ± 4.7 ms at 0 mV to 2 ± 0.6 ms at +100 mV. This faster activation was particularly effective in the lower voltage range far from high Po, e.g., ɑ-Mangostin caused a decrease of more than half of the τ of activation at +20 mV (from 12.2 ± 0.6 ms to 4.98 ± 1.6 ms).

Our data consists of families of different prepulse voltages and a fixed repolarisation step (to -50 mV for 100 nM free Ca_i²⁺, and to -100 mV for 10 µM free Ca_i²⁺). Thus, we are not able to add plots for the voltage-dependence of deactivation in the same way as for activation. However, we can present the deactivation time constants of lower prepulse voltage steps that produce outward currents in symmetrical ion conditions with 10 µM free Ca_i</sup>2+</sup>. For -20 mV and +20 mV prepulse voltages, which better reflect physiological depolarisation, the deactivation time constant shows a 3-to 5-fold increase after ɑ-Mangostin activation.

We now show the plot for the voltage dependence of activation in Fig. S2A and a bar graph for activation/ deactivation time constants at +20 mV as Fig. S2B; data are summarized in Table S5. We hope this adds to illustrating the effect of ɑ-Mangostin under physiological conditions.

(9) Minor: In several parts of the paper, induced shifts to negative voltages are referred to "leftward shifts". It would be useful to be consistent and employ a more specific reference to negative or positive directions.

We thank the reviewer for the careful reading and have harmonized the terminology.

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