Author response:

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

Reviewer 1 (Public Comments):

(1) The central concern for this manuscript is the apparent lack of reproducibility. The way the authors discuss the issue (lines 523-554) it sounds as though they are unable to reproduce their initial results (which are reported in the main text), even when previous versions of AlphaFold2 are used. If this is the case, it does not seem that AlphaFold can be a reliable tool for predicting antibody-peptide interactions.

The driving point behind the multiple sequence alignment (MSA) discussion was indeed to point out that AlphaFold2 (AF2) performance when predicting scFv:peptide complexes is highly dependent upon the MSA, but that is a function of MSA generation algorithm (MMseqs2, HHbiltz, jackhmmer, hhsearch, kalign, etc) and sequence databases, and less an intrinsic function of AF2. It is important to report MSA-dependent performance precisely because this results in changing capabilities with respect to peptide prediction.

Performance also significantly varies with the target peptide and scFv framework changes. By reporting the varying success rates (as a function of MSA, peptide target, and framework changes) we aim to help future researchers craft modified algorithms that can achieve increased reliability at protein-peptide binding predictions. Ultimately, tracking down how MSA generation details vary results (especially when the MSA’s are hundreds long) is significantly outside the scope of this paper. Our goal for this paper was to show a general method for identification of linear antibody epitopes using only sequence information, and future work by us or others should focus on optimization of the process. 

(2) Aside from the fundamental issue of reproducibility, the number of validating tests is insufficient to assess the ability of AlphaFold to predict antibody-peptide interactions. Given the authors' use of AlphaFold to identify antibody binding to a linear epitope within a whole protein (in the mBG17:SARS-Cov-2 nucleocapsid protein interaction), they should expand their test set well beyond Myc- and HA-tags using antibody-antigen interactions from existing large structural databases.

Performing the calculations at the scale that the reviewer is requesting is not feasible at this time. We showed in this manuscript that we were able to predict 3 of 3 epitopes, including one antigen and antibody pair that have not been deposited into the PDB with no homologs. While we feel that an N=3 is acceptable to introduce this method to the scientific community, we will consider adding more examples of success and failure in the future to optimize and refine the method as computational resources become available. Notably, future efforts that attempt high-throughput predictions of this class using existing databases should take particular care to avoid contamination.

(3) As discussed in lines 358-361, the authors are unsure if their primary control tests (antibody binding to Myc-tag and HA-tag) are included in the training data. Lines 324-330 suggest that even if the peptides are not included in the AlphaFold training data because they contain fewer than 10 amino acids, the antibody structures may very well be included, with an obvious "void" that would be best filled by a peptide. The authors must confirm that their tests are not included in the AlphaFold training data, or re-run the analysis with these templates removed.

First, we address the simpler question of templates.

The reruns of AF2 with the local 2022 rebuild, the most reproducible method used with results most on par with the MMSEQS server in the Fall of 2022, were run without templates. This is because the MSA was generated locally; no templates were matched and generated locally. The only information passed then was the locally generated MSA, and the fasta sequence of the unchanging scFv and the dynamic epitope sequence. Because of how well this performed despite the absence of templates, we can confidently say the inclusion of the template flag is not significant with respect to how universally accurately PAbFold can identify the correct epitope. 

Second, we can partially address the question of whether the AlphaFold models had access to models suitable, in theory, for “memorization” of pertinent structural details. 

With respect to tracking the exact role and inclusion of specific PDB entries, the AF2 paper provides the following:

“Structures from the PDB were used for training and as templates (https://www.wwpdb.org/ftp/pdb-ftp-sites; for the associated sequence data and 40% sequence clustering see also https://ftp.wwpdb.org/pub/pdb/derived_data/ and https://cdn.rcsb.org/resources/sequence/clusters/bc-40.out). Training used a version of the PDB downloaded 28 August 2019, while the CASP14 template search used a version downloaded 14 May 2020. The template search also used the PDB70 database, downloaded 13 May 2020 (https://wwwuser.gwdg.de/~compbiol/data/hhsuite/databases/hhsuite_dbs/).”

Three of these links are dead. As such, it is difficult to definitively assess the role of any particular PDB entry with respect to AF2 training/testing, nor what impact homologous training structures given the very large number of immunoglobin structures in the training set. That said, we can summarize information for the potentially relevant PDB entries (l 2or9, which is shown in Fig. 1 and 1frg), and believe it is most conservative to assume that each such entry was within the training set.

PDB entry 2or9 (released 2008): the anti-c-myc antibody 9E10 Fab fragment in complex with an 11-amino acid synthetic epitope: EQKLISEEDLN. This crystal structure is also noteworthy for featuring a binding mode where the peptide is pinned between two Fab. The apo structure (2orb) is also in the database but lacks the peptide and a resolved structure for CDR H3.

PDB entry 1a93 (released 1998): a c-Myc-Max leucine zipper structure, where the c-Myc epitope (in a 34-amino acid protein) adopts an alpha helical conformation completely different from the epitope captured in entry 2or9.

PDB entries 5xcs and 5xcu (released 2017): engineered Fv-clasps (scFv alternatives) in complex with the 9-amino acid synthetic HA epitope: YPYDVPDYA.

PDB entry 1frg (released 1994): anti-HA peptide Fab in complex with HA epitope subset Ace-DVPDYASL-NH2.

Since the 2or9 entry has our target epitope (10 aa) embedded within an 11aa sequence, we have revised this line in the manuscript:

The AlphaFold2 training set was reported to exclude chains of less than 10, which would eliminate the myc and HA epitope peptides. => The AlphaFold2 training set was reported to exclude chains of less than 10, which would eliminate the HA epitope peptide from potential training PDB entries such as 5xcs or 5xcu”

It is important to note that we obtained the best prediction performance for the scFv:peptide pair that had no pertinent PDB entries (mBG17). Specifically, doing a Protein Blast against the PDB using the mBG17 scFv revealed diverse homologs, but a maximum sequence identity of 89.8% for the heavy chain (to an unrelated antibody) and 93.8% for the light chain (to an unrelated antibody). Additionally, while it is possible that the AF2 models might have learned from the complex in pdb entry 2or9, Supplemental Figure 3 shows how often the peptide is “misplaced”, and the performance does not exceed the performance for mBG17.

(4) The ability of AlphaFold to refine the linear epitope of antibody mBG17 is quite impressive and robust to the reproducibility issues the authors have run into. However, Figure 4 seems to suggest that the target epitope adopts an alpha-helical structure. This may be why the score is so high and the prediction is so robust. It would be very useful to see along with the pLDDT by residue plots a structure prediction by residue plot. This would help to see if the high confidence pLDDT is coming more from confidence in the docking of the peptide or confidence in the structure of the peptide.

The reviewer is correct that target mBG17 epitope adopts an alpha helical conformation, and we concur that this likely contributes to the more reliable structure prediction performance.  When we predict the structure of the epitope alone without the mBG17 scFv, AF2 confidently predicts an alpha helix with an average pLDDT of 88.2 (ranging from 74.6 to 94.4). 

Author response image 1.

The AF2 prediction for the mBG17 epitope by itself.

However, as one interesting point of comparison, a 10 a.a. poly-alanine peptide is also consistently folded into an alpha-helical coil by AF2. The A₁₀ peptide is also predicted to bind among the traditional scFv CDR loops, but the pLDDT scores are very poor (Supplemental Figure 5J). We also observed the opposite case; when a peptide has a very unstructured region in the binding domain but is nonetheless still be placed confidently, as seen in Supplemental Figure 3 C&D. Therefore, while we suspect peptides with strong alpha helical propensity are more likely to be accurately predicted, the data suggests that that alpha helix adoption is neither necessary nor sufficient to reach a confident prediction.

(5) Related to the above comment, pLDDT is insufficient as a metric for assessing antibody antigen interactions. There is a chance (as is nicely shown in Figure S3C) that AlphaFold can be confident and wrong. Here we see two orange-yellow dots (fairly high confidence) that place the peptide COM far from the true binding region. While running the recommended larger validation above, the authors should also include a peptide RMSD or COM distance metric, to show that the peptide identity is confident, and the peptide placement is roughly correct. These predictions are not nearly as valuable if AlphaFold is getting the right answer for the wrong reasons (i.e. high pLDDT but peptide binding to a nonCDR loop region). Eventual users of the software will likely want to make point mutations or perturb the binding regions identified by the structural predictions (as the authors do in Figure 4).

We agree with the reviewer that pLDDT is not a perfect metric, and we are following with great interest the evolving community discussion as to what metrics are most predictive of binding affinity (e.g. pAE, or pITM as a decent predictor for binding, but not affinity ranking). To our knowledge, there is not yet a consensus for the most predictive metrics for protein:protein binding nor protein:peptide binding. Intriguingly, since the antigen peptides are so small in our case, the pLDDT of the peptide residues should be mostly reporting on the confidence of the distances to neighboring protein residues.

As to the suggestion for a RMSD or COM distance metric, we agree that these are useful -with the caveat that these require a reference structure. The goal of our method is to quickly narrow down candidate linear epitopes and thereby guide experimentalists to more efficiently determine the actual binding sequence of an antibody-antigen sequence. Presumably this would not be necessary if a reference structure were known. 

It may also be possible to invent a method to filter unlikely binding modes that is specific to antibodies and peptide epitopes that does not require a known reference structure, but this would be an interesting problem for subsequent study.

Reviewer 1 (Recommendations for the Authors):

(1) "Linear epitope" should be more precisely defined in the text. It isn't clear whether the authors hope that they can use AlphaFold to predict where on a given protein antigen an antibody will bind, or which antigenic peptide the antibody will bind to. The authors discuss both problems, and there is an important distinction between the two. If the authors are only concerned with isolated antigenic peptides, rather than linear epitopes in their full length structural contexts, they should be more precise in the introduction and discussion.

We thank the reviewer for the prompt towards higher precision. We are using the short contiguous antigen definition of “linear epitope” that depends on secondary rather than tertiary structure. The linear epitopes this paper considers are short “peptides” that form secondary structure independent of their structure in the complete folded antigen protein. We have clarified our definition of “linear epitope” in the text (lines 64-66). 

(2) Line 101: "Not all portions of the antibody are critical". First, this is not consistent with the literature, particularly where computational biology is concerned.

See https://pubs.acs.org/doi/10.1021/acs.jctc.7b00080 . Second, while I largely agree with what I think the authors are trying to say (that we can largely reduce the problem to the CDR loops), this is inconsistent with what the authors later find, which is that inexplicably the VH/VL scaffold used alters results strongly.

We have adopted verbiage that should be less provocative: “Fortunately, with respect to epitope specificity, antibody constant domains are less critical than the CDR loops and the remainder of the variable domain framework regions.”

(3) Related to the above comment, do the authors have any idea why epitope prediction performance improved for the chimeric scFvs? Is this due to some stochasticity in AlphaFold? Or is there something systematic? Expanding the test dataset would again help answer this question.

We agree that future study with a larger test set could help address this intriguing result, for which we currently lack a conclusive explanation. Part of our motivation for this publication was to bring to light this unexpected result. Notably, these framework differences are not only implicated as a factor in driving AF2 performance, but also changing experimental intracellular performance as reported by our group (DOI: 10.1038/s41467-019-10846-1 ). We can generate a variety of hypotheses for this phenomenon. Just as MSA sub-sampling has been a popular approach to drive AF2 to sample alternative conformations, sequence recombination may be a generically effective way to generate usefully different binding predictions. However, it is difficult to discriminate between recombination inducing subtle structural tweaks that increase protein intracellular fitness and binding, from recombination causing changes to the MSA that affect the likelihood of sampling a good epitope binding conformation. It is also possible that the chimeras are more deftly predicted by AF2 due to differences in sequence representation during the training of the AF2 models (e.g. more exposure to models containing 15F11 or 2E2 structures). We attempted to deconvolute MSA differences by using single-sequence mode (Supplementary Figure 13) but this ablated performance.

(4) Figure 2: The reported consensus pLDDT scores are actually quite low here, suggesting low confidence in the result. This is in strong contrast to the reported consensus scores for mBG17. Again, a larger test dataset would help set a quantitative cutoff for where to draw the line for "trustworthy" AlphaFold predictions in antibody-peptide binding applications.

We agree that a larger dataset will be useful to begin to establish metrics and thresholds and will contribute to the aforementioned community discussion about reliable predictors of binding. Our current focus is not structure prediction per se. In the current work we are more focused on relative binding likelihood and increasing the efficiency of experimental epitope verification by flagging the most likely linear epitopes. Thus, while the pLDDT scores are low for Myc in Figure 2, it is remarkable (and worth reporting) that there is still useful signal in the relative variation in pLDDT. The utility of the signal variation is evident in the ability to short-list correct lead peptides via the two methods we demonstrate (consensus and per-residue max).

(5) Figure 4: if the authors are going to draw conclusions from the actual structure predictions of AlphaFold (not just the pLDDT scores), the side-chain accuracy placement should be assessed in the test dataset (RMSD or COM distance).

We agree with the reviewer that side-chain placement accuracy is important when evaluating the accuracy of AF2 structure predictions. However, here our focus was relative binding likelihood rather than structure prediction. The one case where we attempted to draw conclusions from the structure prediction was in the context of mBG17, where there is not yet an experimental reference structure. Absolutely, if we were to obtain a crystal structure for that complex, we would assess side-chain placement accuracy. 

(6) Lines 493-508: I am not sure that this assessment for why AlphaFold has difficulty with antibody-antigen interactions is correct. If the authors' interpretation is correct (larger complicated structures are more challenging to move) then AlphaFold-Multimer (https://www.biorxiv.org/content/10.1101/2021.10.04.463034v2.full) wouldn't perform as well as it does. Instead, the issue is likely due to the incredibly high diversity in antibody CDR loops, which reduces the ability of the AlphaFold MSA step (which the authors show is quite critical to predictions: Figure S13) to inform structure prediction. This, coupled with the importance of side chain placement in antibody and TCR interactions, which is notoriously difficult (https://elifesciences.org/articles/90681), are likely the largest source of uncertainty in antibody-antigen interaction prediction.

We agree with the reviewer that CDR loop diversity (and associated side chain placement challenges) are a major barrier to successfully predict antibody-antigen complexes. Presumably this is true for both peptide antigens and protein antigens. Indeed, the authors of AlphaFold-multimer admit that the updated model struggles with antibody-antigen complexes, saying “As a limitation, we observe anecdotally that AlphaFold-Multimer is generally not able to predict binding of antibodies and this remains an area for future work.” The point about how loop diversity could reduce MSA quality is well taken. We have included the following thanks to the guidance of the reviewer when discussing MSA sensitivity is discussed later on in lines 570-572.: 

“These challenges are presumably compounded by the incredible diversity of the CDR loops in antibodies which could decrease the useful signal from the MSA as well as drive inconsistent MSA-dependent performance”.

With respect to lines 493-508, we have also rephrased a key sentence to try to better explain that we are comparing the often-good recognition performance for short epitopes to the never-good performance when those epitopes are embedded within larger sequences. Instead of saying, “In contrast, a larger and complicated structure may be more challenging to move during the AlphaFold2 structure prediction or recycle steps.” we now say in lines 520-522 , “In contrast, embedding the epitope within a larger and more complicated structure appears to degrade the ability of AlphaFold2 to sample a comparable bound structure within the allotted recycle steps.”

(7) Related to major comment 1: Are AlphaFold predictions deterministic? That is, if you run the same peptide through the PAbFold pipeline 20 times, will you get the same pLDDT score 20 times? The lack of reproducibility may be in part due to stochasticity in AlphaFold, which the authors could actually leverage to provide more consistent results.

This is a good question that we addressed while dissecting the variable performance. When the random seed is fixed, AF2 returns the same prediction every time. After running this 10 times with a fixed seed, the mBG17 epitope was predicted with an average pLDDT of 88.94, with a standard deviation of 1.4 x 10^-14. In contrast, when no seed is specified, AF2 did not return an *identical* result. However, the results were still remarkably consistent. Running the mBG17 epitope prediction 10 times with a different seed gave an average pLDDT of 89.24, with a standard deviation of 0.49. 

(8) Related to major comment 2: The authors could use, for example, this previous survey of 1833 antibody-antigen interactions (https://www.sciencedirect.com/science/article/pii/S2001037023004725) the authors could likely pull out multiple linear epitopes to test AlphaFold's performance on antibody peptide interactions. A large number of tests are necessary for validation.

We thank the reviewer for this report of antibody-antigen interactions and will use it as a source of complexes in a future expanded study. Given the quantity and complexity of the data that we are already providing, as well as logistical challenges for compute and personnel the reviewer is asking for, we must defer this expansion to future work.

(9) Related to major comment 3: Apologies if this is too informal for a review, but this Issue on the AlphaFold GitHub may be useful: https://github.com/googledeepmind/alphafold/issues/416 .

We thank the reviewer for the suggestion – per our response above we have indeed run predictions with no templates. Since we are using local AlphaFold2 calculations with localcolabfold, the use or non-use of templates is fairly simple: including a “—templates” flag or not.

(10) Related to major comment 4: I am not sure if AlphaFold outputs by-residue secondary structure prediction by default, but I know that Phyre2 does http://www.sbg.bio.ic.ac.uk/~phyre2/html/page.cgi?id=index .

To our knowledge, AF2 does not predict secondary structure independent of the predicted tertiary structure. When we need to analyze the secondary structure we typically use the program DSSP from the tertiary structure. 

(11) The documentation for this software is incomplete. The GitHub ReadMe should include complete guidelines for users with details of expected outputs, along with a thorough step-by-step walkthrough for use.

We thank the reviewer for pointing this out, but we feel that the level of detail we provide in the GitHub is sufficient for users to utilize the method described.

Stylistic comments:

(1) I do not think that the heatmaps (as in 1C, top) add much information for the reader. They are largely uniform across the y-axis (to my eyes), and the information is better conveyed by the bar and line graphs (as in 1C, middle and bottom panels).

We thank the reviewer for this feedback but elect to leave it in on the premise of more data presented is (usually) better. Including the y-axis reveals common patterns such as the lower confidence of the peptide termini, as well as the lack of some patterns that might have occurred. For example, if a subset of five contiguous residues was necessary and sufficient for local high confidence this could be visually apparent as a “staircase” in the heat map.

(2) A discussion of some of the shortcomings of other prediction-based software (lines 7177) might be useful. Why are these tools less well-equipped than AlphaFold for this problem? And if they have tried to predict antibody-antigen interactions, why have they failed?

We agree with the reviewer that a broader review of multiple methods would be interesting and useful. One challenge is that the suite of available methods is evolving rapidly, though only a subset work for multimeric systems. Some detail on deficiencies of other approaches was provided in lines 71-77 originally, although we did not go into exhaustive detail since we wanted to focus on AF2. We view using AF2 in this manner is novel and that providing additional options predict antibody epitopes will be of interest to the scientific community. We also chose AF2 because we have ample experience with it and is a software that many in the scientific community are already using and comfortable with. Additionally, AF2 provided us with a quantification parameter (pLDDT) to assess the peptides’ binding abilities. We think a future study that compares the ability of multiple emerging tools for scFv:peptide prediction will be quite interesting. 

(3) Similar to the above comment, more discussion focused on why AlphaFold2 fails for antibodies (lines 126-128) might be useful for readers.  

We thank the reviewer for the suggestion. The following line has been added shortly after lines 135-137:

“Another reason for selecting AF2 is to attempt to quantify its abilities the compare simple linear epitopes, since the team behind AF-multimer reported that conformational antibody complexes were difficult to predict accurately (14).”

Per earlier responses, we also added text that flags one particular possible reason for the general difficulty of predicting antibody-antigen complexes (the diversity of the CDR loops and associated MSA challenges).

(4) The first two paragraphs of the results section (lines 226-254) could likely be moved to the Methods. Additionally, details of how the scores are calculated, not just how the commands are run in python, would be useful.

Per the reviewer suggestion, we moved this section to the end of the Methods section. Also, to aid in the reader’s digestion of the analysis, the following text has been added to the Results section (lines 256-264):

“Both the ‘Simple Max’ and ‘Consensus’ methods were calculated first by parsing every pLDDT score received by every residue in the antigen sequence sliding window output structures. From the resulting data structure, the Simple Max method simply finds the maximum pLDDT value ever seen for a single residue (across all sliding windows and AF2 models). For the Consensus method, per-residue pLDDT was first averaged across the 5 AF2 models. These averages are reported in the heatmap view, and further averaged per sliding window for the bar chart below.

In principle, the strategy behind the Consensus method is to take into account agreement across the 5 AF2 models and provide insight into the confidence of entire epitopes (whole sliding windows of n=10 default) instead of disconnected, per-residue pLDDT maxima.” 

(5) Figure 1 would be more useful if you could differentiate specifically how the Consensus and Simple Max scoring is different. Providing examples for how and why the top 5 peptide hits can change (quite significantly) using both methods would greatly help readers understand what is going on.

Per the reviewer suggestion, we have added text to discuss the variable hit selection that results from the two scoring metrics. The new text (lines 264-271) adds onto the added text block immediately above:

“Having two scoring metrics is useful because the selection of predicted hits can differ. As shown in Figure 2, part of the Myc epitope makes it into the top 5 peptides when selection is based on summing per-residue maximum pLDDT (despite there being no requirement that these values originate in the same physical prediction). In contrast, a Consensus method score more directly reports on a specific sliding window, and the strength of the highest confidence peptides is more directly revealed with superior signal to noise as shown in Figure 3. Variability in the ranking of top hits between the two methods arises from the fundamental difference in strategy (peptide-centric or residue-centric scoring) as well as close competition between the raw AF2 confidence in the known peptide and competing decoy sequences.”

(6) Hopefully the reproducibility issue is alleviated, but if not the discussion of it (lines 523554) should be moved to the supplement or an appendix.

The ability of the original AF2 model to predict protein-protein complexes was an emergent behavior, and then an explicit training goal for AF2.multimer. In this vein, the ability to predict scFv:peptide complexes is also an emergent capability of these models. It is our hope that by highlighting this capacity, as well as the high level of sensitivity, that this capability will be enhanced and not degraded in future models/algorithms (both general and specialized). In this regard, with an eye towards progress, we think it is actually important to put this issue in the scientific foreground rather than the background. When it comes to improving machine learning methods negative results are also exceedingly important.

Reviewer 2 (Recommendations for the Author):

- Line 113, page 3 - the structures of the novel scFv chimeras can be rapidly and confidently be predicted by AlphaFold2 to the structures of the novel scFv chimeras can be rapidly and confidently predicted by AlphaFold2.

The superfluous “be” was removed from the text.

- Line 276 and 278 page 9 - peptide sequences QKLSEEDLL and EQKLSEEDL in the text are different from the sequences reported in Figures 1 and 2 (QKLISEEDLL and EQKLISEEDL). Please check throughout the manuscript and also in the Figure caption (as in Figure 2).

These changes were made throughout the text. 

- I would include how you calculate the pLDDT score for both Simple Max approach and Consensus analysis.

Good suggestion, this should be covered via the additions noted above.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors bring together implanted radiofrequency coils, high-field MRI imaging, awake animal imaging, and sensory stimulation methods in a technological demonstration. The results are very detailed descriptions of the sensory systems under investigation.

Strengths:

- The maps are qualitatively excellent for rodent whole-brain imaging. - The design of the holder and the coil is pretty clever.

Weaknesses:

- Some unexpected regions appear on the whole brain maps, and the discussion of these regions is succinct.

- The authors do not make the work and e ort to train the animals and average the data from several hundred trials apparent enough. This is important for any reader who would like to consider implementing this technology.

- The data is not available. This does not let the readers make their own assessment of the results.

Thank you for the comments on this manuscript. We have provided more detailed discussion of the unexpected regions(page 18 – line 491-494) and training procedures(page7-9 – line 172-236). We also uploaded the datasets to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts:  (https://zenodo.org/doi/10.5281/zenodo.13821455). 

Reviewer #2 (Public Review):

Summary:

The manuscript by Hike et al. entitled 'High-resolution awake mouse fMRI at 14 Tesla' describes the implementation of awake mouse BOLD-fMRI at high field. This work is timely as the field of mouse fMRI is working toward collecting high-quality data from awake animals. Imaging awake subjects o ers opportunities to study brain function that are otherwise not possible under the more common anesthetized conditions. Not to mention the confounding e  ects that anesthesia has on neurovascular coupling. What has made progress in this area slow (relative to other imaging approaches like optical imaging) is the environment within the MRI scanner (high acoustic noise) - as well as the intolerance of head and body motion. This work adds to a relatively small, but quickly growing literature on awake mouse fMRI. The findings in the study include testing of an implanted head-coil (for MRI data reception). Two designs are described and the SNR of these units at 9.4T and 14T are reported. Further, responses to visual as well as whisker stimulation recorded in acclimated awake mice are shown. The most interesting finding, and most novel, is the observation that mice seem to learn to anticipate the presentation of the stimulus - as demonstrated by activations evident ~6 seconds prior to the presentation of the stimulus when stimuli are delivered at regular intervals (but not when stimuli are presented at random intervals). These kinds of studies are very challenging to do. The surgical preparation and length of time invested into training animals are grueling. I also see this work as a step in the right direction and evidence of the foundations for lots of interesting future work. However, I also found a few shortcomings listed below.

Weaknesses:

(1) The surface coil, although o ering a great SNR boost at the surface, ultimately comes at a cost of lower SNR in deeper more removed brain regions in comparison to commercially available Bruker coils (at room temperature). This should be quantified. A rough comparison in SNR is drawn between the implanted coils and the Bruker Cryoprobe - this should be a quantitative comparison (if possible) - including any di erences in SNR in deeper brain structures. There are drawbacks to the Cryoprobe, which can be discussed, but a more thorough comparison between the implanted coils, and other existing options should be provided (the Cryoprobe has been used previously in awake mouse experiments(Sensory evoked fMRI paradigms in awake mice - Chen, Physiological e ects of a habituation procedure for functional MRI in awake mice using a cryogenic radiofrequency probe – Yoshida, PREVIOUS REFERENCE). Further, the details of how to build the implanted coils should be provided (shared) - this should include a parts list as well as detailed instructions on how to build the units. Also, how expensive are they? And can they be reused?

Thank you for the comment. We did not use a Bruker Cryoprobe for this work but rather a Bruker 4array surface coil. We are unable to compare to a cryoprobe since we do not have access to one for our system. A comparison to previously published data using different scanners could be possible but would require the sequence contain identical parameters to avoid introducing an uncontrollable variable, we are planning to recruit different laboratories to test the implanted RF coils with their existing cryoprobes in the future study. 

We have included an updated figure comparing SNR at different depths across the Bruker 4-array coil and the implanted RF coils. As shown in Supplementary Figure 7B, there is significant SNR enhancement up to 4 mm cortical depth for both single loop and Figure 8 implanted RF coils in comparison to the Bruker 4-array coil.

Author response image 1.

Comparison between implanted and commercial coils. A shows representative coils in the single loop (left) and figure 8 styles (right). Supplementary Table 1 provides a parts list and cost for making these coils and Supplementary Figure 1 provides a circuit diagram to assemble. B presents the SNR line profile values as a function of distance from Pia Matter for each coil tested at 9.4T: commercial phased array surface coil (4 Array), implanted single loop, and implanted figure 8. SNR values were calculated by dividing the signal by the standard deviation of the noise. C-E shows a representative FLASH image with line profile of SNR measurements from each of the coils used to create the graph seen in B. Clear visual improvement in SNR can be seen in figures C-E. C – Commercial phased array. D – Single loop at 9.4T. E – Figure 8 at 9.4T. (N4 array = 6, Nsingle loop = 5, Nfigure 8 = 5)

Additionally, we have added a supplementary figure (supp fig 1) of a circuit diagram, in an effort to disseminate the prototype design of the coils to other laboratories. We have included a detailed parts list with the cost for construction of the coils configured for our scanner(supp table 1). These specifics though would need to be adjusted to the precise field strength/bore size/animal the coil was being built for. As for reusability, the copper wire is cemented to the animal skull and this implantable coil should be considered as consumables for the awake mouse experiments, though the PCB parts can be retrieved.  

(2) In the introduction, the authors state that "Awake mouse fMRI has been well investigated". I disagree with this statement and others in the manuscript that gives the reader the impression that awake experiments are not a challenging and unresolved approach to fMRI experiments in mice (or rodents). Although there are multiple labs (maybe 15 worldwide) that have conducted awake mouse experiments (with varying degrees of success/thoroughness), we are far from a standardized approach. This is a strength of the current work and should be highlighted as such. I encourage the authors to read the recent systematic review that was published on this topic in Cerebral Cortex by Mandino et al. There are several elements in there that should influence the tone of this piece including awake mouse implementations with the Bruker Cryoprobe, prevalence of surgical preparations, and evaluations of stress.

Thank you for the comment. We agree with the reviewer that the current stage of awake mouse fMRI studies remains to be improved.  And, we have revised the Introduction to highlight the state-of-theart of awake mouse fMRI (Page 4 – line 81-88). 

(3) The authors also comment on implanted coils reducing animal stress - I don't know where this comment is coming from, as this has not been reported in the literature (to my knowledge) and the authors don't appear to have evaluated stress in their mice. 

Since question 3 and 4 are highly related to the acclimation procedures, we will answer the two questions together.   

(4) Following on the above point, measures of motion, stress, and more details on the acclimation procedure that was implemented in this study should be included.

We thank the reviewer to raise the animal training issues.  

During the animal training, we have measured both pupil dynamic and eye motion features from training sessions, of which the detailed procedure is described in Methods (page 7-9 – line 172236). 

The training procedure is carried out over a total of 5 weeks with four phases of training: i. Holding animal in hands, ii. Head-fixation and pupillometry, iii. Head-fixation and pupillometry with mockMRI acoustic exposure, iv. Head-fixation and pupillometry with Echo-Planar-Imaging (EPI) in the MR scanner.

Author response table 1.

As shown in Supp Fig 2B, the spectral power of pupil dynamics (<0.02Hz) and eye movements gradually increased as a function of the training time for head-fixed mice exposed to the mock MRI acoustic environment during phase 3.  In phase 4, when head-fixed mice were put into the scanner for the first time, both eye movements and pupil dynamics were initially reduced during scanning but recovered to an acclimated state on Day 2, similar to the level on Day 8 of phase 3.  These behavioral outputs would provide an alternative way to monitor the stress levels of the mice. 

Author response image 2.

The eye movements (A) and power spectra of pupil dynamics (<0.02Hz) (B) change during different training phases.

It should be noted that stress may be related to increased frequency of eye blinking or twitching movements in human subjects(1–3). Whereas, the eyeblink of head-fixed mice has been used for behavioral conditioning to investigate motor learning in normal behaving mice(4–6). Importantly, head-fixed mouse studies have shown that eye movements are significantly reduced compared to the free-moving mice(7). The increased eye movement during acclimation process would indicate an alleviated stress level of the head-fixed mice in our cases. Meanwhile, stress-related pupillary dilation could dominate the pupil dynamics at the early phase of training(8). We have observed a gradually increased pupil dynamic power spectrum at the ultra-slow frequency during phase 3, presenting the alleviated stress-related pupil dilation but recovered pupil dynamics to other factors, including arousal, locomotion, startles, etc. in normal behaving mice.  Despite the extensive training procedure of the present work in comparison to the existing awake mouse fMRI studies (training strategies for awake mice fMRI have been reviewed by Mandino et al. to show the overall training duration of existing studies(9)), the stress remains a confounding factor for the brain functional mapping in head-fixed mice. In particular, a recent study(10) shows that the corticosterone concentration in the blood samples of head-fixed mice is significantly reduced on Day 25 following the training but remains higher than in the control mice. In the discussion section, we have discussed the potential issues of stress-related confounding factors for awake mouse fMRI studies (Page 16 – lines 436-458). 

(1) A. Marcos-Ramiro, D. Pizarro-Perez, M. Marron-Romera, D. Gatica-Perez, Automatic blinking detection towards stress discovery. ICMI 2014 - Proceedings of the 2014 International Conference on Multimodal Interaction 307–310 (2014). https://doi.org/10.1145/2663204.2663239/SUPPL_FILE/ICMI1520.MP4.

(2) M. Haak, S. Bos, S. Panic, L. Rothkrantz, DETECTING STRESS USING EYE BLINKS AND BRAIN ACTIVITY FROM EEG SIGNALS. Lance 21, 76 (2009).

(3) E. Del Carretto Di Ponti E Sessam, Exploring the impact of Stress and Cognitive Workload on Eye Movements: A Preliminary Study. (2023).

(4) S. A. Heiney, M. P. Wohl, S. N. Chettih, L. I. Ru olo, J. F. Medina, Cerebellar-dependent expression of motor learning during eyeblink conditioning in head-fixed mice. J Neurosci 34, 14845–14853 (2014).

(5) S. N. Chettih, S. D. Mcdougle, L. I. Ruffolo, J. F. Medina, Adaptive timing of motor output in the mouse: The role of movement oscillations in eyelid conditioning. Front Integr Neurosci 5, 12996 (2011).

(6) J. J. Siegel, et al., Trace Eyeblink Conditioning in Mice Is Dependent upon the Dorsal Medial Prefrontal Cortex, Cerebellum, and Amygdala: Behavioral Characterization and Functional Circuitry. eNeuro 2, 51–65 (2015).

(7) A. F. Meyer, J. O’Keefe, J. Poort, Two Distinct Types of Eye-Head Coupling in Freely Moving Mice. Current Biology 30, 2116-2130.e6 (2020).

(8) H. Zeng, Y. Jiang, S. Beer-Hammer, X. Yu, Awake Mouse fMRI and Pupillary Recordings in the UltraHigh Magnetic Field. Front Neurosci 16, 886709 (2022).

(9) F. Mandino, S. Vujic, J. Grandjean, E. M. R. Lake, Where do we stand on fMRI in awake mice? Cereb Cortex 34 (2024).

(10) K. Juczewski, J. A. Koussa, A. J. Kesner, J. O. Lee, D. M. Lovinger, Stress and behavioral correlates in the head-fixed method: stress measurements, habituation dynamics, locomotion, and motor-skill learning in mice. Scientific Reports 2020 10:1 10, 1–19 (2020).

(5) It wasn't clear to me at what times the loop versus "Figure 8" coil was being used, nor how many mice (or how much data) were included in each experiment/plot. There is also no mention of biological sex.

Thank you for the comment. We have clarified sex and number. The figure 8 coil was only used as part of development to show the improvement of the coil design for cortical measurements. The detailed information is described in Method (Page 6 – line 127-129 & Page 10 – line 269-270). Additionally animal numbers have been included in the figure captions.

(6) Building on the points above, the manuscript overall lacks experimental detail (especially since the format has the results prior to the methods).

Thank you for the comment. We have modified the manuscript to increase the experimental detail and moved the methods section before the results.

(7) An observation is made in the manuscript that there is an appreciable amount of negative BOLD signal. The authors speculate that this may come from astrocyte-mediated BOLD during brain state changes (and cite anesthetized rat and non-human primate experiments). This is very strange to me. First, the negative BOLD signal is not plotted (please do this), further, there are studies in awake mice that measure astrocyte activation eliciting positive BOLD responses (see Takata et al. in Glia, 2017).

We thank the reviewer to raise the negative BOLD fMRI observation issue.  We added a subplot of the negative BOLD signal changes in the revised Figure 4. This negative BOLD signals across cortical areas could be coupled with brain state changes upon air-pu -induced startle responses. Our future studies are focusing on elucidating the brain-wide activity changes of awake mice with fMRI.  We also provide a detailed discussion of the potential mechanism underlying the negative BOLD fMRI signals. First, as reported in the paper (suggested  by the reviewer),  astrocytic Ca2+ transients coincide with positive BOLD responses in the activated cortical areas, which is aligning with the neurovascular coupling (NVC) mechanism. However, there is emerging evidence to show that astrocytic Ca2+ transients are coupled with both positive and negative BOLD responses in anesthetized rats(11) and awake mice(12). An intriguing observation is that cortex-wide negative BOLD signals coupled with the spontaneous astrocytic Ca2+ transients could co-exist with the positive BOLD signal detected at the activated cortex.  Studies have shown that astrocytes are involved in regulating brain state changes(13), in particular, during locomotion(14) and startle responses(15). These brain state-dependent global negative BOLD responses are also related to the arousal changes of both non-human primates(16) and human subjects(17).  The established awake mouse fMRI platform with ultra-high spatial resolution will enable the brain-wide activity mapping of the functional nuclei contributing to the brain state changes of head-fixed awake mice in future studies. (Page 17-18 – Line 478-490)

(11) M. Wang, Y. He, T. J. Sejnowski, X. Yu, Brain-state dependent astrocytic Ca2+ signals are coupled to both positive and negative BOLD-fMRI signals. Proc Natl Acad Sci U S A 115, E1647–E1656 (2018).

(12) C. Tong, Y. Zou, Y. Xia, W. Li, Z. Liang, Astrocytic calcium signal bidirectionally regulated BOLD-fMRI signals in awake mice in Proc. Intl. Soc. Mag. Reson. Med. 32, (2024).

(13) K. E. Poskanzer, R. Yuste, Astrocytes regulate cortical state switching in vivo. Proc Natl Acad Sci U S A 113, E2675–E2684 (2016).

(14) M. Paukert, et al., Norepinephrine controls astroglial responsiveness to local circuit activity. Neuron 82, 1263–1270 (2014).

(15) R. Srinivasan, et al., Ca2+ signaling in astrocytes from IP3R2−/− mice in brain slices and during startle responses in vivo. Nat Neurosci 18, 708 (2015).

(16) C. Chang, et al., Tracking brain arousal fluctuations with fMRI. Proc Natl Acad Sci U S A 113, 4518– 4523 (2016).

(17) B. Setzer, et al., A temporal sequence of thalamic activity unfolds at transitions in behavioral arousal state. Nat Commun 13 (2022).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

I really enjoyed this work. The maps shown are among the best-quality maps out there. Here are suggestions to the authors.

(1) Both the ACA and VRA are rather unexpected. The authors explain these briefly as being part of the associative cortical areas. Both the ACA and VRA are not canonical associative areas (or at least not to us). This warrants a stronger discussion.

To verify both ACA and VRA as associate areas, we provide the  connectivity map projections from the Allen Brain Atlas (seen below). These projections are derived from a Cre-dependent AAV tracing of axonal projections. We have included an explanation of this in the introduction. 

Author response image 3.

Representative images are shown indicating connections between the barrel cortex and retrosplenial area from an injection in the barrel cortex (Left panel) as well as the visual cortex and cingulate connection from an injection in the visual cortex (Right panel). Images are of connectivity map projections from the Allen Brain Atlas derived from a Cre-dependent AAV tracing of axonal projections

(2) This is a lot of work. But looking at the figures, this is not obvious. We read in the caption that several hundred trials were used. It would be good to also specify how many mice. It would be clearer to represent this info in the figure as well to support the fact that this is not a trivial acquisition.

Thank the reviewer to raise the e ort issue. We have edited the figure to include this information and included the numbers in the text as well

(3) The training protocol is seemingly extensive, but this is only visible by following another reference. Including a description in this work would help the reader make sense of the effort that went into this work.

We thank the reviewer to raise the training protocol issue. We have more thoroughly discussed the training method used for this study (page 7-9 – line 172-236)

(4) I really would love to see that dataset made freely available - this should be the norm.

The datasets have been uploaded to OpenNeuro 

Whisker (https://doi.org/10.18112/openneuro.ds005496.v1.0.1),  Visual (https://doi.org/10.18112/openneuro.ds005497.v1.0.0) and Zenodo:

SNR Line Profile Data & Data Processing Scripts: 

(https://zenodo.org/doi/10.5281/zenodo.13821455). 

(page 21 – line 573-579)

Reviewer #2 (Recommendations For The Authors):

(1) I'm a little confused about the stimulation paradigm and the effect of it causing an effective 2second TR (which is on the long side) - please elaborate (a figure might be helpful). The paradigm for visual stimulation also seems elaborate, can you please explain the logic and how it was developed?

Thank you for raising the detailed stimulation paradigm issues. The stimulation paradigm is independent and does not interfere with the setup of the effective 2-second TR. The 2-second TR is based on the usage of 2-segment EPI, each with a TR of 1-second. The application of 2-segment paradigm enables the echo spacing with 0.52 ms with effective image bandwidth with 3858Hz, assuring less image distortion.  The stimulation paradigm was defined by an “8s on, 32s o ” epoch such to elicit a strong BOLD response and could be used for any reasonable TR duration. 

We have included a figure outlining the stimulation paradigm (Supp Fig. 3)

(2) I had difficulties viewing the movies (on my MAC).

Thank you for this note. We have re-upload the videos in .mov format

Author response:

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

The reviewers found this manuscript to present convincing evidence for associative and non-associative behaviors elicited in male and female mice during a serial compound stimulus Pavlovian fear conditioning task. The work adds to ongoing efforts to identify multifaceted behaviors that reflect learning in classic paradigms and will be valuable to others in the field. The reviewers do note areas that would benefit from additional discussion and some minor gaps in data reporting that could be filled by additional analyses or experiments.

We thank the reviewers and the editors for their thoughtful and constructive critiques of our manuscript. We have updated our manuscript with data from additional experiments as suggested by the reviewers, and we have significantly edited the text and figures to reflect these additions. Our detailed, point-by-point responses are below.

Reviewer #1 (Public Review):

The main goal of the study was to tease apart the associative and non-associative elements of cued fear conditioning that could influence which defensive behaviors are expressed. To do this, the authors compared groups conditioned with paired, unpaired, or shock only procedures followed by extinction of the cue. The cue used in the study was not typical; serial presentation of a tone followed by a white noise was used in order to assess switches in behavior across the transition from tone to white noise. Many defensive behaviors beyond the typical freezing assessments were measured, and both male and female mice were included throughout. The authors found changes in behavioral transitions from freezing to flight during conditioning as the tone transitioned into white noise, and a switch in freezing during extinction such that it became high during the white noise as flight behavior decreased. Overall, this was an interesting analysis of transitions in defensive behaviors to a serially presented cue consisting of two auditory stimuli during conditioning and then extinction.

We thank the Reviewer for their supportive insight.

There are some concerns regarding the possibility that the white noise is more innately aversive than the tone, inducing more escape-like behaviors compared to a tone, especially since the shock only group also showed increased escape-like behaviors during the white noise versus tone. This issue would have been resolved by adding a control group where the order of the auditory stimuli was reversed (white noise->tone).

We appreciate this concern, and we have added two additional groups to address this possibility. We have conducted the same experimental paradigm with 2 reverse-SCS groups (WN—tone), one with paired (new PA-R group), and one with unpaired (new UN-R group), presentations to shock during conditioning. These experiments revealed that during conditioning day 2 in both reverse order groups, WN causes reductions in freezing and increases in locomotor activity (see revised Figure 2D), an effect that is stronger in the UN-R compared to the PA-R group. This locomotor effect is neither darting nor escape jumping in the PA-R group (revised Figure 3G, I; Figure 4G). In the UN-R group, WN induces more activity than the PA-R group (Figure 2D), including some jumping at WN onset (Figure 3H), but no darting (Figure 4G). It is worth noting that WN does not elicit defensive behavior before conditioning at the sound intensity we use (75dB; see Fadok et al. 2017, Borkar et al. 2020, Borkar et al. 2024). Together, these results suggest that WN is an inherently more salient stimulus than tone, and it can elicit defensive behaviors in shock-sensitized mice through non-associative mechanisms. Indeed, stimulus salience is a key factor in this paradigm for inducing activity (see Hersman et al. 2020).

While the more complete assessment of defensive behaviors beyond freezing is welcomed, the main conclusions in the discussion are overly focused on the paired group and the associative elements of conditioning, which would likely not be surprising to the field. If the goal, as indicated in the title, was to tease apart the associative and non-associative elements of conditioning and defensive behaviors, there needs to be a more emphasized discussion and explicit identification of the non-associative findings of their study, as this would be more impactful to the field.

We have rewritten the Discussion to provide a greater emphasis on the findings of the study that are more related to non-associative mechanisms. For example, we argue that cue-salience and changes in stimulus intensity can induce non-associative increases in locomotor behavior and tail rattling in shock-sensitized mice.

Reviewer #2 (Public Review):

Summary:

The authors examined several defensive responses elicited during Pavlovian conditioning using a serial compound stimulus (SCS) as the conditioned stimulus (CS) and a shock unconditioned stimulus (US) in male and female mice. The SCS consisted of tone pips followed by white noise. Their design included 3 treatment groups that were either exposed to the CS and US in a paired fashion, in an unpaired fashion, or only exposed to the shock US. They compared freezing, jumping, darting, and tail rattling across all groups during conditioning and extinction. During conditioning, strong freezing responses to the tone pips followed by strong jumping and darting responses to the white noise were present in the paired group but less robust or not present in the unpaired or shock only groups. During extinction, tone-induced freezing diminished while the jumping was replaced by freezing and darting in the paired group. Together, these findings support the idea that associative pairings are necessary for conditioned defensive responses.

Strengths:

The study has strong control groups including a group that receives the same stimuli in an unpaired fashion and another control group that only receives the shock US and no CS to test the associative value of the SCS to the US. The authors examine a wide variety of defensive behaviors that emerge during conditioning and shift throughout extinction: in addition to the standard freezing response, jumping, darting, and tail rattling were also measured.

We thank the Reviewer for their supportive appraisal of this study’s strengths.

Weaknesses:

This study could have greater impact and significance if additional conditions were added (e.g., using other stimuli of differing salience during the SCS), and determining the neural correlates or brain regions that are differentially recruited during different phases of the task across the different groups.

In the revised manuscript, we have conducted experiments with 2 reverse-SCS groups (WN—tone): one with paired (new PA-R group), and one with unpaired (new UN-R group), presentations to shock during conditioning. These experiments revealed that during conditioning day 2 in both reverse order groups, WN causes reductions in freezing and increases in locomotor activity (see revised Figure 2D), an effect that is stronger in the UN-R compared to the PA-R group. This locomotor effect is neither darting nor escape jumping in the PA-R group (revised Figure 3G, I; Figure 4G). In the UN-R group, WN induces more activity than the PA-R group (Figure 2D), including some jumping at WN onset (Figure 3H), but no darting (Figure 4G). Indeed, stimulus salience is a key factor in this paradigm for inducing activity (see Hersman et al. 2020). Together, these results suggest that WN is an inherently more salient stimulus than tone, and it can elicit defensive behaviors in shock-sensitized mice through non-associative mechanisms. It is worth noting that WN does not elicit defensive behavior before conditioning at the sound intensity we use (75dB; see Fadok et al. 2017, Borkar et al. 2020, Borkar et al. 2024).

We agree that determining the neuronal correlates and brain regions that are involved in defensive ethograms at various stages within this paradigm is of great importance, but we feel that those experiments are beyond the scope of the current study, which is focused on identifying behavioral differences based on associative and non-associative factors.

Reviewer #1 (Recommendations For The Authors):

In LINES 72-73, authors say they used a "truly random procedure" as one of their control groups. Then in LINES 113-116, they describe this group as "unpaired" where the "SCS could not reliably predict footshock". Combined, it is unclear if this group is random or unpaired. The "truly random procedure" is defined, by the cited Rescorla paper, as "the two events are programmed entirely randomly and independently in such a way that some "pairings" of CS and US may occur by chance alone". So, truly random would indicate that the shock may occur during the cue, while unpaired indicates the shock was explicitly unpaired from the cue. If the authors used a random procedure, the groups need to be labeled as random, not unpaired, and the # of cues that happened to coincide with footshock per animal needs to be reported somewhere. If the authors used an unpaired procedure (which appears to be the case based on 40-60s ITI between SCS and footshock being reported), it needs to be clearer and consistent throughout that it was explicitly unpaired, as well as removing the claim in LINE 72-73 that they used a "truly random procedure".

We did indeed use an explicitly unpaired procedure. We have adjusted the text and figures to better reflect this, and we removed any mentions of randomness with regards to the presentations of SCS and footshock.

Despite the lack of significant sex differences, it would still be helpful if data panels with individual data points (e.g. Fig 2E-J), were presented as identifiable by sex (e.g. closed vs open circles for males vs females).

The revised manuscript now compares four or five groups per figure, making data presentation complicated. Providing the individual data points in each panel reduces figure clarity, therefore, we feel it is best to present the data as box-and-whisker plots without them. However, the source data files for each figure are available to the reader and the data are clearly labeled to be identifiable by sex.

Is it not odd that all groups showed similar levels of contextual freezing during the 3min baseline? If shocks are unsignaled in the UN and SO groups, one would expect higher levels of contextual freezing compared to a paired group.

We are not certain why one would expect higher levels of contextual freezing in the UN and SO groups compared to the PA group at the beginning of conditioning day 2. Another study also looked at baseline freezing in a contextual fear group (which is the same as shock only in our study) and in an auditory cued fear conditioning group within the conditioning context, and their data show that freezing during the baseline period is equivalent between groups (Sachella et al., 2022).

During baseline on Extinction Day 1, it does seem that the unpaired and SO groups tend to have higher freezing levels compared to the paired groups. Author response image 1 shows baseline freezing during the first 3 minutes of extinction day 1. After two days of conditioning in the conditioned flight paradigm, contextual freezing either is, or trends to be significantly higher in the UN, UN-R, and SO groups than the PA and PA-R groups.

Author response image 1.

Baseline Freezing levels for all groups during the first extinction session. Baseline period is defined as the first 180 seconds of the session, before any auditory stimulus was presented. PA, Paired; UN, Unpaired; SO, Shock Only; PA-R, Paired Reverse; UN-R, Unpaired Reverse. *p<0.05, **p<0.01, ****p<0.0001.

Do the tone and WN elicit similar levels of defensive behaviors in a naïve mouse? Or have the authors tested WN followed by tone? Is there a potential issue that the WN may be innately aversive which is then amplified with training? i.e. does a tone preferentially induce freezing while WN induces active behaviors, regardless of which sensory stimulus is temporally closer to the shock? If the change in behavior is really due to the pairing and temporal proximity to shock, then there should be increased jumps, etc to the tone if trained with WN->tone.

WN can indeed be used as an aversive stimulus under certain conditions and at sufficiently high decibel levels. In the conditioned flight paradigm, WN is presented at 75dB, which is below the threshold for eliciting an acoustic startle response in a C57BL/6J mouse (Fadok et al. 2009). Also, during pre-exposure, when animals are naïve to the SCS, tone and WN stimuli do not elicit defensive behaviors (see Fadok et al. 2017, Borkar et al. 2020, 2024).

As suggested by the Reviewer, during revision we have included reverse-SCS paired (PA-R) and unpaired (UN-R) groups to test for the role of stimulus salience and stimulus order on defensive ethograms. During conditioning day 2, the PA-R group exhibited little freezing to the WN, with a slightly elevated activity index, and they exhibited robust freezing during tone (revised Figure 2A-H). The activity during the WN in the PA-R group was significantly lower than that of the PA group (Figure 2L). The PA-R group also did not respond to WN with escape jumps or darting (Figure 3I, 4G). The UN-R group displayed greater activity during the WN than the UN and PA-R groups, but less activity than the PA group (Figure 2D, H). The UN-R group did not dart but this group displayed some jumping at WN onset (Figure 3H), like what was observed in the UN group.

These data suggest that WN has inherent, salient properties that can induce some non-associative activity after the mouse has been sensitized by shock (see also Hersman et al. 2020 for more detailed analysis of stimulus salience in the conditioned flight paradigm). However, only in the PA group is robust flight behavior (comprised of high numbers of escape jumps and darting) observed. Therefore, both stimulus salience and temporal order are important for eliciting transitions from freezing to flight.

Fig 3G/4G are hard for me to understand. The figure legends say they're survival graphs but the y-axis labels "Latency to initial jump/dart (% of cohort)" confuses me. What is the purpose of these graphs? Perhaps they are not needed. Or consider presenting them similar to Fig 7C, D as those were more intuitive and faster for me to grasp.

We had intended these plots to show that a greater proportion of the paired group jumps and darts during WN compared to the unpaired group, and that the percentage of the cohort that jumps and darts increases across conditioning trials. Because these graphs were not clear, we have removed them, and we have replaced them with graphs comparing total cohort percentages that jumped (Figure 3I) or darted (Figure 4G) over the whole CD2 session.

For the extinction data, I did not see within group analyses for within or between session fear extinction to the tone. So, for the paired group, were the last 4 trials of Ext 1 significantly lower than the first 4 trials? If not, then they did not show within-session extinction. Also, for the paired group, were the last 4 trials of Ext 1 significantly different than the first 4 trials of Ext 2? This would test for long-term retention and spontaneous recovery.

In the original submission and in the revised manuscript, we calculated a delta change score for freezing during tone in the early versus late blocks of 4 trials, and then we statistically compared these differences across groups (Figure 5C, D). This allowed us to assess between-group differences in changes to tone-evoked freezing during extinction. Freezing to tone did decrease significantly over the first extinction session for the paired group (Early Ext1 vs Late Ext1, paired t-test, t(31) \= 6.23, p<0.0001), and when comparing late Ext1 and early Ext2, we found that tone-evoked freezing did significantly increase (Late Ext1 vs Early Ext2, paired t-test, t(31) \= 5.26, p<0.0001). This increase in cue-induced freezing between days of extinction is characteristic of C57BL/6J mice (Hefner et al., 2008). Our study did not test for more distal timepoints, so we cannot comment on the efficacy of long-term retention or spontaneous recovery.

For the conditioning and extinction data across Figs 2, 5 and 6, what I gather from them is that freezing is high to the tone and low to the WN during conditioning, and then low to the tone, and high to the WN across extinction. Then for activity levels I see they are low to the tone and high to the WN during conditioning, and then low to the WN during extinction. The piece that is missing is what are activity levels like to the tone during extinction. Are they low like in conditioning and remain low in extinction? Or do they increase across extinction as freezing decreases? As I was going through these graphs I drew myself out step function summaries of the freezing and activity levels between tone/WN for conditioning vs extinction; maybe the authors could consider a summary figure.

We thank the Reviewer for their interest. We found that within the paired group, activity to tone remained low throughout both days of extinction (though increased within each session) and did not return to normal activity levels. We present this data in Author response image 2. We thank the Reviewer for the suggestion of a summary figure, but we feel there are too many axes of classification (between-group, within-group, multiple behaviors, tone/WN, conditioning/extinction) to coherently present our findings in a single figure.

Author response image 2.

Trial-by-trial plot of activity index during the tone period of SCS across both extinction sessions for the PA group. SCS, Serial compound stimulus; Ext, extinction; PA, Paired.

In the discussion (LINE 592-3), they discuss that shock sensitization in the SO group may prime a stressed animal to dart more readily to WN upon stimulus transition. Should this not also happen during the transition of silence to tone? What is special about a transition between two auditory stimuli that would result in panic like behavior in an animal that only received shock presentations? This also gets back to an earlier concern above regarding the potentially innately aversiveness of the WN.

After 2 days of shock sensitization, we observe that mice exhibit freezing to the tone during the first three trials of extinction day 1 (Figure 5A). This non-associative freezing response is like that observed in other studies of non-associative fear processing (please see Kamprath and Wotjak, 2004). As trials progress during extinction day 1, mice do become mildly activated during the tone (Author response image 3). The transition to WN in the shock-only group during extinction induces non-associative darting responses, but it does not induce escape jumping behavior (Figure 7).  We hypothesize that the innate salience of the WN is a vital factor contributing to these escalated responses. The importance of stimulus salience in conditioned flight was also demonstrated by Hersman et al., 2020 for SCS conditioning, and by Furuyama et al., 2023 for single tone conditioning.  Just as with conditional freezing responses (Kamprath and Wotjak, 2004), we believe that conditional flight is controlled by summative components, one being associative and the other non-associative.

Author response image 3.

Trial-by-trial plot of activity index during the tone period of SCS across both extinction sessions for the SO group. SCS, Serial compound stimulus; Ext, extinction; SO, Shock Only.

In the discussion (LINE 583), they say that the development of explosive defensive behaviors are "not achievable with traditional single-cue Pavlovian conditioning paradigms". The authors should include a caveat here that the current study did not compare their results to a group of mice that received just WN-shock pairings.

We thank the reviewer for this comment. This statement was meant to highlight that traditional paradigms do not offer an element of signaling the temporal imminence of threat, only its inevitability. It was not our intention to state that defensive escape behaviors were unachievable in single-cue conditioning paradigms, and we regret not making this clear. Indeed, the supplement of Fadok et al. 2017 shows that WN-shock conditioning is capable of inducing flight, Furuyama et al. 2023 shows that tone-shock conditioning is capable of inducing flight under specific parameters, and Gruene et al. 2015 demonstrates that single CS-US pairings induce conditional darting behaviors in female rats. We have adjusted the text to better reflect our intent.  

Minor comment to LINE 613-5: Speaking as someone who has done fear conditioning in both mice and rats, tail rattling may be specific to mice (I have seen this often) and likely not observable in rats (never seen it).

We thank the Reviewer for this information. We have adjusted our text to mainly discuss mouse-specific tail rattling.

Reviewer #2 (Recommendations For The Authors):

The research questions in this study are novel and bring new insight to the field. However, there are some issues that can be addressed to improve the overall quality of the study, namely, the reader is left wanting to know more, especially about how neural circuits contribute to these different defensive behaviors during this task. Below are some recommendations for the authors that would greatly improve the impact and significance of this study.

(1) What are the neural correlates or circuits recruited during these different defensive behaviors across the course of conditioning and extinction? How might they differ between the PA and UN groups? What differences might emerge when an animal is shifting their defensive behavior from freezing to darting, for example? Answering these questions would require intensive additional experiments, therefore more discussion of possible neural mechanisms that might be recruited during this task would be appreciated, given the scope of the subject area.

We agree that understanding the neural circuits recruited during these behaviors and across conditioning and extinction is of vital importance. We are actively working on these questions, and we have published on the role of central amygdala circuits (Fadok et al. 2017) as well as on top-down control of flight by the medial prefrontal cortex (Borkar et al. 2024). Because the current manuscript is focused on learning mechanisms influencing defensive behavior, we would prefer to focus our discussion on that, rather than speculating on possible neural mechanisms. However, we have added a statement in the Discussion (LINES 706-707) emphasizing that future studies should investigate the neuronal mechanisms contributing to threat associations and different defensive behaviors.

(2) Were any vocalizations observed during conditioning or extinction phases? If not, could you speculate how type and occurrence of vocalizations might correlate with the different defensive responses observed?

Audible vocalizations were only observed during footshock presentations (squeaks). Unfortunately, we do not have the proper specialized recording equipment to monitor the full spectrum of mouse vocalizations, especially those in the ultrasonic range. Thus, we cannot speculate on the nuances of vocalizations in mice with respect to this behavioral paradigm. To the best of our knowledge, mice have not been reported to emit specific ultrasonic calls during conditioned threat like those of rats. That said, it would be of interest to determine if mice emit different vocalizations during different defensive behaviors.

(3) The transition from freezing to flight during the SCS is thought to be due to the close proximity of threat imminence between the WN CS and shock US. What if you switched the order of the SCS stimuli to WN followed by tone stimuli? If the salience of the WN stimulus is truly driving the jumping behavior, then it would be observed even if the WN stimulus preceded the pure tone stimulus and that would bring additional evidence that it is the associative value of the stimuli rather than its salience that's driving the defensive behaviors. What do you predict you would observe in rodents that were given a WN-tone SCS paired and unpaired in the same design of this study?

As suggested by the reviewer, we collected data from reverse-SCS paired and unpaired groups and reported our findings within the manuscript. Our detailed findings are also discussed above. Overall, we find that a combination of stimulus salience and temporal proximity, and a summation of non-associative and associative mechanisms, are necessary to elicit explosive flight behavior (escape jumping and darting).

References

Borkar CD, Dorofeikova M, Le QE, Vutukuri R, Vo C, Hereford D, Resendez A, Basavanhalli S, Sifnugel N, Fadok JP (2020) Sex differences in behavioral responses during a conditioned flight paradigm. Behavioural Brain Research 389:112623.

Borkar CD, Stelly CE, Fu X, Dorofeikova M, Le QE, Vutukuri R, Vo C, Walker A, Basavanhalli S, Duong A, Bean E, Resendez A, Parker JG, Tasker JG, Fadok JP (2024) Top-down control of flight by a non-canonical cortico-amygdala pathway. Nature 625: 743-749.

Fadok JP, Krabbe S, Markovic M, Courtin J, Xu C, Massi L, Botta P, Bylund K, Müller C, Kovacevic A, Tovote P, Lüthi A (2017) A competitive inhibitory circuit for selection of active and passive fear response. Nature 542:96-100.

Furuyama T, Imayoshi A, Iyobe T, Ono M, Ishikawa T, Ozaki N, Kato N, Yamamoto R (2023) Multiple factors contribute to flight behaviors during fear conditioning. Scientific Reports 13:10402. 

Gruene TM, Flick K, Stefano A, Shea SD, Shansky RM (2015) Sexually divergent expression of active and passive conditioned fear responses in rats. eLIfe 4:e11352.

Hefner K, Whittle N, Juhasz J, Norcross M, Karlsson RM, Saksida LM, Bussey TJ, Singewald N, Holmes A (2008) Impaired Fear Extinction Learning and Cortico-Amygdala Circuit Abnormalities in a Common Genetic Mouse Strain. Journal of Neuroscience 6:8074-8085.

Hersman S, Allen D, Hashimoto M, Brito SI, Anthony T (2020) Stimulus salience determines defensive behaviors elicited by aversively conditioned serial compound auditory stimuli. elife 9:e53803. 

Kamprath K and Wotjak CT (2004) Nonassociative learning processes determine expression and extinction of conditioned fear in mice. Learning & Memory 11:770-786.

Sachella TE, Ihidoype MR, Proulx CD, Pafundo DE, Medina JH, Mendez P & Piriz J (2022) A novel role for the lateral habenula in fear learning. Neuropsychopharmacology 47:1210-1219.

Author response:

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

We thank the reviewers and editor for their positive view and constructive valuable comments on the manuscript.  Following we address the suggestions of the reviewers.

Reviewer #1 (Public Review):

(1) It will be interesting to monitor the levels of another MIM insertase namely, OXA1. This will help to understand whether some of the observed changes in levels of OXPHOS subunits are related to alterations in the amounts of this insertase.

OXA1 was not detected in the untargeted mass spectrometry analysis, most likely due to the fact that it is a polytopic membrane protein, spanning the membrane five times (1,2). Consequently, we measured OXA1 levels with immunoblotting, comparing patient fibroblast cells to the HC. No significant change in OXA1 steady state levels was observed.

These results are now displayed (Fig. S3B and C) and discussed in the revised manuscript.

Figure 3: How do the authors explain that although TIMM17 and TIMM23 were found to be significantly reduced by Western analysis they were not detected as such by the Mass Spec. method?

The untargeted mass spectrometry in the current study failed to detect the presence of TIMM17 for both, patient fibroblasts and mice neurons, while TIMM23 was detected only for mice neurons and a decrease was observed for this protein but was not significant. This is most likely due to the fact that TIMM17 and TIMM23 are both polytopic membrane proteins, spanning the membrane four times, which makes it difficult to extract them in quantities suitable for MS detection (2,3).

(2) How do the authors explain the higher levels of some proteins in the TIMM50 mutated cells?

The levels of fully functional TIM23 complex are deceased in patients' fibroblasts. Therefore, the mechanism by which the steady state level of some TIM23 substrate proteins is increased, can only be explained relying on events that occur outside the mitochondria. This could include increase in transcription, translation or post translation modifications, all of which may increase their steady state level albite the decrease in the steady state level of the import complex.

(3) Can the authors elaborate on why mutated cells are impaired in their ability to switch their energetic emphasis to glycolysis when needed?

Cellular regulation of the metabolic switch to glycolysis occurs via two known pathways: 1) Activation of AMP-activated protein kinase (AMPK) by increased levels of AMP/ADP (4). 2) Inhibition of pyruvate dehydrogenase (PDH) complexes by pyruvate dehydrogenase kinases (PDK) (5). Therefore, changes in the steady state levels of any of these regulators could push the cells towards anaerobic energy production, when needed. In our model systems, we did not observe changes in any of the AMPK, PDH or PDK subunits that were detected in our untargeted mass spectrometry analysis (see volcano plots below, no PDK subunits were detected in patient fibroblasts). Although this doesn’t directly explain why the cells have an impaired ability to switch their energetic emphasis, it does possibly explain why the switch did not occur de facto.

Author response image 1.

Reviewer #2 (Public Review):

(1) The authors claim in the abstract, the introduction, and the discussion that TIMM50 and the TIM23 translocase might not be relevant for mitochondrial protein import in mammals. This is misleading and certainly wrong!!!

Indeed, it was not in our intention to claim that the TIM23 complex might not be relevant. We have now rewritten the relevant parts to convey the correct message:

Abstract –

Line 25 - “Strikingly, TIMM50 deficiency had no impact on the steady state levels of most of its putative substrates, suggesting that even low levels of a functional TIM23 complex are sufficient to maintain the majority of complex-dependent mitochondrial proteome.”

Introduction –

Line 87 - Surprisingly, functional and physiological analysis points to the possibility that low levels of TIM23 complex core subunits (TIMM50, TIMM17 and TIMM23) are sufficient for maintaining steady-state levels of most presequence-containing proteins. However, the reduced TIM23CORE component levels do affect some critical mitochondrial properties and neuronal activity.

Discussion –

Line 339 – “…surprising, as normal TIM23 complex levels are suggested to be indispensable for the translocation of presequence-containing mitochondrial proteins…”

Line 344 – “…it is possible that unlike what occurs in yeast, normal levels of mammalian TIMM50 and TIM23 complex are mainly essential for maintaining the steady state levels of intricate complexes/assemblies.”

Line 396 – “In summary, our results suggest that even low levels of TIMM50 and TIM23CORE components suffice in maintaining the majority of mitochondrial matrix and inner membrane proteome. Nevertheless, reductions in TIMM50 levels led to a decrease of many OXPHOS and MRP complex subunits, which indicates that normal TIMM50 levels might be mainly essential for maintaining the steady state levels and assembly of intricate complex proteins.”

Reviewer #1 (Recommendations For The Authors):

(1) Lines 25-26: The authors write "Strikingly, TIMM50 deficiency had no impact on the steady state levels of most of its substrates". Since the current data challenges the definition of some proteins as substrates of TIMM50, I suggest using the term "putative substrates".

Changed as suggested

(2) Line 27: It is not clear whether the wording "general import role of TIM23" it refers to the TIM23 protein or the TIM23 complex. This should be clarified.

Clarified. It now states "TIM23 complex".

(3) Line 72: should be "and plays".

Changed as suggested.

(4) It will be helpful to include in Figure 1 a small scheme of TIMM50 and to indicate in which domain the T252M mutation is located.

We predicted the AlphaFold human TIMM50 structure and indicated the mutation site and the different TIMM50 domains. The structure is included in Fig. 1A.

(5) I suggest labelling the "Y" axis in Fig. 1B as "Protein level (% of control)".

Changed as suggested in Fig. 1C (previously Fig. 1B) and in Fig. 2C.

(6) Line 179: since the authors tested here only about 10 mitochondrial proteins (out of 1500), I think that the word "many" should be replaced by "several representative" resulting in "steady state levels of several representative mitochondrial proteins".

Changed as requested.

(7) Line 208: correct typo.

Typo was corrected.

(8) Figure 4 is partially redundant as its data is part of Figure 3. The authors can consider combining these two figures. Accordingly, large parts of the legend of Figure 4 are repeating information in the legend to Figure 3 and can refer to it.

We revamped Figures 3 and 4. Figure 3 now shows the analysis of fibroblasts proteomics while Figure 4 focuses on neurons proteomics. We also modified the legend of Figure 4.

Reviewer #2 (Recommendations For The Authors):

(1) Abstract: 'Strikingly, TIMM50 deficiency had no impact on the steady state levels of most of its substrates, challenging the currently accepted import dogma of the essential general import role of TIM23 and suggesting that fully functioning TIM23 complex is not essential for maintaining the steady state level of the majority of mitochondrial proteins'. This sentence needs to be rephrased. The data do not challenge any dogma! The authors only show that lower levels of functional TIM23 are sufficient.

We have rewritten all the relevant sentences as suggested (details are also mentioned in response to reviewer 2 public review point 1)

(2) Introduction: 'Surprisingly, functional and physiological analysis points to the possibility that TIMM50 and a fully functional TIM23 complex are not essential for maintaining steady-state levels of most presequence-containing proteins'. This again needs to be rephrased.

Rewritten as suggested (details mentioned in response to reviewer 2 public review point 1)

(3) Discussion: 'In summary, our results challenge the main dogma that TIMM50 is essential for maintaining the mitochondrial matrix and inner membrane proteome, as steady state level of most mitochondrial matrix and inner membrane proteins did not change in either patient fibroblasts or mouse neurons following a significant decrease in TIMM50 levels.' This again needs to be rephrased.

Rewritten as suggested (details mentioned in response to reviewer 2 public review point 1)

(4) The analysis of the proteomics experiment should be improved. The authors show in Figures 3 and 4 several times the same volcano plots in which different groups of proteins are indicated. It would be good to add (a) a principal component analysis to show that the replicates from the mutant samples are consistently different from the controls, (b) a correlation plot that compares the log-fold-change of P1 to that of P2 to show which of the proteins are consistently changed in P1 and P2 and (c) a GO term analysis to show in an unbiased way whether mitochondrial proteins are particular affected upon TIMM50 depletion.

Figures 3 and 4 have been changed to avoid redundancy. Figure 3 now focuses on fibroblasts proteomics (with additional analysis), while Figure 4 focuses on neurons proteomics. PCA analysis was added in Fig S1, showing that the proteomics replicates of both patients (P1 and P2) are consistently different than the healthy control (HC) replicates. Correlation plots were added in Figure 3C and D, showing high correlation of the downregulated and upregulated mitochondrial proteins between P1 and P2. These plots further highlight that MIM proteins are more affected than matrix proteins and that the OXPHOS and MRP systems comprise the majority of significantly downregulated proteins in both patients. GO term analysis was performed for all the detected proteins that got significantly downregulated in both patients. The GO term analysis is displayed in Figure S3A, and shows that mitochondrial proteins, mainly of the OXPHOS and MRP machineries, are particularly affected.

(5) Figure 1. The figure shows the levels of TIM and TOM subunits in two mutant samples. The quantifications suggest that the levels of TIMM21, TOMM40, and mtHsp60 are not affected. However, from the figure, it seems that there are increased levels of TIMM21 and reduced levels of TOMM40 and mtHsp60. Unfortunately, in the figure most of the signals are overexposed. Since this is a central element of the study, it would be good to load dilutions of the samples to make sure that the signals are indeed in the linear range and do scale with the amounts of samples loaded.

The representative WB panels display the Actin loading control of the representative TIMM50 repeat (the top panel). However, each protein was tested separately, at least three times, and was normalized to its own Actin loading control.

(6) Figure 2B. All panels are shown in color except the panel for TIMM17B which is grayscale. This should be changed to make them look equal.

All the western blot panels were changed to grayscale.

(7) Discussion: 'Despite being involved in the import of the majority of the mitochondrial proteome, no study thus far characterized the effects of TIMM50 deficiency on the entire mitochondrial proteome.' This sentence is not correct as proteomic data were published previously, for example for Trypanosomes (PMID: 34517757) and human cells (PMID: 38828998).

We have corrected the statement to “Despite being involved in the import of the majority of the mitochondrial proteome, little is known about the effects of TIMM50 deficiency on the entire mitochondrial proteome.”

(8) A recent study on a very similar topic was published by Diana Stojanovki's group that needs to be cited: PMID: 38828998. The results of this comprehensive study also need to be discussed!!!

We have added the following in the discussion:

Line 362 – “These observations are similar to the recent analysis of patient-derived fibroblasts which demonstrated that TIMM50 mutations lead to severe deficiency in the level of TIMM50 protein (6,7). Notably, this decrease in TIMM50 was accompanied with a decrease in the level of other two core subunits, TIMM23 and TIMM17. However, unexpectedly, proteomics analysis in our study and that conducted by Crameri et al., 2024 indicate that steady state levels of most TIM23-dependent proteins are not affected despite a drastic decrease in the levels of the TIM23CORE complex (7). The most affected proteins constitute of intricate complexes, such as OXPHOS and MRP machineries. Thus, both these studies indicate a surprising possibility that even reduced levels of the TIM23CORE components are sufficient for maintaining the steady state levels of most presequence containing substrates.

(1) Homberg B, Rehling P, Cruz-Zaragoza LD. The multifaceted mitochondrial OXA insertase. Trends Cell Biol. 2023;33(9):765–72.

(2) Carroll J, Altman MC, Fearnley IM, Walker JE. Identification of membrane proteins by tandem mass spectrometry of protein ions. Proc Natl Acad Sci U S A. 2007;104(36):14330–5.

(3) Ting SY, Schilke BA, Hayashi M, Craig EA. Architecture of the TIM23 inner mitochondrial translocon and interactions with the matrix import motor. J Biol Chem [Internet]. 2014;289(41):28689–96. Available from: http://dx.doi.org/10.1074/jbc.M114.588152

(4) Trefts E, Shaw RJ. AMPK: restoring metabolic homeostasis over space and time. Mol Cell [Internet]. 2021;81(18):3677–90. Available from: https://doi.org/10.1016/j.molcel.2021.08.015

(5) Zhang S, Hulver MW, McMillan RP, Cline MA, Gilbert ER. The pivotal role of pyruvate dehydrogenase kinases in metabolic flexibility. Nutr Metab. 2014;11(1):1–9.

(6) Reyes A, Melchionda L, Burlina A, Robinson AJ, Ghezzi D, Zeviani M.  Mutations in TIMM50 compromise cell survival in OxPhos‐dependent metabolic conditions . EMBO Mol Med. 2018;

(7) Crameri JJ, Palmer CS, Stait T, Jackson TD, Lynch M, Sinclair A, et al. Reduced Protein Import via TIM23 SORT Drives Disease Pathology in TIMM50-Associated Mitochondrial Disease. Mol Cell Biol [Internet]. 2024;0(0):1–19. Available from: https://doi.org/10.1080/10985549.2024.2353652

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):  

Summary:

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

However, the results as they are currently presented are not easy to follow and could use some restructuring, especially the electrophysiology. Also, the main conclusion that the authors draw from the data, that aDLS and pVLS contribute to different phases of discrimination learning and influence the animal's response strategy in different ways, is not strongly supported by the data and deserves some additional caveats and limitations of the study in the discussion. 

We appreciate the reviewer’s valuable feedback, which has been beneficial for improvement of our manuscript. In response to the reviewer’s comments, we have revised multiple parts of the manuscript, including explanations of electrophysiological data. We have also provided additional data to support our main conclusion and addressed caveats and limitations related to the data in the Discussion section. For more details, please refer to the responses to each comment.

Comment 1: The authors have rigorously used PET neuroimaging, which is an interesting noninvasive method to track brain activity during behavioral states. However, in the case of a freely moving behavior where the scans are performed ~30 minutes after the behavioral task, it is unclear what conclusions can be drawn about task-specific brain activity. The study hinges on the neuroimaging findings that both areas of the lateral striatum (aDLS and pVLS) show increased activity during acquisition, but the DMS shows a reduction in activity during the late stages of behavior, and some of these findings are later validated with complementary experiments. However, the limitations of this technique can be further elaborated on in the discussion and the conclusions.

As described in our response to the following two comments (a, b) from the reviewer, in the PET imaging study we first analyzed task-related activity by comparing ¹⁸F-FDG uptake on different days of the auditory discrimination task with that on Day 4 of the single lever press task as a control. Next, we analyzed learning-dependent activity by comparing the uptake on different days of the discrimination task with that on Day 2 of the same task. Based on the results of both analyses, we concluded that the activity in the striatal subregions changes during the progress of discrimination learning. The behavioral significance of striatal subregions was tested by excitotoxic lesion and pharmacological blockade experiments. The explanation of imaging data analysis may have been insufficient to fully communicate dynamic changes in the activity of striatal subregions. Therefore, we have clarified our voxel-based statistical parametric analysis method to better explain the dynamic activity changes in the striatal subregions. Please refer to the following responses to comments 1 (a, b).

Comment 1 (a): In commenting on the unilateral shifts in brain striatal activity during behavior, the authors use the single lever task as a control, where many variables affecting neuronal activity might be different than in the discriminatory task. The study might be better served using Day 2 measurements as a control against which to compare activity of all other sessions since the task structures are similar.

We initially analyzed task-related activity by comparing ¹⁸F-FDG uptake on one of Days 2, 6, 10, or 24 of auditory discrimination task with that on Day 4 of the single lever press task. This task was used as a control that does not require a decision process based on the auditory stimulus. We observed significant increases in the activity of the unilateral aDLS on Day 6 and in that of the bilateral pVLS on Day 10 of the discrimination task. We also observed a significant decrease in the unilateral DMS on Day 24 (see Figures 2F and 2G). Next, as suggested, we compared the uptake on one of Days 6, 10, or 24 with that on Day 2 as a control to evaluate learning-dependent activity. The activity showed significant increases in the bilateral aDLS on Day 6 and in the unilateral pVLS on Day 10, and a significant decrease in the bilateral DMS on Day 24 (see Figures 2H). 

The reviewer has suggested a discrepancy in the activity of the unilateral or bilateral striatal subregions under certain conditions between the image data (shown in Figures 2F–H) and plot data (Figures 2J–L). This discrepancy is also suggested in the following Comment 1 (b). For example, in the image data the brain activity was increased in the unilateral (left) aDLS on Day 6 of the discrimination task as compared to Day 4 of the single lever task (Figure 2F). In the plot data, ¹⁸F-FDG uptake reached a peak on Day 6 in both the left and right sides of the aDLS (Figure 2J), and the uptake in the left aDLS on Day 6 significantly increased relative to the value of the single lever press, whereas the value in the right aDLS on Day 6 tended to increase relative to that of the single lever press with no significant difference. The plot data showing the unilaterality in the aDLS activation relative to the single lever press are consistent with the image data. On the other hand, the ¹⁸F-FDG uptake in the aDLS on Day 6 compared to the value on Day 2 was significantly increased in both sides. Similar observations were made in the activity in the pVLS on Day 10 compared to that on Day 2, as well as in the DMS activity on Day 24 relative to that of the single lever press. 

Our analysis of both task-related and learning-dependent activities revealed dynamic changes in striatal subregions during discrimination learning. We investigated the brain regions in which ¹⁸F-FDG uptake significantly increased or decreased during the learning processes, applying a statistical significance threshold (p < 0.001, uncorrected) and an extent threshold, by using a voxel-based statistical parametric analysis. In the image data, the voxels showing significant differences between two conditions are visualized on the brain template. The plot data show the amount of ¹⁸FFDG uptake in the voxels, which was detected by the voxel-based analysis. The insufficient explanation of the data analysis of PET imaging in the initial manuscript may have led to a misunderstanding regarding the activity in the unilateral or bilateral striatal subregions. Therefore, we have revised the explanation for voxel-based statistical parametric analysis, adding a more detailed description of the thresholds in the text (page 7, lines 143–145) and Methods (page 27, lines 672–675).

Comment 1 (b): From the plots in J, K, and L, it seems that shifts in activity in the different substructures are not unilateral but consistently bilateral, in contrast to what is mentioned in the text. Possibly the text reflects comparisons to the single lever task, and here again, I would emphasize comparing within the same task.

Please see our response to the first comment (a) regarding our explanation of the consistency in the activity of the unilateral or bilateral striatal subregions between the image and plot data. We have also revised the explanation in the corresponding sections of the manuscript, as described above.

Comment 2: In Figure 2, the authors present compelling data that chronic excitotoxic lesions with ibotenic acid in the aDLS, pVLS, and DMS produce differential effects on discrimination learning. However, the significant reduction in success rate of performance happens as early as Day 6 in both IBO groups in both aDLS and pVLS mice. This would seem to agree with conclusions drawn about the role of aDLS in the middle stages of learning in Figure 2, but not the pVLS, which only shows an increased activity during the late stages of the behavior.  

Figure 3 shows the behavioral effects of ibotenic acid injections into striatal subregions in rats. For the aDLS injection, we performed two-way repeated ANOVA, which revealed a significant main effect of group or day and a significant interaction of group × day, and added the simple main effects between the treatments to the figure (Figure 3G). We observed significant differences in the success rate mainly at the middle stage of learning. In contrast, for the pVLS injection there was no significant interaction for group × day, although the main effects of group or day was significant by two-way repeated ANOVA (Figure 3H). Consequently, it was unclear as to when exactly the significant reduction occurred. These results indicate that the aDLS and pVLS are necessary for the acquisition of auditory discrimination, and that the aDLS is mainly required for the middle stage. Similar results were observed in the win-shift-win strategy in the aDLS and pVLS (Figures 3J and 3K).

Next, we performed temporal inhibition of neuronal activity in striatal subregions by muscimol treatment in order to examine whether the activity in the subregions is linked with learning processes at different stages. In this experiment, muscimol was injected into the aDLS or pVLS at the middle or late stage, and the resultant effects on the success rate were investigated. The success rate in the muscimol-injected groups into the aDLS significantly decreased at the middle stage, but not at the early and late stages (Figure 4C). In contrast, the rate in the muscimol groups into the pVLS significantly decreased at the late stage, but not at the early or middle stages (Figure 4D). The results indicate that the aDLS and pVLS are mainly involved in the processes at the middle and late stages, respectively, and support the PET imaging data showing the activation of two striatal subregions at the various stages.

We have now provided the results of simple main effects analysis for the aDLS lesion (Figures 3G and 3J) and revised the description of the Results section (page 8, lines 174–178, page 8, lines 186–188, and page 9, line 205-206) and Figure legend (page 44, lines 1000‒1003, and page 44, lines 1010–1013). We have also added the results of simple main effects analysis in Figure 3J.

Comment 3: In Figure 4, the authors show interesting data with transient inactivation of subregions of the striatum with muscimol, validating their findings that the aDLS mediates the middle and the pVLS the late stages of learning, and the function of each area serves different strategies. However, the inference that aDLS inactivation suppresses the WSW strategy "moderately" is not reflected in the formal statistical value p=0.06. While there still may be a subtle effect, the authors would need to revise their conclusions appropriately to reflect the data. In addition, the authors could try a direct comparison between the success rate during muscimol inhibition in the mid-learning session between the aDLS and pVLS-treated groups in Figure 4C (middle) and 4D (middle). If this comparison is not significant, the authors should be careful to claim that inhibition of these two areas differentially affects behavior.

In Figure 4E, aDLS inhibition showed a tendency to reduce slightly win-shift-win strategy at the middle stage (t[14] = 2.038, p = 0.061, unpaired Student’s t-test). In accordance with the reviewer’s comment, we changed the word “moderate” to “subtle” (page 12, line 272).

In the temporal inhibition of the striatal subregions, the aDLS and pVLS experiments (panels C and D, respectively) were conducted separately. Since it is difficult to directly compare the data obtained from different experiments, we did not carry out a direct comparison of the success rate between the aDLS and pVLS injections. 

Comment 4: The authors have used in vivo electrophysiological techniques to systematically investigate the roles of the aDLS and the pVLS in discriminatory learning, and have done a thorough analysis of responses with each phase of behavior over the course of learning. This is a commendable and extremely informative dataset and is a strength of the study. However, the result could be better organized following the sequence of events of the behavioral task to give the reader an easier structure to follow. Ideally, this would involve an individual figure to compare the responses in both areas to Cue, Lever Press, Reward Sound, and First Lick (in this order).

We first showed changes in the proportion of event-related neurons during the acquisition phase (Figure S5). Next, we conducted a detailed analysis of the characteristics of aDLS and pVLS neuronal activity. Specifically, we found several types of event-related neurons, including: (1) reward sound-related neurons representing behavioral outcomes in the aDLS; (2) first licking-related neurons showing sustained activity after the reward in the aDLS and pVLS; and (3) cue-onset and cue-response neurons associated with the beginning and ending of a behavior in the pVLS.

Descriptions of the characteristics of event-related neurons according to the sequence of events in a trial, as the reviewer has suggested, is another way to provide an easy structure for understandings on the electrophysiological data. However, we focused on the characteristics of aDLS neurons at the middle stage and pVLS neurons at the late stage of discrimination learning. Therefore, we explained the electrophysiological data based on the order of learning stages rather than the sequence of events in the trial, as described above.

Comment 5: An important conceptual point presented in the study is that the aDLS neurons, with learning, show a reduction in firing rates and responsiveness to the first lick as well as the behavioral outcome, and don't play a role in other task-related events such as cue onset. However, the neuroimaging data in Figure 2 seems to suggest a transient enhancement of aDLS activity in the mid-stage of discriminatory learning, that is not reflected in the electrophysiology data. Is there an explanation for this difference?

In the ¹⁸F-FDG PET imaging study, the brain activity in the aDLS reached a peak at the middle stage of the acquisition phase of auditory discrimination (Figure 2J). In the multi-unit electrophysiological recording experiment, the firing activity of the aDLS neuron subpopulations related to the behavioral outcome showed no significant differences among the three stages (Figure 5E), while the proportion of these subpopulations were gradually reduced through the progress of learning stages (Figure 5F). The extent of the firing activity and length of the firing period of other subpopulations showing sustained activation after the reward appeared to show a learning-dependent decrease (Figures 6B and 6C), although the proportion of these subpopulations indicated no correlation with the progress of the learning (Figure 6D). Patterns of the temporal changes in brain activity in striatal subregions across the learning stages did not match completely the time variation in the property or proportion of specific event-related neurons. In our electrophysiological analysis, we identified well-isolated neurons from the striatal subregions during the auditory discrimination task, focusing on putative medium spiny neurons (Figures S4E–S4G). Based on the combinatorial pattern of the tone instruction cue (high tone/H or low tone /L), and lever press (right/R or left/L), we categorized the electrophysiological data into the four trials, including the HR, LL. LR, and HL. We identified HR or LL type neurons showing significant changes in the firing rate related to specific events, such as cue onset, choice response, reward sound, and first licking compared to the baseline firing rate. These neurons were further divided into two groups with increased or decreased activity relative to the baseline firing (Figures S5A and S5B). In the present study, we focused on event-related neurons with increased activity. Because of the analysis limited to neuronal subpopulations related to specific events with the increased activity, it is difficult to fully explain dynamic shifts in the brain activity of striatal subregions dependent on the progress of learning by the time variation of firing activity of individual event-related neurons. The activity of other subpopulations in the striatum may be involved in the shift in brain activity during the learning processes. In addition, recent studies have reported that the activity of glial cells influences the uptake of ¹⁸FFDG (Zimmer et al., Nat Neurosci., 2017) and that these cells regulate spike timingdependent plasticity (Valtcheva and Venance, Nat Commun, 2016). Changes in glial cellular activity, through the control of synaptic plasticity, may partly contribute to the pattern formation of learning-dependent shifts in brain activity.

To explain the difference in the time course between the brain activity and the firing activity of specific event-related neurons, we have added the aforementioned information to the Limitations section (pages 21 to 22, lines 512–539). 

Comment 6: A significant finding of the study is that CO-HR and CO-LL responses are strikingly obvious in the pVLS, but not in the aDLS, in line with the literature that the posterior (sensory) striatum processes sound. This study also shows that responses to the highfrequency tone indicating a correct right-lever choice increase with learning in contrast to the low-frequency tone responses. To further address whether this difference arises from the task contingency, and not from the frequency representation of the pVLS, an important control would be to switch the cue-response association in a separate group of mice, such that high-frequency tones require a left lever press and vice versa. This would also help tease apart task-evoked responses in the aDLS, as I am given to understand all the recording sites were in the left striatum.

We did not conduct an experiment switching cue-response association in the auditory discrimination task. However, the transient activity of cue onset-related neurons in the pVLS, as the reviewer has suggested, did not appear at the early stage of learning, but was observed in a learning-dependent manner (Figures 7A and S8E). In addition, the cue onset-HR activity showed a slight but notable difference between the HR and LL trials at the middle and late stages (Figure 7B), but there was no difference in activity in the HL and LR incorrect trials at the corresponding stages (Wilcoxon signed rank test; early, p = 0.375, middle, p = 0.931, and late, p = 0.668). These results suggest that the activity of cue onset-related neurons in the pVLS is associated with the stimulus and response association (task contingency) rather than the tone frequency.

Reviewer #1 (Recommendations For The Authors):

Minor comment 1: The readability and appeal of this study would be improved by explaining the various neuronal response types, and task-related events in slightly more detail in the results section, and minimizing the use of non-standard abbreviations wherever possible.

As suggested, we have replaced the abbreviations related to electrophysiological events (CO, CR, RS, and FL) with the original terms, and improved the explanation for neuronal response types and event-related neurons. 

Minor comment 2: It would be helpful to label DLS and VLS recordings more clearly on the figures instead of only in the figure caption.

Thank you for pointing this out. The terms “aDLS” and “pVLS” have now been added to the panels showing firing pattern of neurons: “aDLS” in Figures 5D, 6A, S6A, S7A, S8A, S8B. S8C, and S8D; and “pVLS” in Figures 6F, 7A, 7D, S6D, S6E, S7F, S8E, and S8F.

Minor comment 3: The authors suggest that aDLS HR- and LL- neurons are more sensitive to the behavioral outcome than those in pVLS (Fig 5 and S5). However, their conclusions are based on sample sizes as low as n=3 for each response type.

We identified event-related neurons from single neurons detected in both the aDLS and pVLS using the same criteria. In the pVLS, we found a small number of neurons that increased their activity during the period when the reward sound is presented (Figures S6D and S6E) (6, 4, and 17 HR type neurons at the early, middle, and late stages, respectively; 3, 5, and 15 LL type neurons at the early, middle, and late stages, respectively). The number of LL type neurons at the early stage was particularly lower, as the reviewer has suggested. However, when we plotted the firing rates of these neurons around the event, their activity did not reflect behavioral outcome. In the aDLS, we detected a large number of reward sound-related neurons representing behavioral outcome (Figures 5 and S6A) (43, 37, and 44 HR type neurons at the early, middle, and late stages, respectively; 49, 62, and 59 LL type neurons at the early, middle, and late stages, respectively). These observations suggest that aDLS neurons are more sensitive to behavioral outcomes than pVLS neurons.

Minor comment 4: Typo in Figure 4C and D, right plots, y-axis label: "subtracted".

The typographic errors in Figures 4C–4H have now been corrected to “subtracted”.

Reviewer #2 (Public Reviews):

The study by Setogawa et al. aims to understand the role that different striatal subregions belonging to parallel brain circuits have in associative learning and discrimination learning (S-O-R and S-R tasks). Strengths of the study are the use of multiple methodologies to measure and manipulate brain activity in rats, from microPET imaging to excitotoxic lesions and multielectrode recordings across anterior dorsolateral (aDLS), posterior ventral lateral (pVLS)and dorsomedial (DMS) striatum. The main conclusions are that the aDLS promotes stimulus-response association and suppresses response-outcome associations. The pVLS is engaged in the formation and maintenance of the stimulus-response association. There is a lot of work done and some interesting findings however, the manuscript can be improved by clarifying the presentation and reasoning. The inclusion of important controls will enhance the rigor of the data interpretation and conclusions.

We appreciate the reviewer’s valuable feedback, which has been beneficial in our endeavor to improve our manuscript. In response to the comments, we have revised the description of the experimental methods and underlying rationale, as well as the Results section. We have also provided additional data for some of the experiments that support the conclusions. For more details, please refer to the responses to each comment, included below.

Reviewer #2 (Recommendations For The Authors):

Comment 1: Generally, the manuscript is hard to read because of the cumbersome sentence structure, overuse of poorly defined acronyms, and lack of clarity on the methods used.

According to the following comments (a)–(d), we have revised the corresponding text in the manuscript to clarify the sentence structure, definitions of terms, and methodology. 

Comment 1 (a): For example, the single lever task used as a control for the auditory discrimination task could be introduced better, explaining the reasoning and the strategy for subtracting it from the images obtained during the discrimination phase at the start of the section.

We analyzed task-related activity by comparing ¹⁸F-FDG uptake on Days 2, 6, 10, or 24 of auditory discrimination task with that on Day 4 of the single lever press task. This task was used as a control that does not require a decision process based on the auditory stimulus. For clarification, we have provided a more detailed explanation of the flow of the single lever press task used in the PET experiment, including the rationale for employing this task as a control (page 6, lines 129–135). We have also revised the explanation of voxel-based statistical parametric analysis, adding a more detailed description of the thresholds (page 7, lines 143–145).

Comment 1 (b): Another example is that important methodological information is buried deep in the text and complicates the interpretation of the results.

We have revised the following sentences in the manuscript in order to provide clearer methodological information.

(1) As described above, explanations for the single lever task (page 6, lines 129–135) and voxel-based statistical parametric analysis were added (page 7, lines 143–145). 

(2) Definition of the early, middle, and late stages were described in the initial behavioral experiment (page 6, lines 113–119). 

(3) Abbreviations related to behavioral strategies (WSW and LSL) and electrophysiological events (CO, CR, RS, and FL) were replaced with the original terms. 

Comment 1 (c): The specie being studied is not stated in the abstract, nor the introduction, and only in the middle of the result section. Please include the specie in the abstract and the first part of the result also for clarity.

We included the name of the species (rats) in the Abstract (page 3, line 47), at the end of the Introduction (page 5, lines 87–88) and at the beginning of the Results (page 5, line 109).

Comment 1 (d): The last part of the intro is copied/pasted from the abstract. Please revise.

The last part of the Introduction was revised accordingly (page 5, lines 97–104).

Comment 2: The glucose microPET imaging is carried out 30 mins after the rats performed the task and it is expected to capture activation during the task. Is this correct? This assumption has to be validated with an experiment, which is a control showing a validation of the microPET approach used, and this way can report activation of brain areas during the task completed 20-30 minutes before. For example, V1 or A1 would be a control that we would expect to be activated during the task.

Our PET experiment was conducted in accordance with previously established methods (Cui et al, Neuroimage, 2015), where rats received intravenous administration of ¹⁸FFDG solution just before the start of the behavioral session, which lasted for 30 min. The ¹⁸F-FDG uptake in the brain starts immediately and reaches the maximum level until 30 min after the administration, and the level is kept at least for 1 h (Mizuma et al., J Nucl Med, 2010). The rats were returned to their home cages, and a 30-min PET scan started 25 min after the session. The start time of the scan was chosen to allow for sufficient reduction of 18F radioactivity in arterial blood to increase the S/N ratio of the radioactivity (Mizuma et al., J Nucl Med, 2010). As shown in Table S1, we confirmed that the brain activity in the medial geniculate body (auditory thalamus) was increased on Days 6 and 10 in the acquisition phase, although the activity in the auditory cortex was not changed, which is consistent with the results of a previous study reporting that the auditory cortex does not show the causality for the pure-tone discrimination task (Gimenez et al., J Neurophysiol., 2015).

Comment 3: Why are Days 2, 6, 10, and 13 chosen and compared for the behavior? Why aren't these the same days chosen in the other part of the study? It is unclear why authors focused on these days and why the focus changed later.

We conducted daily training of the discrimination task. The success rate reached a plateau on Day 13 and was maintained until Day 24 (Figure 1B). Based on these results, we categorized the learning processes into the acquisition and learned phases, and then divided the acquisition phase into the early (< 60%), middle (60–80%), and late (> 80%) stages. In the PET experiment, we selected Days 2, 6, and 10 as the representatives of each stage during the acquisition phase. In addition, we also selected Day 24 for the learned phase.  However, no scan was performed on Day 13 due to the transition between the two phases.   

Comment 4: (A) Is the learning and acquisition of the single lever press and discrimination task completed by day 4? Or are rats still learning? The authors claimed no changes in DMS activity between single lever press & discrimination, and therefore DMS isn't involved in learning. But to make this claim we should have measures that the learning has already happened, which I am not sure have been provided. (B) On this same point, the DMS activity is elevated on Day 4 of a single lever press compared to the aDLS and pVLS. So is it possible that the activity in DMS was already elevated on Day 4 of single lever press training? Especially given that DMS is supposedly involved in goal-directed behavior?

(A) In the single lever press task, the number of lever presses plateaued on Day 2 (Figure 1C). In addition, we analyzed response time and its variability, which plateaued from Day 3 and Day 2, respectively (see Author response image 1). These results indicate that the learning in the task was completed by Day 4. In the auditory discrimination task, Day 4 corresponded to the transition period from the early-tomiddle stages of the acquisition phase, suggesting that learning was still progressing. 

In the imaging analysis, we examined task-related activity by comparing ¹⁸F-FDG uptake on either day of the discrimination task with that on Day 4 of the single lever press task, and did not find any changes in the brain activity in the DMS. In addition, we investigated learning-related activity, and the DMS activity did not change during acquisition phase. These results suggest that the DMS is not involved in the acquisition phase of learning. Furthermore, comparisons between Days 10 and Day 24 showed a decrease in DMS activity during the learned phase, suggesting that DMS activity was downregulated during the learned phase. In addition, chronic lesion in the DMS indicated that the success rate in the discrimination task was comparable between the control and lesioned groups (Figure 3I), whereas the response time lengthened throughout the learning in the lesioned group compared to the controls (Figure S1C). These results support our notion that the DMS contributes to the execution, but not learning, of discriminative behavior (Figure 3I and S1C).

Author response image 1.

Performance of single lever press task conducted before auditory discrimination task. (A) Number of lever presses. (B) Response time (Kruskal-Wallis test, χ² = 38.063, p = 2.7 × 10^-8, post hoc Tukey–Kramer test, p = 0.047 for Day 1 vs. Day 2; p = 2.3 × 10^-7 for Day 1 vs. Day 3; and p = 4.0 × 10^-6 for Day 1 vs. Day 4; p = 0.019 for Day 2 vs. Day 3; p = 0.082 for Day 2 vs. Day 4; p = 0.951 for Day 3 vs. Day 4). (C) Response time variability (Kruskal-Wallis test, χ² = 28.929, p = 2.3 × ^-6, post hoc Tukey–Kramer test, p = 0.077 for Day 1 vs. Day 2; p = 5.7 × 10^-6 for Day 1 vs. Day 3; and p = 1.3 × 10^-4 for Day 1 vs. Day 4; p = 0.060 for Day 2 vs. Day 3; p = 0.253 for Day 2 vs. Day 4; p = 0.912 for Day 3 vs. Day 4). Data obtained from the task shown in Figure 2C are plotted as the median and quartiles with the maximal and minimal values. *p < 0.05, **p < 0.01, and ***p < 0.001.

(B) We compared ¹⁸F-FDG uptakes among striatal subregions on Day 4 of the single lever press task (334.8 ± 2.86, 299.0 ± 1.71, and 336.8 ± 2.18 for the aDLS, pVLS, and DMS, respectively; one-way ANOVA, F[2,41] = 104.767, p = 2.1 × 10^-16). The uptake was comparable between the aDLS and DMS (post hoc Tukey-Kramer test, p = 0.058), but it was significantly lower in the pVLS compared to either of the other two subregions (post hoc Tukey-Kramer test, aDLS vs. pVLS, p = 5.1 × 10^-9, post hoc Tukey-Kramer test, pVLS vs. DMS, p = 5.1 × 10^-9). However, since we did not measure the brain activity in the single lever task outside of Day 4, it is unclear whether there was an increase in DMS activity during the acquisition of the task. Similarly, since we did not confirm the behavioral modes, which include goal-directed and habitual actions, it is difficult to conclude that the lever presses in the task were controlled by the goaldirected mode. However, our chronic lesion experiment suggests that the DMS is involved in the execution of discrimination behavior (Figure S1C). A clearer understanding of the DMS function in discrimination learning is an important challenge in the future.

Comment 5: It seems like the procedure of microPET imaging affects performance on the task. The anesthesia used maybe? Figures 2C and D show evidence that the behavior was negatively affected on the days on which microPET imaging was performed after the training. Can the author clarify/comment?

Isoflurane anesthesia may slightly reduce behavioral performance. We carried out anesthesia (median [interquartile range]: 6 [5–8] min) during the insertion of the catheter for FDG injection, and set a recovery period of at least 2 h until the beginning of the behavioral session, to minimize the impact of anesthesia. The performances in Figure 2E were similar to those in the intact rats (compared to Figures 1C–1F), suggesting that the procedure for PET scans does not affect the acquisition of discrimination. 

We have added detailed information on the isoflurane anesthesia to the Methods section (page 26, lines 649–653).

Comment 6: More on clarity. Section 3 of the results (muscimol inactivation) refers a lot to "the behavioral strategies" without really clarifying what these are - are they referring to WSW / LSL (which also could use a better introduction) or goal-directed/habitual or stimulus-response/stimulus-outcome?

The dorsal striatum is involved in both behavioral strategies based on stimulus-response association and the response-outcome association during instrumental learning. To assess the impact of striatal lesions on the behavioral strategies, we analyzed the proportion of response attributed to two strategies in all responses of each session. One is the “win-shift-win” strategy, which is considered to reflect the behavioral strategy based on the stimulus-response association. In this strategy, after a correct response in the previous trial, the rats press the opposite lever in the current trial in response to a shift of the instruction cue, resulting in the correct response.  Another strategy is the “lose-shift-lose” strategy, which is considered to appear as a consequence of the behavioral strategy based on the response-outcome association. In this strategy, after an error response in the previous trial, the rats press the opposite lever in the current trial despite a shift of the instruction cue, leading to another error response.

We have revised the explanations of the behavioral strategies in the section of the Results section (page 9, lines 192–201). 

Comment 7: Related to WSW / LSL needing a better introduction, on lines 192/193 authors describe a result where they saw the WSW and LSL strategies increase and decrease, respectively, in saline-injected mice. Is the change in performance expected or an undesired effect of the saline injection? This is not clear now and it should be clarified.

The explanations of the win-shift-win and lose-shift-lose strategies have been revised in the Results section on excitotoxic lesion experiment (page 9, lines 192–201) as described in our response to Comment 6. Win-shift-win is an indicator of correct responses, while lose-shift-lose indicates errors. Therefore, win-shift-win is predicted to increase, and lose-shift-lose decrease, as discrimination learning progresses. Indeed, in the results of the behavioral experiments, shown in Figure 1, both indicators change in a similar pattern to those in the results of the lesion experiments (Figure 3).

We have added the explanation of the proportions of both strategies in intact rats (page 9, lines 203–204) with a supplementary figure (Figure S2) and accompanying legend (page 56, lines 1173–1177).

Comment 8: Muscimol experiments - two questions/comments. How often do rats receive muscimol?

In this section, muscimol is given on day 2 and on days after the animals hit a 60% or 80% success rate. Can the authors provide a mean and SEM for when are those injections?

The first injection was conducted on Day 2 to target the early stage. The second and third injections were conducted on the days after the success rate had reached 60% and 80% for the first time through the training, respectively, to target the middle and late stage. respectively. These conditions are described in the Results (page 10, lines 234– 237) and Methods (page 26, lines 633–636). The mean and s.e.m. of the injection day at the middle and late stages were not significantly different between the saline and muscimol-injected groups into the aDLS (see Author response image 2A) and pVLS (see Author response image 2B).

Author response image 2.

Injection days during auditory discrimination learning. Injections with saline (SAL) and muscimol (MUS) into the aDLS (A) or pVLS (B) were performed after the success rate had reached 60% (middle stage) and 80% (late stage) for the first time through the training, respectively (A, Wilcoxon signed rank test, middle, Z = 65, p = 0.772, late, Z = 56.5, p = 0.242 for the aDLS; B, Wilcoxon signed rank test, middle, Z = 39, p = 1.000, late, Z = 43, p = 0.587). Data are indicated as the median and quartiles with the maximal and minimal values. 

Comment 9: Muscimol experiments. Can the authors comment on the effects on performance vs learning? What happens on the days after Muscimol? Does performance bounce back or is it still impaired?

We conducted a transient inhibition experiment with muscimol to examine whether the neuronal activity in the striatal subregions is linked with the processes at different stages. In this experiment, to lower the possibility that compensation of learning may occur during a session after the muscimol injection (Day N), we limited the session time to 15 min (45 trials) and evaluated the impact of the injection on the success rate at specific stages. The success rate in the muscimol-injected groups into the aDLS significantly decreased at the middle stage compared to the corresponding salineinjected groups, but not at the early and late stages (Figure 4C), and the rate in the muscimol groups into the pVLS significantly decreased at the late stage compared with the respective saline groups, but not at the early and middle stages (Figure 4D). Our results demonstrated that the aDLS and pVLS mainly function at the middle and late stages of the auditory discrimination task, respectively. 

In addition, we here reply to comment 10 as for the comparison of success rates before (Day N-1) and after (Day N+1) the injections (see Author response image 3). We focused on two injections into the aDLS at the middle stage and into the pVLS at the late stage, in which the rate was reduced soon after the muscimol injection on Day N. The success rate for the two injections showed no significant main effect regarding group (saline/muscimol) or day (Days N-1/N+1) and no significant interactions for group × day. Moreover, the success rate was not significantly increased on Day N+1 as compared to Day N-1, even in the saline-injected control group, probably because of the limited session time soon after the injection. Therefore, we consider that it was difficult to define the effects of drug injection on the learning of auditory discrimination in our behavioral protocol for the transient inhibition experiment, and that the reduced rates observed in the muscimol-injected group on Day N mostly reflect the impacts of muscimol at least partly on the performance of discriminative behavior. 

Author response image 3.

Comparison of success rate between days before (Day N1) and after (Day N+1) the injections into striatal subregions. Success rate in the saline (SAL)- and muscimol (MUS)-injected groups into the aDLS (A) or pVLS (B) at the early, middle, and late stages of auditory discrimination learning (two-way repeated ANOVA; early, day, F[1,14] = 5.266, p = 0.038, group, F[1,14] = 0.276, p = 0.608, day × group, F[1,14] = 0.118, p = 0.736; middle, day, F[1,14] = 4.110, p = 0.062, group, F[1,14] = 0.056, p = 0.816, day × group, F[1,14] = 1.150, p = 0.302; late, day, F[1,14] = 6.408, p = 0.024, group, F[1,14] = 0.229, p = 0.640, day × group, F[1,14] = 1.277, p = 0.278 for the aDLS; and early, day, F[1,10] = 0.115, p = 0.746, group, F[1,10] = 2.414, p = 0.151, day × group, F[1,10] = 0.157, p = 0.700; middle, day, F[1,10] = 0.278, p = 0.610, group, F[1,10] = 0.511, p = 0.491, day × group, F[1,10] = 4.144, p = 0.069; late, day, F[1,10] = 0.151, p = 0.705, group, F[1,10] = 0.719, p = 0.416, day × group, F[1,10] = 0.717, p = 0.417 for the pVLS). Data are indicated as the mean ± s.e.m.

Comment 10: Muscimol data has a pair before and after, can the authors show this comparison at early, middle, and late training? Not just the subtraction.

The comparison of success rates before and after drug injection is shown in Author response image 3.

Comment 11: Ephys recordings. These are complex figures and include a large number of acronyms. It would help to define them again and help the reader through these figures so the reader can focus on understanding the finding more than the figure presentation.

We replaced the abbreviations related to electrophysiological events (CO, CR, RS, and FL) with the original terms, and improved the explanation in the text and figures. 

Comment 12: Figure 7B/E - on correct trials, they see a difference in the cue response to high tone / low tone but no difference in the choice. This is the one that seemed like a topography issue.

The transient activity of cue onset-related neurons in the pVLS did not appear at the early stage of learning, but was observed in a learning-dependent manner (Figures 7A and S8E). In addition, the cue onset-HR activity showed a slight but notable difference between the HR and LL trials at the middle and late stages (Figure 7B), whereas there was no difference between activities in the HL and LR incorrect trials at the corresponding stages (Wilcoxon signed rank test; early, p = 0.375, middle, p = 0.931, and late, p = 0.668). These results suggest that the cue onset-related neurons in the pVLS represents the stimulus and response association (task contingency) rather than the topography of tone frequency.

Comment 13: Animals were normally trained for 60 minutes but on muscimol days only trained for 15 mins. On PET days only trained for 30 minutes. Ephys sessions were 60 mins. Is this correct? Why?

We determined the session time for each experiment by considering both technical and behavioral aspects. In the initial behavioral experiment, the session time was set to 60 min per day. Under this condition, the rats acquired the discrimination learning within 13 days. In the imaging experiment, the session without a PET scan was conducted for 60 min, while the session with a PET scan was carried out for 30 min as described previously (Cui et al, Neuroimage, 2015). This time schedule produced a learning curve similar to that of the initial behavioral experiment. In the transient inhibition experiment, the sessions without drug injections lasted for 60 min. As described in our response to the comment 2, the time of the session soon after the injection was limited to 15 min to lower the possibility of compensation of learning during the session. In the chronic lesion and electrophysiological experiments, all sessions were conducted for 60 min, corresponding to the initial experiment. 

References

Mizuma, H., Shukuri, M., Hayashi, T., Watanabe, Y. & Onoe, H. Establishment of in vivo brain imaging method in conscious mice. Journal of Nuclear Medicine 51, 10681075 (2010).

Cui, Y., et al. A voxel-based analysis of brain activity in high-order trigeminal pathway in the rat induced by cortical spreading depression. Neuroimage 108, 17-22 (2015).

Zimmer, E.R., et al. [18 F] FDG PET signal is driven by astroglial glutamate transport. Nat Neurosci 20, 393-395 (2017).

Valtcheva, S. & Venance, L. Astrocytes gate Hebbian synaptic plasticity in the striatum. Nature communications 7, 13845 (2016).

Gimenez T.L., Lorenc M., Jaramillo S. Adaptive categorization of sound frequency does not require the auditory cortex in rats. J Neurophysiol 114:1137-1145 (2015).

Author Response

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

We are pleased to send you a revised version of our manuscript entitled “voyAGEr: free web interface for the analysis of age-related gene expression alterations in human tissues” and the associated shiny web app, in which we incorporate the referees’ feedback. We would like to express our gratitude for their time and valuable insights, which have contributed to the improvement of our work. We appreciate the rigorous evaluation process that eLife maintains.

In this letter, we address each of the reviewers' comments and concerns, point-by-point, offering detailed responses and clarifications. We have made several revisions to our manuscript following their recommendations.

We must note that the revised version of the manuscript has two novel joint first authors, Rita Martins-Silva and Alexandre Kaizeler, who performed all the requested reanalyses, given that the initial first author, Arthur Schneider, already left our lab. We must also point to the following minor unsolicited improvements we took the opportunity to make:

• Added a comprehensive tutorial to the GitHub repository on how to navigate through voyAGEr’s features.

• Implemented sample randomisation in the scatter plots depicting gene expression across the age axis to ensure data privacy.

• Implemented minor adjustments within the web app to enhance user comprehension and clarity when visualizing the data.

• Improved clarity of the methodological sections.

Reviewer 1

(1.1) While this may be obvious to others for some reason that escaped me, I was unsure what was the basis for the authors' choice of 16 years as the very specific sliding window size. If I'm not alone in this, it might add clarity for other readers and users if this parameter choice were explained and justified more explicitly.

We apologise for our omission in providing the rationale behind our choice in the previous version. We chose 16 years as our sliding window size because this was the minimum needed to guarantee the presence of more than one sample per window, across all the tissues considered in the study (Figure R1 below).

We added the following sentence to the manuscript (v. Methods, ShARP-LM):

“This was the minimum age span needed to guarantee the presence of more than one sample per window, across all considered tissues.”

(1.2) "In particular, tissue-specific periods of major transcriptional changes in the fifth and eighth decades of human lifespan have been revealed, reflecting the so-called digital aging and consistently with what is observed in mice" here I think that "consistently" should be "consistent".

We thank the reviewer for the comment and following the suggestion, we have revised 'Consistently' to 'consistent' as it is the correct usage in our sentence.

(1.3) "On a different note, sex biases have been reported in for the expression of SALL1 and KAL1 in adipose tissue and lung, respectively." Here I think that "in for" should be "in".

As recommended by the reviewer, we have replaced ‘in for’ for ‘in’. As we substituted KAL1, the current sentence now stands as “On a different note, sex biases have been reported in the expression of SALL1 and DDX43 in adipose tissue and lung, respectively”.

(1.4) "We downloaded the matrix with the RNA-seq read counts for each gene in each GTEx v7 sample from the project's data portal (https://www.gtexportal.org/)." In my pdf manuscript this hyperlink appears to be broken.

We appreciate the reviewer's attention to the broken link, and we have rectified the issue. The link should now be fully operational, effectively directing users to the GTEx Portal.

(1.5) Under methods, I might suggest "Development platform" or "Development platforms" over "Development's platform" as a heading.

We have modified the heading of this section in the methods to 'Development Platforms', as we believe it better reflects the information conveyed.

Reviewer 2

(2.1) In this tool/resource paper, it is crucial that the data used is up-to-date to provide the most comprehensive and relevant information to users. However, the authors utilized GTEx v7, which is an outdated (2016) version of the dataset. It is worth noting that GTEx v8 includes over 940 individuals, representing a 35% increase in individuals, and a 50% increase in the total number of samples. The authors should check the newer versions of GTEx and update the data.

When the development of the voyAGEr web application began, GTEx version 7 was the most up to date. Nevertheless, we agree that the version 8 offers a notably more extensive dataset, encompassing a larger number of individuals, samples, and introducing new tissues. Consequently, we have updated our application to incorporate the data from GTEx version 8.

(2.2) The authors did not address any correction for batch effects or RNA integrity numbers, which are known to affect transcriptome profiles. For instance, our analysis of GTEx v8 Cortex tissue revealed that after filtering out lowly expressed genes, in the same way authors did, PC1 (which accounts for 24% of the variation) had a Spearman's correlation value of 0.48 (p<6.1e-16) with RNA integrity number.

We acknowledge the validity of the reviewer’s comment and appreciate the importance of such corrections to enhancing data interpretation. In response, we conducted a thorough unbiased investigation into potential batch effects, with the COHORT variable emerging as the primary driver of those observed across most tissues. Furthermore, SMRIN (as the reviewer pointed), DTHHRDY, MHSMKYRS and the number of detected genes in each sample were consistently associated with the primary sources of variation. As a result, we implemented batch effect correction for those five conditions, in a tissue-specific manner.

We provide a detailed explanation of the batch effect correction methodology and its importance in the biological interpretation of results in the Methods section, specifically under "Read count data pre-processing". Additionally, we have included two new supplementary figures, Sup. Figures 7 and 8, to illustrate a batch effect example in lung tissue and emphasise the critical role of this correction in data interpretation.

(2.3) The data analyzed in the GTEx dataset is not filtered or corrected for the cause of death, which can range from violent and sudden deaths to slow deaths or cases requiring a ventilator. As a result, the data may not accurately represent healthy aging profiles but rather reflect changes in the transcriptome specific to certain diseases due to the age-related increase in disease risk. While the authors do acknowledge this limitation in the discussion, stating that it is not a healthy cohort and disease-specific analysis is not feasible due to the limited number of samples, it would be useful for users to have the option to analyze only cases of fast death, excluding ventilator cases and deaths due to disease. This is typically how GTEx data is utilized in aging studies. Alternatively, the authors should consider including the "cause of death" variable in the model.

This comment is closely related to the prior discussion (point 2.2). Notably, two of the covariates selected for batch effect correction, namely, DTHHRDY (Death classification based on the 4-point Hardy Scale1) and COHORT (indicating whether the participant was a postmortem, organ, or surgical donor1), have a direct relevance to this issue, i.e., both relate to the cause of death of the individual.

1 According to the nomenclature of variables described in https://www.ncbi.nlm.nih.gov/projects/gap/cgibin/ GetListOfAllObjects.cgi?study_id=phs000424.v9.p2&object_type=variable

We therefore effectively account for their influence on gene expression, mitigating these factors' impact.

This approach represents a compromise, as it is practically infeasible to ascertain the absence of underlying health conditions in the remaining samples, even if only considering cases of “fast death”. Hence, we opted to keep all samples, independently of the cause of death of its donor, to dilute potential effects associated with individual causes of death.

(2.4) The age distribution varies across tissues which may impact the results of the study. The authors' claim that age distribution does not affect the outcomes is inconclusive. Since the study aims to provide cross-tissue analysis, it is important to note that differing age distributions across tissues can influence the overall results. To address this, the authors should conduct downsampling to different age distributions across tissues and evaluate the level of tissue-specific or common changes that remain after the distributions are made similar.

We acknowledge that variations in age distributions are evident across different tissues, with brain tissues displaying a notably pronounced disparity (green density lines in Figure R2 below).

To address this issue comprehensively, we conducted tissue-specific downsampling, by reducing the number of samples in a given age window to the minimum available sample size within all age windows for a given tissue. The histograms (density plots) of the number of samples per age window of 16 years considered in the ShARP-LM model, as well as the minimum number of samples in each age window, per tissue are illustrated in Figure R1. After performing downsampling, we computed the logFC and p-value of differential expression for each gene, per age window, and compared them (for all genes in a given age window) with those involving all samples.

Despite changes in logFC with downsampling, a considerable positive correlation is maintained (Figure R3, top panel). This suggests that the overall trends in gene expression changes persist. However, the downsampling process expectedly results in a decrease of statistical power within each age window concomitant with the decreased sample size, evident from the shift of genes from the third to the first quadrant in Figure R3, bottom panel. Consequently, we have opted for maintaining results encompassing all samples and removing the paragraph in the Discussion that asserted the absence of age distribution impact on the overall outcomes (“Indeed, we found no confounding between the distribution of samples’ ages and the trend of gene expression progression over age in any tissue.”), as we deem it inaccurate, potentially leading to misinterpretation. We have added a supplementary figure (Supplementary Figure 8, identical to Figure R3) illustrating the effect of downsampling, and the following paragraph to the manuscript’s Discussion section:

“When downsampling to ensure a balanced age distribution, a loss of statistical power is apparent but a considerable positive correlation with the original results is maintained and a substantial number of significant alterations remain so (Supplementary Figure 8).”

We acknowledge that this limitation can be addressed with the growing accumulation of human tissue transcriptomes in publicly available databases, a trend we anticipate in the near future. We are committed to promptly updating voyAGEr with any new data releases that may offer a solution to this concern.

Nonetheless, we want to underscore, as the reviewer has astutely pointed out, that while voyAGEr can facilitate cross-tissue comparisons, it must be done with caution. In this regard, we inserted the following paragraph into the Discussion:

“Due to the tissue-specific nature of the pre-processing steps (v. Read count data preprocessing in the Methods section), and given that most of the plotted gene expression distributions are centred and scaled by tissue, it is important to note that voyAGEr may not be always suited for direct comparisons between different tissues. For instance, it does not allow to directly ascertain if a gene exhibits different expression levels in different tissues or if the expression of a particular gene in one tissue changes more drastically with age than in another tissue.”

(2.5) The GTEx resource is extremely valuable, however, it comes with challenges. GTEx contains tissue samples from the same individuals across different tissues, resulting in varying degrees of overlap in sample origin across tissues as not all tissues are collected for all individuals. This could affect the similar/different patterns observed across tissues. As this tool is meant for broader use by the community, it is crucial for the authors to either rule out this possibility by conducting a cross-tissue comparison using a non-parametric model that accounts for the dependency between samples from the same individual, or to provide information on the degree of similarity between samples so that the users can keep this possibility in mind when using the tool for hypothesis generation.

We agree that the variable degrees of overlap between tissues (Figure R4) could lead to a confounding between trends in a population of common individuals and those associated with age. We therefore examined the contributions of variables 'donor,' 'tissue,' and 'age' to the overall variance in the data (Figure R5, panel A), having normalised the data collectively across all tissues. Tissue and donor contribute approximately 90% and 10% of the variance, respectively. Age exhibits minimal impact (around 1%), which may be attributed to the relative subtlety of its effects on gene expression and to the tissue specificity of ageing-associated changes. Notably, removing the 'donor' variable does not transfer this variance to 'age', suggesting a limited confounding between these variables (see Figure R5, panel B).

We also specifically examined the pairs of tissues exhibiting the lowest (Brain Amygdala / Small Intestine), median (Pancreas / Heart Left Ventricle), and highest (Kidney Cortex / Muscle Skeletal) percentages of shared donors. We identified and selectively removed samples from shared donors while maintaining the original sample size imbalance between tissues. Subsequently, we calculated each gene’s mean expression within each age window from the ShARP-LM pipeline, followed by each gene’s Pearson’s correlation of expression between tissue pairs. The resulting coefficients, both with and without the removal of common donors, were compared in scatter plots (Figure R6, left plots). As this process inherently involves downsampling, which may impact results (v. comment 2.4), we performed additional downsampling by randomly removing samples from both tissues according to the proportions defined for the removal of common donors (Figure R6, right plots).

In the chosen scenarios, we note a similar impact between the targeted removal of common donors and random downsampling. Nevertheless, the effects of removing samples may vary according to the absolute number of remaining samples. Consequently, singling out individual cases may not provide conclusive insights. To systematically address this, we represented all tissue pairs in a heatmap, colour-coded based on whether the removal of common donors is more impactful (red) or less impactful (blue) than random downsampling (Figure R7). The values depicted in the heatmap, denoted as the Impact of Common Donors (ICD), are computed for each tissue pair. This calculation involves several steps: first, we determined the absolute difference in Pearson’s correlation for each gene’s mean expression within each age window from the ShARP-LM pipeline, between the original data and the subset of data without common donors (DiffWoCD) or with random downsampling (DiffRD). Subsequently, the medians of DiffWoCD and DiffRD are computed, and the difference between these median values provides the ICD for each tissue pair. Due to the unidirectional nature of correlation (i.e., the results for tissue 1 vs tissue 2 mirror those for tissue 2 vs tissue 1), the resulting matrix is triangular in form.

We have added a supplementary figure (Supplementary Figure 4, a composition of Figures R4-R7, together with a scatterplot relating the values of heatmaps R4 and R7) that aims to provide guidance to users when interpreting specific tissue pairs, acknowledging inherent limitations (refer to comment 2.4). We have also inserted the following paragraph into the manuscript’s Discussion section:

“Furthermore, we must emphasise that the majority of GTEx donors contributed samples to multiple tissues (Supplementary Figure 4A), potentially introducing biases and confounders when comparing gene expression patterns between tissues. Our analyses of variance (Supplementary Figure 4B) and downsampling to control for common donors (Supplementary Figures 4C-E) suggest very limited global confounding between the impacts of donor and age on gene expression and that any potential cross-tissue bias not to depend much on the proportion of common donors (Supplementary Figure 4E). However, this effect must be taken into account when comparing specific pairs of tissues (e.g., Colon – Transverse and Whole Blood, Supplementary Figure 4D).”

(2.6) The authors aimed to create an open-source and ever-evolving resource that could be adapted and improved with new functionality. However, this goal was only partially achieved. Although the code for the web app is open source, crucial components such as the statistical tests or the linear model are not included in the repository, limiting the tool's customizability and adaptability.

We greatly appreciate the reviewer’s concern and share their commitment to maintaining the principles of openness, reproducibility, and adaptability for voyAGEr. voyAGEr was primarily designed as a visualisation tool, displaying pre-processed results, and indeed only the code for the Shiny app itself was accessible through the project's GitHub repository.

To address this shortcoming, we have made the entire data preprocessing script publicly available in the GitHub repository of voyAGEr. This script encompasses, among others, filtration, normalisation, batch effect correction, the ShARP-LM pipeline and statistical tests employed, and module definition. Moreover, the web app itself offers functionality to export relevant plots and tables.

(2.7) Furthermore, the authors' choice of visualization platform (R shiny) may not be the best fit for extensibility and open-source collaboration, as it lacks modularity. A more suitable alternative could be production-oriented platforms such as Flask or FastAPI.

We appreciate this thoughtful concern. The decision to use Shiny was primarily driven by our data having already been prepared in the R environment during pre-processing steps. Consequently, and as the web app serves the purpose of visualisation only (and not data processing), Shiny is as a natural and convenient extension of our scripts, enabling data visualisation seamlessly.

We acknowledge that Shiny may lack the modularity required for optimal open-source collaboration. While we recognise the merits of alternative platforms like Flask or FastAPI, we decided to keep Shiny because the current iteration of voyAGEr offers significant value to the community. Transitioning to a different platform would be a time-consuming endeavour, that would postpone the release of such resource.

However, the reviewer’s feedback regarding modularity and open-source collaboration is duly noted and highly valuable. We will certainly take it into account when developing new web applications within our laboratory.

(2.8) To facilitate collaboration and improve the tool's adaptability, data resulting from the preprocessing pipeline should be made publicly available. This would make it easier for others to contribute and extend the tool's functionality, ultimately enhancing its value for the scientific community.

As outlined in point 2.6 of this rebuttal letter, certain metadata used in our analysis are subject to restricted access. To address this, we have taken several measures to foster transparency and reproducibility of our analyses. First, we have made the scripts for data pre-processing publicly available, along with a comprehensive explanation of our methodology within the main manuscript. This empowers users to replicate our analyses and provides a foundation for those interested in contributing to the tool's development. Furthermore, we have created new issues on voyAGEr’s GitHub repository, outlining novel features and improvements we envision for the application in the future. We actively encourage users to engage with this section.

(2.9) It is unfortunate that the manuscript has no line numbers, which makes pointing out language issues or typos cumbersome. Below are some minor typos present in the current version mostly due to inconsistent usage of British vs US English, and the authors would be advised to do a thorough proofreading for the final submission.

• Page 12: Inconsistent spelling of "analyzed" and "analysed". Should be "analyzed", since US English is used throughout the rest of the paper.

• Page 14: "randomised"

• Page 15: "emphasise"

We apologise for it and include line numbers in the revised version. We have opted for British English and corrected the manuscript accordingly.

(2.10) Some figures in the supplemental material have a low resolution (e.g. S. Fig 5). Especially figures that are not based on screenshots would ideally be of a higher resolution.

As voyAGEr is designed as a web application for visualisation, it is inherent that some screenshots of the final resource may have lower resolutions. In response to this concern, we re-generated the figures in this manuscript with a resolution that maintains clarity and readability. We also recreated figures not derived from screenshots, further improving their resolution.

We saved all figures in PDF format and are sending them together with this letter and the revised manuscript, to address any potential issues related to low-resolution figures that may occur during the export of the Word document.

<(2.11) In Fig. 1 in the bottom row the sex labels are hard to see.

We have adapted the figure to address this concern.

(2.12) Math symbols and equations are not well formatted. For example, the GE equation on p. 13, or Oiij equation should be properly typeset. Also, the Oiij notation might be confusing, I believe the authors meant to use a capital "I", i.e. OI_ij.

We have incorporated these recommendations into the revised manuscript.

(2.13) The Readme file in the git repo is very short. It would be helpful to have build and run instructions.

We have updated the README file in the GitHub repository, which now contains, among other features, instructions for launching the Shiny app and building the associated Docker image. Additionally, a simple tutorial has also been included to assist users in navigating through voyAGEr's functionalities.

(2.14> "Module" tab's UI inconsistent to other tabs (i.e. "Gene" and "Tissue"), since it contains an "About" page. Adding the "About" page in the actual "Module" page might make the UI clearer.

We believed that the Modules section, due to its distinct methodology, would benefit from an additional tab explaining its underlying rationale. We relate to the reviewer’s concern regarding the use of tabs throughout the application and made changes to the app in order to ensure consistency.

(2.15) I would suggest changing the type of the article to "Tools and Resources".

We agree and followed the reviewer’s suggestion.

Reviewer 3

(3.1) In the gene-centric analyses section of the result, to improve this manuscript and database, linear regression tests accounting for the entire range of age should be added. The authors' algorithm, ShARP-LM, tests locally within a 16-year window which makes it has lower power than the linear regression test with the whole ages. I suspect that the power reduction is strongly affected in the younger age range since a larger number of GTEx donors are enriched in old age. By adding the results from the lm tests, readers would gain more insight and evidence into how significantly their interest genes change with age.

We are grateful for the reviewer's thoughtful and pertinent recommendation and have thus conducted linear regression tests covering the entire age range. The outcomes of these tests have been integrated into the web application, denoted by a dotted orange line on the 'Gene Expression Alterations Over Age' plots. Additionally, a summary of statistics of overall changes, encompassing pvalues, t-statistics, and logFC per year, has been included below the plot title. We have also updated the manuscript to include such changes (v. Methods, Gene-centric visualisation of tissue-specific expression changes across age):

“We also applied a linear model across the entire age range, thereby providing users with more insight and supporting evidence into how a specific gene changes with age. For visualisation purposes, we incorporated a dashed orange line, with the logFC per year for the Age effect as slope, in the respective scatter plots (Figure 3B c). We depict the Sex effect therein by prominent dots on the average samples, with pink and blue denoting females and males, respectively.”

Concerning the observation about the potential reduction in statistical power due to the limited number of samples in younger ages, we acknowledge its validity. Indeed, we have addressed this issue in the manuscript's Discussion (v. Supplementary Figure 6).

(3.1) In line with the ShARP-LM test results, it is not clear which criterion was used to define the significant genes and the following enrichment analyses. I assume that the criterion is P < 0.05, but it should be clearly noted. Additionally, the authors should apply adjusted p-values for multiple-test correction. The ideal criterion is an adjusted P < 0.05. However, if none or only a handful of genes were found to be significant, the authors could relax the criteria, such as using a regular P < 0.01 or 0.05.

We apologise for any confusion regarding the terminology "significant genes." Our choice to use nonadjusted p-values for determining the significance of gene expression changes with Age, Sex, and their interaction was deliberate, and we would like to clarify our reasoning:

(1) In the "Gene" tab of the application, individual genes are examined. When users inquire about a specific gene, multiple-testing correction of the p-value does not apply.

(2) In the "Tissue" tab, using adjusted p-values and a threshold of 0.05 yielded very few differentially expressed genes, limiting the utility of Peaks. Our objective therein is not to assess the significance of alterations in individual genes but to provide a metric for global alterations within a tissue. We then determine significance based on the False Discovery Rate (FDR), using the p-values as a nominal metric of gene expression alterations.

To avoid using the concept of “differential expression”, commonly linked to significance, we now refer to 'altered genes' in both the manuscript and the app. For clarity and to align with voyAGEr's role as a hypothesis-generation tool, we define 'altered genes' as those with non-adjusted p-values < 0.01 or < 0.05, as discriminated in the Methods section.

(3.3) In the gene-centric analyses section, authors should provide a full list of donor conditions and a summary table of conditions as supplementary.

We appreciate the suggestion and we have now included a reference that directs readers to those data, alternatively to including this information as an additional supplementary table. We would like to emphasise that the web app includes information on donor conditions we hypothesise to affect gene expression.

3.4) The tissue-specific assessment section has poor sub-titles. Every title has to contain information.

We agree and revised the sub-titles to more accurately reflect the information conveyed in each corresponding section.

(3.5) I have an issue understanding the meaning of NES from GSEA in the tissue-specific assessment section. The authors performed GSEA for the DEGs against the background genes ordered by tstatistics (from positive to negative) calculated from the linear model. I understand the p-value was two-tailed, which means that both positive and negative NES are meaningful as they represent up-regulated expression direction (positive coefficient) and down-regulated expression direction (negative coefficient) with age, respectively, within a window. However, in the GSEA section of Methods, authors were not fully elaborate on this directionality but stated, "The NES for each pathway was used in subsequent analyses as a metric of its over- or downrepresentation in the Peak". The authors should clearly elaborate on how to interpret the NES from their results.

We added the following paragraph to the manuscript’s Methods section, in order to clarify the NES’ directionality:

“We extracted the GSEA normalised enrichment score (NES), which represents the degree to which a certain gene set is overrepresented at the extreme ends of the ranked list of genes. A positive NES corresponds to the gene set’s overrepresentation amongst up-regulated genes within the age window, whereas a negative NES signifies its overrepresentation amongst down-regulated genes. The NES for each pathway was used in subsequent analyses as a metric of its up- or down-regulation in the Peak.”

(3.6) In the Modules of co-expressed genes section, the authors did not explain how or why they selected the four tissues: brain, skeletal muscle, heart (left ventricle), and whole blood. This should be elaborated on.

We apologise for not providing a detailed explanation for this selection. As the ‘Modules of coexpressed genes’ section was primarily intended as a proof of concept, we opted to include tissues for which we had a substantial number of samples available and availability of comprehensive cell type signatures, those being the tissues that met such criteria. Nonetheless, as the diversity of cell type signatures increases (e.g., through the increasing availability of scRNA-seq datasets), we plan to encompass a wider range of tissues in the near future. However, as this task is time-demanding and in order to avoid a substantial delay in the release of voyAGEr, we opted to approach this issue in the next version of the App and included a dedicated issue in the projects’ GitHub repository so that users can share their preferences of the next tissues to include.

We also added a brief sentence in this regard to the Methods section of the manuscript:

“The four tissues (Brain - Cortex, Muscle - Skeletal, Heart - Left Ventricle, and Whole Blood) covered by the Module section of voyAGEr were selected due to their relatively high sample sizes and availability of comprehensive cell type signatures. The increasing availability of human tissue scRNA-seq datasets (e.g., through the Human Cell Atlas) will allow future updates of voyAGEr to encompass a wider range of tissues.”

(3.7) In the modules of the co-expressed genes section, the authors did not provide an explanation of the "diseases-manual" sub-tab of the "Pathway" tab of the voyAGEr tool. It would be helpful for readers to understand how the candidate disease list was prepared and what the results represent.

We greatly appreciate the reviewer's feedback, and in response, we have restructured the 'Modules of co-expressed genes' method section to provide a more comprehensive explanation of the 'diseases' sub-section. To clarify, we obtained a curated set of diseases and their associated genes from DisGeNET v.7.0. We assessed the enrichment of modules in relation to these diseases through two methods: a manual approach utilising Fisher’s tests (i.e. comparing the genes of a given module with the genes associated with a given disease) and another through use of the disgenet2r package, employing the function disease_enrichment. Significance of these enrichments were determined by adjusting p-values using the Benjamini-Hochberg correction.

(3.8) Most figures have low resolutions, and their fonts are too small to read.

As already mentioned in issue 2.10, we have recreated all of the images with better resolution to enhance legibility. We also exported such figures in PDF, which we attach to this revision.

(3.9) Authors used GTEx V7, which is not latest version. Although researchers have developed a huge amount of pipelines and tools for their research, most of them were neglected without a single update. I am sure many users, including myself, would appreciate it if the authors kept updating the database with GTEx V8 for the future version of the database.

We express our gratitude to the reviewer for their valuable suggestion, and, as already explained in issue 2.1, we have incorporated GTEx V8 into voyAGEr.

(3.10) I would like to have an option for downloading the results as a whole for gene, tissue, and coexpressed genes. This would be a great option for secondary analysis by users.

The implementation of such feature would be a time-demanding endeavour that would delay the release of voyAGEr, and we therefore chose not to perform it for this version. However, we agree that it would be a good resource for secondary analyses and acknowledge the possibility of adding this feature in the future. For now, voyAGEr allows the user to download all plots and corresponding data.

(3.11) How the orders of tissues in the heatmaps (both gene and tissue section) were determined? Did the authors apply hierarchical clustering? If not, I would recommend the authors perform the hierarchical clustering and add it to display the heatmap display.

We apologise for the oversight in explaining the process behind determining the order of tissues. To clarify, we employed hierarchical clustering to establish the tissue order for visualisation within the app. Although the reviewer suggested adding a dendrogram to illustrate this clustering, we decided against it. The reason for such is that including a dendrogram, while informative, is not essential for the app's primary purpose.

(3.12) I understand that this is a vast amount of work, but I hope that the authors can expand the coexpressed module analysis to include other tissues in the future version of the database.

Knowing what co-expressed genes in line with aging are and their pathway and disease enrichments across tissues would be highly informative, and I'm sure many users, including myself, would greatly appreciate it. <br /> We express our gratitude to the reviewer for the valuable suggestion and for acknowledging the extensive effort required to incorporate new tissues into the module section. We completely agree that understanding co-expressed genes across the aging process is of significant value, and we are committed to the ongoing inclusion of additional tissues. As already stated in issue 3.6, comprehensive list of tissues slated for integration in future voyAGEr versions is readily available on voyAGEr’s GitHub repository.

Author response image 1.

Density plots (“smoothed” histograms) of the distribution of numbers of samples per moving age window for the ShARP-LM pipeline, categorised by tissue. The numerical value within each rectangle represents the minimum number of samples observed across all age windows for that particular tissue.

Author response image 2.

Density lines (“smoothed” histograms) of the distribution of the age of donors per tissue. As depicted in the chart, there are more samples for older ages, particularly of brain tissues.

Author response image 3.

Effect of downsampling in ShARP-LM results. A – Per tissue violin plots of gene-wide distributions of Pearson’s correlation coefficients between original and downsampled logFC values for the Age variable across age windows, with tissues coloured by and ordered by increasing percentage of downsampling-associated reduction in the number of samples. B – Density scatter plots of comparison of associated original and downsampled p-values for each tissue, coloured by the downsampling percentage in each age window, highlighting the low range of p-values (from 0 to 0.1). Despite changes in logFC with downsampling, a considerable correlation in significance is maintained, although downsampling naturally results in a loss of statistical power, evident by the shift of points towards the first quadrant (dashed lines: p-value = 0.05).

Author response image 4.

Heatmap depicting the percentage of common donors between pairs of tissues. A given square illustrates the percentage of all samples of tissue in the x axis (Tissue 1) that is in common with the tissue in the y axis (Tissue 2)

Author response image 5.

Assessment of the relative contributions of different sources to the dataset’s variance. A - tissue accounts for approximately 90% of the total variance, while donor contributes around 10%; age has a minimal impact (1%), likely due to the relative subtlety of its effects on gene expression and to the tissue specificity of ageing dynamics. B - Removal of the donor variable does not transfer variance to age, suggesting limited confounding between the two variables.

Author response image 6.

Impact of the relative proportion of common donors on gene expression correlation between tissue pairs. Panels A, B, and C showcase the tissue pairs with the highest (Muscle Skeletal / Kidney Cortex), median (Pancreas / Heart Left Ventricle), and lowest (Small Intestine / Brain Amygdala) percentages of common donors, respectively. The left panels illustrate gene-bygene Pearson’s correlations of gene expression between the two tissues, comparing the scenarios with (x-axis) and without (yaxis) the removal of common donors. The ri ght panels depict the same comparisons, but with random downsampling (y-axis) in both tissues based on the proportions defined for common donor removal. The depicted examples show that the outcomes are comparable when removing common donors or employing random downsampling.

Author response image 7.

Comparison of the impacts of removing common donor samples and random downsampling across tissue pairs. The heatmap is coloured based on whether the removal of common donors has a greater (red) or lesser impact (blue) than random downsampling. The values depicted in the heatmap, denoted as the Impact of Common Donors (ICD), are computed for each tissue pair. This calculation involves several steps: first, by determining the absolute difference in Pearson’s correlation for each gene’s mean expression within each age window from the ShARP-LM pipeline, between the original data and the subset of data without common donors (DiffWoCD) or with random downsampling (DiffRD). Subsequently, the medians of DiffWoCD and DiffRD are computed, and the difference between these median values provides the ICD for each tissue pair. Due to the unidirectional nature of correlation (i.e., the results for tissue 1 vs tissue 2 mirror those for tissue 2 vs tissue 1), the resulting matrix is triangular in form. Grey tiles denote NA values, i.e., where the tissue-tissue comparison does not have a meaning, namely self-self and between sex-specific tissues. Top right insert: density line (“smoothed” histogram) of all ICD values.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors present a modelling study to test the hypothesis that horizontal gene transfer (HGT) can modulate the outcome of interspecies competition in microbiomes, and in particular promote bistability in systems across scales. The premise is a model developed by the same authors in a previous paper where bistability happens because of a balance between growth rates and competition for a mutual resource pool (common carrying capacity). They show that introducing a transferrable element that gives a "growth rate bonus" expands the region of parameter space where bistability happens. The authors then investigate how often (in terms of parameter space) this bistability occurs across different scales of complexity, and finally under selection for the mobile element (framed as ABR selection).

Strengths:

The authors tackle an important, yet complex, question: how do different evolutionary processes impact the ecology of microbial ecosystems? They do a nice job at increasing the scales of heterogeneity and asking how these impact their main observable: bistability.

We appreciate the reviewer for agreeing with the potential value of our analysis. We are also grateful for the constructive comments and suggestions on further analyzing the influence of the model structure and the associated assumptions. We have fully addressed the raised issues in the updated manuscript and below.

Weaknesses:

The author's starting point is their interaction LV model and the manuscript then explores how this model behaves under different scenarios. Because the structure of the model and the underlying assumptions essentially dictate these outcomes, I would expect to see much more focus on how these two aspects relate to the specific scenarios that are discussed. For example:

A key assumption is that the mobile element conveys a multiplicative growth rate benefit (1+lambda). However, the competition between the species is modelled as a factor gamma that modulates the competition for overall resource and thus appears in the saturation term (1+ S1/Nm + gamma2*S2/Nm). This means that gamma changes the perceived abundance of the other species (if gamma > 1, then from the point of view of S1 it looks like there are more S2 than there really are). Most importantly, the relationship between these parameters dictates whether or not there will be bistability (as the authors state).

This decoupling between the transferred benefit and the competition can have different consequences. One of them is that - from the point of view of the mobile element - the mobile element competes at different strengths within the same population compared to between. To what degree introducing such a mobile element modifies the baseline bistability expectation thus strongly depends on how it modifies gamma and lambda.

Thus, this structural aspect needs to be much more carefully presented to help the reader follow how much of the results are just trivial given the model assumptions and which have more of an emergent flavour. From my point of view, this has an important impact on helping the reader understand how the model that the authors present can contribute to the understanding of the question "how microbes competing for a limited number of resources stably coexist". I do appreciate that this changes the focus of the manuscript from a presentation of simulation results to more of a discussion of mathematical modelling.

We thank the reviewer for the insightful suggestions. We agree with the reviewer that the model structure and the underlying assumptions need to be carefully discussed, in order to understand the generality of the theoretical predictions. In particular, the reviewer emphasized that how HGT affects bistability might depend on how mobile genetic elements modified growth rates and competition. In the main text, we have shown that when mobile genes only influence species growth rates, HGT is expected to promote multistability (Fig. 1 and 2). However, when mobile genes modify species interactions, the effect of HGT on multistability is dependent on how mobile genes change competition strength (Fig. 3a to f). When mobile genes increase competition, HGT promotes multistability (Fig. 3c and e). In contrast, when mobile genes relax competition, HGT is expected to reduce multistability (Fig. 3d and f).

In light of the reviewer’s comments, we have further generalized the model structure, by accounting for the scenario where mobile genes simultaneously modify growth rates and competition. The effect of mobile genes on growth rates is represented by the magnitude of 𝜆’s, and the influence on competition is described by another parameter 𝛿. By varying these two parameters, we can evaluate how the model structure and the underlying assumptions affect the baseline expectation. We performed additional simulations with broad ranges of 𝜆 and 𝛿 values. In particular, we analyzed whether HGT would promote the likelihood of bistability in two-species communities compared with the scenario without gene transfer (Fig. 3g-i). Our results suggested that: (1) With or without HGT, reducing 𝜆 (increasing neutrality) promotes bistability; (2) With HGT, increasing 𝛿 promotes bistability; (2) Compared with the population without HGT, gene transfer promotes bistability when 𝛿 is zero or positive, while reduces bistability when 𝛿 is largely negative. These results agree with the reviewer’s comment that the baseline bistability expectation depends on how HGT modifies gamma and lambda. In the updated manuscript, we have thoroughly discussed how the model structure and the underlying assumptions can influence the predictions (line 238-253). 

We further expanded our analysis, by calculating how other parameters, including competition strength, growth rate ranges, and death/dilution rate, would affect the multistability of communities undergoing horizontal gene transfer (Fig. S2, S3, S9, S10, S11, S12, S13, S15). Together with the results presented in the first draft, these analysis enables a more comprehensive understanding of how different mechanisms, including but not limited to HGT, collectively shaped community multistability. In the updated manuscript, the reviewer can see the change of focus from exploring the effects of HGT to a more thorough discussion of the mathematical model. The revised texts highlighted in blue and the supplemented figures reflect such a change.

Reviewer #2 (Public review):

Summary:

In this work, the authors use a theoretical model to study the potential impact of Horizontal Gene Transfer on the number of alternative stable states of microbial communities. For this, they use a modified version of the competitive Lotka Volterra model-which accounts for the effects of pairwise, competitive interactions on species growth-that incorporates terms for the effects of both an added death (dilution) rate acting on all species and the rates of horizontal transfer of mobile genetic elements-which can in turn affect species growth rates. The authors analyze the impact of horizontal gene transfer in different scenarios: bistability between pairs of species, multistability in communities, and a modular structure in the interaction matrix to simulate multiple niches. They also incorporate additional elements to the model, such as spatial structure to simulate metacommunities and modification of pairwise interactions by mobile genetic elements. In almost all these cases, the authors report an increase in either the number of alternative stable states or the parameter region (e.g. growth rate values) in which they occur.

In my opinion, understanding the role of horizontal gene transfer in community multistability is a

very important subject. This manuscript is a useful approach to the subject, but I'm afraid that a thorough analysis of the role of different parameters under different scenarios is missing in order to support the general claims of the authors. The authors have extended their analysis to increase their biological relevance, but I believe that the analysis still lacks comprehensiveness.

Understanding the origin of alternative stable states in microbial communities and how often they may occur is an important challenge in microbial ecology and evolution. Shifts between these alternative stable states can drive transitions between e.g. a healthy microbiome and dysbiosis. A better understanding of how horizontal gene transfer can drive multistability could help predict alternative stable states in microbial communities, as well as inspire novel treatments to steer communities towards the most desired (e.g. healthy) stable states.

Strengths:

(1) Generality of the model: the work is based on a phenomenological model that has been extensively used to predict the dynamics of ecological communities in many different scenarios.

(2) The question of how horizontal gene transfer can drive alternative stable states in microbial communities is important and there are very few studies addressing it.

We thank the reviewer for the positive comments on the potential novelty and conceptual importance of our work. We are also grateful for the constructive suggestions on the generality and comprehensiveness of our analysis. In particular, we agree with the reviewer that a thorough analysis of the role of different parameter could further improve the rigor of this work. We have fully addressed the raised issues in the updated manuscript and below.

Weaknesses:

(1) There is a need for a more comprehensive analysis of the relative importance of the different model parameters in driving multistability. For example, there is no analysis of the effects of the added death rate in multistability. This parameter has been shown to determine whether a given pair of interacting species exhibits bistability or not (see e.g. Abreu et al 2019 Nature Communications 10:2120). Similarly, each scenario is analyzed for a unique value of species interspecies interaction strength-with the exception of the case for mobile genetic elements affecting interaction strength, which considers three specific values. Considering heterogeneous interaction strengths (e.g. sampling from a random distribution) could also lead to more realistic scenarios - the authors generally considered that all species pairs interact with the same strength. Analyzing a larger range of growth rates effects of mobile genetic elements would also help generalize the results. In order to achieve a more generic assessment of the impact of horizontal gene transfer in driving multistability, its role should be systematically compared to the effects of the rest of the parameters of the model.

We appreciate the suggestions. For each of the parameters that the reviewer mentioned, we have performed additional simulations to evaluate its importance in driving multistability. 

For the added death rate, we have calculated the bistability feasibility of two-species populations under different values of 𝐷. Our results suggested that (1) varying death rate indeed changed the bistability probability of the system; (2) when the death rate was zero, mobile genetic elements that only modify growth rates would have no effects on system’s bistability. These results highlighted the importance of added death rate in driving multistability (Fig. S2, line 136-142). 

For the interspecies interaction strength, we first extended our analysis on two-species populations. By calculating the bistability probability under different values of 𝛾, we showed that when interspecies interaction strength was smaller than 1, the influence of HGT on population bistability became weak (Fig. S3, line 143-147). We also considered heterogenous interaction strengths in multispecies communities, by randomly sampling 𝛾_ij values from uniform distributions. While our results suggested the heterogeneous distribution of 𝛾_ij didn’t fundamentally change the main conclusion, the mean value and variance of 𝛾_ij affected the influence of HGT on multistability. The effects of HGT on community multistability becomes stronger when the mean value of 𝛾_ij gets larger than 1 and the variance of 𝛾_ij is small (Fig. S12, line 190-196).

We also analyzed different ranges of growth rates effects of mobile genetic elements. In particular, we sampled 𝜆_ij values from uniform distributions with given widths. Greater width led to larger range of growth rate effects. We used five-species populations as an example and tested different ranges. Our results suggested that multistability was more feasible when the growth rate effects of MGEs were small. The qualitative relationship between HGT and community was not dependent on the range of growth rate effects (Fig. S13, line 197-205).

(2) The authors previously developed this theoretical model to study the impact of horizontal gene transfer on species coexistence. In this sense, it seems that the authors are exploring a different (stronger interspecies competition) range of parameter values of the same model, which could potentially limit novelty and generality.

We appreciate the comment. In a previous work (PMID: 38280843), we developed a theoretical model that incorporated horizontal gene transfer process into the classic LV framework. This model provides opportunities to investigate the role of HGT in different open questions of microbial ecology. In the previous work, we considered one fundamental question: how competing microbes coexist stably. In this work, however, we focused on a different problem: how alternative stable states emerge in complex communities. While the basic theoretical tool that we applied in the two works were similar, the scientific questions, application contexts and the implications of our analysis were largely different. The novelty of this work arose from the fact that it revealed the conceptual linkage between alternative stable states and a ubiquitous biological process, horizontal gene transfer. This linkage is largely unknown in previous studies. Exploring such a linkage naturally required us to consider stronger interspecies competitions, which in general would diminish coexistence but give rise to multistability. We believe that the analysis performed in this work provide novel and valuable insights for the field of microbial ecology. 

With all the supplemented simulations that we carried out in light of the all the reviewer’s comments, we believe the updated manuscript also provide a unified framework to understand how different biological processes collectively shaped the multistability landscape of complex microbiota undergoing horizontal gene transfer. The comprehensive analyses performed and the diverse scenarios considered in this study also contribute to the novelty and generality of this work.  

(3) The authors analyze several scenarios that, in my opinion, naturally follow from the results and parameter value choices in the first sections, making their analysis not very informative. For example, after showing that horizontal gene transfer can increase multistability both between pairs of species and in a community context, the way they model different niches does not bring significantly new results. Given that the authors showed previously in the manuscript that horizontal gene transfer can impact multistability in a community in which all species interact with each other, one might expect that it will also impact multistability in a larger community made of (sub)communities that are independent of (not interacting with) each-which is the proposed way for modelling niches. A similar argument can be made regarding the analysis of (spatially structured) metacommunities. It is known that, for smaller enough dispersal rates, space can promote regional diversity by enabling each local community to remain in a different stable state. Therefore, in conditions in which the impact of horizontal gene transfer drives multistability, it will also drive regional diversity in a metacommunity.

Thanks. Based on the reviewer’s comments, we have move Fig. 3 and 4 to Supplementary Information. In the updated manuscript, we have focused more on analyzing the roles of different parameters in shaping community multistability.

(4) In some cases, the authors consider that mobile genetic elements can lead to ~50% growth rate differences. In the presence of an added death rate, this can be a relatively strong advantage that makes the fastest grower easily take over their competitors. It would be important to discuss biologically relevant examples in which such growth advantages driven by mobile genetic elements could be expected, and how common such scenarios might be.

We appreciate the suggestion. Mobile genetic elements can drive large growth rate differences when they encode adaptative traits like antibiotic resistance (line 197-198). 

We also analyzed different ranges of growth rates effects of mobile genetic elements, by sampling 𝜆_ij values from uniform distributions with given widths. Our results suggested that multistability was more feasible when the fitness effects of MGEs were small (Fig. S13b). The qualitative relationship between HGT and community was not dependent on the range of growth rate effects (Fig. S13a and b). We discussed these results in line 197-205 of the updated main text.

Reviewer #3 (Public review):

Hong et al. used a model they previously developed to study the impact of horizontal gene transfer (HGT) on microbial multispecies communities. They investigated the effect of HGT on the existence of alternative stable states in a community. The model most closely resembles HGT through the conjugation of incompatible plasmids, where the transferred genes confer independent growth-related fitness effects. For this type of HGT, the authors find that increasing the rate of HGT leads to an increasing number of stable states. This effect of HGT persists when the model is extended to include multiple competitive niches (under a shared carrying capacity) or spatially distinct patches (that interact in a grid-like fashion). Instead, if the mobile gene is assumed to reduce between-species competition, increasing HGT leads to a smaller region of multistability and fewer stable states. Similarly, if the mobile gene is deleterious an increase in HGT reduces the parameter region that supports multistability.

This is an interesting and important topic, and I welcome the authors' efforts to explore these topics with mathematical modeling. The manuscript is well written and the analyses seem appropriate and well-carried out. However, I believe the model is not as general as the authors imply and more discussion of the assumptions would be helpful (both to readers + to promote future theoretical work on this topic). Also, given the model, it is not clear that the conclusions hold quite so generally as the authors claim and for biologically relevant parameters. To address this, I would recommend adding sensitivity analyses to the manuscript.

We thank the reviewer for the agreeing that our work addressed an important topic and was wellconducted. We are also grateful for the suggestion on sensitivity analysis, which is very helpful to improve the rigor and generality of our conclusion. All the raised issues have been fully addressed in the updated manuscript and below.

Specific points

(1) The model makes strong assumptions about the biology of HGT, that are not adequately spelled out in the main text or methods, and will not generally prove true in all biological systems. These include:

a) The process of HGT can be described by mass action kinetics. This is a common assumption for plasmid conjugation, but for phage transduction and natural transformation, people use other models (e.g. with free phage that adsorp to all populations and transfer in bursts).

b) A subpopulation will not acquire more than one mobile gene, subpopulations can not transfer multiple genes at a time, and populations do not lose their own mobilizable genes. [this may introduce bias, see below].

c) The species internal inhibition is independent of the acquired MGE (i.e. for p1 the self-inhibition is by s1).

These points are in addition to the assumptions explored in the supplementary materials, regarding epistasis, the independence of interspecies competition from the mobile genes, etc. I would appreciate it if the authors could be more explicit in the main text about the range of applicability of their model, and in the methods about the assumptions that are made.

We are grateful for the reviewer’s suggestions. In main text and methods of the updated manuscript, we have made clear the assumptions underlying our analysis. For point (a), we have clarified that our model primarily focused on plasmid transfer dynamics (line 74, 101, 517). Therefore, the process of HGT can be described by mass action kinetics, which is commonly assumed for plasmid transfer (line 537-538). For point (b), our model allows a cell to acquire more than one mobile genes. Please see our response to point (3) for details. We have also made it clear that we assumed the populations would not lose their own mobile gene completely (line 526-527). For (c), we have also clarified it in the updated manuscript (line 111-112, 527-528). 

We have also performed a series of additional simulations to show the range of applicability of our model. In particular, we discuss the role of other mechanisms, including interspecies interaction strength, the growth rate effects of MGEs, MGE epistasis and microbial death rates in shaping the multistability of microbial communities undergoing HGT. These results were provided in Fig. S2, S3, S9, S10, S11, S12, S13 and S15.

(2) I am not surprised that a mechanism that creates diversity will lead to more alternative stable states. Specifically, the null model for the absence of HGT is to set gamma to zero, resulting in pij=0 for all subpopulations (line 454). This means that a model with N^2 classes is effectively reduced to N classes. It seems intuitive that an LV-model with many more species would also allow for more alternative stable states. For a fair comparison, one would really want to initialize these subpopulations in the model (with the same growth rates - e.g. mu1(1+lambda2)) but without gene mobility.

We appreciate the insightful comments. The reviewer was right that in our model HGT created additional subpopulations in the community. However, with or without HGT, we calculated the species diversity and multistability based on the abundances of the 𝑁 species (s_i in our model), instead of all the p_ij subpopulations. Therefore, although there exist more ‘classes’ in the model with HGT, the number of ‘classes’ considered when we calculated community diversity and multistability was equal. In light of the reviewer’s suggestion, we have also performed additional simulations, where we initialized the subpopulations in the model with nonzero abundances. Our results suggested that initializing the p_ij subpopulations with non-zero abundances didn’t change the main conclusion (Fig. S11, line 188-189).

(3) I am worried that the absence of double gene acquisitions from the model may unintentionally promote bistability. This assumption is equivalent to an implicit assumption of incompatibility between the genes transferred from different species. A highly abundant species with high HGT rates could fill up the "MGE niche" in a species before any other species have reached appreciable size. This would lead to greater importance of initial conditions and could thus lead to increased multistability.

This concern also feels reminiscent of the "coexistence for free" literature (first described here http://dx.doi.org/10.1016/j.epidem.2008.07.001 ) which was recently discussed in the context of plasmid conjugation models in the supplementary material (section 3) of https://doi.org/10.1098/rstb.2020.0478 .

We appreciate the comments. Our model didn’t assume the incompatibility between MGEs transferred from different species. Instead, it allows a cell to acquire more than one MGEs. In our model, p_ij described the subpopulation in the 𝑖-th species that acquired the MGE from the 𝑗th species. Here, p_ij can have overlaps with p_ik (𝑗 ≠ 𝑘). In other words, a cell can belong to p_ij and p_ik at the same time. The p_ij subpopulation is allowed to carry the MGEs from the other species. In the model, we used to describe the influence of the other MGEs on the growth of p_ij.

We also thank the reviewer for bringing two papers into our attention. We have cited and discussed these papers in the updated manuscript (line 355-362).

(4) The parameter values tested seem to focus on very large effects, which are unlikely to occur commonly in nature. If I understand the parameters in Figure 1b correctly for instance, lambda2 leads to a 60% increase in growth rate. Such huge effects of mobile genes (here also assumed independent from genetic background) seem unlikely except for rare cases. To make this figure easier to interpret and relate to real-world systems, it could be worthwhile to plot the axes in terms of the assumed cost/benefit of the mobile genes of each species.

Thanks for the comments. In the main text, we presented one simulation results that assumed relatively large effects of MGE on species fitness, as the reviewer pointed out. In the updated manuscript, we have supplemented numerical simulations that considered different ranges of fitness effects, including the fitness effect as small as 10% (Fig. S13a). We have also plotted the relationship between community multistability and the assumed fitness effects of MGEs, as the reviewer suggested (Fig. S13b). Our results suggested that multistability was more feasible when the fitness effects of MGEs were small, and changing the range of MGE fitness effects didn’t fundamentally change our main conclusion. These results were discussed in line 197-205 of the updated main text.

Something similar holds for the HGT rate (eta): given that the population of E. coli or Klebsiella in the gut is probably closer to 10^9 than 10^12 (they make up only a fraction of all cells in the gut), the assumed rates for eta are definitely at the high end of measured plasmid transfer rates (e.g. F plasmid transfers at a rate of 10^-9 mL/CFU h-1, but it is derepressed and considered among the fastest - https://doi.org/10.1016/j.plasmid.2020.102489 ). To adequately assess the impact of the HGT rate on microbial community stability it would need to be scanned on a log (rather than a linear) scale. Considering the meta-analysis by Sheppard et al. it would make sense to scan it from 10^-7 to 1 for a community with a carrying capacity around 10^9.

We thank the reviewer for the constructive suggestion. We have carried out additional simulations by scanning the 𝜂 value from 10^-7 to 1. The results suggested that increasing HGT rates started to promote multistability when 𝜂 value exceeded 10^-2 per hour (Fig. S9, line 337-346). This corresponds to a conjugation efficiency of 10^-11 cell^-1 ∙ mL^-1∙ mL when the maximum carrying capacity equals 10⁹ cells ∙ mL^-1, or a conjugation efficiency of 10^-14 cell^-1 ∙ hr^-1∙ mL when the maximum carrying capacity equals 10¹² cells ∙ mL^-1.

(5) It is not clear how sensitive the results (e.g. Figure 2a on the effect of HGT) are to the assumption of the fitness effect distribution of the mobile genes. This is related to the previous point that these fitness effects seem quite large. I think some sensitivity analysis of the results to the other parameters of the simulation (also the assumed interspecies competition varies from figure to figure) would be helpful to put the results into perspective and relate them to real biological systems.

We appreciate the comments. In light of the reviewer’s suggestion, we have changed the range of the fitness effects and analyzed the sensitivity of our predictions to this range. As shown in Fig. S13, changing the range of MGE fitness effects didn’t alter the qualitative interplay between HGT and community multistability. We have also examined the sensitivity of the results to the strength of interspecies competition strength (Fig. S3, S10, S12). These results suggested that while the strength of interspecies interactions played an important role in shaping community multistability, the relationship between HGT rate and multistability was not fundamentally changed by varying interaction strength. In addition, we examined the role of death rates (Fig. S2). In the updated manuscript, we discussed the sensitivity of our prediction to these parameters in line 136-147, 190205, 335-354.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Please find below a few suggestions that, in my opinion, could help improve the manuscript.

TITLE

It might not be clear what I 'gene exchange communities' are. Perhaps it could be rewritten for more specificity (e.g. '...communities undergoing horizontal gene transfer').

We have updated the title as the reviewer suggested.

ABSTRACT

The abstract could also be edited to improve clarity and specificity. Terms like 'complicating factors' are vague, and enumerating specific factors would be better. The results are largely based on simulations, no analytical results are plotted, so I find that the sentence starting with 'Combining theoretical derivation and numerical simulations' can be a bit misleading.

We appreciate the suggestions. We have enumerated the specific factors and scenarios in the updated abstract (line 18-26). We have also replaced 'Combining theoretical derivation and numerical simulations' with ‘Combining mathematical modeling and numerical simulations’.

INTRODUCTION

-  Line 42, please revise this paragraph. The logical flow is not so clear, it seems a bit like a list of facts, but the main message might not be clear enough. Also, it would be good to define 'hidden' states or just rewrite this sentence.

We appreciate the suggestion. In the updated manuscript, we have rewritten this paragraph to improve the logical flow and clarity (line 46-52).

-  Line 54, there is little detail about both theoretical models and HGT in this paragraph, and mixing the two makes the paragraph less focused. I suggest to divide into two paragraphs and expand its content. For example, you could explain a bit some relevant implications of MGE.

We appreciate the suggestion. In the updated manuscript, we have divided this paragraph into two paragraphs, focusing on theoretical models and HGT, respectively (line 55-71). In particular, we have added explanations on the implications of MGEs (line 66-69), as the reviewer suggested.

-  Line 72, as mentioned in the abstract, it would be better to explicitly mention which confounding factors are going to be discussed.

Thanks for the suggestion. We have rewritten this part as “We further extended our analysis to scenarios where HGT changed interspecies interactions, where microbial communities were subjected to strong environmental selections and where microbes lived in metacommunities consisting of multiple local habitats. We also analyzed the role of different mechanisms, including interspecies interaction strength, the growth rate effects of MGEs, MGE epistasis and microbial death rates in shaping the multistability of microbial communities. These results created a comprehensive framework to understand how different dynamic processes, including but not limited to HGT rates, collectively shaped community multistability and diversity” (line 75-82).

RESULTS

-  The basic concepts (line 77) should be explained with more detail, keeping the non-familiar reader in mind. The reader might not be familiar with the concept of bistability in terms of species abundance. Also, note that mutual inhibition does not necessarily lead to positive feedback, as an interaction strength between 0 and 1 might still be considered inhibition. In any case, in Figure 1 it is not obvious how the positive feedback is represented, the caption should explain it. Note that neither the main text nor the caption explains the metaphor of the landscape and the marble that you are using in Figure 1a.

We have rewritten this paragraph to provide more details on the basic concepts (line 86-99). We have removed the statement about ‘mutual inhibition’ to avoid being misleading. We have also updated the caption of Fig. 1a to explain the metaphor of the landscape and the marble (line 389396). 

-  In the classical LV model, bistability does not depend on growth rates, but only on interaction strength. Therefore, I think that much of the results are significantly influenced by the added death rate. I believe that if the death rate is set to zero, mobile genetic elements that only modify growth rates will have no effect on the system's bistability. Because of this, I think that a thorough analysis of the role of the added death (dilution) rate and the distribution of growth rates is especially needed.

We are grateful for the reviewer’s insightful comments. In the updated manuscript, we have thoroughly analyzed the role of the added death (dilution) rate on the bistability of communities composed of two species (Fig. S2). Indeed, as the reviewer pointed out, if the death rate equals zero, mobile genetic elements that only modify growth rates will have no effect on the system's bistability. We have discussed the role of death rate in line 136-142 of the updated manuscript.

We have also expanded our analysis on the distribution of growth rates. In particular, we considered different ranges of growth rates effects of mobile genetic elements, by sampling 𝜆_ij values from uniform distributions with given widths (Fig. S13). Greater width led to larger range of growth rate effects. We used five-species populations as an example and tested different ranges.

Our results suggested that multistability was more feasible when the growth rate effects of MGEs were small (Fig. S13b). The qualitative relationship between HGT and community was not dependent on the range of growth rate effects (Fig. S13a). These results are discussed in line 197205 of the updated manuscript.

-  The analysis uses gamma values that, in the absence of an added death rate, render a species pair bistable. Therefore, multistability would be quite expected for a 5 species community. Note that, multistability is possible in communities of more than 2 species even if all gamma values are smaller than 1. Analyzing a wide range of interaction strength distributions would really inform on the relative role of HGT in multistability across different community scenarios.

We are grateful for the reviewer’s suggestion. In light of the reviewer’s comments, in the updated manuscript, we have performed additional analysis by focusing on a broader range of interaction strengths (Fig. S3, S10, S12), especially the gamma values below 1 (Fig. S10). Our results agreed with the reviewer’s notion that multistability was possible in communities of more than 2 species even if all gamma values were smaller than 1 (Fig. S10). 

-  I would recommend the authors extend the analysis of the model used for Figures 1 and 2. Figures 3 and 4 could be moved to the supplement (see my point in the public review), unless the authors extend the analysis to explain some non-intuitive outcomes for niches and metacommunities.

Thanks. In the updated manuscript we have performed additional simulations to extend the analysis in Figure 1 and 2. These results were presented in Fig. S2, S3, S9, S10, S11, S12, and S13. We have also moved Figure 3 and 4 to SI as the reviewer suggested.

-  The authors seem to refer to fitness and growth rates as the same thing. This could lead to confusion - the strongest competitor in a species pair could also be interpreted as the fittest species despite being the slowest grower. I think there's no need to use fitness if they refer to growth rates. In any case, they should define fitness if they want to use this concept in the text.

We are grateful for the insightful suggestion. To avoid confusion, we have used ‘growth rate’ throughout the updated manuscript.

-  Across the text, the language needs some revision for clarity, specificity, and scientific style. In lines 105 - 109 there are some examples, like the use of 'in a lot of systems', and ' interspecies competitions' (I believe they mean interspecies interaction strengths).

We appreciate the reviewer for pointing them out. We have thoroughly checked the text and made the revisions whenever applicable to improve the clarity and specificity.

-  Many plots present the HGT rate on the horizontal axis. Could the authors explain why is it that the rate of HGT is relatively important for the number of alternative stable states? I understand how from zero to a small positive number there is a qualitative change. Beyond that, it shouldn't affect bistability too much, I think. If I am right, then other parameters could be more informative to plot in the horizontal axis. If I am wrong, I think that providing an explanation for this would be valuable.

Thanks. To address the reviewer’s comment, we have systematically analyzed the effects of HGT on community multistability, by scanning the HGT rate from 10^-7 to 10⁰hr^-1 . In communities of two or multiple species, our simulation results showed that multistability gradually increased with HGT rate when HGT rate exceeded 10²hr^-1. These results, presented in Fig. S9 and discussed in line 337-346, provided a more quantitative relationship between multistability and HGT rate.

While in this work we showed the potential role of HGT in modulating community multistability, our results didn’t exclude the role of the other parameters. Motivated by the comments raised by the reviewers, in the updated manuscript, we have performed additional simulations to analyze the influence of other parameters in shaping community multistability. These parameters include death or dilution rate (Fig. S2), interaction strength (Fig. S3, S9, S10, S11, S12, S14, S15), 𝜆 range (Fig. S13, S15) and 𝛿 value (Fig. 3g, h, i). In many of the supplemented results (Fig. S2b, S3b, S13b, Fig. 3g, 3h and 3i), we have also plotted the data by using these parameters as the x axis. We believe the updated work now provided a more comprehensive framework to understand how different mechanisms, including but not limited to HGT, might shape the multistability of complex microbiota. These points were discussed in line 136-147, 190-205, 238-253, 334-354 of the updated main text. 

-  My overall thoughts on the case of antibiotic exposure are similar to those of previous sections. Very few of the different parameters of the model are analyzed and discussed. In this case, the authors increased the interaction strength to ~0.4 times higher compared to previous sections. Was this necessary, and why?

Thanks for the comments. In the previous draft, the interaction strength 𝛾=1.5 was tested as an example. Motivated by the reviewer’s comments, in the updated manuscript, we have examined different interaction strengths, including the strength ( 𝛾 = 1.1 ) commonly tested in other scenarios. The prediction equally held for different 𝛾 values (Fig. S15). We have also analyzed different 𝜆 ranges (Fig. S15). These results, together with the analyses presented in the earlier version of the manuscript, suggested the potential role of HGT in promoting multistability for communities under strong selection. The supplemented results were presented in Fig. S15 and discussed in line 293-295 of the updated manuscript.

-  Line 195, if a gene encodes for the production of a public good, why would its HGT reduce interaction strength? I can think of the opposite scenario: the gene is a public good, and without HGT there is only one species that can produce it. Let's imagine that the public good is an enzyme that deactivates an antibiotic that is present in the environment, and then the species that produces has a positive interaction with another species in a pairwise coculture. If HGT happens, the second species becomes a producer and does not need the other one to survive in the presence of antibiotics anymore. The interaction can then become more competitive, as e.g. competition for resources could become the dominant interaction.

We are grateful for pointing it out. In the updated manuscript, we have removed this statement.

DISCUSSION

-  L 267 "by comparison with empirical estimates of plasmid conjugation rates from a previous study [42], the HGT rates in our analysis are biologically relevant in a variety of natural environments". The authors are using a normalized model and the relevance of other parameter values is not discussed. If the authors want to claim that they are using biologically relevant HGT, they should also discuss whether the rest of the parameter values are biologically relevant. I recommend relaxing this statement about HGT rates.

We appreciate the suggestion. We agree with the reviewer that other parameters including the death/dilution rate, interactions strength and 𝜆 ranges are also important in shaping community multistability. We have performed additional analysis to show the effects of these parameters. In light of the reviewer’s suggestion, we have relaxed this statement and thoroughly discussed the context-dependent effect of HGT as well as the roles of different parameters (line 334-354).

-  Last sentence: "Therefore, inhibiting the MGE spread using small molecules might offer new opportunities to reshape the stability landscape and narrow down the attraction domains of the disease states". It is not clear what procedure/technique the authors are suggesting. If they want to keep this statement, the authors should give more details on how small molecules can be/are used to inhibit MGE.

We appreciated the comments. Previous studies have shown some small molecules like unsaturated fatty acids can inhibit the conjugative transfer of plasmids. By binding the type IV secretion traffic ATPase TrwD, these compounds limit the pilus biogenesis and DNA translocation. We have provided more details regarding this statement in the updated manuscripts (line 376-379).

METHODS

-  Line 439, mu_i should be presented as the maximum 'per capita' growth rate.

We have updated the definition of 𝜇i following the suggestion (line 529).

-  Line 444, this explanation is hard to follow, please expand it to provide more details. You could provide an example, like explaining that all individuals from S1 have the MGE1 and therefore they have mu_1 = mu_01 ... After HGT, their fitness changes if they get the plasmid from S2, so a term lambda2 appears.

Thanks. In the updated manuscript, we have expanded the explanation by providing an example as the reviewer suggested (line 534-537).

-  The normalization assumes a common carrying capacity Nm (Eqs 1-4) and then it's normalized (Eqs. 5-8). It would be better to start from a more general scenario in which each species has a different carrying capacity and then proceed with the normalization.

We appreciate the suggestion. In the updated manuscript, we have started our derivation from the scenario where each species has a different carrying capacity before proceeding with the normalization (section 1 of Methods, line 516-554). The same equations can be obtained after normalization.

-  I think that the meaning of kappa (the plasmid loss rate) is not explained in the text.

Thanks for pointing it out. We have explained the meaning of kappa in the updated text (line 108, 154, 539-541, 586-587, 607).

SUPPLEMENT

-  Figure S4, what are the different colors in panel b?

In panel b of Fig. S4, the different colors represent the simulation results repeated with randomized growth rates. We have made it clear in the updated SI.

Reviewer #3 (Recommendations for the authors):

(1) Please extend your description of the model, so it is easier to understand for readers who have not read the first paper. Especially the choice to describe the model as species and subpopulations, as opposed to writing it as MGE-carrying and MGE-free populations of each species makes it quite complicated to understand which parameters influence each other.

Thanks for the suggestion. We have extended the model description in the updated manuscript, which provides a more detailed introduction on model configurations and parameter definitions (line 86-99, 101-113, 151-159). We have also updated the Methods to extend the model description.

(2) Please define gamma_ji in equation 13 and eta_jki in equation 14 (how to map the indices onto the assumed directionality of the interaction).

We have defined these two parameters in the updated manuscript (line 584-586, 630-632).

(3)  Line 511: please add at the beginning of this paragraph that you are assuming a grid-like arrangement of patches which will be captured by dispersal term H.

We have updated this paragraph to make this assumption clear (line 636-637).

(4)  Line 540: "used in our model" (missing a word).

We have corrected it in the updated manuscript.

(5)  Currently the analyses looking at the types of growth effects HGT brings (Figures 5-7) feel very "tacked on". These are not just "confounding factors", but rather scenarios that are much more biologically realistic than the assumption of independent effects. I would introduce them earlier in the text, as I think many readers may not trust your results until they know this was considered (+ how it changes the conclusions).

We are grateful for the suggestion. We agree with the reviewer that these biologically realistic scenarios should be introduced earlier in the text. In the updated manuscript, we have moved these analyses forward, as sections 3, 4 and 5. We have also avoided the term “confounding factors”. Instead, in the updated manuscript, we have separated these analyses into different sections, and clearly described each scenario in the section title (line 217-218, 254, 275).

(6)  In some places the manuscript refers to HGT, in others to MGE presence (e.g. caption of Figure 6). These are not generally the same thing, as HGT could also occur due to extracellular vesicles or natural transformation etc. Please standardize the nomenclature and make it clearer which type of processes the model describes.

We appreciate the comment. The model in this work primarily focused on the process of plasmid transfer. We have made it clear throughout the main text. 

(7)  In many figures the y-axis starts at a value other than 0. This is a bit misleading. In addition, I would recommend changing the title "Area of bistability region" to "Area of bistability" or perhaps even "Area of multistability" (since more than two species are considered).

Thanks for the suggestion. We have updated all the relevant figures to make sure that their y-axes start at 0. We have also changed the title “Area of bistability region” to “Area of multistability”, whenever it is applicable.

(8)  Figure 7: what are the assumed fitness effects of the mobile genes in the simulation? Which distribution were they drawn from? Please add this info to the figure caption here and elsewhere.

In Figure 7, we explored an extreme scenario of the fitness effects of the mobile genes, where the population was subjected to strong environmental selection and only cells carrying the mobile gene could grow. Therefore, the carriage of the mobile gene changed the species growth rate from 0 to a positive value µ_i. When calculating the number of stable states in the communities, we randomly drew the µ_i values from a uniform distribution between 0.3 and 0.7 hr^-1. We had added this information in the figure caption (line 505-508) and method (line 615-617) of the updated manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study puts forth the model that under IFN-B stimulation, liquid-phase WTAP coordinates with the transcription factor STAT1 to recruit MTC to the promoter region of interferon-stimulated genes (ISGs), mediating the installation of m⁶A on newly synthesized ISG mRNAs. This model is supported by strong evidence that the phosphorylation state of WTAP, regulated by PPP4, is regulated by IFN-B stimulation, and that this results in interactions between WTAP, the m⁶A methyltransferase complex, and STAT1, a transcription factor that mediates activation of ISGs. This was demonstrated via a combination of microscopy, immunoprecipitations, m⁶A sequencing, and ChIP. These experiments converge on a set of experiments that nicely demonstrate that IFN-B stimulation increases the interaction between WTAP, METTL3, and STAT1, that this interaction is lost with the knockdown of WTAP (even in the presence of IFN-B), and that this IFN-B stimulation also induces METTL3-ISG interactions.

Strengths:

The evidence for the IFN-B stimulated interaction between METTL3 and STAT1, mediated by WTAP, is quite strong. Removal of WTAP in this system seems to be sufficient to reduce these interactions and the concomitant m⁶A methylation of ISGs. The conclusion that the phosphorylation state of WTAP is important in this process is also quite well supported.

Weaknesses:

The evidence that the above mechanism is fundamentally driven by different phase-separated pools of WTAP (regulated by its phosphorylation state) is weaker. These experiments rely relatively heavily on the treatment of cells with 1,6-hexanediol, which has been shown to have some off-target effects on phosphatases and kinases (PMID 33814344).

Given that the model invoked in this study depends on the phosphorylation (or lack thereof) of WTAP, this is a particularly relevant concern.

We are grateful for the reviewer’s positive comment and constructive feedback. 1,6-hexanediol (hex) was considered an inhibitor of hydrophobic interaction, thereby capable of dissolving protein phase separation condensates. Hex (5%-10% w/v) was still widely used to explore the phase separation characteristic and function on various protein, including some phosphorylated proteins such as pHSF1, or kinases such as NEMO1-3. Since hydrophobic interactions involved in various types of protein-protein interaction, the off-target effects of hex were inevitable. It has been reported that hex impaired RNA polymerase II CTD-specific phosphatase and kinase activity at 5% concentration4, which led to the reviewer’s concern. In response to this concern, we investigated the phosphorylation level of WTAP under hex concentration gradient treatment. Surprisingly, we found that both 2% and 5% hex maintained the PPP4c-mediated dephosphorylation level of WTAP but still led to the dissolution of WTAP LLPS condensates (Figure 5-figure supplement 1H; Author response image 1), indicating that hex dispersed WTAP phase separation in a phosphorylation-independent manner. Consistent with our findings, Ge et al. used 10% hex to dissolve WTAP phase separation condensates5. Additionally, we found the phosphorylation level of STAT1 was not affected by both 2% and 5% hex, revealing the off-target and impairment function of hex on kinases or phosphatases might not be universal (Figure 5-figure supplement 1H). Collectively, since the 5% hex we used did not influence the de-phosphorylation event of WTAP, function of WTAP LLPS mediating interaction between methylation complex and STAT1 revealed by our results was independent from its phosphorylation status.

Author response image 1.

mCherry-WTAP-rescued HeLa cells were treated with 10 ng/mL IFN-β together with or without 2% or 5% hex and 20 μg/mL digitonin for 1 hour or left untreated. Phase separation of mCherry-WTAP was observed through confocal microscopy. The number of WTAP condensates that diameter over 0.4 μm of n = 20 cells were counted through ImageJ and shown. Scale bars indicated 10 μm. All error bars, mean values ± SD, P-values were determined by unpaired two-tailed Student’s t-test of n = 20 cells in (B). For (A), similar results were obtained for three independent biological experiments.

Related to this point, it is also interesting (and potentially concerning for the proposed model) that the initial region of WTAP that was predicted to be disordered is in fact not the region that the authors demonstrate is important for the different phase-separated states.

A considerable number of proteins undergo phase separation via interactions between intrinsically disordered regions (IDRs). IDR contains more charged and polar amino acids to present multiple weakly interacting elements, while lacking hydrophobic amino acids to show flexible conformations6. In our study, we used PLAAC websites (http://plaac.wi.mit.edu/) to predict IDR domain of WTAP, and a fragment (234-249 amino acids) was predicted as prion-like domain (PLD). However, deletion of this fragment failed to abolish the phase separation properties of WTAP, which might be the main confusion to reviewers. To explain this issue, we checked the WTAP structure (within part of MTC complex) from protein data bank (https://www.rcsb.org/structure/7VF2) and found that the prediction of IDR has been renewed due to the update of different algorithm. IDR of WTAP expanded to 245-396 amino acids, encompassing the entire CTD region. Our results demonstrate that the CTD was critical for WTAP LLPS, as CTD deficiency significantly inhibited the formation of liquid condensates both in vitro and in cells. Also, phosphorylation sites on CTD were important for the phase transition of WTAP. These observations highlight the phosphorylation status on CTD region as a key driving force of phase separation, consistent with the established role of IDR in regulating LLPS. We have revised our description on WTAP IDR in our article following the reviewers’ suggestion.

Taking all the data together, it is also not clear to me that one has to invoke phase separation in the proposed mechanism.

In this article, we observed that WTAP underwent phase transition during virus infection and IFN-β treatment, and proposed a novel mechanism whereby post translational modification (PTM)-driven WTAP LLPS was required for the m⁶A modification of ISG mRNAs. To verify the hypothesis, we first demonstrated the relationship between PTM and phase separation of WTAP. We constructed WTAP 5ST-D and 5ST-A mutant to mimic WTAP phosphorylation and dephosphorylation status respectively, and figured out that dephosphorylated WTAP underwent LLPS. We also found that PPP4 was the main phosphatase to regulate WTAP dephosphorylation. To further investigation, we introduced the potent PPP4 inhibitor, fostriecin. Consistent with our findings in PPP4 deficient model, fostriecin treatment significantly inhibited the IFN-β-induced dephosphorylation of WTAP and disrupted its LLPS condensates, indicating that PPP4 was the key phosphatase recruited by IFN-β to regulate WTAP, confirming that PTM governs WTAP LLPS dynamics (Figure 2-figure supplement 1C and H). Furthermore, fostriecin-induced impairment of WTAP phosphorylation and phase separation correlated with reduced m⁶A modification level and elevated ISGs expression level (Figure 4C and Figure 4-figure supplement 1E). These findings together emphasized that dephosphorylation is required for WTAP LLPS.

As for the function of WTAP LLPS, we assumed that WTAP might undergo LLPS to sequester STAT1 together with m⁶A methyltransferase complex (MTC) for mediating m⁶A deposition on ISG mRNAs co-transcriptionally under IFN-β stimulation. Given that hex dissolved WTAP LLPS condensates without affecting dephosphorylation status (Figure 5-figure supplement 1H; Author response image 1), various experiments we performed previously actually confirmed the critical role of WTAP LLPS during m⁶A modification (Figure 4A), as well as the mechanism that WTAP phase separation enhanced the interaction between MTC and STAT1 (Figure 5E-F). Subsequent to reviewer’s comments, more experiments were conducted for further validation. We found the WTAP liquid condensates formed by wild type (WT) WTAP or WTAP 5ST-A mutant (which mimics dephosphorylated-WTAP) could be dissembled by hex, which also led to the impairment of the interaction between STAT1, METTL3 and WTAP (Figure 5-figure supplement 1E). In addition, in vitro experiments demonstrated that hex treatment significantly disrupted the interaction between recombinant GFP-STAT1 and mCherry-WTAP which expressed in the E. coli system (Figure 5F and Figure 5-figure supplement 1G). Notably, this prokaryotic expression system lacks endogenous phosphorylation machinery, resulting in non-phosphorylated mCherry-WTAP. For further validation, we performed the interaction of WTAP WT or 5ST-A with the promoter regions of ISG as well as the m⁶A modification of ISG mRNAs were attenuated by WTAP LLPS dissolution (Figure 4E and Figure 6E). These findings together revealed that WTAP LLPS were the critical mediators of the STAT1-MTC interactions, ISG promoter regions binding and the co-transcription m⁶A modification.

Collectively, our results demonstrated that IFN-β treatment recruited PPP4c to dephosphorylate WTAP, thereby driving the formation of WTAP liquid condensates which were essential for facilitating STAT1-MTC interaction and m⁶A deposition, subsequently mediated ISG expression. Since we revealed a strong association between PTM-regulated WTAP phase transition and its m⁶A modification function, WTAP LLPS was a novel and functionally distinct mechanism that must be reckoned with in this study.

Author response image 2.

Wild type (WT) WTAP or 5ST-A mutant-rescued WTAP^sgRNA THP-1-derived macrophages are stimulated with or without with 10 ng/mL IFN-β together followed with 2% or 5% 1,6-hexanediol (hex) and 20 μg/mL digitonin for 1 hour or left untreated. antibody and imaged using confocal microscope. Scale bars indicated 10 μm.

Reviewer #2 (Public review):

In this study, Cai and colleagues investigate how one component of the m⁶A methyltransferase complex, the WTAP protein, responds to IFNb stimulation. They find that viral infection or IFNb stimulation induces the transition of WTAP from aggregates to liquid droplets through dephosphorylation by PPP4. This process affects the m⁶A modification levels of ISG mRNAs and modulates their stability. In addition, the WTAP droplets interact with the transcription factor STAT1 to recruit the methyltransferase complex to ISG promoters and enhance m⁶A modification during transcription. The investigation dives into a previously unexplored area of how viral infection or IFNb stimulation affects m⁶A modification on ISGs. The observation that WTAP undergoes a phase transition is significant in our understanding of the mechanisms underlying m⁶A's function in immunity. However, there are still key gaps that should be addressed to fully accept the model presented.

Major points:

(1) More detailed analyses on the effects of WTAP sgRNA on the m⁶A modification of ISGs:

a. A comprehensive summary of the ISGs, including the percentage of ISGs that are m⁶A-modified. merip-isg percentage

b. The distribution of m⁶A modification across the ISGs. Topology

c. A comparison of the m⁶A modification distribution in ISGs with non-ISGs. Topology

In addition, since the authors propose a novel mechanism where the interaction between phosphorylated STAT1 and WTAP directs the MTC to the promoter regions of ISGs to facilitate co-transcriptional m⁶A modification, it is critical to analyze whether the m⁶A modification distribution holds true in the data.

We appreciate the reviewer’s summary of our manuscript and the constructive assessment. We have conducted the related analysis accordingly to present the m⁶A modification in ISGs in our model as reviewers suggested. Our results showed that about 64.29% of core ISGs were m⁶A modified under IFN-β stimulation (Figure 3-figure supplement 1B; Figure 3G), which was consistent with the similar percentage in previous studies[7,8]. The m⁶A distribution of the ISGs transcripts including IFIT1, IFIT2, OAS1 and OAS2 was validated (Figure 3-figure supplement 1H).

Generally, m⁶A deposition preferentially located in the vicinity of stop codon, while m⁶A modification was highly dynamic under different cellular condition. However, we compared the topology of m⁶A deposition of ISGs with non-ISGs, and found that m⁶A modification of ISG mRNAs showed higher preference of coding sequences (CDS) localization compared to global m⁶A deposition (Figure 3H). Similarly, various researches uncovered the m⁶A deposition regulated by co-transcriptionally m⁶A modification preferred to locate in the CDS [9-11]. Since our results of m⁶A modification distribution of ISGs was consistent with the co-transcriptional m⁶A modification characteristics, we believed that our hypothesis and results were correlated and consistent.

(2) Since a key part of the model includes the cytosol-localized STAT1 protein undergoing phosphorylation to translocate to the nucleus to mediate gene expression, the authors should focus on the interaction between phosphorylated STAT1 and WTAP in Figure 4, rather than the unphosphorylated STAT1. Only phosphorylated STAT1 localizes to the nucleus, so the presence of pSTAT1 in the immunoprecipitate is critical for establishing a functional link between STAT1 activation and its interaction with WTAP.

Thank you for the constructive comments. As we showed in Figure 4, we found the enhanced interaction between phase-separated WTAP and the nuclear-translocated STAT1 which were phosphorylated under IFN-β stimulation, indicating the importance of phosphorylation of STAT1. We repeated the immunoprecipitation experiments to clarify the function of pSTAT1 in WTAP interaction. Our results showed that IFN-β stimulation induced the interaction of WTAP with both pSTAT1 and STAT1 (Figure 5-figure supplement 1C), indicating that most of the WTAP-associated STAT1 was phosphorylated. Taken together, our data proved that LLPS WTAP bound with nuclear-translocated pSTAT1 under IFN-β stimulation.

(3) The authors should include pSTAT1 ChIP-seq and WTAP ChIP-seq on IFNb-treated samples in Figure 5 to allow for a comprehensive and unbiased genomic analysis for comparing the overlaps of peaks from both ChIP-seq datasets. These results should further support their hypothesis that WTAP interacts with pSTAT1 to enhance m⁶A modifications on ISGs.

Thank you for raising this thoughtful comment. In this study, MeRIP-seq and RNA-seq along with immunoprecipitation and immunofluorescence experiments supported that phase transition of WTAP enhanced its interaction to pSTAT1, thus mediating ISGs m⁶A modification and expression by enhancing its interaction with nuclear-translocated pSTAT1 during virus infection and IFN-β stimulation. However, how WTAP-mediated m⁶A modification was related to STAT1-mediated transcription remained unclear. Several researches have revealed the recruitment of m⁶A methyltransferase complex (MTC) to transcription start sites (TSS) of coding genes and R-loop structure by interacting with transcriptional factors STAT5B, SMAD2/3, DNA helicase DDX21, indicating the engagement of MTC mediated m⁶A modification on nascent transcripts at the very beginning of transcription [11-13]. These researches inspired us that phase-separated WTAP could be recruited to the ISG promoter regions via interacting with nuclear-translocated pSTAT1. To validate this mechanism, we have conducted ChIP-qPCR experiments targeting STAT1 and WTAP, revealed that IFN-β induced the comparable recruitment dynamics of both STAT1 and WTAP to ISG promoter regions (Figure 6A-B). Notably, STAT1 deficiency significantly abolished the bindings between WTAP and ISG promoter regions (Figure 6C). These findings established nuclear-translocated STAT1-dependent recruitment of phase separated WTAP and ISG promoter region, substantiated our hypothesis within the current study. We totally agree that ChIP-seq data will be more supportive to explore the mechanism in depth. We will continuously focus on the whole genome chromatin distribution of WTAP and explore more functional effect of transcriptional factor-dependent WTAP-promoter regions interaction in the future.

Minor points:

(1) Since IFNb is primarily known for modulating biological processes through gene transcription, it would be informative if the authors discussed the mechanism of how IFNb would induce the interaction between WTAP and PPP4.

Protein phosphatase 4 (PPP4) is a multi-subunit serine/threonine phosphatase complex that participates in diverse biologic process, including DDR, cell cycle progression, and apoptosis[14]. Several signaling pathway such as NF-κB and mTOR signaling, can be regulated by PPP4. Previous research showed that deficiency of PPP4 enhanced IFN-β downstream signaling and ISGs expression, which was consistent with our findings that knockdown of PPP4C impaired WTAP-mediated m⁶A modification, enhanced the ISGs expression[15,16]. Since there was no significant enhancement in PPP4 expression level during 0-3 hours of IFN-β stimulation in our results, we explored the PTM that may influence the protein-protein interaction, such as ubiquitination. Intriguingly, we found the ubiquitination level of PPP4 was enhanced after IFN-β stimulation, which may affect the interaction between PPP4 and WTAP (Author response image 3). Further investigation between PPP4 and WTAP will be conducted in our future study.

Author response image 3.

HEK 293T transfected with HA-ubiquitin (HA-Ub) and Flag-PPP4 were treated with 10 ng/mL IFN-β or left untreated. Whole cell lysate (WCL) was collected and immunoprecipitation (IP) experiment using anti-Flag antibody was performed, followed with immunoblot. Similar results were obtained for three independent biological experiments.

(2) The authors should include mCherry alone controls in Figure 1D to demonstrate that mCherry does not contribute to the phase separation of WTAP. Does mCherry have or lack a PLD?

According to the crystal structure of mCherry protein in protein structure database RCSB-PDB, mCherry protein presents as a β-barrel protein, with no IDRs or multivalent interaction domains including PLD, indicating that mCherry protein has no capability to undergo phase separation. This characteristic makes it a suitable protein to tag and trace the localization or expression levels of proteins, and a negative control for protein phase separation studies. As the reviewer suggested, we include mCherry alone controls in the revised version (Figure 1D).

(3) The authors should clarify the immunoprecipitation assays in the methods. For example, the labeling in Figure 2A suggests that antibodies against WTAP and pan-p were used for two immunoprecipitations. Is that accurate?

Due to the lack of phosphorylated-WTAP antibody, the detection of phosphorylation of WTAP was conducted by WTAP-antibody-mediated immunoprecipitation. We conducted immunoprecipitation to pull-down WTAP protein by WTAP antibody, then used antibody against phosphoserine/threonine/tyrosine (pan-p) to detect the phosphorylation level of WTAP. To avoid the misunderstanding, we have modified the description from pan-p to pWTAP (pan-p) in figures and revised the figure legends.

(4) The authors should include overall m⁶A modification levels quantified of GFP^sgRNA and WTAP^sgRNA cells, either by mass spectrometry (preferably) or dot blot.

We thank reviewer for raising these useful suggestions. As we showed in Figure 3F and J-K, the m⁶A modification event and degradation of ISG mRNAs were significantly depleted in WTAP^sgRNA cell lines, indicating that function of WTAP was deficient. Thus, we used the WTAP^sgRNA #2 cell line to perform most of our experiment. Furthermore, we also found 46.4% of global m⁶A modification was decreased in WTAP^sgRNA THP-1 cells than that of control cells with or without IFN-β stimulation (Author response image 4), further validating that level of m⁶A modification was significantly affected in WTAP^sgRNA cells. Taken together, our data confirmed that m⁶A methyltransferase activity was efficiently inhibited in our WTAP^sgRNA cells.

Author response image 4.

Control (GFP^sgRNA) and WTAP^sgRNA #2 THP-1-derived macrophages were treated with 10 ng/mL IFN-β for 4 hours. Global m⁶A level was detected and quantified through ELISA assays. All error bars, mean values ± SEM, P-values were determined by two-way ANOVA test independent biological experiments.

Reviewer #3 (Public review):

Summary:

This study presents a valuable finding on the mechanism used by WTAP to modulate the IFN-β stimulation. It describes the phase transition of WTAP driven by IFN-β-induced dephosphorylation. The evidence supporting the claims of the authors is solid, although major analysis and controls would strengthen the impact of the findings. Additionally, more attention to the figure design and to the text would help the reader to understand the major findings.

Strength:

The key finding is the revelation that WTAP undergoes phase separation during virus infection or IFN-β treatment. The authors conducted a series of precise experiments to uncover the mechanism behind WTAP phase separation and identified the regulatory role of 5 phosphorylation sites. They also succeeded in pinpointing the phosphatase involved.

Weaknesses:

However, as the authors acknowledge, it is already widely known in the field that IFN and viral infection regulate m⁶A mRNAs and ISGs. Therefore, a more detailed discussion could help the reader interpret the obtained findings in light of previous research.

We are grateful for the positive comments and the unbiased advice by the reviewer. To interpret our findings in previous research, we have revised the manuscript carefully and added more detailed discussion on ISG mRNAs m⁶A modification during virus infection or IFN stimulation.

It is well-known that protein concentration drives phase separation events. Similarly, previous studies and some of the figures presented by the authors show an increase in WTAP expression upon IFN treatment. The authors do not discuss the contribution of WTAP expression levels to the phase separation event observed upon IFN treatment. Similarly, METTL3 and METTL14, as well as other proteins of the MTC are upregulated upon IFN treatment. How does the MTC protein concentration contribute to the observed phase separation event?

We thank reviewer for pointing out the importance of the concentration dependent phase transition. Previously, Ge et al. discovered that expression level of WTAP was up-regulated during LPS stimulation, thereby promoting WTAP phase separation ability and m⁶A modification, indicating that WTAP concentration indeed affects the phase separation event. In our article, we have generated the phase diagram with different concentration of recombinant mCherry-WTAP in vitro (Figure 1-figure supplement 1C). For in cells experiments, we constructed the TRE-mCherry-WTAP HeLa cells in which the expression of mCherry-WTAP was induced by doxycycline (Dox) in a dose-dependent manner (Author response image 5A). We detected the LLPS of mCherry-WTAP at different concentrations by increasing the doses of Dox, and found that WTAP automatically underwent LLPS only in an artificially high expression level (Author response image 5B). However, the cells we used to detect the WTAP phase separation in our article was mCherry-WTAP-rescued HeLa cells, in which mCherry-WTAP was introduced in WTAP^sgRNA HeLa cells to stably express mCherry-WTAP. We had adjusted and verified the mCherry-WTAP expression level precisely to make the protein abundance similar to endogenous WTAP in wild type (WT) HeLa cells (Author response image 5C). We also repeated the IFN-β stimulation experiments and found no significant increase of WTAP protein level (Figure 5-figure supplement 1A). These findings indicated the phase separation of WTAP in our article was not artificially induced due to the extremely high protein expression level.

MTC protein expression level was crucial for m⁶A modification during virus infection event. Rubio et al. and Winkler et al. revealed that WTAP, METTL3 and METTL14 were up-regulated after 24 hours of HCMV infection[8,17]. Recently, Ge et al. proposed that WTAP protein was degraded after 12 hours of VSV and HSV stimulation5,18. However, these studies only focused on the virus infection event, how the MTC protein expression change after direct IFN-β stimulation was still unclear. Our study investigated the transition change of WTAP under IFNβ stimulation in a short time, we detected the expression level of MTC proteins within 6 hours of IFN-β treatment, and found no significant enhancement of WTAP, METTL3 or METTL14 protein level and mRNA level (Figure 5-figure supplement 1B and Figure 5-figure supplement 1A;). Our in vitro experiments showed that introducing CFP-METTL3 protein have no significant influence on WTAP phase separation (Figure 4H). Additionally, we performed in cells experiments and found that increased expression of METTL3 had no effect on WTAP phase separation event (Author response image 5D). Taken together, WTAP phase separation can be promoted by dramatically increased concentration of WTAP both in vitro and in cells, but the phase separation of WTAP under IFN-β stimulation in our study was not related with the expression level of MTC proteins.

Author response image 5.

(A) Immunoblot analysis of the expression of mCherry-WTAP in TRE-mCherry-WTAP HeLa cells treated with different doses of doxycycline (Dox). Protein level of mCherry-WTAP was quantified and normalized to β-actin of n=3 independent biological experiments. Results were obtained for three independent biological experiments. (B) Phase separation diagram of mCherry-WTAP in TRE-mCherry-WTAP HeLa cells treated with different doses of Dox were observed through confocal microscopy. Representative images for three independent biological experiments were shown in b while number of WTAP condensates that diameter over 0.4 μm of n=80 cells were counted and shown as medium with interquartile range. Dotted white lines indicated the location of nucleus. Scale bars indicated 10 μm. (C) Immunoblot analysis of the expression of endogenous WTAP in wildtype (WT) HeLa cells and mCherry-WTAP-rescued WTAP^sgRNA HeLa cells. (D) mCherry-WTAP-rescued HeLa cells were transfected with 0, 200 or 400 ng of Flag-METTL3, followed with 10 ng/mL IFN-β for 1 hour or left untreated (UT). Phase separation of mCherry-WTAP was observed through confocal microscopy. The number of WTAP condensates that diameter over 0.4 μm of n = 20 cells were counted through ImageJ and shown. Representative images of n=20 cells were shown. All error bars, mean values ± SD were determined by unpaired two-tailed Student’s t-test of n = 3 independent biological experiments in (A). For (A, C), similar results were obtained for three independent biological experiments.

How is PP4 related to the IFN signaling cascade?

Both reviewer #2 and reviewer #3 raised a similar point on the relationship between PPP4 and IFN signaling. In short, protein phosphatase 4 (PPP4) participates in diverse biologic process, including DDR, cell cycle progression and apoptosis14 and several signaling pathway. Previous research showed that deficiency of PPP4 enhanced IFN-β downstream signaling and ISGs expression, which was consistent with our findings that knockdown of PPP4C impaired WTAP-mediated m⁶A modification, and enhanced the ISGs expression[15,16]. Since there was no significant enhancement in PPP4C expression level during 0-3 hours of IFN-β stimulation in our results, we tried to explore the post-translation modification which may influence the protein-protein interaction, such as ubiquitination. Intriguingly, we found the ubiquitination level of PPP4 was enhanced after IFN-β stimulation, which may affect the interaction between PPP4 and WTAP (Author response image 4). Investigation between PPP4 and WTAP will be conducted in our further study (also see minor points 1 of reviewer#2).

In general, it is very confusing to talk about WTAP KO as WTAPgRNA.

As we describe above, all WTAP-deficient THP-1 cells were generated using the CRISPR-Cas9 system with WTAP-specific sgRNA, and used bulk cells instead of the monoclonal knockout cell for further experiments. Since monoclonal knockout cells were not obtained, we refer it as WTAP^sgRNA THP-1 cells rather than WTAP-KO THP-1 cells. We confirmed that WTAP expression was efficiently knocked down in WTAP^sgRNA THP-1 cells, and the m⁶A modification level was significantly impaired (Figure 3I, Figure 3-figure supplement 1A and Author response image 4), which was suitable for mechanism investigation.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Related to the points raised in 'weaknesses' above, if the authors want to claim that this mechanism is reliant on WTAP phase-separated states, additional controls should be done to demonstrate this. Based on the available data it seems that it is just as likely that the phosphorylation state of WTAP is mediating interactions with other factors and/or altering its subcellular localization, which may or may not be related to phase separation.

We are grateful for the constructive suggestions. As we showed in , Figure 5-figure supplement 1H; Author response image 1 along with the explanation above, 5% hex dispersed the phase separation condensates of WTAP without affecting its phosphorylation status, proving the interaction between STAT1 and methylation complex impaired by hex was depended on WTAP LLPS but not its phosphorylation status (Figure 5E-H). To further confirmed the recruitment of WTAP LLPS on ISG promoter region, we performed the immunoprecipitation and ChIP-qPCR experiments of wild type (WT) WTAP, 5ST-D and 5ST-A rescued THP-1 cells. Our results uncovered the interaction between de-phosphorylated-mimic WTAP mutant and STAT1, and its binding ability with ISG promoter regions were depleted by hex without affecting its phosphorylation status (Author response image 2, Figure 5-figure supplement 1 F, Figure 6E). Taken together, we identified the de-phosphorylation event that regulated phase transition of WTAP during IFN-β stimulation, and proposed that LLPS of WTAP mediated by dephosphorylation was the key mechanism to bind with STAT1 and mediate the m⁶A modification on ISG mRNAs.

Reviewer #2 (Recommendations for the authors):

The author order is different for the main text and the supplementary file.

Thank you for pointing out this mistake. We have corrected it in our revised version.

Reviewer #3 (Recommendations for the authors):

Signaling molecules? Do you mean RNA or protein post-translational modification?

Thank you for pointing out this problem. In this sentence, we mean the post-translational modification of signaling proteins. We have corrected this mistake in our revised version.

Line 145: Do you mean Figure 1C?

We have corrected it in our revised version.

Line 214: Are the cells KO for WTAP? Do you mean CRISPR KO? In general, it is easier to present WTAPgRNA as WTAPKO.

Thank you for the constructive suggestion. As we explained above, in this project, all WTAP-deficient THP-1 cells were generated using the CRISPR-Cas9 system with WTAP-specific sgRNA, and used bulk cells instead of the monoclonal knockout cells. We confirmed that WTAP expression was efficiently knocked down in WTAP^sgRNA THP-1 cells, and the m⁶A modification level was significantly impaired (Figure 3I, Figure3-figure supplement 1A and Author response image 4). Since monoclonal knockout cells were not obtained, we refer it as WTAP^sgRNA THP-1 cells rather than WTAP-KO THP-1 cells.

Line 221: WTAP KO has no effect on the expression level of transcription factors?

Thank you for pointing out the uncritical expression. We have corrected this in our revised version.

Figure 3C: I would suggest removing the tracks and showing the expression levels in TPMs.

According to the reviewer’s suggestion, we have analyzed the results and showed the ISGs expression levels in fold change of TPMs (Figure 3D).

Figure 4C: It seems that the IP efficiency from METTL3 is lower in WTAP KO cells. That may impact the author's conclusions.

We have repeated the immunoprecipitation experiments of METTL3 and confirmed the immunoprecipitation (IP) efficiency from METTL3 had no difference between WTAP^sgRNA cells and the control cells (Figure 5C).

I would suggest performing an IP of WTAP with the 5StoA mutation to confirm the missing interaction with WTAP.

According to the reviewer’s suggestion, we investigated the interaction between STAT1 and WTAP in WT cells and WTAP 5ST-A-rescued THP-1 cells. Our results showed that interaction between STAT1, METTL3 and WTAP were enhanced with WTAP 5ST-A mutation, which was depleted by hex treatment (Figure 5-figure supplement 1E). Thus, the interaction of WTAP WT or 5ST-A with the promoter regions of ISG were attenuated by WTAP LLPS dissolution (Figure 6E). Taken together, the interaction between STAT1 and MTC were relied on LLPS of WTAP.

In the graphical abstract, it is confusing to represent WTAP as a line. All other proteins are presented as circles. It is easy to confuse WTAP protein with an RNA. Additionally, m⁶A is too big in size. It should be smaller than a protein.

We thank the reviewer for raising this suggestion. We have modified the graphical abstract to avoid the confusion in our revised version (Figure 6F).

References

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The model of phosphotransfer from Y169 IKK to S32 IkBa is compelling and an important new contribution to the field. In fact, this model will not be without controversy, and publishing the work will catalyze follow-up studies for this kinase and others as well. As such, I am supportive of this paper, though I do also suggest some shortening and modification.

We appreciate the reviewers candid response on the difficulty of this study and the requirement of follow-up studies to confirm a direct transfer of the phosphate. We also have edited the manuscript to make it shorter.

Generally, the paper is well written, but several figures should be quantified, and experimental reproducibility is not always clear. The first 4 figures are slow-going and could be condensed to show the key points, so that the reader gets to Figures 6 and 7 which contain the "meat" of the paper.

We have indicated the experimental reproducibility in the methodology section against each assay. We have shortened the manuscript corresponding to sections describing figures 1-4. However, when we talked to some of our colleagues whose expertise do not align with kinases and IKK, we realized that some description were necessary to introduce them to the next figures. Additionally, we added Fig. S6 indicating that the radiolabelled phospho-IKK2 Y169F is unable to transfer its own phosphate group(s) to the substrate IkBa.

Reviewer #2 (Public Review):

Phosphorylation of IκBα is observed after ATP removal, although there are ambiguous requirements for ADP.

We agree with the reviewer that this observation is puzzling. We hypothesize that ADP is simultaneously regulating the transfer process likely through binding to the active site.

It seems that the analysis hinges on the fidelity of pan-specific phosphotyrosine antibodies.

We agree with the reviewer. To bolster our conclusion, we used antibodies from two different sources. These were Monoclonal mouse anti-Phospho-Tyrosine (catalogue number: 610000) was from BD Biosciences or from EMD Millipore (catalogue no. 05-321X).

The analysis often returns to the notion that tyrosine phosphorylation(s) (and critical active site Lys44) dictate IKK2 substrate specificity, but evidence for this seems diffuse and indirect. This is an especially difficult claim to make with in vitro assays, omitting the context of other cellular specificity determinants (e.g., localization, scaffolding, phosphatases).

We agree with the concerns that the specificity could be dependent on other cellular specificity determinants and toned down our claims where necessary. However, we would like to point out that the specificity of IKK2 towards S32 and S36 of IkBa in cells in response to specific stimuli is well-established. It is also well-established that its non-catalytic scaffolding partner NEMO is critical in selectively bringing IkBa to IKK from a large pool of proteins. The exact mechanism of how IKK2 choose the two serines amongst many others in the substrate is not clear.

Multiple phosphorylated tyrosines in IKK2 were apparently identified by mass spectrometric analyses, but the data and methods are not described. It is common to find non-physiological post-translational modifications in over-expressed proteins from recombinant sources. Are these IKK2 phosphotyrosines evident by MS in IKK2 immunoprecipitated from TNFa-stimulated cells? Identifying IKK2 phosphotyrosine sites from cells would be especially helpful in supporting the proposed model.

Mass spectrometric data for identification of phosphotyrosines from purified IKK2 is now incorporated (Figure S3A). Although we have not analyzed IKK2 from TNF-a treated cells in this study, a different study of phospho-status of cellular IKK2 indicated tyrosine phosphorylation (Meyer et al 2013).

Reviewer #3 (Public Review):

The identity and purity of the used proteins is not clear. Since the findings are so unexpected and potentially of wide-reaching interest - this is a weakness. Similar specific detection of phospho-Ser/Thr vs phospho-Tyr relies largely on antibodies which can have varying degrees of specificity.

We followed a stringent purification protocol of several steps (optimized for the successful crystallization of the IKK2) that removed most impurities (PMID: 23776406, PMID: 39227404). The samples analysed with ESI MS did not show any significant contaminating kinase from the Sf9 cells.

Sequence specific phospho-antibodies used in this study are very well characterized and have been used in the field for years (Basak et al 2007, PMID: 17254973). We agree on the reviewer’s concerns on the pan-specific phospho-antibodies. Since phospho-tyrosine detection is the crucial aspect of this study, we minimized such bias by using pan-specific phosphotyrosine antibodies from two independent sources.

Reviewer #1 (Recommendations For The Authors):

I understand that Figure 3 shows that K44M abolishes both S32/26 phosphorylation and tyrosine phosphorylation, but not PEST region phosphorylation. This suggests that autophosphorylation is reflective of its known specific biological role in signal transduction. But I do not understand why "these results strongly suggest that IKK2-autophosphorylation is critical for its substrate specificity". That statement would be supported by a mutant that no longer autophosphorylates, and as a result shows a loss of substrate specificity, i.e. phosphorylates non-specific residues more strongly. Is that the case? Maybe Darwech et al 2010 or Meyer et al 2013 showed this.

Later figures seem to address this point, so maybe this conclusion should be stated later in the paper.

We have now clarified this in the manuscript and moved the comment to the next section. We have consolidated the results in Figure 3 and 4 in the previous version into a single figure in Figure. The text has also been modified accordingly.

Page 10: mentions DFG+1 without a proper introduction. The Chen et al 2014 paper appears to inform the author's interest in Y169 phosphorylation, or is it just an additional interesting finding? Does this publication belong in the Introduction or the Discussion?

The position of Y169 at the DFG+1 was intriguing and the 2014 article Chen et al further bolstered our interest in this residue to be investigated. We think this publication is important in both sections. 

To understand the significance of Figure 4D, we need a WT IKK2 control: or is there prior literature to cite? This is relevant to the conclusion that Y169 phosphorylation is particularly important for S32 phosphorylation.

We have now added a new supplementary figure where activities of WT and Y169F IKK2 towards WT and S32/S36 mutants are compared (Figure S3F). At a similar concentration, the activity of WT-IKK2 is many fold higher than that of YtoF mutants (Fig. 4C). The experiments were performed simultaneously, although samples were loaded on different gels but otherwise processed in a similar way. The corresponding data is now included in the manuscript as Figure S3F.

The cold ATP quenching experiment is nice for testing the model that Y169 functions as a phospho sink that allows for a transfer reaction. However, there is only a single timepoint and condition, which does not allow for a quantitative analysis. Furthermore, a positive control would make this experiment more compelling, and Y169F mutant should show that cold ATP quenching reduces the phosphorylation of IkBa.

We thank the reviewer for appreciating our experimental design, and pointing out the concerns. We kept the ATP-time point as the maximum of the non-competition experiment. Also, we took 50mM ATP to compare its competition with highest concentration of ADP used. The idea behind using the maximum time and ATP (comparable to ADP) was to capture the effect of competitive-effect of ATP, if any, that would be maximal in the given assay condition in comparison with the phospho-transfer set up in absence of cold ATP. We agree that finer ranges of ATP concentration and time points would have enabled more quantitative analyses. We have now included data where different time intervals are tested (Figure S5D).

Why is the EE mutant recognized by anti-phospho-serine antibodies? In Figure 2F.

We anticipate Serine residues besides those in the activation loop to be phosphorylated when IKK2 is overexpressed and purified from the Sf9 cells. Since Glu (E) mimics phospho-Ser, the said antibody cross reacts with the IKK2-EE that mimics IKK2 phosphorylated at Ser177 and 181.

Figure 7B is clear, but 7C does not add much.

We have now removed the Fig. 7C in the current version. Figure 7 is now renumbered as Figure 6 that does not contain the said cartoon.  

Reviewer #2 (Recommendations For The Authors):

Regarding the specificity arguments (see above in public review), the authors note that NEMO is very important in IKK specificity, and - if I'm understanding correctly - most of these assays were performed without NEMO. Would the IKK2-NEMO complex change these conclusions?

NEMO is a scaffolding protein whose action goes beyond the activation of the IKK-complex. In cells, NEMO brings IkBa from a pool of thousands of proteins to its bonafide kinase when the cells encounter specific signals. In other words, NEMO channels IKK-activity towards its bonafide substrate IkBa at that moment. Though direct proof is lacking, it is likely that NEMO present IkBa in the correct pose to IKK such that the S32/S36 region of IkBa is poised for phosphorylation. The proposed mechanism in the current study further ensures the specificity and fidelity of that phosphorylation event. We believe this mechanism will be preserved in the IKK-NEMO complex unless proven otherwise. As shown below, IKK2 undergoes tyrosine autophosphorylation in presence of NEMO.

Author response image 1.

The work primarily focuses on Y169 as a candidate target for IKK autophosphorylation. This seems reasonable given the proximity to the ATP gamma phosphate. However, Y188F more potently disrupted IκBα phosphorylation. The authors note that this could be due to folding perturbations, but this caveat would also apply to Y169F. A test for global fold perturbations for both Tyr mutants would be helpful.

Y188 is conserved in S/T kinases and that in PKA (Y204) has been studied extensively using structural, biochemical and biophysical tools. It was found in case of PKA that Y204 participates in packing of the hydrophobic core of the large lobe. Disruption of this core structure by mutation allosterically affect the activity of the kinase. We also observed similar engagement of Y188 in IKK2’s large lobe, and speculated folding perturbations in analogy with the experimental evidence observed in PKA. What we meant was mutation of Y188 would allosterically affect the kinase activity. Y169 on the other hand is unique at that position, an no experimental evidence on the effect of phospho-ablative mutation of this residue exist in the literature. Hence, we refrained from speculating its effect on the folding or conformational allostery, however, such a possibility cannot be ruled out. 

I struggled to follow the rationalization of the results of Figure 4D, the series of phosphorylation tests of Y169F against IκBα with combinations of phosphoablative or phosphomimetic variants at Ser32 and Ser36. This experiment is hard to interpret without a direct comparison to WT IKK2.

We agree with the reviewer’s concerns. Through this experiment we wanted to inform about the importance of Tyr-phosphorylation of IKK2 in phosphorylating S32 of IκBα which is of vital importance in NF-kB signaling. We have now provided a comparison with WT-IKK2 in the supplementary Figure S3F. We hope this will help bring more clarity to the issue.

MD simulations were performed to compare structures of unphosphorylated vs. Ser-phosphorylated (p-IKK2) vs. Ser+Tyr-phosphorylated (P-IKK2) forms of IKK2. These simulations were performed without ATP bound, and then a representative pose was subject to ADP or ATP docking. The authors note distortions in the simulated P-IKK2 kinase fold and clashes with ATP docking. Given the high cellular concentration of ATP, it seems more logical to approach the MD with the assumption of nucleotide availability. Most kinase domains are highly dynamic in the absence of substrate. Is it possible that the P-IKK2 poses are a result of simulation in a non-physiological absence of bound ATP? Ultimately, this MD observation is linked to the proposed model where ADP-binding is required for efficient phospho-relay to IκBα. Therefore, this observation warrants scrutiny. Perhaps the authors could follow up with binding experiments to directly test whether P-IKK2 binds ADP and fails to bind ATP.

We thank that reviewer for bringing up this issue. This is an important issue and we must agree that we don’t fully understand it yet. We took more rigorous approach this time where we used three docking programs: ATP and ADP were docked to the kinase structures using LeDock and GOLD followed by rescoring with AutoDock Vina. We found that ATP is highly unfavourable to P-IKK2 compared to ADP. To further address these issues, we performed detailed MM-PBSA (Molecular Mechanics Poisson-Boltzmann Surface Area) analyses after MD-simulation to estimate binding free energies and affinities of ADP and ATP for each of the three differently phosphorylated states of IKK2. These analyses (Figure S4 E and F) clearly indicate that phosphorylated IKK2 have much higher preference for ADP over ATP. However, it does not negate ATP-binding by P-IKK2 in a different pose that may not support kinase activity.

We could not perform any binding experiment because of the following reason. We incubated FL IKK2 WT with or without cold ATP for 30mins, and then incubated these samples with ³²P-ATP and analysed the samples by autoradiography after resolving them on a 10% SDS-PAGE. We found that even after pre-incubation of the kinase with excess cold ATP it still underwent autophosphorylation when radioactive ATP was added as shown below. This prevented us from doing direct binding experiment with ATP as it would not represent true binding event. We also noticed that after removal of bulk ATP post autophosphorylation, phosphorylated IKK2 is capable of further autophosphorylation when freshly incubated with ATP. We have not been able to come up with a condition that would only account for binding of ATP and not hydrolysis. 

Author response image 2.

The authors could comment on whether robust phosphorylation of NEMO was expected (Figure 1D). On a related note, why is NEMO a single band in the 1D left panel and double bands on the right?

No, we did not expect robust phosphorylation of NEMO. However, robust phosphorylation of NEMO is observed only in the absence of IκBα. In presence of IκBα, phosphorylation of NEMO goes down drastically. These were two different preparations of NEMO. When TEV-digestion to remove His-tag is incomplete it gives two bands as the tagged and untagged versions cannot be separated in size exclusion chromatography which is the final step.

Page 14, line 360. "...observed phosphorylation of tyrosine residue(s) only upon fresh ATP-treatment..." I'm not sure I understand the wording here (or the relevance of the citation). Is this a comment on unreported data demonstrating the rapid hydrolysis of the putative phosphotyrosine(s)? If so, that would be helpful to clarify and report in the supporting information.

In our X-ray crystallographic studies with phosphorylated IKK2 we failed to observe any density of phosphate moiety. Furthermore, this IKK2 showed further autophosphorylation when incubated with fresh ATP. These two observations lead us to believe that some of the autophosphorylation are transient in nature. However, quantitative kinetic analyses of this dephosphorylation have not been performed.

Figure S3 middle panel: The PKA substrate overlaid on the IKK2 seems sterically implausible for protein substrate docking. Is that just a consequence of the viewing angle? On a related note, Figure S3 may be mislabeled as S4 in the main text).

It is a consequence of the viewing angle. Also, we apologize for this inadvertent mislabelling. It has been corrected in the current version.

Reviewer #3 (Recommendations For The Authors):

The detection of phosphorylated amino acids relies largely on antibodies which can have a varying degree of specificity. An alternative detection mode of the phospho-amino acids for example by MS would strengthen the evidence.

We agree with the concern of specificity bias of antibodies. We tried to minimize such bias by using two different p-Tyr antibodies as noted previously and also in the methodology section. We were also able to detect phospho-tyrosine residues by MS/MS analyses, representative spectra are now added (Figure S3A).

IKK2 purity - protocol states "desired purity". What was the actual purity and how was it checked? MS would be useful to check for the presence of other kinases.

Purity of the recombinantly purified IKK2s are routinely checked by silver staining. A representative silver stained SDS-PAGE is shown (Figure S1C). It may be noted that, there’s a direct correlation of expression level and solubility, and hence purification yield and quality with the activity of the kinase. Active IKK2s express at much higher level and yields cleaner prep. In our experience, inactive IKKs like K44M give rise to poor yield and purity. We analysed K44M by LC MS/MS to identify other proteins present in the sample. We did not find any significant contaminant kinase the sample (Figure S1D). The MS/MS result is attached.

Figure 1C&D: where are the Mw markers? What is the size of the band? What is the MS evidence for tyrosine phosphorylation?

We have now indicated MW marker positions on these figures.

MS/MS scan data for the two peptides containing pTyr169 and pTyr188 are shown separately (Figure S3A).

Figure 2F: Why is fresh ATP necessary? Why was Tyr not already phosphorylated? The kinetics of this process appear to be unusual when the reaction runs to completion within 5 minutes ?

As stated earlier, we believe some of the autophosphorylation are transient in nature. We think the Tyr-phosphorylation are lost due to the action of cellular phosphatases. We agree with the concern of the reviewer that, the reaction appears to reach completion within 5 minutes in Fig 2F. We believe it is probably due to the fact that the amount of kinase used in this study exceeds the linear portion of the dynamic range of the antibody used. Lower concentration of the kinase do show that reaction does not reach completion until 60mins as shown in Fig. 2A.

Figure 3: Can the authors exclude contamination with a Tyr kinase in the IKK2-K44M prep? The LC/MS/MS data should be included.

We have reanalysed the sample on orbitrap to check if there’s any Tyr-kinase or any other kinase contamination. We used Spodoptera frugiperda proteome available on the Uniprot website for this analysis. These analyses confirmed that there’s no significant kinase contaminant present in the fraction (Figure S1D).

What is the specificity of IKK-2 Inhibitor VII? Could it inhibit a contaminant kinase?

This inhibitor is highly potent against IKK2 and the IKK-complex, and to a lesser extent to IKK1. No literature is available on its activity on other kinases. In an unrelated study, this compound was used alongside MAPK inhibitor SB202190 wherein they observed completely different outcomes of these two inhibitors (Matou-Nasri S, Najdi M, AlSaud NA, Alhaidan Y, Al-Eidi H, Alatar G, et al. (2022) Blockade of p38 MAPK overcomes AML stem cell line KG1a resistance to 5-Fluorouridine and the impact on miRNA profiling. PLoS ONE 17(5):e0267855. https://doi.org/10.1371/journal.pone.0267855). This study indirectly proves that IKK inhibitor VII does not fiddle with the MAPK pathways. We have not found any literature on the non-specific activity of this inhibitor.

Figure 6B: the band corresponding to "p-IkBa" appears to be similar in the presence of ADP (lanes 4-7) or in the absence of ADP but the presence of ATP (lane 8).

Radioactive p-IκBα level is more when ADP is added than in absence of ADP. In presence of cold ATP, radioactive p-IκBα level remains unchanged. This result strongly indicate that the addition of phosphate group to IκBα happens directly from the radioactively labelled kinase that is not competed out by the cold ATP.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, the authors engineer the endogenous left boundary of the Drosophila eve TAD, replacing the endogenous Nhomie boundary by either a neutral DNA, a wildtype Nhomie boundary, an inverted Nhomie boundary, or a second copy of the Homie boundary. They perform Micro-C on young embryos and conclude that endogenous Nhomie and Homie boundaries flanking eve pair with head-to-tail directionality to form a chromosomal stem loop. Abrogating the Nhomie boundary leads to ectopic activation of genes in the former neighboring TAD by eve embryonic stripe enhancers. Replacing Nhomie by an inverted version or by Homie (which pairs with itself head-to-head) transformed the stem loop into a circle loop. An important finding was that stem and circle loops differentially impact endogenous gene regulation both within the eve TAD and in the TADs bracketing eve. Intriguingly, an eve TAD with a circle loop configuration leads to ectopic activation of flanking genes by eve enhancers - indicating compromised regulatory boundary activity despite the presence of an eve TAD with intact left and right boundaries.

Strengths:

Overall, the results obtained are of high-quality and are meticulously discussed. This work advances our fundamental understanding of how 3D genome topologies affect enhancer-promoter communication.

Weaknesses:

Though convincingly demonstrated at eve, the generalizability of TAD formation by directional boundary pairing remains unclear, though the authors propose this mechanism could underly the formation of all TADs in Drosophila and possibly even in mammals. Strong and ample evidence has been obtained to date that cohesin-mediated chromosomal loop extrusion explains the formation of a large fraction of TADs in mammals. 

(1.1) The difficultly with most all of the studies on mammal TADs, cohesin and CTCF roadblocks is that the sequencing depth is not sufficient, and large bin sizes (>1 kb) are needed to visualize chromosome architecture.  The resulting contact profiles show TAD neighborhoods, not actual TADs.

The problem with these studies is illustrated by comparing the contact profiles of mammalian MicroC data sets at different bin sizes in Author response image 1.  In this figure, the darkness of the “pixels” in panels E, F, G and H was enhanced by reducing brightness in photoshop.

Author response image 1.

Mammalian MicroC profiles different bun sizes

Panels A and C show “TADs” using bin sizes typical of most mammalian studies (see Krietenstein et al. (2023) (Krietenstein et al. 2020)).  At this level of resolution, TADs, the “trees” that are the building blocks of chromosomes, are not visible.  Instead, what is seen are TAD neighborhoods or “forests”.  Each neighborhood consists of several dozen individual TADs.  The large bins in these panels also artificially accentuated TAD:TAD interactions, generating a series of “stripes” and “dots” that correspond to TADs bumping into each other and sequences getting crosslinked.  For example, in panel A there is prominent stripe on the edge of a “TAD” (blue arrow).  In panel C, this stripe resolves into a series of dots arranged as parallel, but interrupted “stripes” (green and blue arrows).  At the next level of resolution, it can be seen that the stripe marked by the blue arrow and magenta asterisk is generated by contacts between the left boundary of the TAD indicated by the magenta bar with sequences in a TAD (blue bar) ~180 kb way.  While dots and stripes are prominent features in contact profiles visualized with larger bin sizes (A and C), the actual TADs that are observed with a bin size of 200 bp (examples are underlined by black bars in panel G) are not bordered by stripes, nor are they topped by obvious dots.  The one possible exception is the dot that appears at the top of the volcano triangle underlined with magenta.

The chromosome 1 DNA segment from the MicroC data of Hseih et al. (2023) (Hsieh et al. 2020) shows a putative volcano triangle with a plume (indicated by a V in Author response image 1 panels D, F and H).  Sequences in the V TAD don’t crosslink with their immediate neighbors, and this gives a “plume” above the volcano triangle, as indicate by the light blue asterisk in panels D, F and H.  Interestingly the V TAD does contact two distant TADs, U on the left and W on the right. The U TAD is ~550 kb from V, and the region of contact is indicated by the black arrow.  The W TAD is ~585 kb from V, and the region of contact is indicated by the magenta arrow.  While the plume still seems to be visible with a bin size of 400 bp (light blue asterisk), it is hard to discern when the bin size is 200 bp, as there are not enough reads.

The evidence demonstrating that cohesin is required for TAD formation/maintenance is based on low resolution Hi-C data, and the effects that are observed are on TAD neighborhoods (forests) and not TADs (trees).  In fact, there is published evidence that cohesin is not required in mammals for TAD formation/maintenance.  In an experiment from Goel et al. 2023 the authors depleted the cohesin component Rad21 and then visualized the effects on TAD organization using the high resolution region capture MicroC (RCMC) protocol.  The MicroC contact map in this figure visualizes a ~250 kb DNA segment around the Ppm1pg locus at 250 bp resolution.  On the right side of the diagonal is the untreated control, while the left side shows the MicroC profile of the same region after Rad21 depletion.  The authors indicated that there was a 97% depletion of Rad21 in their experiment.  However, as is evident from a comparison of the experimental and control, loss of Rad21 has no apparent effect on the TAD organization of this mammalian DNA segment.

Several other features are worth noting.  First, unlike the MicroC experiments shown in Author response image 1, there are dots at the apex of the TADs in this chromosomal segment.  In the MicroC protocol, fixed chromatin is digested to mononucleosomes by extensive MNase digestion.  The resulting DNA fragments are then ligated, and dinucleosome-length fragments are isolated and sequenced. 

DNA sequences that are nucleosome free in chromatin (which would be promoters, enhancers, silencers and boundary elements) are typically digested to oligonucleotides in this procedure and won’t be recovered. This means that the dots shown here must correspond to mononucleosome-length elements that are MNase resistant.  This is also true for the dots in the MicroC contact profiles of the Drosophila Abd-B regulatory domain (see Fig. 2B in the paper).  Second, the TADs are connected to each other by 45o stripes (see blue and green arrowheads).  While it is not clear from this experiment whether the stipes are generated by an active mechanism (enzyme) or by some “passive” mechanism (e.g., sliding), the stripes in this chromosomal segment are not generated by cohesin, as they are unperturbed by Rad21 depletion.  Third, there are no volcano triangles with plumes in this chromosomal DNA segment.  Instead, the contact patterns (purple and green asterisks) between neighboring TADs closely resemble those seen for the Abd-B regulatory domains (compare Goel et al. 2023 with Fig. 2B in the paper).  This similarity suggests that the TADs in and around Ppm1g may be circle-loops, not stem-loops.  As volcano triangles with plumes also seem to be rare in the MicroC data sets of Krietenstein et al. (Krietenstein et al. 2020) and Hesih et al. (Hsieh et al. 2020) (with the caveat that these data sets are low resolution: see Author response image 1), it is possible that much of the mammalian genome is assembled into circle-loop TADs, a topology that can’t be generated by the cohesin loop extrusion (bolo tie clip) /CTCF roadblock model.

While Rad21 depletion has no apparent effect on TADs, it does appear to impact TAD neighborhoods.  This is in a supplemental figure in Goel et al. (Goel et al. 2023).  In this figure, TADs in the Ppm1g region of chromosome 5 are visualized with bin sizes of 5 kb and 1 kb.  A 1.2 Mb DNA segment is shown for the 5 kb bin size, while an 800 kb DNA segment is shown for the 1 kb bin size.  As can be seen from comparing the MicroC profiles in Author response image 2 with that in Goel et al. 2023, individual TADs are not visible.  Instead, the individual TADs are binned into large TAD “neighborhoods” that consist of several dozen or more TADs.

Unlike the individual TADs shown in Goel et al. 2023, the TAD neighborhoods in Author response image 2 are sensitive to Rad21 depletion.  The effects of Rad21 depletion can be seen by comparing the relative pixel density inside the blue lines before (above the diagonal) and after (below the diagonal) auxin-induced Rad21 degradation.  The reduction in pixel density is greatest for more distant TAD:TAD contacts (farthest from the diagonal).  By contrast, the TADs themselves are unaffected (Goel et al. 2023), as are contacts between individual TADs and their immediate neighbors.  In addition, contacts between partially overlapping TAD neighborhoods are also lost.  At this point it isn’t clear why contacts between distant TADs in the same neighborhood are lost when Rad21 is depleted; however, a plausible speculation is that it is related to the functioning of cohesin in holding newly replicated DNAs together until mitosis and whatever other role it might have in chromosome condensation.

Author response image 2.

Ppm1g full locus chr5

Moreover, given the unique specificity with which Nhomie and Homie are known to pair (and exhibit "homing" activity), it is conceivable that formation of the eve TAD by boundary pairing represents a phenomenon observed at exceptional loci rather than a universal rule of TAD formation. Indeed, characteristic Micro-C features of the eve TAD are only observed at a restricted number of loci in the fly genome…..

(1.2) The available evidence does not support the claim that nhomie and homie are “exceptional.”  To begin with, nhomie and homie rely on precisely the same set of factors that have been implicated in the functioning of other boundaries in the fly genome.  For example, homie requires (among other factors) the generic boundary protein Su(Hw) for insulation and long-distance interactions (Fujioka et al. 2024).  (This is also true of nhomie: unpublished data.)  The Su(Hw) protein (like other fly polydactyl zinc finger proteins) can engage in distant interactions.  This was first shown by Sigrist and Pirrotta (Sigrist and Pirrotta 1997), who found that the su(Hw) element from the gypsy transposon can mediate long-distance regulatory interactions (PRE dependent silencing) between transgenes inserted at different sites on homologous chromosomes (trans interactions) and at sites on different chromosomes.

The ability to mediate long-distance interactions is not unique to the su(Hw) element, or homie and nhomie.  Muller et al. (Muller et al. 1999) found that the Mcp boundary from the Drosophila BX-C is also able to engage in long-distance regulatory interactions—both PRE-dependent silencing of mini-white and enhancer activation of mini-white and yellow.  The functioning of the Mcp boundary depends upon two other generic insulator proteins, Pita and the fly CTCF homolog (Kyrchanova et al. 2017).  Like Su(Hw) both are polydactyl zinc finger proteins, and they resemble the mammalian CTCF protein in that their N-terminal domain mediates multimerization (Bonchuk et al. 2020; Zolotarev et al. 2016).  Figure 6 from Muller et el. 1999 shows PRE-dependent “pairing sensitive silencing” interactions between transgenes carrying a mini-white reporter, the Mcp and scs’ (Beaf dependent)(Hart et al. 1997) boundary elements, and a PRE closely linked to Mcp.  In this experiment flies homozygous for different transgene inserts were mated and the eye color was examined in their transheterozygous progeny.  As indicated in the figure, the strongest trans-silencing interactions were observed for inserts on the same chromosomal arm; however, transgenes inserted on the left arm of chromosome 3 can interact across the centromere with transgenes inserted on the right arm of chromosome 3. 

Figure 5C (left) from Muller et el. 1999 shows a trans-silencing interaction between w#11.102 at 84D and w#11.16 approximately 5.8 Mb away, at 87D.  Figure 5C (right) shows a trans-silencing interaction across the centromere between w#14.29 on the left arm of chromosome 3 at 78F and w#11.102 on the right arm of chromosome 3 at 84D. The eye color phenotype of mini-white-containing transgenes is usually additive: homozygyous inserts have twice as dark eye color as the corresponding hemizygous inserts.  Likewise, in flies trans-_heterozygous for _mini-white transgenes inserted at different sites, the eye color is equivalent to the sum of the two transgenes.  This is not true when mini-white transgenes are silenced by PREs.  In the combination shown in panel A, the t_rans-_heterozygous fly has a lighter eye color than either of the parents.  In the combination in panel B, the _trans-_heterozygous fly is slightly lighter than either parent.

As evident from the diagram in Figure 6 from Muller et el. 1999, all of the transgenes inserted on the 3rd chromosome that were tested were able to participate in long distance (>Mbs) regulatory interactions.  On the other hand, not all possible pairwise interactions are observed.  This would suggest that potential interactions depend upon the large scale (Mb) 3D folding of the 3rd chromosome.

When the scs boundary (Zw5 dependent) (Gaszner et al. 1999) was added to the transgene to give sMws’, it further enhanced the ability of distant transgenes to find each other and pair.  All eight of the sMws’ inserts that were tested were able to interact with at least one other sMws’ insert on a different chromosome and silence mini-white.  Vazquez et al. () subsequently tagged the sMws’ transgene with LacO sequences (ps0Mws’) and visualized pairing interactions in imaginal discs.  Trans-heterozygous combinations on the same chromosome were found paired in 94-99% of the disc nuclei, while a trans-heterozygous combination on different chromosomes was found paired in 96% of the nuclei (Table 3 from Vazquez et al. 2006).  Vazquez et al. also examined a combination of four transgenes inserted on the same chromosome (two at the same insertion site, and two at different insertion sites).  In this case, all four transgenes were clustered together in 94% of the nuclei (Table 3 from Vazquez et al. 2006).  Their studies also suggest that the distant transgenes remain paired for at least several hours.  A similar experiment was done by Li et al. (Li et al. 2011), except that the transgene contained only a single boundary, Mcp or Fab-7.  While pairing was still observed in trans-heterozygotes, the frequency was reduced without scs and scs’.

It is worth pointing out that there is no plausible mechanism in which cohesin could extrude a loop through hundreds of intervening TADs, across the centromere (ff#13.101_ßà_w#11.102: Figure 6 from Muller et el. 1999; w#14.29_ßà_w#11.02: Figure 6 from Muller et el. 1999 and 5) and come to a halt when it “encounters” Mcp containing transgenes on different homologs.  The same is true for Mcp-dependent pairing interactions in cis (Fig. 7 in Muller et al. (Muller et al. 1999)) or Mcp-dependent pairing interactions between transgenes inserted on different chromosomes (Fig. 8 in Muller et al. (Muller et al. 1999); Line 8 in Table 3 from Vazquez et al. 2006). 

These are not the only boundaries that can engage in long-distance pairing.  Mohana et al. (Mohana et al. 2023) identified nearly 60 meta-loops, many of which appear to be formed by the pairing of TAD boundary elements.  Two examples (at 200 bp resolution from 12-16 hr embryos) are shown in Author response image 3.

Author response image 3.

Metaloops on the 2nd and 3rd chromosomes: circle-loops and multiple stem-loops

One of these meta-loops (panel A) is generated by the pairing of two TAD boundaries on the 2nd chromosome.  The first boundary, blue, (indicated by blue arrow) is located at ~2,006, 500 bp between a small TAD containing the Nplp4 and CG15353 genes and a larger TAD containing 3 genes, CG33543, Obp22a and Npc2a.  Nplp4 encodes a neuropeptide.  The functions of CG15354 and CG33543 are unknown.  Obp22a encodes an odorant binding protein, while Npc2a encodes the Niemann-Pick type C-2a protein which is involved sterol homeostasis.  The other boundary (purple: indicated by purple arrow) is located between two TADs 2.8 Mb away at 4,794,250 bp.  The upstream TAD contains the fipi gene (CG15630) which has neuronal functions in male courtship, while the downstream TAD contains CG3294, which is thought to be a spliceosome component, and schlaff (slf) which encodes a chitin binding protein.  As illustrated in the accompanying diagram, the blue boundary pairs with the purple boundary in a head-to-head orientation, generating a ~2.8 Mb loop with a circle-loop topology.  As a result of this pairing, the multi-gene (CG33543, Obp22a and Npc2a) TAD upstream of the blue boundary interacts with the CG15630 TAD upstream of the purple boundary.  Conversely the small Nplp4:CG15353 TAD downstream of the blue boundary interacts with the CG3294:slf TAD downstream of the purple boundary.  Even if one imagined that the cohesin bolo tie clip was somehow able to extrude 2.8 Mb of chromatin and then know to stop when it encountered the blue and purple boundaries, it would’ve generated a stemloop, not a circle-loop.

The second meta-loop (panel B) is more complicated as it is generated by pairing interactions between four boundary elements.  The blue boundary (blue arrow) located ~4,801,800 bp (3L) separates a large TAD containing the RhoGEF64C gene from a small TAD containing CG7509, which encodes a predicted subunit of an extracellular carboxypeptidase.  As can be seen in the MicroC contact profile and the accompanying diagram, the blue boundary pairs with the purple boundary (purple arrow) which is located at ~7,013, 500 (3L) just upstream of the 2nd internal promoter (indicated by black arrowhead) of the Mp (Multiplexin) gene.  This pairing interaction is head-to-tail and generates a large stem-loop that spans ~2.2 Mb.  The stem-loop brings sequences upstream of the blue boundary and downstream of the purple boundary into contact (the strings below a bolo tie clip), just as was observed in the boundary bypass experiments of Muravyova et al. (Muravyova et al. 2001) and Kyrchanova et al. (Kyrchanova et al. 2008).  The physical interactions result in a box of contacts (right top) between sequences in the large RhoGEF64C TAD and sequences in a large TAD that contains an internal Mp promoter.  The second pairing interaction is between the brown boundary (brown arrow) and the green boundary (green arrow).  The brown boundary is located at ~4 805,600 bp (3L) and separates the TAD containing CG7590 from a large TAD containing CG1808 (predicted to encode an oxidoreductase) and the Dhc64C (Dynein heavy chain 64C) gene.  The green boundary is located at ~6,995,500 bp (3L), and it separates a TAD containing CG32388 and the biniou (bin) transcription factor from a TAD that contains the most distal promoter of the Mp (Multiplexin) gene (blue arrowhead).  As indicated in the diagram, the brown and green boundaries pair with each other head-to-tail, and this generates a small internal loop (and the final configuration would resemble a bolo tie with two tie clips).  This small internal loop brings the CG7590 TAD into contact with the TAD that extends from the distal Mp promoter to the 2nd internal Mp promoter.  The resulting contact profile is a rectangular box with diagonal endpoints corresponding to the paired blue:purple and brown:green boundaries.  The pairing of the brown:green boundaries also brings the TADs immediately downstream of the brown boundary and upstream of the green boundary into contact with each other, and this gives a rectangular box of interactions between the Dhc64C TAD, and sequences in the bin/CG3238 TAD.  This box is located on the lower left side of the contact map.

Since the bin and Mp meta-loops in Author response image 3B are stem-loops, they could have been generated by “sequential” cohesin loop extrusion events.  Besides the fact that cohesin extrusion of 2 Mb of chromatin and breaking through multiple intervening TAD boundaries challenges the imagination, there is no mechanism in the cohesion loop extrusion/CTCF roadblock model to explain why cohesion complex 1 would come to a halt at the purple boundary on one side and the blue boundary on the other, while cohesin complex 2 would instead stop when it hits the brown and green boundaries.  This highlights another problem with the cohesin loop extrusion/CTCF roadblock model, namely that the roadblocks are functionally autonomous: they have an intrinsic ability to block cohesin that is entirely independent of the intrinsic ability of other roadblocks in the neighborhood.  As a result, there is no mechanism for generating specificity in loop formation.  By contrast, boundary pairing interactions are by definition non-autonomous and depend on the ability of individual boundaries to pair with other boundaries: specificity is built into the model. The mechanism for pairing, and accordingly the basis for partner preferences/specificity, are reasonably well understood.  Probably the most common mechanism in flies is based on shared binding sites for architectural proteins that can form dimers or multimers (Bonchuk et al. 2021; Fedotova et al. 2017).  Flies have a large family of polydactyl zinc finger DNA binding proteins, and as noted above, many of these form dimers or multimers and also function as TAD boundary proteins.  This pairing principle was first discovered by Kyrchanova et al. (Kyrchanova et al. 2008).  This paper also showed that orientation-dependent pairing interactions is a common feature of endogenous fly boundaries.  Another mechanism for pairing is specific protein:protein interactions between different DNA binding factors (Blanton et al. 2003).  Yet a third mechanism would be proteins that bridge different DNA binding proteins together.  The boundaries that use these different mechanisms (BX-C boundaries, scs, scs’) depend upon the same sorts of proteins that are used by homie and nhomie.  Likewise, these same set of factors reappear in one combination or another in most other TAD boundaries.  As for the orientation of pairing interactions, this is most likely determined by the order of binding sites for chromosome architectural proteins in the partner boundaries.

…and many TADs lack focal 3D interactions between their boundaries.

(1.3) The idea that flies differ from mammals in that they “lack” focal 3D interactions is simply mistaken.  One of the problems with drawing this distinction is that most all of the “focal 3D interactions” seen mammalian Hi-C experiments are a consequence of binning large DNA segments in low resolution restriction enzyme-dependent experiments.  This is even true in the two “high” resolution MicroC experiments that have been published (Hsieh et al. 2020; Krietenstein et al. 2020).  As illustrated above in Author response image 1, most of the “focal 3D interactions” (the dots at the apex of TAD triangles) seen with large bin sizes (1 kb and greater) disappear when the bin size is 200 bp and TADs rather than TAD neighborhoods are being visualized.

As described in point #1.1, in the MicroC protocol, fixed chromatin is first digested to mononucloesomes by extensive MNase digestion, processed/biotinylated, and ligated to give dinucleosome-length fragments, which are then sequenced.  Regions of chromatin that are nucleosome free (promoters, enhancers, silencers, boundary elements) will typically be reduced to oligonucleotides in this procedure and will not be recovered when dinucleosome-length fragments are sequenced.  The loss of sequences from typical paired boundary elements is illustrated by the lar meta-loop shown in Author response image 4 (at 200 bp resolution).  Panels A and B show the contact profiles generated when the blue boundary (which separates two TADs that span  the Lar (Leukocyteantigen-related-like) transcription unit interacts with the purple boundary (which separates two TADs in a gene poor region ~620 kb away).  The blue and purple boundaries pair with each other head-to-head, and this pairing orientation generates yet another circle-loop.  In the circle-loop topology, sequences in the TADs upstream of both boundaries come into contact with each other, and this gives the small dark rectangular box to the upper left of the paired boundaries (Author response image 4A).  (Note that this small box corresponds to the two small TADs upstream of the blue and purple boundaries, respectively. See panel B.)  Sequences in the TADs downstream of the two boundaries also come into contact with each other, and this gives the large box to the lower right of the paired boundaries.  While this meta-loop is clearly generated by pairing interactions between the blue and purple boundaries, the interacting sequences are degraded in the MicroC protocol, and sequences corresponding to the blue and purple boundaries aren’t recovered.  This can be seen in panel B (red arrow and red arrowheads).  When a different Hi-C procedure is used (dHS-C) that captures nucleosome-free regions of chromatin that are physically linked to each other (Author response image 4C & D), the sequences in the interacting blue and purple boundaries are recovered and generate a prominent “dot” at their physical intersection (blue arrow in panel D).

Author response image 4.

Lar metaloop. Panels A & bB: MicroC. Panels C & D: dHS-C

While sequences corresponding to the blue and purple boundaries are lost in the MicroC procedure, there is at least one class of elements that engage in physical pairing interactions whose sequences are (comparatively) resistant to MNase digestion.  This class of elements includes many PREs ((Kyrchanova et al. 2018); unpublished data), the boundary bypass elements in the Abd-B region of BX-C (Kyrchanova et al. 2023; Kyrchanova et al. 2019a; Kyrchanova et al. 2019b; Postika et al. 2018), and “tethering” elements (Batut et al. 2022; Li et al. 2023).  In all of the cases tested, these elements are bound in nuclear extracts by a large (>1000 kD) GAGA factor-containing multiprotein complex called LBC.  LBC also binds to the hsp70 and eve promoters (unpublished data).  Indirect end-labeling experiments (Galloni et al. 1993; Samal et al. 1981; Udvardy and Schedl 1984) indicate that the LBC protects a ~120-180 bp DNA segment from MNase digestion.  It is likely that this is the reason why LBC-bound sequences can be recovered in MicroC experiments as dots when they are physically linked to each other.  One such example (based on the ChIP signatures of the paired elements) is indicated by the green arrow in panel B and D of Author response image 4.  Note that there are no dots corresponding to these two LBC elements within either of the TADs immediately downstream of the blue and purple boundaries.  Instead the sequences corresponding to the two LBC elements are only recovered when the two elements pair with each other over a distance of ~620 kb.  The fact that these two elements pair with each other is consistent with other findings which indicate that, like classical boundaries, LBC elements exhibit partner preferences.  In fact, LBC elements can sometimes function as TAD boundaries.  For example, the Fab-7 boundary has two LBC elements, and full Fab-7 boundary function can be reconstituted with just these two elements (Kyrchanova et al. 2018).

Reviewer #2 (Public Review):

"Chromatin Structure II: Stem-loops and circle-loops" by Ke*, Fujioka*, Schedl, and Jaynes reports a set of experiments and subsequent analyses focusing on the role of Drosophila boundary elements in shaping 3D genome structure and regulating gene expression. The authors primarily focus on the region of the fly genome containing the even skipped (eve) gene; eve is expressed in a canonical spatial pattern in fly embryos and its locus is flanked by the well-characterized neighbor of homie (nhomie) and homie boundary elements. The main focus of investigation is the orientation dependence of these boundary elements, which had been observed previously using reporter assays. In this study, the authors use Crispr/Cas9 editing followed by recombination-mediated cassette exchange to create a series of recombinant fly lines in which the nhomie boundary element is either replaced with exongenous sequence from phage 𝝀, an inversion of nhomie, or a copy of homie that has the same orientation as the endogenous homie sequence. The nhomie sequence is also regenerated in its native orientation to control for effects introduced by the transgenesis process.

The authors then perform high-resolution Micro-C to analyze 3D structure and couple this with fluorescent and colorimetric RNA in situ hybridization experiments to measure the expression of eve and nearby genes during different stages of fly development. The major findings of these experiments are that total loss of boundary sequence (replacement with 𝝀 DNA) results in major 3D structure changes and the most prominent observed gene changes, while inversion of the nhomie boundary or replacement with homie resulted in more modest effects in terms of 3D structure and gene expression changes and a distinct pattern of gene expression change from the 𝝀 DNA replacement. As the samples in which the nhomie boundary is inverted or replaced with homie have similar Micro-C profiles at the eve locus and show similar patterns of a spurious gene activation relative to the control, the observed effects appear to be driven by the relative orientation of the nhomie and homie boundary elements to one another.

Collectively, the findings reported in the manuscript are of broad interest to the 3D genome field. Although extensive work has gone into characterizing the patterns of 3D genome organization in a whole host of species, the underlying mechanisms that structure genomes and their functional consequences are still poorly understood. The perhaps best understood system, mechanistically, is the coordinated action of CTCF with the cohesin complex, which in vertebrates appears to shape 3D contact maps through a loop extrusion-pausing mechanism that relies on orientation-dependent sequence elements found at the boundaries of interacting chromatin loops.

(2.1) The notion that mammalian genome is shaped in 3D by the coordinate action of cohesin and CTCF has achieved the status of dogma in the field of chromosome structure in vertebrates.  However, as we have pointed out in #1.1, the evidence supporting this dogma is far from convincing.  To begin with, it is based on low resolution Hi-C experiments that rely on large bin sizes to visualize so-called “TADs.”  In fact, the notion that cohesin/CTCF are responsible on their own for shaping the mammalian 3D genome appears to be a result of mistaking a series of forests for the actual trees that populate each of the forests.

As illustrated in Author response image 1 above, the “TADs” that are visualized in these low resolution data sets are not TADs at all, but rather TAD neighborhoods consisting of several dozen or more individual TADs.  Moreover, the “interesting” features that are evident at low resolution (>1 kb)—the dots and stripes—largely disappear at resolutions appropriate for visualizing individual TADs (~200 bp).

In Goel et al. 2023, we presented data from one of the key experiments in Goel et al. (Goel et al. 2023).  In this experiment,  the authors used RCMC to generate high resolution (~250 bp) MicroC contact maps before and after Rad21 depletion.  Contrary to dogma, Rad21 depletion has absolutely no effect on TADs in a ~250 kb DNA segment—and these TADs look very much like the TADs we observe in the Drosophila genome, in particular in the Abd-B region of BX-C that is thought to be assembled into a series of circle-loops (see Fig. 2B).

While Goel et al. (Goel et al. 2023) observed no effect of Rad21 depletion on TADs, they found that loss of Rad21 disturbs long-distance (but not short-distance) contacts in large TAD neighborhoods when their RCMC data set is visualized using bin sizes of 5 kb and I kb.  This is shown in Author response image 2.  The significance of this finding is, however, uncertain.  It could mean that the 3D organization of large TAD neighborhoods have a special requirement for cohesin activity.  On the other hand, since cohesin functions to hold sister chromosomes together after replication until they separate during mitosis (and might also participate in mitotic condensation), it is also possible that the loss of long-range contacts in large TAD neighborhoods when Rad21 is depleted is simply a reflection of this particular activity.  Further studies will be required to address these possibilities.

As for CTCF: a careful inspection of the ChIP data in Goel et al. 2023 indicates that CTCF is not found at each and every TAD boundary.  In fact, the notion that CTCF is the be-all and end-all of TAD boundaries in mammals is truly hard to fathom.  For one, the demands for specificity in TAD formation (and in regulatory interactions) are likely much greater than those in flies, and specificity can’t be generated by a single DNA binding protein.  For another, several dozen chromosomal architectural proteins have already been identified in flies.  This means that (unlike what is thought to be true in mammals) it is possible to use a combinatorial mechanism to generate specificity in, for example, the long distance interactions in RFig 6 and 7.  As noted in #2.1 above, many of the known chromosomal architectural proteins in flies are polydactyl zinc finger proteins (just like CTCF).  There are some 200 different polydactyl zinc finger proteins in flies, and the function of only a hand full of these is known at present.  However, it seems likely that a reasonable fraction of this class of DNA binding proteins will ultimately turn out to have an architectural function of some type (Bonchuk et al. 2021; Fedotova et al. 2017).  The number of different polydactyl zinc finger protein genes in mammals is nearly 3 times that of flies.  It is really possible that of these, only CTCF is involved in shaping the 3D structure of the mammalian genome?

Despite having a CTCF paralog and cohesin, the Drosophila genome does not appear to be structure by loop extrusion-pausing. The identification of orientation-dependent elements with pronounced structural effects on genome folding thus may shed light on alternative mechanisms used to regulated genome structure, which in turn may yield insights into the significance of particular folding patterns.

(2.2) Here we would like to draw the reviewer’s and reader’s attention to Author response image 3, which shows that orientation-dependent pairing interactions have a significant impact on physical interactions between different sequences.  We would also refer the reader to two other publications.  One of these is Kyrchanova et al. (Kyrchanova et al. 2008), which was the first to demonstrate that orientation of pairing interactions matters.  The second is Fujioka et al. (Fujioka et al. 2016), which describes experiments indicating that nhomie and homie pair with each other head-to-tail and with themselves head-to-head.

On the whole, this study is comprehensive and represents a useful contribution to the 3D genome field. The transgenic lines and Micro-C datasets generated in the course of the work will be valuable resources for the research community. Moreover, the manuscript, while dense in places, is generally clearly written and comprehensive in its description of the work. However, I have a number of comments and critiques of the manuscript, mainly centering on the framing of the experiments and presentation of the Micro-C results and on manner in which the data are analyzed and reported. They are as follows:

Major Points:

(1) The authors motivate much of the introduction and results with hypothetical "stem loop" and "circle loop" models of chromosome confirmation, which they argue are reflected in the Micro-C data and help to explain the observed ISH patterns. While such structures may possibly form, the support for these specific models vs. the many alternatives is not in any way justified. For instance, no consideration is given to important biophysical properties such as persistence length, packing/scaling, and conformational entropy. As the biophysical properties of chromatin are a very trafficked topic both in terms of experimentation and computational modeling and generally considered in the analysis of chromosome conformation data, the study would be strengthened by acknowledgement of this body of work and more direct integration of its findings.

(2.3) The reviewer is not correct in claiming that “stem-loops” and “circle-loops” are “hypothetical.”  There is ample evidence that both types of loops are present in eukaryotic genomes, and that loop conformation has significant readouts in terms of not only the physical properties of TADs but also their functional properties.  Here we would draw the reviewer’s attention to Author response image 3 and Author response image 4 for examples of loops formed by the orientation-dependent pairing of yet other TAD boundary elements.  As evident from the MicroC data in these figures, circle-loops and stem-loops have readily distinguishable contact patterns.  The experiments in Fujioka et al. (Fujioka et al. 2016) demonstrate that homie and nhomie pair with each other head-to-tail, while they pair with themselves head-to-head.  The accompany paper (Bing et al. 2024) also provides evidence that loop topology is reflected both in the pattern of activation of reporters and in the MicroC contact profiles.  We would also mention again Kyrchanova et al. (Kyrchanova et al. 2008), who were the first to report orientation-dependent pairing of endogenous fly boundaries.

At this juncture it would premature to try to incorporate computational modeling of chromosome conformation in our studies.  The reason is that the experimental foundations that would be essential for building accurate models are lacking.  As should be evident from RFigs. 1-3 above, studies on mammalian chromosomes are simply not of high enough resolution to draw firm conclusions about chromosome conformation: in most studies only the forests are visible.  While the situation is better in flies, there are still too many unknown.  As just one example, it would be important to know the orientation of the boundary pairing interactions that generate each TAD.  While it is possible to infer loop topology from how TADs interact with their neighbors (a plume versus clouds), a conclusive identification of stem- and circle-loops will require a method to unambiguously determine whether a TAD boundary pairs with its neighbor head-to-head or headto-tail.

(2) Similar to Point 1, while there is a fair amount of discussion of how the observed results are or are not consistent with loop extrusion, there is no discussion of the biophysical forces that are thought to underly compartmentalization such as block-polymer co-segregation and their potential influence. I found this absence surprising, as it is generally accepted that A/B compartmentalization essentially can explain the contact maps observed in Drosophila and other non-vertebrate eukaryotes (Rowley, ..., Corces 2017; PMID 28826674). The manuscript would be strengthened by consideration of this phenomenon.

(2.4) Compartments in mammals have typically been identified and characterized using lowresolution data sets, and these studies have relied on visualizing compartments using quite large bin sizes (>>1 kb).  Our experiments have nothing to do with the large-scale compartments seen in these Hi-C experiments.  Instead, we are studying the properties of individual TADs: how TADs are formed, the relationship between TAD topology and boundary:boundary pairing, and the impact of TAD topology on interactions between TADs in the immediate neighborhood.  There is no evidence to date that these large compartments or “block polymer co-segregation” have a) any impact on the properties of individual boundary elements, b) have a role in determining which boundary elements actually come together to form a given TAD, c) impact the orientation of the interactions between boundaries that generate the TAD or d) determine how TADs tend to interact with their immediate neighbors.  

In more recent publications (c.f., Harris et al. 2023) compartments have shrunk in size and instead of being units of several hundred kb, the median length of the “compartmental” unit in mammalian cells is about12 kb. This is not too much different from the size of fly TADs.  However, the available evidence does not support the idea that block polymer co-segregation/co-repulsion drive the TAD:TAD interactions seen in MicroC experiments.  For example, according to this “micro-compartment” model, the specific patterns of interaction between TADs in the CG3294 meta-loop in Author response image 3 would be driven by block polymer co-segregation and co-repulsion. In this model, the TAD upstream of the blue boundary (which contains CG33543, the odorant binding protein gene Obp22a and the Npc2a gene which encodes a protein involved in sterol homeostasis) would share the same chromatin state/biophysical properties as the TAD upstream of the purple boundary, which has the fipi gene. While it is true that CG33543, Obp22a and also the fipi gene are not expressed in embryos, Npc2a is expressed at high levels during embryogenesis, yet it is part of the TAD that interacts with the fipi TAD.  The TAD downstream of the blue boundary contains CG15353 and Nplp4 and it interacts with the TAD downstream of the purple boundary which contains CG3294 and slf.  CG15353 and Nplp4 are not expressed in the embryo and as such should share a compartment with a TAD that is also silent. However, slf is expressed at a high level in 1216 hr embryos, while CG3294 is expressed at a low level.  In neither case would one conclude that the TADs upstream and downstream of the blue and purple boundaries, respectively, interact because of shared chromatin/biophysical states that drive block polymer co-segregation corepulsion. 

One might also consider several gedanken experiments involving the long-range interactions that generate the CG3294 meta-loop in Author response image 3.    According to the micro-compartment model the patchwork pattern of crosslinking evident in the CG3294 meta-loop arises because the interacting  TADs share the same biochemical/biophysical properties, and this drives block polymer cosegregation and co-repulsion.  If this model is correct, then this patchwork pattern of TAD:TAD interactions would remain unchanged if we were to delete the blue or the purple boundary.  However, given what we know about how boundaries can find and pair with distant boundaries (c.f., Figure 6 from Muller et el. 1999 and the discussion in #1.2), the result of these gedanken experiments seem clear: the patchwork pattern shown in Author response image 3A will disappear.  What would happen if we inverted the blue or the purple boundary? Would the TAD containing CG33543, Obp22a and Npc2a still interact with fipi as would be expected from the compartment model?  Or would the pattern of interactions flip so that the CG33543, Obp22a and Npc2a TAD interacts with the TAD containing CG3294 and slf?  Again we can anticipate the results based on previous studies: the interacting TADs will switch when the CG3294 meta-loop is converted into a stem-loop.  If this happened, the only explanation possible in the compartment model is that the chromatin states change when the boundary is inverted so that TAD upstream of blue boundary now shares the same chromatin state as the TAD downstream of the purple boundary, while the TAD downstream of the blue boundary shares same state as the TAD upstream of the purple boundary.  However, there is no evidence that boundary orientation per se can induce a complete switch in “chromatin states” as would be required in the compartment model. 

While we have not done these experimental manipulations with the CG3294 meta-loop, an equivalent experiment was done in Bing et al. (Bing et al. 2024).  However, instead of deleting a boundary element, we inserted a homie boundary element together with two reporters (gfp and LacZ) 142 kb away from the eve TAD.  The result of this gedanken “reverse boundary deletion” experiment is shown in Author response image 5.  Panel A shows the MicroC contact profile in the region spanning the transgene insertion site and the eve TAD in wild type (read “deletion”) NC14 embryos.  Panel B shows the MicroC contact profile from 12-16 hr embryos carrying the homie dual reporter transgene inserted at -142 kb.  Prior to the “deletion”, the homie element in the transgene pairs with nhomie and homie in the eve TAD and this generates a “mini-metaloop.”  In this particular insert, the homie boundary in the transgene (red arrow) is “pointing” in the opposite orientation from the homie boundary in the eve TAD (red arrow).  In this orientation, the pairing of the transgene homie with eve nhomie/homie brings the LacZ reporter into contact with sequences in the eve TAD.  Since a mini-metaloop is formed by homie_à _nhomie/homie pairing, sequences in TADs upstream and downstream of the transgene insert interact with sequences in TADs close to the eve TAD (Author response image 5B).  Taken together these interactions correspond to the interaction patchwork that is typically seen in “compartments” (see boxed region and inset).  If this patchwork is driven as per the model, by block polymer co-segregation and co-repulsion, then it should still be present when the transgene is deleted.  However, panel A shows that the interactions linking the transgene and the sequences in TADs next to the transgene to eve and TADs next to eve disappear when the homie boundary (plus transgene) is “deleted” in wild type flies.

Author response image 5.

Boundary deletion and compartments

A second experiment would be to invert the homie boundary so that instead of pointing away from eve it points towards eve.  Again, if the compartmental patchwork is driven by block polymer co-segregation and co-repulsion, inverting the homie boundary in the transgene should have no effect on the compartmental contact profile.  Inspection of Fig. 7 in Bing et al. (Bing et al. 2024) will show that this prediction doesn’t hold either.  When homie is inverted, sequences in the eve TAD interact with the gfp reporter not the LacZ reporter.  In addition, there are corresponding changes in how sequences in TADs to either side of eve interact with sequences to either side of the transgene insert.  

Yet another “test” of compartments generated by block polymer co-segregation/co-repulsion is provided by the plume above the eve volcano triangle.  According to the compartment model, sequences in TADs flanking the eve locus form the plume above the eve volcano triangle because their chromatin shares properties that drive block polymer co-segregation.  These same properties result in repulsive interactions with chromatin in the eve TAD, and this would explain why the eve TAD doesn’t crosslink with its neighbors.  If the distinctive chromatin properties of eve and the neighboring TADs drive block polymer co-segregation and co-repulsion, then inverting the nhomie boundary or introducing homie in the forward orientation should have absolutely no effect on the physical interactions between chromatin in the eve TAD and chromatin in the neighboring TADs.  However, Figures 4 and 6 in this paper indicate that boundary pairing orientation, not block polymer co-segregation/co-repulsion, is responsible for forming the plume above the eve TAD. Other findings also appear to be inconsistent with the compartment model. (A) The plume topping the eve volcano triangle is present in NC14 embryos when eve is broadly expressed (and potentially active throughout the embryo).  It is also present in 12-16 hr embryos when eve is only expressed in a very small subset of cells and is subject to PcG silencing everywhere else in the embryo.  B) According to the compartment model the precise patchwork pattern of physical interactions should depend upon the transcriptional program/chromatin state that is characteristic of a particular developmental stage or cell type.  As cell fate decisions are just being made during NC14 one might expect that most nuclei will share similar chromatin states throughout much of the genome.  This would not be true for 12-16 hr embryos.  At this stage the compartmental patchwork would be generated by a complex mixture of interactions in cells that have quite different transcriptional programs and chromatin states.  In this case, the patchwork pattern would be expected to become fuzzy as a given chromosomal segment would be in compartment A in one group of cells and in compartment B in another.   Unlike 12-16 hr embryos,  larval wing discs would be much more homogeneous and likely give a distinct and relatively well resolved compartmental pattern. We’ve examined the compartment patchwork of the same chromosomal segments in NC14 embryos, 12-16 hr embryos and larval wing disc cells.  While there are some differences (e.g., changes in some of the BX-C TADs in the wing disc sample) the compartmental patchwork patterns are surprisingly similar in all three cases. Nor is there any “fuzziness” in the compartmental patterns evident in 12-16 hr embryos, despite the fact that there are many different cell types at this stage of development.  C) TAD interactions with their neighbors and compartmental patchworks are substantially suppressed in salivary gland polytene chromosomes.  This would suggest that features of chromosome structure might be the driving force behind many of the “compartmental” interactions as opposed to distinct biochemical/biophysical of properties of small chromosomal segments that drive polymer co- segregation/co-repulsion.  

(3) The contact maps presented in the study represent many cells and distinct cell types. It is clear from single-cell Hi-C and multiplexed FISH experiments that chromosome conformation is highly variable even within populations of the same cell, let alone between cell types, with structures such as TADs being entirely absent at the single cell level and only appearing upon pseudobulking. It is difficult to square these observations with the models of relatively static structures depicted here. The authors should provide commentary on this point.

(2.5) As should be evident from Author response image 1, single-cell Hi-C experiments would not provide useful information about the physical organization of individual TADs, TAD boundaries or how individual TADs interact with their immediate neighbors.  In addition, since they capture only a very small fraction of the possible contacts within and between TADs, we suspect that these single-cell studies aren’t likely to be useful for making solid conclusions about TAD neighborhoods like those shown in Author response image 1 panels A, B, C and D, or Author response image 2.  While it might be possible to discern relatively stable contacts between pairs of insulators in single cells with the right experimental protocol, the stabilities/dynamics of these interactions may be better judged by the length of time that physical interactions are seen to persist in live imaging studies such as Chen et al. (2018), Vazquez et al. (2006) and Li et al. (2011).

The in situ FISH data we’ve seen also seems problematic in that probe hybridization results in a significant decondensation of chromatin.  For two probe sets complementary to adjacent ~1.2 kb DNA sequences, the measured center-to-center distance that we’ve seen was ~110 nM.  This is about 1/3rd the length that is expected for a 1.2 kb naked DNA fragment, and about 1.7 times larger than that expected for a beads-on-a-string nucleosome array (~60 nM).  However, chromatin is thought to be compacted into a 30 nM fiber, which is estimated to reduce the length of DNA by at least another ~6 fold.  If this estimate is correct, FISH hybridization would appear to result in a ~10 fold decompaction of chromatin.  A decompaction of this magnitude would necessarily be followed by a significant distortion in the actual conformation of chromatin loops.

(4) The analysis of the Micro-C data appears to be largely qualitative. Key information about the number of reads sequenced, reaps mapped, and data quality are not presented. No quantitative framework for identifying features such as the "plumes" is described. The study and its findings would be strengthened by a more rigorous analysis of these rich datasets, including the use of systematic thresholds for calling patterns of organization in the data.

Additional information on the number of reads and data quality have been included in the methods section. 

(5) Related to Point 4, the lack of quantitative details about the Micro-C data make it difficult to evaluate if the changes observed are due to biological or technical factors. It is essential that the authors provide quantitative means of controlling for factors like sampling depth, normalization, and data quality between the samples.

In our view the changes in the MicroC contact patterns for the eve locus and its neighbors when the nhomie boundary is manipulated are not only clear cut and unambiguous but are also readily evident in the Figs that are presented in the manuscript.  If the reviewer believes that there aren’t significant differences between the MicroC contact patterns for the four different nhomie replacements, it seems certain that they would also remain unconvinced by a quantitative analysis.

The reviewer also suggests that biological and/or technical differences between the four samples could account for the observed changes in the MicroC patterns for the eve TAD and its neighbors.  If this were the case, then similar changes in MicroC patterns should be observed elsewhere in the genome.  Since much of the genome is analyzed in these MicroC experiments there is an abundance of internal controls for each experimental manipulation of the nhomie boundary.  For two of the nhomie replacements, nhomie reverse and homie forward, the plume above the eve volcano triangle is replaced by clouds surrounding the eve volcano triangle.  If these changes in the eve MicroC contact patterns are due to significant technical (or biological) factors, we should observe precisely the same sorts of changes in TADs elsewhere in the genome that are volcano triangles with plumes.   Author response image 6 shows the MicroC contact pattern for several genes in the Antennapedia complex.  The deformed gene is included in a TAD which, like eve, is a volcano triangle topped by a plume.  A comparison of the deformed MicroC contact patterns for nhomie forward (panel B) with the MicroC patterns for nhomie reverse (panel C) and homie forward (panel D) indicates that while there are clearly technical differences between the samples, these differences do not result in the conversion of the deformed plume into clouds as is observed for the eve TAD.  The MicroC patterns elsewhere in Antennapedia complex are also very similar in all four samples.  Likewise, comparisons of regions elsewhere in the fly genome indicate that the basic contact patterns are similar in all four samples.   So while there are technical differences which are reflected in the relative pixel density in the TAD triangles and the LDC domains, these differences do not result in converting plumes into clouds nor do the alter the basic patterns of TAD triangles and LDC domains.  As for biological differences— the embryos in each sample are at roughly the same developmental stage and were collected and processed using the same procedures. Thus, the biological factors that could reasonably be expected to impact the organization of specific TADs (e.g., cell type specific differences) are not going to impact the patterns we see in our experiments. 

Author response image 6.

(6) The ISH effects reported are modest, especially in the case of the HCR. The details provided for how the imaging data were acquired and analyzed are minimal, which makes evaluating them challenging. It would strengthen the study to provide much more detail about the acquisition and analysis and to include depiction of intermediates in the analysis process, e.g. the showing segmentation of stripes.

The imaging analysis is presented in Fig. 5 is just standard confocal microscopy.  Individual embryos were visualized and scored.  An embryo in which stripes could be readily detected was scored as ‘positive’ while an embryo in which stripes couldn’t be detected was scored as ‘negative.’   

Recommendations for the authors:

Editor comments:

It was noted that the Jaynes lab previously published extensive genetic evidence to support the stem loop and circle loop models of Homie-Nhomie interactions (Fujioka 2016 Plos Genetics) that were more convincing than the Micro-C data presented here in proof of their prior model. Maybe the authors could more clearly summarize their prior genetic results to further try to convince the reader about the validity of their model.

Reviewer #1 (Recommendations For The Authors):

Below, I list specific comments to further improve the manuscript for publication. Most importantly, I recommend the authors tone down their proposal that boundary pairing is a universal TAD forming mechanism.

(1) The title is cryptic.

(2) The second sentence in the abstract is an overstatement: "In flies, TADs are formed by physical interactions between neighboring boundaries". Hi-C and Micro-C studies have not provided evidence that most TADs in Drosophila show focal interactions between their bracketing boundaries. The authors rely too strongly on prior studies that used artificial reporter transgenes to show that multimerized insulator protein binding sites or some endogenous fly boundaries can mediate boundary bypass, as evidence that endogenous boundaries pair.

Please see responses #1.1 and #1.3 and figures Author response image 1 and Author response image 3.  Note that using dHS-C, most TADs that we’ve looked at so far are topped by a “dot” at their apex.

(3) Line 64: the references do not cite the stated "studies dating back to the '90's'".

The papers cited for that sentence are reviews which discussed the earlier findings.  The relevant publications are cited at the appropriate places in the same paragraph.  

(4) Line 93: "On the other hand, while boundaries have partner preferences, they are also promiscuous in their ability to establish functional interactions with other boundaries." It was unclear what is meant here.

Boundaries that a) share binding sites for proteins that multimerized, b) have binding sites for proteins that interact with each other, or c) have binding sites for proteins that can be bridged by a third protein can potentially pair with each other.  However, while these mechanisms enable promiscuous pairing interactions, they will also generate partner preferences (through a greater number of a, b and/or c).

(5) It could be interesting to discuss the fact that it remains unclear whether Nhomie and Homie pair in cis or in trans, given that homologous chromosomes are paired in Drosophila.

The studies in Fujioka et al. (Fujioka et al. 2016) show that nhomie and homie can pair both in cis and in trans.  Given the results described in #1.2, we imagine that they are paired in both cis and trans in our experiments.

(6) Line 321: Could the authors further explain why they think that "the nhomie reverse circle-loop also differs from the nhomie deletion (λ DNA) in that there is not such an obvious preference for which eve enhancers activate expression"?

The likely explanation is that the topology/folding of the altered TADs impacts the probability of interactions between the various eve enhancers and the promoters of the flanking genes.  

(7) The manuscript would benefit from shortening the long Discussion by avoiding repeating points described previously in the Results.

(8) Line 495: "If, as seems likely, a significant fraction of the TADs genome-wide are circle loops, this would effectively exclude cohesin-based loop extrusion as a general mechanism for TAD formation in flies". The evidence provided in this manuscript appears insufficient to discard ample evidence from multiple laboratories that TADs form by compartmentalization or loop extrusion. Multiple laboratories have, for example, demonstrated that cohesin depletion disrupts a large fraction of mammalian TADs. 

Points made here and in #9 have been responded to in #1.1, #2.1 and #2.4 above.  We would suggest that the evidence for loop extrusion falls short of compelling (as it is based on the analysis of TAD neighborhoods, not TADs—that is forests, not trees) and given the results reported in Goel et al. (in particular Fig. 4 and Sup Fig. 8) is clearly suspect. This is not to mention the fact that cohesin loop-extrusion can’t generate circle-loops TADs, yet circle-loops clearly exist.  Likewise, as discussed in #2.4, it is not clear to us that the shared chromatin states, polymer co-segregation and co-repulsion account for the compartmental patchwork patterns of TAD;TAD interactions. The results from the  experimental manipulations in this paper and the accompanying paper, together with studies by others (e.g., Kyrchanova et al. (Kyrchanova et al. 2008), Mohana et al. (Mohana et al. 2023) would also seem to be at odds with the model for compartments as currently formulated.  

The unique properties of Nhomie and Homie, namely the remarkable specificity with which they physically pair over large distances (Fujioka et al. 2016) may rather suggest that boundary pairing is a phenomenon restricted to special loci. Moreover, it has not yet been demonstrated that Nhomie or Homie are also able to pair with the TAD boundaries on their left or right, respectively.

Points made here were discussed in detail in #1.2.  As described in detail in #1.2, It is not the case that nhomie and homie are in “unique” or “special.”  Other fly boundaries can do the same things.  As for whether nhomie and homie pair with their neighbors:  We haven’t done transgene experiments (e.g., testing by transvection or boundary bypass).  Likewise, in MicroC experiments there are no obvious dots at the apex of the neighboring TADs that would correspond to nhomie pairing with the neighboring boundary to the left and homie pairing with the neighboring boundary to the right. However, this is to be expected. As we discussed in in #1.3 above, only MNase resistant elements will generate dots in standard MicroC experiments.  On the other hand, when boundary:boundary interactions are analyzed by dHS-C (c.f., Author response image 4), there are dots at the apex of both neighboring TADs.  This would be direct evidence that nhomie pairs with the neighboring boundary to the left and homie pairs with the neighboring boundary to the right.

(9) The comment in point 8 also applies to the concluding 2 sentences (lines 519-524) of the Discussion.

See response to 8 above. Otherwise, the concluding sentences are completely accurate. Validation of the cohesin loop extrusion/CTCF roadblock model will required demonstrating a) that all TADs are either stem-loops or unanchored loops and b) that TAD endpoints are always marked by CTCF. 

The likely presence of circle-loops and evidence that TAD boundaries that don’t have CTCF (c.f.,Goel et al. 2023) already suggests that this model can’t (either fully or not all) account for TAD formation in mammals. 

(10) Figs. 3 and 6: It would be helpful to add the WT screenshot in the same figure, for direct comparison.

It is easy enough to scroll between Figs-especially since nhomie forward looks just like WT.

(11) Fig. 6: It would be helpful to show a cartoon view of a circle loop to the right of the Micro-C screenshot, as was done in Fig. 3.

Good idea.   Added to the Fig.

(12) Fig. 5: It would be helpful to standardize the labelling of the different genotypes throughout the figures and panels ("inverted" versus "reverse" versus an arrow indicating the direction).

Fixed.

Reviewer #2 (Recommendations For The Authors):

Minor Points:

(1) The Micro-C data does not appear to be deposited in an appropriate repository. It would be beneficial to the community to make these data available in this way.

This has been done.

(2) Readers not familiar with Drosophila development would benefit from a gentle introduction to the stages analyzed and some brief discussion on how the phenomenon of somatic homolog pairing might influence the study, if at all.

We included a rough description the stages that were analyzed for both the in situs and MicroC. We thought that an actual description of what is going on at each of the stages wasn’t necessary as the process of development is not a focus of this manuscript.  In other studies, we’ve found that there are only minor differences in MicroC patterns between the blastoderm stage and stage 12-16 embryos.  While these minor differences are clearly interesting, we didn’t discuss them in the text.   In all of experiments chromosomes are likely to be paired.  In NC14 embryos (the stage for visualizing eve stripes and the MicroC contact profiles in Fig. 2) replication of euchromatic sequences is thought to be quite rapid.  While homolog pairing is incomplete at this stage, sister chromosomes are paired.  In stage 12-16 embryos, homologs will be paired and if the cells are arrested in G2, then sister chromosome will also be paired.  So in all of experiments, chromosomes (sisters and/or homologs) are paired. However, since we don’t have examples of unpaired chromosomes, our experiments don’t provide any info on how chromosome pairing might impact MicroC/expression patterns.

(3) "P > 0.01" appears several times. I believe the authors mean to report "P < 0.01".

Fixed.  

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Author response:

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

eLife assessment

This valuable study examines the role of a host in conditions that shift pathogenicity of opportunistic microbes. The use of single-cell microbial transcriptomics and metabolomics to demonstrate the host's effects on pathogen dynamics is interesting and convincing. However, the connection to host antimicrobial peptides driving these effects is incomplete and would benefit from additional evidence and improved explanation in the text. This paper has the potential to be of broad interest to those working in host-microbe (microbiome and pathogen) interactions.

We appreciate the editors for organizing our manuscript and providing eLife assessment. We went through each comment and carried out some necessary experiments. According to the comments, we here provide additional evidence that further supports our findings in this revised manuscript.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this work, Wang and colleagues used Drosophila-Serratia as a host-microbe model to investigate the impact of the host on gut bacteria. The authors showed that Drosophila larvae reduce S. marcescens abundance in the food likely due to a combination of mechanical force and secretion of antimicrobial peptides. S. marcescens exposed to Drosophila larvae lost virulence to flies and could promote larval growth similar to typical Drosophila gut commensals. These phenotypic changes were reflected in the transcriptome and metabolome of bacteria, suggesting that the host could drive the switch from pathogenicity to commensalism in bacteria. Further, the authors used single-cell bacterial RNA-seq to demonstrate the heterogeneity in gut bacterial populations.

Strengths:

This is a valuable work that addresses an important question of the effect of the host on its gut microbes. The authors could convincingly demonstrate that gut bacteria are strongly affected by the host with important consequences for both interacting partners. Moreover, the authors used state-of-the-art bacterial single-cell RNA-seq to reveal heterogeneity in host-associated commensal populations.

Weaknesses:

Some of the conclusions are not fully supported by the data.

Specifically, in lines 142-143, the authors claim that larva antagonizes the pathogenicity of S. marcescens based on the survival data. I do not fully agree with this statement. An alternative possibility could be that, since there are fewer S. marcescens in larvae-processed food, flies receive a lower pathogen load and consequently survive. Can the authors rule this out?

Also, the authors propose that Drosophila larvae induce a transition from pathogenicity to commensalism in S. marcescens and provide nice phenotypic and transcriptomic data supporting this claim. However, is it driven only by transcriptional changes? Considering high mutation rates in bacteria, it is possible that S. marcescens during growth in the presence of larvae acquired mutations causing all the observed phenotypic and transcriptional changes. To test this possibility, the authors could check how long S. marcescens maintains the traits it acquires during growth with Drosophila. If these traits persist after reculturing isolated bacteria, it is very likely they are caused by genome alterations, if not - likely it is a phenotypic switch driven by transcriptional changes.

We thank the reviewer for providing a feasible method to distinguish the shift in transcriptional profile from genomic mutations. According to this valuable suggestion, we checked phenotypic and transcriptional changes after re-culturing the bacterium that had coexisted with larvae. We found that all phenotypes can be recovered after re-culturing. The new data supported our previous result that a phenotypic switch was driven by transcriptional changes rather than genome mutations. We now add these results to the text with figure supplement 3 (line 147-151, 192-194). Please see the following text.

“To rule out the possibility that phenotypic alterations could stem from genomic mutations, we examined the prodigiosin yield and CFUs of re-culturing S. marcescens that had coexisted with larvae. Our results showed that neither prodigiosin yield nor CFUs of re-culturing S. marcescens differed from the original strain (Figure 2-figure supplement 3A-C), suggesting that a phenotypic switch was driven primarily by transcriptional reprogramming.” “Consistent with the previous result that this phenotypic switch was driven by transcriptional changes, the expression of virulent and growth genes was recovered after re-culturing (Figure 3-figure supplement 3D, E).”

For the first question, we admit the possibility that the high morality of flies could result from the acquirement of a higher pathogen load, because of an increase in the bacterial load of single S. marcescens. However, host pathogenesis is normally determined by the virulence of pathogens rather than the number of bacteria. For example, hosts constantly harbor astonishing commensals in their guts, but remain healthy. This evidence suggests that it was the property (virulence) of a pathogen that is more important to affect the health status of the hosts. Moreover, an increase in virulence of single S. marcescens was verified by real-time PCR (Fig. 2F) and TE (Fig. 2G). Taken together, we could draw a conclusion that the impaired survival of flies challenged with single S. marcescens mainly arose from an increase in the virulence of S. marcescens. Thanks for your understanding!

Reviewer #2 (Public Review):

Summary:

While many studies have explored the impacts of pathogens on hosts, the effect of hosts on pathogens has received less attention. In this manuscript, Wang et al. utilize Drosophila melanogaster and an opportunistic pathogen, Serratia marcescens, to explore how the host impacts pathogenicity. Beginning with an observation that larval presence and density impacted microbial growth in fly vials (which they assess qualitatively as the amount of 'slick' and quantitatively as microbial load/CFUs), the authors focus on the impact of axenic/germ-free larvae on an opportunistic pathogen S. marcescens. Similar to their observations with general microbial load, they find that larvae reduce the presence of a pinkish slick of Sm, indicative of its secondary metabolite prodigiosin. The presence of larvae alters prodigiosin production, pathogen load, pathogen cellular morphology, and virulence, and this effect is through transcriptional and metabolic changes in the pathogen. Overall, they observe a loss of virulence factors/pathways and an increase in pathways contributing to growth. Given the important role the host plays in this lifestyle shift, the authors then examined host features that might influence these effects, focusing on the role of antimicrobial peptides (Amps). The authors combine the use of synthetic Amps and an Amp-deficient fly line and conclude much of the larval inhibitory effect is due to their production of AMPs.

Strengths:

This is a very interesting question and the use of Drosophila-Serratia marcescens is a great model to explore these interactions and effects.

The authors have an interesting and compelling phenotype and are asking a unique question on the impact of the host on the pathogen. The use of microbial transcriptomics and metabolomics is a strength, especially in order to assess these impacts on the pathogen level and at the single-cell level to capture heterogeneity.

Weaknesses:

Overall, the writing style in the manuscript makes it difficult to fully understand and appreciate the data and its interpretation.

The data on the role of AMPs would benefit from strengthening. Some of the arguments in the text of that section are also counterintuitive. The authors show that △AMP larvae have a reduced impact on Sm as compared to wt larvae, but it seems less mild of an effect than that observed with wt excreta (assuming the same as secreta in Figures 7, should be corrected or harmonized). Higher doses of AMPs give a phenotype similar to wt larvae, but a lower dose (40 ng/ul) gives phenotypes more similar to controls. The authors argue that this data suggests AMPs are the factor responsible for much of the inhibition, but their data seems more to support that it's synergistic- you seem to still need larvae (or some not yet defined feature larvae make, although secreta/excreta was not sufficient) + AMPs to see similar effects as wt. Based on positioning and color scheme guessing that AMP 40ng/ul was used in Figures 7D-H, but could not find this detail in the text, methods, or figure legend and it should be indicated. This section does not seem to be well supported by the provided data, and this inconsistency greatly dampened this reviewer's enthusiasm for the paper.

We thank the reviewer’s valuable comments and suggestions. We admitted that some photos of the pinkish slick (prodigiosin) are counterintuitive in Figure 7 as well as figure supplement 2B. Here comes the reason. Single S. marcescens produced prodigiosin that only stayed on the surface of fly agar medium. As we know, larvae can agitate food and form a stratification of prodigiosin, even making higher prodigiosin yield inside food lighter than the surface slick of prodigiosin. We mentioned it in the previous manuscript line 166-168. This is why some photos treated with excreta and a lower dose of AMP seemed more intense than those with WT larvae. However, we precisely quantified the prodigiosin yield inside food with the spectrophotometer, so we provided a prodigiosin yield following the photos of the slick. Therefore, we drew our conclusions mainly relying on the quantification of the prodigiosin yield. We actually used cecropin A for our experiments, so we added this information in the text. We hope that our replies can reignite your enthusiasm for our manuscript, and thanks for your great support!

Reviewer #3 (Public Review):

In this study, Wang and coworkers established a model of Drosophila-S. marcescens interactions and thoroughly examined host-microbe bidirectional interactions. They found that:

(1) Drosophila larvae directly impact microbial aggregation and density;

(2) Drosophila larvae affect microbial metabolism and cell wall morphology, as evidenced by reduced prodigiosin production and EPS production, respectively;

(3) Drosophila larvae attenuate microbial virulence;

(4) Drosophila larvae modulate the global transcription of microbes for adaptation to the host;

(5) Microbial single-cell RNA sequencing (scRNA-seq) analysis revealed heterogeneity in microbial pathogenicity and growth;

(6) AMPs are key factors controlling microbial virulence phenotypes.

Taken together, they concluded that host immune factors such as AMPs are directly involved in the pathogen-to-commensal transition by altering microbial transcription.

General comments:

In general, this study is intriguing as it demonstrates that host immune effectors such as AMPs can serve as critical factors capable of modulating microbial transcription for host-microbe symbiosis. However, several important questions remain unanswered. One such question is: What is the mechanism by which AMPs modulate the pathogen-to-commensal transition? One hypothesis suggests that antimicrobial activity may influence microbial physiology, subsequently modulating transcription for the transition from pathogen to commensal. In this context, it is imperative to test various antibiotics with different modes of action (e.g., targeting the cell wall, transcription, or translation) at sub-lethal concentrations to determine whether sub-lethal doses of antimicrobial activity are sufficient to induce the pathogen-to-commensal transition.

Thank you for the important comments on our manuscript. We checked the effect of antibiotics (5 μg/μl kanamycin and 10 μg/μl ampicillin) on the virulence switch of S. marcescens. We found that the two antibiotics with the sub-lethal doses similarly resulted in a decrease in prodigiosin yield and virulence expression of S. marcescens. Intriguingly, the two antibiotics also resulted in a dramatic decline in the bacterial load and the expression of genes involved in cell growth. These results suggest that antibiotics reduced the virulence primarily through suppressing most activities of bacteria.

We found that larvae and AMPs at 40 μg/μl modestly resulted in a decrease in bacterial load and an increase in the relative level of genes involved in cellular proliferation, suggesting that AMPs could maintain the exponential phase of bacterial growth. This result is consistent that Drosophila larvae can support the long-term persistence of commensals in the shared habitat (DOI: 10.1016/j.cmet.2017.11.011). The inhibition could prevent bacteria from rapidly exhausting their nutritional resources, and consequently maintain symbiosis. It is likely that AMPs could maintain S. marcescens at the exponential phase of cell growth and prevent bacteria from rapidly exhausting their nutritional resources.

Author response image 1.

(A) Representative images of surface slick with S. marcescens alone, with kanamycin (5 μg/μl) and ampicillin (10 μg/μl). (B) The prodigiosin production of S. marcescens alone, with kanamycin (5 μg/μl) and ampicillin (10 μg/μl). n = 6 for each. (C) Bacterial loads of S. marcescens alone, with kanamycin (5 μg/μl) and ampicillin (10 μg/μl). n = 6 for each. (D, E) RT-qPCR analysis of the expression levels of downregulated and upregulated genes in the S. marcescens alone, with kanamycin (5 μg/μl) and ampicillin (10 μg/μl). n = 3 for each. Means ± SEMs. All variables have different letters, they are significantly different (p < 0.05). If two variables share a letter, they are not significantly different (p > 0.05). ns, no significance. Kruskal-Wallis test followed by Dunn’s multiple comparisons test.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Here are some specific points that need to be addressed:

(1) Lack of statistical analysis for many figures. The authors should perform and report the statistical analysis for all figures where it is currently lacking, specifically, Figures 2C, D, E, F, H; Figures 3E, F; Figures 7G, H; Figure S2E, Figures S3D, E.

Thanks for your valuable suggestions. We re-checked the manuscript and performed the statistical analysis for these figures.

(2) For graphs showing dots, it should be specified what exactly individual dots show and how many animals were used per replicate. Also, time points at which specific analysis was performed should be specified.

We provided the important information in the legends in the revised manuscript.

(3) Figure 2. No letters illustrating statistical significance are shown, although this is claimed in the legend (line 848).

We added statistical significance in the updated Figure 2.

(4) In Figure 7, the authors used AMPs of defined concentration, but it is not specified what exactly these AMPs are. Please provide the full composition of the AMP mix used.

We used the antimicrobial peptide cecropin A produced by a silkworm. We added this information in the methods line 487-488 and Figure 7 legend.

(5) Figure S2B. To me, it looks like that medium with larvae is redder than after mechanical force. I find it hard to believe the quantification in panel C that the medium with larvae has 3 times less pigment as compared to the mechanical force.

Larvae could only agitate the surface of food (~0.4 cm), but sticks completely agitated the food up to 3 cm. Thus, the layer of food with pink pigment with agitation seemed much deeper than with larvae, which was responsible for the counterintuitively. We explained it in the previous manuscript (line 166-168). “Of note, the surface of the slick with agitation appeared lighter than that of larvae, mainly due to a stratification of prodigiosin following agitation.”

(6) The authors need to proofread the manuscript as there are missing words, terms that need definition, and wrong terms. For example, L86 - naked eye?, L117 - what do the authors mean by co-culture?, L309 - not resist but rather combat, L347 - Species? or competition?, Figure 2A - 2nd?

We have corrected these errors in the new manuscript. We added an "eye" in L86. Co-culture means “S. marcescens in co-culture”. Interspecies competition for nearly the same or similar nutrients and space occurs in the habitat.

(7) The authors should reorganize either the text or the figures' order in a way that the figures are described in a consecutive order (Figure 1A, B ... and not Figure 1D first and then 1A).

Thanks for your valuable advice. We reorganize the order of the text.

(8) Do the authors have an idea which bacteria they quantified in Figures 1E to 1G? I didn't find the medium that was used for culturing. Also, in Figure 1F, Is the control group comprised of females or males?

Mixed bacteria (bacteria in the living environment of Drosophila) were quantified in the NA medium that supports the growth of Drosophila microbiota (Jia Y, et al. Nat Commun. 2021) line 474-475. The control group comprised of both males and females with a 1:1 ratio. Similarly, the aged group contained 100 50-day-aged flies, male: female = 1:1. We provided details in Figure 1 legend line 849-850, 851-852.

(9) L118-129. it is not possible to make all these statements without any statistical analysis. To me, at 96h both treatments have the same CFUs, while the authors claim they are different.

We added statistical analysis in the current version. In fact, single S. marcescens became collapsed after 72 h post inoculation, and the CFU number of single S. marcescens declined step by step. The bacterial load of S. marcescens in co-culture was comparable (at 96 h post-inoculation, p>0.05) or higher (at 120 h post-inoculation, p＜0.001) than S. marcescens alone, possibly explained by the possibility that bacteria rapidly exhausted the nutritional resources and collapsed through population suicide. We rewrote this sentence line 125-129 in the updated manuscript.

(10) L136. term "symbionts" is not appropriate here.

We change “symbionts” into “S. marcescens”.

(11) In Figure 1, the authors used flies of different fitness: weak, strong, and infertile. They should be specific and describe exactly what these terms mean, are these mutants or treatments that affect the fitness?

We apologize for this missing information and add them in the method and legend. Strong flies (wild-type fly CS), weak flies (yw; Sp/CyO; MKRS/TM6B), infertile flies (dfmr150M null mutant) Figure 1 legend line 849-850.

(12) Figure S2. The title of this figure is misleading, please modify it. Mechanical force did affect S. marcescens but to a lesser degree as compared to larvae.

Thank you for your suggestion. We admit that mechanical force affected S. marcescens but to a lesser degree as compared to larvae, so we changed the title to "Biological factors mainly determine S. marcescens lifestyle."

Reviewer #2 (Recommendations For The Authors):

General improvement to writing and presentation (see below):

Describing confluent growth would make more sense than 'slick' and then using descriptions of broken, etc. "colour intensity of the surface slick".

We used the slick to describe visible surface films of bacteria, which has been used in the previous study (DOI: 10.1038/s43705-023-00307-8). Slick is equal to confluent growth, but seems simple and easy than confluent growth. To make sense, we add this reference to the text.

We reorganized the text of Figure 1.

Suggest more specific language to describe observations. For example: Bacterial loading - S. marcescens growth (for example: the presence of dense fly populations reduced Sm growth).

Thanks for the suggests. We replaced some of them.

Symbiont, microbiota, microbiome, etc were all used interchangeably throughout the manuscript, but I am not sure I would call Sm part of the indigenous microbiome. Suggest to ensure proper usage and then harmonize throughout the ms.

We used microbes and microbiome to replace symbiont and microbiota, respectively.

Details missing from the message and Figure legends that would be helpful (including and especially Figure 7 - what AMP concentration?)

Thanks for valuable comments. According to this comment, we provided concrete details in the Materials and methods and Figure 7 legend about AMPs, including the source and concentration of AMPs line 487-488, 954-955. Please see the response below.

L73: define 'these issues" maybe or lead better with the prior sentence, it is not evident as currently written.

Change "to address these issues" to " To investigate whether and/or how the host modulates bacterial lifestyles,” and merge two paragraphs.

L74: repetitive sentence with the above.

Thanks for pointing out this detail. We deleted it.

L86: naked 'eye'.

Added.

L87: what is meant by 'weak flies'?

Genotypes were added in the updated manuscript. Weak fly stocks display weaker activity and generate fewer eggs than WT flies.

L96: bacterial load, not loading.

Corrected.

L128: no evidence to support, could be reflective of increased numbers in dying/dead larvae that impact total numbers in the vial.

The number of CFUs of S. marcescens alone was gradually decreased at 96 h post-inoculation. In addition, we observed pale biofilm on the surface of the medium at the late stage. The numbers of CFUs of S. marcescens alone at the later stages were reduced (compared to the peak load at 48 h post-inoculation), so it was deterred that bacteria could undergo ecological suicide. Ecological suicide of the bacterial population was similarly examined by recording the number of CFUs in the medium over time (Ratzke C, et al. Nat Ecol Evol. 2018.). Taken together, we draw a conclusion that bacteria possibly underwent ecological suicide.

L129: the prior sentence is in contradiction, reduced load only at early time points in the presence of larvae....

Thanks for pointing out this detail. We added " before 72 h post-inoculation " in the sentence.

L134: data is only focused on S marcescens, so inferring to 'symbionts' broadly is outside study.

We change “symbionts” into “S. marcescens”.

L139: sentence poorly written and confusing.

We re-organized this sentence.

To this end, we sought to examine the S. marcescens lifestyle switch from pathogenicity to commensalism by assessing the respective survival of flies on the fly medium that had been processed by single or coexisting S. marcescens.

L189: evidence for long-term symbiosis is not well established in this paper, suggest editing this language throughout to more specifically reflect what the data supports and leave such interpretations to discussion points and future work.

Thanks for your valuable advice. We deleted long-term and “thereby promoting the fitness of symbionts in the long maintenance.”.

L192; used metabolomics to assess the impacts of larvae on bacterial metabolism, as currently written does not make sense.

We rewrote this sentence. “Next, we investigated whether larvae could further elicit changes in the metabolism of S. marcescens using untargeted metabolomics.”

L331: the use of monitored here is not correct/odd.

We changed 'monitored' to 'reshaping’.

L340: While the authors initially see a cost to Sm in reduced load (CFUs) at 120 h populations associated with larvae become higher - there is also a cost to producing virulence factors, which their RNASeq and metabolomics data support - trade-offs between growth and virulence.

Thanks for your suggestion. We added “before 72 hours post inoculation” to define the early stage of the bacterial growth in the sentence.

Reviewer #3 (Recommendations For The Authors):

(1) Figures 1 A-D: What defines weak and strong flies, and what criteria determine the robustness of flies? How was the experiment conducted? The manuscript lacks details on this matter.

We thank you for your comments. We lack a criterium, but the robustness of flies comes from daily experience. Weak fly stocks display weak activity and generate fewer eggs than WT flies. Genotypes with different robustness were added in the legend in the updated manuscript

(2) The authors mentioned, "Noteworthily, the number of CFUs of S. marcescens alone was lower than S. marcescens in co-cultures at the late stage (at 96 h post inoculation), likely that bacteria rapidly exhausted their nutritional resources and underwent ecological suicide." How did they determine that the bacteria exhausted nutritional resources and underwent ecological suicide? One might speculate that larvae could have removed the bacteria simply by consuming them.

Thanks for this comment. Virtually, there were no larvae inside the vials with single S. marcescens, so bacterial cells were not consumed. However, the numbers of CFUs of S. marcescens alone at the later stages were reduced (compared to the peak load at 48 h post-inoculation), so it was deterred that bacteria could undergo ecological suicide. Ecological suicide of the bacterial population was examined by recording the number of CFUs in the medium over time (Ratzke C, et al. Nat Ecol Evol. 2018.). A similar method was also applied to the number of CFUs of S. marcescens. Taken together, we draw a conclusion that bacteria possibly underwent ecological suicide.

(3) Figure 2E: The experimental details should be provided in the text. What was the CFU of the bacteria used in this survival experiment?

We provided further experimental details in the legend line 869-870. The same amount of inocula was used in both single and coculturing S. marcescens.

(4) The experimental data in Figures 2G and 2H do not sufficiently prove the relationship between the width of the cell wall and virulence, as it lacks experimental validation.

Previous studies (DOI: 10.1371/journal.ppat.1005946) reveal that glucosylating toxins on the surface are primary virulence determinants, so an increased surface-anchored polysaccharide and protein profile promotes the virulence of the pathogen. Alterations in cell surface (the width of the cell wall) can be examined by TE. Moreover, TE was used to observe changes in the virulence of S. marcescens (DOI: 10.1093/nar/gkab1186). We think that the width of the cell wall could be used to reflect virulence in S. marcescens.

(5) While it's acknowledged that agitation decreases the color intensity of the bacteria, comparing mechanical agitation with larval crawling seems inappropriate, as the mechanical forces exerted by both methods are not of the same magnitude.

Thanks for the suggestion. In fact, food was agitated more heavily by glass sticks than by larvae, because larvae merely agitated the surface of food (about 0.5 cm-depth). If the decrease in bacterial load and color was related to the magnitude of agitation, larvae would confer a less decrease (from the decrease in stick agitation) in bacterial load than the sticks. Consequently, it would further support our result that biofactors more importantly confer the inhibition of S. marcescens than force.

(6) Figure 4D: with this metabolome data, they mentioned, "host suppresses differentiation of S. marcescens into the population with pathogenicity." What evidence supports the claim that downregulation of amino acid metabolism, phosphotransferase system, and ABC transporter directly correlates with decreased pathogenicity?

Thanks for the comment. Earlier studies showed that amino acid-derived quorum sensing molecules are closely related to bacterial pathogenicity (Defoirdt T. PLoS Pathog. 2019; Wen J, et al. Microbiol Spectr. 2022). Moreover, the phosphotransferase system and ABC transporter can transport and/or produce virulence factors. Therefore, we claimed that downregulation of amino acid metabolism, phosphotransferase system, and ABC transporter directly were related to decreased pathogenicity. To support this claim, we add some references in the updated manuscript line 662-664, 827-830.

(7) Serotonin: Does serotonin also reduce the virulence of S. marcescens?

Our primary result showed that serotonin indeed could reduce the virulence of S. marcescens (figure supplement 4), because the survival rate of adult flies was increased and the expression levels of virulence-related genes of S. marcescens alone in the case of serotonin.

(8) Figures 6D, E, H, I: The expression of key genes should be verified using quantitative real-time polymerase chain reaction (qRT-PCR), as scRNA-seq expression levels might not accurately reflect the true expression levels.

Bacterial single-cell RNA-seq can evaluate alterations in gene expression in the single-cell resolution. The expression of key genes screened by scRNA-seq was changed only in subpopulations, so the average expression of these genes would be comparable when mixed with a large population. We are afraid that qRT-PCR could be illegible to verify the expression of genes in subpopulations.

(9) Figure 7: The authors mentioned. "AMPs were supplemented to fly food". However, I could not find information regarding which AMPs and their respective concentrations (i.e., concentration of each AMP) were used in this study. This is a critical aspect of the research; therefore, details should be provided.

Thanks for your important suggestions. We used the antimicrobial peptide cecropin A, which is produced by silkworms. We provided this information in the methods line 487-488. The concentrations of cecropin A were added in Figure 7 legend.

(10) Figure 7: Delta AMP + AMP exhibited a stronger effect on the bacteria compared to AMP alone, indicating that immune effectors other than AMP may be involved. Since the IMD pathway is necessary for most immune effectors, including AMP, it would be interesting to test IMD pathway mutant animals and compare them with Delta AMP. Delta AMP + AMP exhibited a stronger effect on the bacteria compared to AMP alone. 

We appreciate this important question. Indeed, Delta AMP + AMP exhibited a stronger effect on the bacteria compared to AMP alone. We admitted that immune effectors other than AMP may be involved. Alternatively, mechanical force, to a less extent, accounted for the stronger effect on the bacteria (Explained by larvae agitation in figure supplement 2). To rule out this possibility, we examined the effect of total immune effectors on the bacterial load and the prodigiosin yield of S. marcescens using the IMD pathway mutant (RelE20 larvae). Our result showed that the optical density and yield of prodigiosin in Delta AMP group did not significantly differ from the ones in RelE20 group. Moreover, the load of S. marcescens associated with Delta AMP mutant was comparable to that of S. marcescens associated with RelE20 mutant. These results suggested that AMPs play a major role in recapitulating the response of _S. marcescens t_o larvae.

“To rule out the potential role of other immune effectors, we turned to the IMD pathway mutant RelE20 that is deficient in total immune effectors. Our result showed that the optical density and yield of prodigiosin in RelE20 group did not significantly differ from the ones in DAMP group (figure supplement 7A, B). Moreover, the load of S. marcescens associated with RelE20 mutant was comparable to that of S. marcescens associated with Delta AMP mutant (figure supplement 7C).”

We now added these results in the text line 326-331.

Author response:

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

Reviewer #2:

Line 295 – was the time post-infection, which varies considerably between groups and across samples, taken into consideration when comparison of response was between ChatCre mice (4-9 weeks post-infection) and WT mice (four to five weeks post-infection)?

Thank you for your comment. We did not originally assess the effects of time post-injection on DREADD response. Generally, AAV transgene expression has been demonstrated to be long-term and stable in the CNS of mice.[1] However, there is some variation in the reporting time of peak transgene expression[2], and this may potentially impact our results.

In investigating this issue further, we discovered an error in our reporting as we did have n = 1 wild-type mouse that underwent EMG recordings 62 days (~9 weeks) post-AAV injection. This has been corrected in the manuscript (lines 87-88).

Addressing this question is challenging due to the uneven distribution of time points within the 4–9-week windows for each group. Essentially, there were two groups per cohort, one studied at 4-5 weeks and one at 8-9 weeks. More specifically:

- Wild-type cohort: n = 10 animals were studied 28–33 days post-injection, and n = 1 at 62 days.

- ChAT-Cre cohort: n = 4 animals were studied 28–30 days post-injection, and n = 5 at 56–59 days.

We performed Pearson correlation analyses between time post-injection and diaphragm EMG response to DREADD activation (peak amplitude and area under the curve, AUC) for both cohorts (Author response image 1):

- ChAT-Cre: No significant correlations were found (peak amplitude: r² = -0.117, r = -0.1492, p = 0.702, Figure 1a-b; AUC:r² = -0.0883, r = 0.2184, p = 0.572, Figure 1c-d).

- Wild type: Initial analysis of all data showed significant correlations (peak amplitude:r² = 0.362, r = 0.6523, p = 0.0296, Figure 1a; AUC: r² = 0.347, r = 0.6424, p = 0.033, Figure 1c), suggesting a moderate positive correlation between time post-injection and EMG response. However, when the single 8–9-week wild-type mouse was excluded, these correlations were no longer significant (peak amplitude: r² = 0.172, r = 0.5142, p = 0.128, Figure 1b; AUC: r² = 0.23, r = 0.5614, p = 0.0913, Figure1d).

Comparing wild-type and ChAT-Cre groups directly was unreliable due to the single wild-type mouse studied at the later time point. We attempted to model time post-injection as a continuous variable (i.e., exact days post-injection) using a restricted maximum likelihood mixed linear model in JMP; however, the analysis could not be performed because there were not sufficient overlapping time points between the two cohorts (i.e., not all days post-injection were represented in both groups). To mitigate this, we binned animals into two groups: 4–5 weeks and 8–9 weeks post-injection. This analysis returned a significant interaction between cohort and time post-injection (p = 0.0391), however there were no significant multiple comparisons upon Tukey post hoc test (i.e., p > 0.05).

Based on these findings, we feel confident that time post-injection is unlikely to have a significant impact on diaphragm EMG response to DREADD activation in the ChAT-Cre cohort. However, in the wild-type cohort, it is difficult to draw definitive conclusions, as only one animal was studied at the 8–9-week time point. For similar reasons, it remains unclear whether the relationship between time post-AAV transduction and DREADD response differs between cohorts. Given the inconclusive nature of these results, we have elected not to include this analysis in the manuscript. Nevertheless, to ensure transparency, we have provided Author response image 1 below of peak amplitude and AUC plotted against time, allowing readers to evaluate the data independently.

Author response image 1.

Plots of diaphragm EMG peak amplitude (a-b) and area under the curve (c-d) vs. days post-AAV injection for wild-type (blue) and ChAT-Cre (orange) mice. Pearson correlation analyses were performed to assess the relationship between time post-AAV injection and diaphragm EMG DREADD response in wild-type and ChAT-Cre mouse cohorts. r², r, and p-values are shown in each panel for both cohorts. Panels a and c display peak amplitude and AUC, respectively, including all animals. Panels b and d present the same variables with the n = 1 wild-type mouse at the 9-week time point excluded; ChAT-Cre data is unchanged between corresponding panels. Scatter points represent data from individual animals. Polynomial trendlines are displayed for each cohort with wild-type in blue and ChAT-Cre in orange.

REFERENCES

(1) Kim, J. Y., Grunke, S. D., Levites, Y., Golde, T. E. & Jankowsky, J. L. Intracerebroventricular viral injection of the neonatal mouse brain for persistent and widespread neuronal transduction. J Vis Exp, 51863 (2014). https://doi.org/10.3791/51863

(2) Hollidge, B. S. et al. Kinetics and durability of transgene expression after intrastriatal injection of AAV9 vectors. Front Neurol 13, 1051559 (2022). https://doi.org/10.3389/fneur.2022.1051559

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

Response to reviewer’s public reviews:

We chose the dose of J60 based on a prior publication that established that off-target effects were possible at relatively high doses[1]. The dose that we used (0.1 mg/kg) was 30-fold less than the dose that was reported in that paper to potentially have off-target responses (3 mg/kg). Further, Author response image 1 shows the results of experiments in which J60 was given to animals that did not have the excitatory DREADD expressed in the spinal cord. This includes a sample of mice (n = 2) and rats (n = 3), recorded from using the same diaphragm EMG procedure described in the manuscript. The figure shows that there was no consistent response to the J60 at 0.1 mg/kg in the “control experiment” in which the DREADD was not expressed in the spinal cord.

Author response image 1.

Diaphragm EMG response to J60 administrated to naïve rats and mice. Panel a-b show raw EMG values at baseline, following vehicle (saline) and J60 administration for the left and right hemidiaphragm. Panel c-d shows EMG values normalized to baseline. Neither One-way RM ANOVA (panel a-b) nor paired t-test (panel c-d) returned significant p values (p < 0.05).

Response to specific reviewer comments:

Reviewer #1:

How old were the animals at the time of AAV injection, and in subsequent experiments?

The wildtype cohort of mice were 7-9 weeks old at time of AAV injection and DREADD experiments took place 4-5 weeks after AAV injection. ChAT-Cre mice were 6-10 weeks old at time of AAV injection and DREADD experiments took place 4-9 weeks after AAV injection. ChAT-Cre rats were 2-5 months old at time of AAV spinal injection. These animals underwent plethysmography recordings 3-4 months post-AAV injection and subsequently phrenic nerve recording 3-8 weeks later. These details have been added to the Method section.

How many mice were excluded from electrophysiology experiments due to deteriorating electrode contact?

No mice were excluded from electrophysiology experiments due to deteriorating electrode contact. If you are referring to the n = 1 excluded ChAT-Cre mouse (line 368) this animal was excluded because it showed no histological evidence of DREADD expression (lines 200-206).

What was the urethane dose?

The urethane dose for phrenic nerve recordings was 2.1 g/kg. See methods section line 395.

A graphical timeline of the experimental progression for plethysmography and electrophysiology studies would enhance clarity.

A graphical timeline has been added. See Figure S6.

Significance indicators in the figures would greatly enhance clarity. It is a little awkward to have to refer to supplemental tables to figure out statistical differences.

Significance indicators have been added. See Figures 1, 2, 4, and 5

In Figures 1, 2, and 5, individual data points should be shown, as in Fig 4.

Thank you for this suggestion. We agree that, in general, it is best practice to scatter individual data points. However, when we drafted the new figures, it was apparent that including individual scatter points, in this case, created very “cluttered” figures that were very difficult to interpret.

More detail regarding the plethysmography studies is needed. Was saline/J60 infused via a tail vein catheter? Were animals handled during the infusion? How long is the "IV" period? What volume of fluid was delivered?

All IV infusions were delivered via a tail vein catheter. Animals were not handled during infusion nor at any point during the recording. An IV catheter was externalized via a port in the plethysmograph allowing for IV infusion without handling of the animal or opening the plethysmograph. The infusion period for both saline and J60 was standardized to 2 minutes. The volume of fluid of both saline and J60 was standardized to 0.6 mL. This information has been added to the methods section (lines 408-410, 415-16, 419-420).

Reviewer #2:

The abstract could be improved by briefly highlighting the rationale, scope, and novelty of the study - the intro does a great job of highlighting the scope of the study and the research questions.

A brief explanation of the rationale, scope, and novelty of the study has been added to the abstract. See lines 2-8.

Line 18, specifies that this was done under urethane anesthesia.

This detail has been added to the abstract (line 20).

The methods section should be moved to the end of the manuscript according to Journal policy.

The methods section has been moved to the end of the manuscript.

The authors mention the use of both female and male rats but it is not indicated if they tested for and observed any differences between sexes across experiments.

We included the use of both male and female animals in this study to improve the generalizability of the results. However, we were not adequately powered for sex comparisons and therefore did not perform any statistical analysis to assess differences between sexes across experiments. Text has been added to the methods section (lines 534-537) to clarify.

Line 40, since delivery of J60 was performed in both IV and IP, this general statement should be updated.

This detail has been revised to include both IV and IP. See line 43.

Line 42. "First, we determined if effective diaphragm activation requires focal DREADD expression targeting phrenic motor neurons, or if non-specific expression in the immediate vicinity of the phrenic motor nucleus would be sufficient...." I don't think that in the experiments with wild-type mice the authors can claim that they selectively targeted the cervical propriospinal network (in isolation from the motoneurons). Given the fact that the histological analysis did not quantify interneurons or motoneurons in the spinal cord, authors should be cautious in proposing which neuronal population is activated in the non-specific approach.

We agree, and this was a poorly worded statement in our original text. We agree that wild-type DREADD expression was not limited to the cervical propriospinal networks but likely a mix of interneurons and motoneurons. The text has been edited to reflect that (see lines 56-60).

AAV virus source is not described.

All AAVs were obtained from the UF Powell Gene Therapy Center. Details of virus source and production have been added to the methods section. See lines 336-347.

Line 108-125. Because the diaphragm EMG recordings are only described for mice here, I would suggest editing this methods section to clearly state mice instead of vaguely describing "animals" in the procedure.

“Animals” has been changed to “mice” to avoid ambiguity.

Line 120, add parenthesis.

Parenthesis has been added.

Line 126. Whole body plethysmography protocol. Three hypercapnic hypoxic challenges are a lot for a rat within a 3-hour recording session in freely behaving rats. Did the authors verify with control/ vehicle experiments that repeated challenges in the absence of J60 do not cause potentiation of the response? I understand that it is not possible to invert the order of the injections (due to likely long-term effects of J60) or it is too late to perform vehicle and J60 injections on different days, but controls for repeated challenges should be performed in this type of experiment, especially considering the great variability in the response observed in Figure 4 (in normoxic conditions).

We did not conduct control experiments to assess the impact of repeated hypercapnic hypoxic challenges on the naïve response (i.e., in the absence of J60). However, our experimental protocol was designed such that each experimental period (i.e., post-vehicle or post-J60 infusion) was normalized to baseline recordings taken immediately prior to the vehicle or J60 infusion. While repeated exposure to hypercapnic hypoxic challenges may have altered respiratory output, we are confident that normalizing each experimental period to its respective baseline effectively captures the impact of DREADD activation on ventilation, independent of any potential potentiation that may have occurred due to gas challenge exposure. We have included raw values for all plethysmography outcomes (see Figure 4, panels a-c) to ensure full data transparency. Still, we believe that the baseline-normalized values more accurately reflect the impact of DREADD activation on the components of ventilation.

Furthermore, why the response to the hypercapnic hypoxic challenges are not reported? These could be very interesting to determine the effects of DREADD stimulation on chemosensory responses and enhance the significance of the study.

Response to the hypercapnic hypoxic challenges has been added to the manuscript. See Figure S3 and results section lines 162-167. Briefly, there were no statistically significant (p < 0.05) differences in tidal volume, respiratory rate, or minute ventilation between J60 vs sham condition during hypercapnic-hypoxic ventilatory challenges.

Line 200 - what is the reason behind performing a qualitative analysis of mCherry in various quadrants? This limits the interpretation of the results. If the authors used Chat-cre rats, the virus should only be in Chat+ MN. Knowing how selective the virus is, and whether its expression was selective for Phrenic MN versus other MN pools, could address several technical questions.

We agree that detailed quantification of expression by motoneuron pool would be of value in future work.  However, for these initial proof-of-concept experiments, we performed the quadrant-based qualitative analysis of mCherry expression to provide a simple comparison of mCherry expression between groups (i.e., ChAT-Cre vs. wildtype mice). This analysis allowed us to: 1) show the reader that each animal included in the study showed evidence of mCherry expression and 2) give the reader an idea of patterns of mCherry expression throughout the mid-cervical spinal cord. Additionally, it is important to note that while ChAT is a marker of motoneurons some populations of interneurons also express ChAT(2-4).

Given the increased values of Dia EMG AUC and no changes in respiratory rate, did the authors determine if there was a change in the inspiratory time with J60 administration?

We did not assess inspiratory time.

High death rate in DREADD WT mice - was histological analysis performed on these mice? Could it be due to the large volume injected into the spinal cord that affects not only descending pathways but also ascending ones? Or caused by neuronal death due to the large volume of viral solution in injected in mice.

Histological analysis was performed on these animals to assess mCherry expression only (i.e., no staining for NeuN or other markers was performed). While the reviewer's speculations are reasonable, we feel these reasons are unlikely to explain the death rate in DREADD WT mice as ChAT-Cre mice received the same volume injected into their spine and lived up until and during diaphragm EMG recordings. Additionally, WT mice lived for 4-5 weeks post-injection which would be past the acute phase that a large immune response to the viral dose would have occurred.

Line 299-304. Can you please clarify whether these rats were tested under anesthesia?

These rats were assessed under anesthesia. This detail has been added (line 146).

Given some of the unexpected results on cardiovascular parameters in urethane anesthetized rats, did the authors test the effects of J60 in the absence of AAV construct infection?

A small cohort (n = 2) of urethane anesthetized naïve wildtype rats were given the J60 ligand (IV, 0.1 mg/kg dose). We did observe a sudden drop in blood pressure after J60 administration that was sustained for the duration of the recording. One animal showed a 12% decrease in mean arterial blood pressure following J60 administration while the other showed a 35% decrease. Thus, it does appear that in this preparation the J60 ligand is producing a drop in arterial blood pressure.

Line 393. I believe this comment is referred to the intrapleural and diaphragmatic injection. Maybe this should clarified in the sentence.

This sentence has been revised for clarity (see lines 248-250).

Figures 1 and 2. It would be informative to show raw traces of the Diaphragm EMG to demonstrate the increase in tonic EMG. It is not possible to determine that from the integrated traces in Figures 1A and B.

Thank you for bringing up this concern. While the mean data in Figures 1F and 2F do indicate that, on average, animals had tonic diaphragm EMG responses to DREADD activation, the examples given in Figures 1A and 2A show minimal responses. This makes it difficult to fully appreciate the tonic response from those particular traces. However, clear tonic activity can be appreciated from Figures 5A and S2. In these figures, tonic activity is evident from the integrated EMG signals, presenting as a sustained increase in baseline activity between bursts—essentially an upward shift from the zero point.

References

(1) Van Savage, J. & Avegno, E. M. High dose administration of DREADD agonist JHU37160 produces increases in anxiety-like behavior in male rats. Behav Brain Res 452, 114553 (2023). https://doi.org/10.1016/j.bbr.2023.114553

(2) Mesnage, B. et al. Morphological and functional characterization of cholinergic interneurons in the dorsal horn of the mouse spinal cord. J Comp Neurol 519, 3139-3158 (2011). https://doi.org/10.1002/cne.22668

(3) Gotts, J., Atkinson, L., Yanagawa, Y., Deuchars, J. & Deuchars, S. A. Co-expression of GAD67 and choline acetyltransferase in neurons in the mouse spinal cord: A focus on lamina X. Brain Res 1646, 570-579 (2016). https://doi.org/10.1016/j.brainres.2016.07.001

(4) Alkaslasi, M. R. et al. Single nucleus RNA-sequencing defines unexpected diversity of cholinergic neuron types in the adult mouse spinal cord. Nat Commun 12, 2471 (2021). https://doi.org/10.1038/s41467-021-22691-2

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this manuscript, Eaton et al. examine the regulation of transcription directionality using a powerful genomic approach (more about the methodology below). Their data challenge the notion that the polyadenylation signal-reading Cleavage and Polyadenylation (CPA) complex is responsible for controlling promoter directionality by terminating antisense transcription. Namely, depletion of the required CPA factor RBBP6 has little effect on antisense transcription measured by POINT. They find instead that initiation is intrinsically preferential in the sense direction and additionally maintained by the activities of an alternative processing complex called Integrator, together with the kinase CDK9. In the presence of CDK9 activity, depletion of Integrator endoribonuclease INTS11 leads to globally increased transcription in the antisense direction, and minor effects in the sense direction. However, CDK9 inhibition reveals that sense transcription is also sensitive to INS11 depletion. The authors suggest that CDK9 activity is stronger in the sense direction, preventing INTS11-mediated premature termination of sense transcrpts.

Strengths:

The combination of acute depletion of the studied factors using degron approaches (important to limit possible secondary effects), together with novel and very sensitive nascent transcriptomics methods POINT and sPOINT is very powerful. The applied spike-in normalization means the analysis is more rigorous than most. Using this methodology allowed the authors to revisit the interesting question of how promoter/transcription directionality is determined.

The data quality appears very good and the fact that both global analysis as well as numerous gene-specific examples are shown makes it convincing.

The manuscript is well written and hence a pleasure to read.

We appreciate this positive assessment.

Weaknesses:

I am slightly worried about the reproducibility of the data - it is unclear to me from the manuscript if and which experiments were performed in replicate (lack of table with genomic experiments and GEO access, mentioned in more detail in below recommendations to authors), and the methods could be more detailed.

All sequencing data was deposited with GEO. Multiple biological replicates were performed for each sequencing experiment.  Bigwig files are presented as a table in the GEO submissions. This data has now been made public.

A separate discussion section would be useful, particularly since the data provided challenge some concepts in the field. How do the authors interpret U1 data from the Dreyfuss lab in light of their results? How about the known PAS-density directionality bias (more PAS present in antisense direction than in sense) - could the differential PAS density be still relevant to transcription directionality?

As suggested, we have expanded our discussion to relate our findings to existing data. We think the results from the Dreyfuss lab are very important and highlight the role of U1 snRNA in enforcing transcriptional elongation.  It does this in part by shielding PAS sequences.  Recent work from our lab also shows that U1 snRNA opposes the Restrictor complex and PNUTS, which otherwise suppress transcription (Estell et al., Mol Cell 2023).  Most recently, the Adelman lab has demonstrated that U1 snRNA generally enhances transcription elongation (Mimoso and Adelman., Mol Cell 2023).  Our work does not challenge and is not inconsistent with these studies.

The role of U1 in opposing PAS-dependent termination inspired the idea that antisense transcriptional termination may utilise PASs.  This was because such regions are rich in AAUAAA and comparatively poor in U1 binding sites. However, our RBBP6 depletion and POINT-seq data suggest that PAS-dependent termination is uncommon in the antisense direction. As such, other mechanisms suppress antisense transcription and influence promoter directionality. In our paper, we propose a major role for the Integrator complex.

We do not completely rule out antisense PAS activity and discuss the prior work that identified polyadenylated antisense transcripts. Nevertheless, this was detected by oligo-dT primed RT-PCR/Northern blotting, which cannot determine the fraction of non-polyadenylated RNA that could result from PAS-independent termination (e.g. by Integrator).  To do that requires an analysis of total nascent transcription as achieved by our POINT-seq.  Based on these experiments, Integrator depletion has a greater impact on antisense transcription than RBBP6 depletion. 

I find that the provided evidence for promoter directionality to be for the most part due to preferential initiation in the sense direction should be stressed more. This is in my eyes the strongest effect and is somehow brushed under the rug.

We agree that this is an important finding and incorporated it into the title and abstract.  As the reviewer recommends, we now highlight it further in the new discussion.

References 12-17 report an effect of Integrator on 5' of protein-coding genes, while data in Figure 2 appears contradictory. Then, experiments in Figure 4 show a global effect of INST11 depletion on promoter-proximal sense transcription. In my opinion, data from the 2.5h time-point of depletion should be shown alongside 1.5h in Figure 2 so that it is clear that the authors found an effect similar to the above references. I find the current presentation somehow misleading.

We are grateful for this suggestion and present new analyses demonstrating that our experiment in Figure 2 concurs with previous findings (Supplemental Figures 2A and B). Our original heatmap (Figure 2E) shows a very strong and general antisense effect of INTS11 loss. On the same scale, the effects in the sense direction are not as apparent, which is also the case using metaplots.  New supplemental figure 2A now shows sense transcription from this experiment in isolation and on a lower scale, demonstrating that a subset of genes shows promoter-proximal increases in transcription following INTS11 depletion.  This is smaller and less general than the antisense effect but consistent with previous findings.  Indeed, our new analysis in supplemental figure 2B shows that affected protein-coding genes are lowly expressed, in line with Hu et al., Mol Cell 2023. This explains why a sense effect is not as apparent by metaplot, for which highly expressed genes contribute the most signal.

As a result of our analyses, we are confident that the apparently larger effect at the 2.5hr timepoint (Figure 4) that we initially reported is due to experimental variability and not greater effects of extended INTS11 depletion. Overlaying the 1.5h and 2.5h datasets (Supplemental Figure 4B) revealed a similar number of affected protein-coding genes with a strong (83%) overlap between the affected genes.  To support this, we performed qPCR on four affected protein-coding transcripts which revealed no significant difference in the level of INTS11 effect after 2.5h vs 1.5h (Supplemental Figure 4C).

We now present data for merged replicates in Figures 2 and 4 which reveal very similar average profiles for -INTS11 vs +INTS11 at both timepoints. Overall, we believe that we have resolved this discrepancy by showing that it amounts to experimental variability and because the most acutely affected protein-coding genes are lowly expressed. As detailed above, we show this in multiple ways (and validate by qPCR) We have revised the text accordingly and removed our original speculation that differences reflected the timeframe of INTS11 loss.

Conclusion/assessment:

This important work substantially advances our understanding of the mechanisms governing the directionality of human promoters. The evidence supporting the claims of the authors is compelling, with among others the use of advanced nascent transcriptomics including spike-in normalization controls and acute protein depletion using degron approaches.

In my opinion, the authors' conclusions are in general well supported.

Not only the manuscript but also the data generated will be useful to the wide community of researchers studying transcriptional regulation. Also, the POINT-derived novel sPOINT method described here is very valuable and can positively impact work in the field.

We are grateful for the reviewers' positive assessment of our study.

Reviewer #2 (Public Review):

Summary:

Eaton and colleagues use targeted protein degradation coupled with nascent transcription mapping to highlight a role for the integrator component INST11 in terminating antisense transcription. They find that upon inhibition of CDK9, INST11 can terminate both antisense and sense transcription - leading to a model whereby INST11 can terminate antisense transcription and the activity of CDK9 protects sense transcription from INST11-mediated termination. They further develop a new method called sPOINT which selectively amplifies nascent 5' capped RNAs and find that transcription initiation is more efficient in the sense direction than in the antisense direction. This is an excellent paper that uses elegant experimental design and innovative technologies to uncover a novel regulatory step in the control of transcriptional directionality.

Strengths:

One of the major strengths of this work is that the authors endogenously tag two of their proteins of interest - RBBP6 and INST11. This tag allows them to rapidly degrade these proteins - increasing the likelihood that any effects they see are primary effects of protein depletion rather than secondary effects. Another strength of this work is that the authors immunoprecipitate RNAPII and sequence extracted full-length RNA (POINT-seq) allowing them to map nascent transcription. A technical advance from this work is the development of sPOINT which allows the selective amplification of 5' capped RNAs < 150 nucleotides, allowing the direction of transcription initiation to be resolved.

We appreciate this positive assessment.

Weaknesses:

While the authors provide strong evidence that INST11 and CDK9 play important roles in determining promoter directionality, their data suggests that when INST11 is degraded and CDK9 is inhibited there remains a bias in favour of sense transcription (Figures 4B and C). This suggests that there are other unknown factors that promote sense transcription over antisense transcription and future work could look to identify these.

We agree that other (so far, unknown) factors promote sense transcription over antisense, which was demonstrated by our short POINT.  We have provided an expanded discussion on this in the revision. In our opinion, demonstrating that sense transcription is driven by preferential initiation in that direction is a key finding and we agree that the identification of the underlying mechanism constitutes an interesting avenue for future study.

Reviewer #3 (Public Review):

Summary:

Using a protein degradation approach, Eaton et al show that INST11 can terminate the sense and anti-sense transcription but higher activity of CDK9 in the sense direction protects it from INS11-dependent termination. They developed sPOINT-seq that detects nascent 5'-capped RNA. The technique allowed them to reveal robust transcription initiation of sense-RNA as compared to anti-sense.

Strengths:

The strength of the paper is the acute degradation of proteins, eliminating the off-target effects. Further, the paper uses elegant approaches such as POINT and sPOINT-seq to measure nascent RNA and 5'-capped short RNA. Together, the combination of these three allowed the authors to make clean interpretations of data.

We appreciate this positive assessment.

Weaknesses:

While the manuscript is well written, the details on the panel are not sufficient. The methods could be elaborated to aid understanding. Additional discussion on how the authors' findings contradict the existing model of anti-sense transcription termination should be added.

We have added more detail to the figure panels, which we hope will help readers to navigate the paper more easily. Specifically, the assay employed for each experiment is indicated in each figure panel. As requested, we provide a new and separate discussion section in the revision.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Congratulations on this important piece of work!

Some specific suggestions.

MAJOR

-The data are not available (Accession "GSE243266" is currently private and is scheduled to be released on Sep 01, 2026.) This should be corrected and as a minimum, the raw sequencing files as well as the spike-in scaled bigwig files should be provided in GEO.

We have made the data public. Raw and bigwig files are provided as part of the GEO upload.

MINOR

- It would be useful for readers if you could include catalog numbers of the reagents used in the study.

We have included this information in our revision.

- A table in experimental procedures summarizing the genomic experiments performed in this study as well as published ones reanalyzed here would be helpful.

This is now provided as part of the resources table.

- It would be easier for reviewers to evaluate the manuscript if the figure legends were included together with the figures on one page. This is now allowed by most journals.

We have used this formatting in the revision.

- Providing some captions for the results sections would be helpful.

We have included subheadings as suggested.

Reviewer #2 (Recommendations For The Authors):

Generally, I would suggest writing the experiment-type above panels where it is not immediately obvious what they are so a reader can appreciate the figures without referencing the legend. E.g. write POINT-seq on Figure 1B just to make it obvious to someone looking at the figures what methodology they are looking at. Likewise, you could write RNAPII ChIP-seq for Supplementary Figures 3D and 3E.

We have carried out this recommendation.

Can a y-axis be indicated on POINT-seq genome browser tracks? This could make them easier to interpret.

Y-axis scales are provided as RPKM as stated in the figure legends.

The authors could address/speculate in the text why there is less POINT-seq signal for the antisense transcript in the treatment condition in Figure 1B? Or could consider including a different example locus where this is not the case for clarity.

Acute depletion of poly(A) factors (like RBBP6) results in a strong read-through beyond the poly(A) signal of protein-coding genes as Figure 1 shows.  However, it also causes a reduction in transcription levels, which can be seen in the figure and is correctly noted by the reviewer in this comment.  We see this with other poly(A) factor depletions (e.g. CPSF73 and CPSF30 – Eaton et al., 2020 and Estell et al., 2021) and other labs have observed this too (e.g for CPSF73-dTAG depletion (Cugusi et al., Mol Cell 2022)).  Plausible reasons include a limited pool of free RNAPII due to impaired transcriptional termination or limited nucleotide availability due to their incorporation within long read-through transcripts. For these reasons, we have retained the example in Figure 1B as a typical representation of the effect. Moreover, the heatmap in Figure 1D fairly represents the spectrum of effects following RBBP6 loss – highlighting the strong read-through beyond poly(A) signals and the marginal antisense effects.

"The established effect of INTS11 at snRNAs was detected in our POINT-seq data and demonstrates the efficacy of this approach (Figure 2B)." The authors could explain this point more clearly in the text and describe the data - e.g. As expected, depletion of INTS11 leads to increased POINT-seq signal at the 3' end of snRNAs, consistent with defects in transcriptional termination. This is highlighted by the RNU5A-1 and RNU5B-1 loci (Figure 2B).

We agree and have added more context to clarify this.

I would suggest adjusting the scale of the heatmap in Figure 2E - I think it would be easier to interpret if the value of 0 was white - with >0 a gradient of orange and <0 a gradient of blue (as is done in Figure 1C). I think making this change would make the point as written in the text clearer i.e. "heatmap analysis demonstrates the dominant impact of INTS11 on antisense versus sense transcription at most promoters (Figure 2E)." I'm assuming most of the sense transcription would be white (more clearly unchanging) when the scale is adjusted.

We agree and have done this. The reviewer is correct that most sense transcription is unchanged by INTS11 loss.  However, as we alluded to in the original submission, a subset of transcripts shows a promoter-proximal increase after INTS11 depletion. We have expanded the analyses of this effect (see responses to other comments) but stress that it is neither as general nor as large as the antisense effect.

The authors make the point that there is mildly increased transcription over the 5' end of some genes upon INST11 depletion and show a track (Supplementary Fig 2A). It is not immediately obvious from the presentation of the meta-analysis in Figure 2D how generalisable this statement is. Perhaps the size of the panel or thickness of the lines in Figure 2D could be adjusted so that the peak of the control (in blue) could be seen. Perhaps an arrow indicating the peak could be added? I'm assuming the peak at the TSS is slightly lower in the control compared to INST11 depletion based on the authors' statement.

We have provided multiple new analyses of this data to highlight where there are promoter-proximal effects of INTS11 loss in the sense direction.  Please see our response to the public review of reviewer 1 and new supplemental figures 2A, 2B, 4A and 4B which highlight the sense transcription increased in the absence of INTS11.

The authors label Figure 4 "Promoters lose their directionality when CDK9 is inhibited" - but in INST11 depleted cells treated with CDK9i they find that there still is a bias towards sense transcription. Suggested edit "Some promoter directionality is lost when CDK9 is inhibited" or similar.

We agree and have made this change.

The authors conclude that INTS11-mediated effects are the result of perturbation of the catalytic activities of Integrator, the authors should perform rescue experiments with the catalytically dead E203Q-INTS11 mutant.

This is a very good suggestion and something we had intended to pursue.  However, as we will describe below (and shown in Supplemental Figure 4G), there were confounding issues with this experiment.

The E203Q mutant of INTS11 is widely used in the literature to test for catalytic functions of INTS11.  However, we have found that this mutation impairs the ability of INTS11 to bind other Integrator modules in cells. Based on co-immunoprecipitation of flag-tagged WT and E203Q derivatives, INTS1 (backbone module), 10 (tail module), and 8 (phosphatase module) all show reduced binding to E203Q vs. WT. Because E203Q INTS11 is defective in forming Integrator complexes, rescue experiments might not fully distinguish the effects of INTS11 activity from those caused by defects in complex assembly. While this may at first seem unexpected, in the analogous 3’ end processing complex, catalytic mutants of CPSF73 (which is highly related to INTS11) negatively affect its interaction with other complex members (Kolev and Steitz, EMBO Reports 2005).

We hypothesise that INTS11 activity is most likely involved in attenuating promoter-proximal transcription, but we cannot formally rule out other explanations and discuss this in our revision. Regardless of how INTS11 attenuates transcription, our main conclusion is on its requirement to terminate antisense transcription whether this involves its cleavage activity or not.

The authors suggest that CDK9 modulates INTS11 activity/assembly and suggest this may be related to SPT5. Is there an effect of CDK9 inhibition on the snRNA's highlighted in Figure 2B?

We believe that snRNAs are different from protein-coding genes concerning CDK9 function. Shona Murphy’s lab previously showed that, unlike protein-coding genes, snRNA transcription is insensitive to CDK9 inhibition, and that snRNA processing is impaired by CDK9 inhibition (Medlin et al., EMBO 2003 and EMBO 2005).  We reproduce these findings by metaanalysis of 15 highly expressed and well-separated snRNAs and by qRT-PCR of unprocessed RNU1-1, RNU5A-1 and RNU7-1 snRNA following CDK9 inhibition. We observe snRNA read-through by POINT-seq following INTS11 loss whether CDK9 is inhibited or not (left panel, below). Note the higher TES proximal signal in CDK9i conditions, which likely reflects the accumulation of unprocessed snRNA as validated by qPCR for three example snRNAs (right panel, below).

Author response image 1.

For Figure 4, would similar results be observed using inhibitors targeting other transcriptional CDKs such as CDK7,12/13?

In response to this suggestion, we analysed four selected protein-coding transcripts (the same 4 that we used to validate the CDK9i results) by qRT-PCR in a background of CDK7 inhibition using the THZ2 compound (new Supplemental Figure 4E).  THZ2 suppresses transcription from these genes as expected.  Interestingly, expression is restored by co-depleting Integrator, recapitulating our findings with CDK9 inhibition.  As CDK7 is the CDK-activating kinase for CDK9, its inhibition will also inhibit CDK9 so THZ2 may simply hit this pathway upstream of where CDK9 inhibitors.  Second, CDK7 may independently shield transcription from INTS11.  We allude to both interesting possibilities.

What happens to the phosphorylation state of anti-sense engaged RNAPII when INTS11 is acutely depleted and/or CDK9 is inhibited? This could be measured by including Ser5 and Ser2 antibodies in the sPOINT-seq assay and complemented with Western Blot analysis.

We have performed the western blot for Ser5 and Ser2 phosphorylation as suggested.  Both signals are mildly enhanced by INTS11 loss, which is consistent with generally increased transcription.  Ser2p is strongly reduced by CDK9 inhibition, which is consistent with the loss of nascent transcription in this condition.  Interestingly, both modifications are partly recovered when INTS11 is depleted in conjunction with CDK9 inhibition. This is consistent with the effects that we see on POINT-seq and shows that the recovered transcription is associated with some phosphorylation of RNAPII CTD.  This presumably reflects the action(s) of kinases that can act redundantly with CDK9.

We have not performed POINT-seq with Ser5p and Ser2p antibodies under these various conditions.  Our rationale is that our existing data uses an antibody that captures all RNAPII (regardless of its phosphorylation status), which we feel most comprehensively assays transcription in either direction. Moreover, the lab of Fei Chen (Hu et al., Mol Cell 2023) recently published Ser5p and Ser2p ChIP-seq following INTS11 loss. By ChIP-seq, they observe a bigger increase in antisense RNAPII occupancy vs. sense providing independent and orthogonal support for our POINT-seq data.  Interestingly, this antisense increase is not paralleled by proportional increases in Ser5p or Ser2p signals.  This suggests that the unattenuated antisense transcription resulting from INTS11 loss does not have high Ser5p or Ser2p.  Since CDK7 and 9 are major Ser5 and 2 kinases, this supports our model that their activity is less prevalent for antisense transcription.  We now discuss these data in our revision.   

The HIV reporter RNA experiments should be performed with the CDK9 inhibitor added to the experimental conditions. Presumably CDK9 inhibition would result in no upregulation of the reporter upon addition of TAT and/or dTAG. Perhaps the amount of TAT should be reduced to still have a dynamic window in which changes can be detected. It is possible that reporter activation is simply at a maximum. Can anti-sense transcription be measured from the reporter?

We have performed the requested CDK9 inhibitor experiment to confirm that TAT-activated transcription from the HIV promoter is CDK9-dependent (new supplemental figure 4F).  Consistent with previous literature on HIV transcription, CDK9 inhibition attenuates TAT-activated transcription.  Importantly, and in line with our other experiments, depletion of INTS11 results in significant restoration of transcription from the HIV promoter when CDK9 is inhibited. Thus, TAT-activated transcription is CDK9-dependent and, as for endogenous genes, CDK9 prevents attenuation by INTS11.

While TAT-activated transcription is high, we do not think that the plasmid is saturated. When considering this question, we revisited previous experiments using this system to study RNA processing (Dye et al., Mol Cell 1999, Cell 2001, Mol Cell 2006). In these cases, mutations in splice sites or polyadenylation sites have a strong effect on RNA processing and transcription around HIV reporter plasmids. Effects on transcription and RNA processing are; therefore, apparent in the appropriate context. In contrast, we find that the complete elimination of INTS11 has no impact on RNA output from the HIV reporter. Our original experiment assessing the impact of INTS11 loss in +TAT conditions used total RNA.  One possibility is that this allows non-nascent RNA to accumulate which might confound our interpretation of INTS11 effects on ongoing transcription.  However, the new experiment described in the paragraph above was performed on chromatin-associated (nascent) RNA to rule this out.  This again shows no impact of INTS11 loss on HIV promoter-derived transcription in the presence of TAT.

To our knowledge, antisense transcription is not routinely assayed from plasmids. They generally employ very strong promoters (e.g. CMV, HIV) to drive sense transcription.  Crucially, their circular nature means that RNAPII going around the plasmid could interfere with antisense transcription coming the other way which does not happen in a linear genomic context. This is why we restricted our use of plasmids to looking at the effects of stimulated CDK9 recruitment (via TAT) on transcription rather than promoter directionality.   

The authors should clearly state how many replicates were performed for the genomics experiments. Ideally, a signal should be quantified and compared statistically rather than relying on average profiles only.

We have stated the replicate numbers for sequencing experiments in the relevant figure legends. All sequencing experiments were performed in at least two biological replicates, but often three. In addition, we validated their key conclusions by qPCR or with orthogonal sequencing approaches.

Reviewer #3 (Recommendations For The Authors):

The authors provide strong evidence in support of their claims.

ChIP-seq of pol2S5 and S2 upon INST11 and CDK9 inhibition will strengthen the observation that transcription in the sense direction is more efficient.

We view the analysis of total RNAPII as the most unbiased way of establishing how much RNAPII is going one way or the other. Importantly, ChIP-seq was very recently performed for Ser2p and Ser5p RNAPII derivatives in the lab of Fei Chen (Hu et al., Mol Cell 2023). Their data shows that loss of INTS11 increases the occupancy of total RNAPII in the antisense direction more than in the sense direction, which is consistent with our finding. Interestingly, the increased antisense RNAPII was not paralleled with an increase in Ser2p or Ser5p. This suggests that, following INTS11 loss, the unattenuated antisense transcription is not associated with full/normal Ser2p or Ser5p. These modifications are normally established by CDK7 and 9; therefore, this published ChIP-seq suggests that they are not fully active on antisense transcription when INTS11 is lost. This supports our overall model that CDK9 (and potentially CDK7 as suggested for a small number of genes in new Supplemental Figure 4E) is more active in the sense direction to prevent INTS11-dependent attenuation. We now discuss these data in our revision.

In Supplementary Figure 2, the eRNA expression increases upon INST11 degradation, I wonder if the effects of this will be appreciated on cognate promoters? Can the authors test some enhancer:promoter pairs?

We noticed that some genes (e.g. MYC) that are regulated by enhancers show reduced transcription in the absence of INTS11. Whilst this could suggest a correlation, the transcription of other genes (e.g. ACTB and GAPDH) is also reduced by INTS11 loss although they are not regulated by enhancers.  A detailed and extensive analysis would be required to establish any link between INTS11-regulated enhancer transcription and the transcription of genes from their cognate promoters.  We agree that this would be interesting, but it seems beyond the scope of our short report on promoter directionality.

Line 111, meta plot was done of 1316 genes. Details on this number should be provided. Overall, the details of methods and analysis need improvement. The layout of panels and labelling on graphs can be improved.

We have now explained the 1316 gene set.  In essence, these are the genes separated from an expressed neighbour by at least 10kb.  This distance was selected because depletion of RBBP6 induces extensive read-through transcription beyond the polyadenylation site of protein-coding genes.  To avoid including genes affected by transcriptional read-through from nearby transcription units we selected those with a 10kb gap between them. This was the only selection criteria so is unlikely to induce any unintended biases. Finally, we have added more information to the figure panels and their legends, which we hope will make our manuscript more accessible.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This useful study integrates experimental methods from materials science with psychophysical methods to investigate how frictional stabilities influence tactile surface discrimination. The authors argue that force fluctuations arising from transitions between frictional sliding conditions facilitate the discrimination of surfaces with similar friction coefficients. However, the reliance on friction data obtained from an artificial finger, together with the ambiguous correlative analyses relating these measurements to human psychophysics, renders the findings incomplete.

Our main goal with this paper was to show that the most common metric, i.e. average friction coefficient—widely used in tactile perception and device design – is fundamentally unsound, and to offer a secondary parameter that is compatible with the fact that human motion is unconstrained, leading to dynamic interfacial mechanics.

We understand the Reviewers wanted, through biomechanical measurements, to demonstrate that humans using instabilities. This is seemingly reasonable, but in individual responses, we explain the significant challenges and fundamental unknowns to those experiments. We believe this paper sets forth an important step to approach this problem. At the same time, we have made several changes in the discussion, conclusion, and title to clarify that our study is correlative between mechanical characterization and human testing.

In short, there are still several fundamental unknowns that prevented us from basing the study around biomechanical measurements: (1) a decision-making model would need to be created, but it is unknown if tactile decision making follows other models, (2) it is further unknown what constitutes “tactile evidence”, though at our manuscript’s conclusion, we propose that friction instabilities are better suited for to be tactile evidence than the averaging of friction coefficients from a narrow range of human exploration (3) in the design of samples, from a friction mechanics and materials perspective, it is not at this point, possible to pre-program surfaces a priori to deliver friction instabilities and instead must be experimentally determined – especially when attempting to achieve this in controlled surfaces that do not create other overriding tactile cues, like macroscopic bumps or large differences in surface roughness. (4) Given that the basis for tactile percepts, like which object feels “rougher” or “smoother” is not sufficiently established, it is necessary to use a 3-alternative forced choice task which avoids asking objects along a preset perceptual dimension – a challenge recognized by Reviewer 3. However, this would bring in issues of memory in the decision-making model. (5) The prior points are compounded by the fact that, we believe, tactile exploration must be performed in an unconstrained manner, i.e., without an apparatus generating motion onto a stationary finger. Work by Liu et al. (IEEE ToH, 2024) showed that recreating friction obtained during free exploration onto a stationary finger was uninterpretable by the participants, hinting at the importance of efference copies.[1] We believe that many of the above-mentioned issues constitutes a significant advance in knowledge and would require discussion and dissemination with the community.

Our changes to the manuscript

Page 1 & SI Page 1, Title

“Alternatives to Friction Coefficient: Fine Touch Perception Correlates with Frictional Instabilities”

Reviewer 1 (Public review):

Summary:

In this paper, Derkaloustian et. al look at the important topic of what affects fine touch perception. The observations that there may be some level of correlation with instabilities are intriguing. They attempted to characterize different materials by counting the frequency (occurrence #, not of vibration) of instabilities at various speeds and forces of a PDMS slab pulled lengthwise over the material. They then had humans make the same vertical motion to discriminate between these samples. They correlated the % correct in discrimination with differences in frequency of steady sliding over the design space as well as other traditional parameters such as friction coefficient and roughness. The authors pose an interesting hypothesis and make an interesting observation about the occurrences of instability regimes in different materials while in contact with PDMS, which is interesting for the community to see in the publication. It should be noted that the finger is complex, however, and there are many factors that may be quite oversimplified with the use of the PDMS finger, and the consideration and discounting of other parameters are not fully discussed in the main text or SI. Most importantly, however, the conclusions as stated do not align with the primary summary of the data in Figure 2.

Strengths:

The strength of this paper is in its intriguing hypothesis and important observation that instabilities may contribute to what humans are detecting as differences in these apparently similar samples.

We thank Reviewer 1 for their time on the manuscript, recognizing the approach we took, and offering constructive feedback. We believe that our conclusions, in fact, are supported by the primary summary of the data in Fig. 2 but we believe that our use of R² could have led to misinterpretation. The trend with friction coefficient and percent correct was indeed statistically significant but was spurious because the slope was negative. In the revision, we add clarifying comments throughout, change from R² to r as to highlight the negative trend, and adjust the figures to better focus on friction coefficient.

Finally, we added a new section to discuss the tradeoffs between using a real human finger versus a mock finger, and which situations may warrant the use of one or the other. In short, for our goal of characterizing surfaces to be used in tactile experiments, we believe a mock finger is more sustainable and practical than using real humans because human fingers are unique per participant, humans move their fingers at constantly changing pressures and velocities, and friction generated during free exploring human cannot be satisfactorily replicated by moving a sample onto a stationary finger. But, we do not disagree that for other types of experiments, characterizing a human participant directly may be more advantageous.

Weaknesses:

Comment 1

The most important weakness is that the findings do not support the statements of findings made in the abstract. Of specific note in this regard is the primary correlation in Figure 2B between SS (steady sliding) and percent correct discrimination. Of specific note in this regard is the primary correlation in Figure 2B between SS (steady sliding) and percent correct discrimination. While the statistical test shows significance (and is interesting!), the R-squared value is 0.38, while the R-squared value for the "Friction Coefficient vs. Percent Correct" plot has an R-squared of 0.6 and a p-value of < 0.01 (including Figure 2B). This suggests that the results do not support the claim in the abstract: "We found that participant accuracy in tactile discrimination was most strongly correlated with formations of steady sliding, and response times were negatively correlated with stiction spikes. Conversely, traditional metrics like surface roughness or average friction coefficient did not predict tactile discriminability."

We disagree that the trend with friction coefficient suggests the results do not support the claim because the correlation was found to be negative. However, we could have made the comparison more apparent and expanded on this point, given its novelty.

While the R² value corresponding to the “Friction Coefficient vs. Percent Correct” plot is notably higher, our results show that the slope is negative, which would be statistically spurious. This is because a negative correlation between percent correct (accuracy in discriminating surfaces) and difference in friction coefficient means that the more similar two surfaces are (by friction coefficient), the easier it would be for people to tell them apart. That is, it incorrectly concludes that two identical surfaces would be much easier to tell apart than two surfaces with greatly different friction coefficients.

This is counterintuitive to nearly all existing results, but we believe our samples were well-positioned to uncover this trend by minimizing variability, by controlling multiple physical parameters in the samples, and that the friction coefficient — typically calculated in the field as an average friction coefficient — ignores all the dynamic changes in forces present in elastic systems undergoing mesoscale friction, i.e., human touch, as seen in Fig. 1 in a mock finger and Fig. 3 in a real finger. By demonstrating this statistically spurious trend, we believe this strongly supports our premise that an alternative to friction coefficient is needed in the design of tactile psychophysics and haptic interfaces.

We believe that this could have been misinterpreted, so we took several steps to improve clarity, given the importance of this finding: we separated the panel on friction coefficient to its own panel, we changed from R² to r throughout, and we added clarifying text. We also added a small section focusing on this spurious trend.

Our changes to the manuscript

Page 1, Abstract

“In fact, the typical method of averaging friction coefficients led to a spurious correlation which erroneously suggests that distinct objects should feel identical and identical objects should feel distinct.”

Page 7

“As Fig. 1 was constructed from friction measurements, we can also calculate an average friction coefficient, µ, by averaging the friction coefficient obtained at each of the 16 combinations of masses and velocities (Table 1). This calculation is a standard approach in tactile studies for summarizing friction measurements, or in some cases, surfaces are never characterized at multiple masses and velocities. However, summarizing friction data in this manner has been considered as conceptually questionable by others from a mechanics perspective.[3] Fig. 1 shows that the type of instabilities and friction forces encountered on a single surface can vary widely depending on the conditions. As a result, large variations in the friction coefficient are expected, depending on the mass and velocity — even though measurements originate from the same surface. This variability in friction coefficient can be seen with the large interquartile range of friction coefficients, which shows that the variation in friction coefficient across a single surface is similar, or even larger, than the differences in average friction coefficient across two different surfaces. The observation that friction coefficients vary so widely on a single surface calls into question the approach of analyzing how humans may perceive two different objects based on their average friction coefficients.”

Page 9, Fig. 2 Caption

“D) GLMM of accuracy vs. difference in average friction coefficient , showing a negative correlation. E) GLMMs of accuracy vs. other commonly used material properties or parameters: ΔAverage roughness R_a, ΔHurst exponent H, and ΔWater contact angle hysteresis (º) (N = 10 participants_, _n = 600 total trials).”

Page 9

“Considering all instabilities individually, we found that only steady sliding was a positive, statistically significant predictor. (r \= 0.62, p < 0.05, shown in Fig. 2B).”

Page 10

“To compare the value of looking at frictional instabilities, we also performed GLMM fits on common approaches in the field, like a friction coefficient or material property typically used in tactile discrimination, shown in Fig. 2D-E. Interestingly, in Fig. 2D, we observed a spurious, negative correlation between friction coefficient (typically and often problematically simplified as across all tested conditions) and accuracy (r = -0.64, p < 0.01); that is, the more different the surfaces are by friction coefficient, the less people can tell them apart. This spurious correlation would be the opposite of intuition, and further calls into question the common practice of using friction coefficients in touch-related studies. Interestingly, this spurious correlation was also found by Gueorguiev et al.[21] The alternative, two-term model which includes adhesive contact area for friction coefficient[32] was even less predictive (see Fig. S6A of SI). We believe such a correlation could not have been uncovered previously as our samples are minimal in their physical variations. Yet, the dynamic changes in force even within a single sample are not considered, despite being a key feature of mesoscale friction during human touch.

We investigate different material properties in Fig. 2E. Differences in average roughness R_a (or other parameters, like root mean square roughness R_rms (Fig. S6A of SI) did not show a statistically significant correlation to accuracy. Though roughness is a popular parameter, correlating any roughness parameter to human performance here could be moot: the limit of detecting roughness differences has previously been defined as 13 nm on structured surfaces[36] and much higher for randomly rough surfaces,[49] all of which are magnitudes larger than the roughness differences between our surfaces. The differences in contact angle hysteresis – as an approximation of the adhesion contributions[50] – do not present any statistically significant effects on performance.”

Page 11-12

“Despite the correlative nature of this study, we still obtained high correlations compared to existing biomechanical studies[4,19,21], which we speculate is because instabilities are an important predictive phenomenon for models of human touch. We believe that biomechanical studies, including more sophisticated techniques, like spatially resolved force maps from digital image correlation[5,42] may yield stronger correlations and results if they analyze data based on instabilities.

Added References

(2) Khamis, H. et al. Friction sensing mechanisms for perception and motor control: passive touch without sliding may not provide perceivable frictional information. J. Neurophysiol. 125, 809– 823 (2021).

(6) Olczak, D., Sukumar, V. & Pruszynski, J. A. Edge orientation perception during active touch. J. Neurophysiol. 120, 2423–2429 (2018).

Comment 2, Part 1

Along the same lines, other parameters that were considered such as the "Percent Correct vs. Difference in Sp" and "Percent Correct vs. Difference in SFW" were not plotted for consideration in the SI. It would be helpful to compare these results with the other three metrics in order to fully understand the relationships.

We have added these plots to the SI. We note that we had checked these relationships and discussed them briefly, but did not include the plot. The plots show that the type of instability was not as helpful as its presence or absence.

Our changes to the manuscript

Page 9

“Furthermore, a model accounting for slow frictional waves alone specifically shows a significant, negative effect on performance (p < 0.01, Fig. S5 of SI), suggesting that in these samples and task, the type of instability was not as important.”

“Fig. S5. GLMM fits of participant accuracy vs. the differences in instability incidence for individual instability types. Left: accuracy vs. differences in formation of slow frictional waves (SFW) between pairs. P1 and P5 have the same x-axis value and are shifted for clarity. Right: accuracy vs. differences in formation of stiction spikes (Sp).”

SI Page 4

“and no correlation between accuracy and stiction spikes (Fig. S5).”

Comment 2, Part 2

Other parameters such as stiction magnitude and differences in friction coefficient over the test space could also be important and interesting.

We agree these are interesting and have thought about them. We are aware that others, like Gueorguiev et al., have studied stiction magnitudes, and though there was a correlation, the physical differences in surface roughness (glass versus PMMA) investigated made it unclear if these could be generalized further.[3] We are unsure how to proceed here with a satisfactory analysis of stiction magnitude, given that stiction spikes are not always generated. In fact, Fig. 1 shows that for many velocities and pressures, stiction spikes are not formed. In ongoing work, however, we are always cognizant that if stiction spikes are a dominant factor, then a secondary analysis on their magnitude would be important. We offer some speculation on why stiction spikes may be overrepresented in the literature:

(1) They are prone to being created if the finger was loaded for a long time onto a surface prior to movement, thus creating adhesion by contact aging which is unlike active human exploration. We avoid this by discarding the first pull in our measurements, which is a standard practice in mechanical characterization if contact aging needs to be avoided.

(2) The ranges of velocities and pressures explored by others were small.

(3) In an effort to generate strong tactile stimuli, highly adhesive or rough surfaces are used.

(4) Stiction spikes are visually distinctive on a plot, but we are unaware of any mechanistic reason that mechanoreceptors would be particularly sensitive to this low frequency event over other signals.

We interpret “difference in friction coefficient over the test space” to be, for a single surface, like C4, to find the highest average friction for a condition of single velocity and mass and subtract that from the lowest average friction for a condition of single velocity and mass. We calculated the difference in friction coefficient in the typical manner of the field, by averaging all data collected at all velocities and masses and assigning a single value for all of a surface, like C4. We had performed this, and have the data, but we are wary of overinterpreting secondary and tertiary metrics because they do not have any fundamental basis in traditional tribology, and this value, if used by humans, would suggest that they rapidly explore a large parameter space to find a “maximum” and “minimum” friction. Furthermore, the range in friction across the test space, after averaging, can be smaller than the range of friction experienced at different masses and velocities on a single surface. We have tabulated and newly included these values (the interquartile range of friction coefficients of different masses and velocities per surface) in Table 1.

Fig. 2D shows a GLMM fit between percent correct responses across our pairs and the differences in friction coefficient for each pair, where we see a spurious negative correlation. As we had the data of all average friction coefficients for each condition for a given material, we also looked at the difference in maximum and minimum friction coefficients. For our tested pairs, these differences also lined up on a statistically significant, negative GLMM fit (r = -0.86, p < 0.005). However, the values for a given surface can vary drastically, with an interquartile range of 1.20 to 2.09 on a single surface. We fit participant accuracy to the differences in these IQRs across pairs. This also led to a negative GLMM fit (r = -0.65, p < 0.05). However, we are hesitant to add this plot to the manuscript for the reasons stated previously.

Comment 3, Part 1

Beyond this fundamental concern, there is a weakness in the representativeness of the PDMS finger, the vertical motion, and the speed of sliding to real human exploration.

Overall, this is a continuous debate that we think offers two solutions, and we are not advocating for an “either-or” case. There is always a tradeoff between using a synthetic model of a finger versus a real human finger, and there is a place for both models. That is, while our mock finger will be “better” the more similar it is to a human finger, it is not our goal to fully replace a human finger. Rather our goal is to provide a consistent method of characterizing surfaces that is sufficiently similar to human touch as to be a useful and predictive tool.

The usefulness of the mock finger is in isolating the features of each surface that is independent of human variability, i.e., instabilities that form without changing loading conditions between sliding motions or even within one sliding motion. Of course, with this method, we still require confirmation of these features still forming during human exploration, which we show in Fig. 3. We believe that this method of characterizing surfaces at the mesoscale will ultimately lead to more successful human studies on tactile perception. Currently, and as shown in the paper, characterizing surfaces through traditional techniques, such as a commercial tribometer (friction coefficient, using a steel or hard metal ball), roughness (via atomic force microscopy or some other metrology), surface energy are less or not at all predictive. Thus, we believe this mock finger is better than the current state-of-the-art characterizing surfaces (we are also aware of a commercial mock finger company, but we were unable to purchase or obtain an evaluation model).

One of the main – and severe – limitations of using a human finger is that all fingers are different, meaning any study focusing on a particular user may not apply to others or be recreated easily by other researchers. We do not think it is feasible to set a standard for replication around a real human finger as that participant may no longer be available, or willing to travel the world as a “standard”. Furthermore, the method in which a person changes their pressures and velocities is different. We note that this is a challenge unique to touch perception – how an object is touched changes the friction generated, and thus the tactile stimulus generated, whereas a standardized stimulus is more straightforward for light or sound.

However, we do emphasize that we have strongly considered the balance between feasibility and ecological validity in the design of a mock finger. We have a mock finger, with the three components of stiffness of a human finger (more below). Furthermore, we have also successfully used this mock finger in correlations with human psychophysics in previous work, where findings from our mechanical experiments were more predictive of human performance[4–7] than other available methods.

Our changes to the manuscript Added (Page 2-3)

“Mock finger as a characterization tool

We use a mechanical setup with a PDMS (poly(dimethylsiloxane)) mock finger to derive tactile predictors as opposed to direct biomechanical measurements on human participants. While there is a tradeoff in selecting a synthetic finger over a real human finger to modeling human touch, human fingers themselves are also highly variable[23] both in their physical shape and their use during human motion. Our goal is to design a consistent method of characterization of samples that can be easily accessed by other researchers and does not rely on a standard established around single human participant. We believe that sufficient replication of surface, bulk properties, and contact geometry results in characterization that isolates consistent features of surfaces that are not derived from human-to-human variability. We have used this approach to successfully correlate human results with mock finger characterization previously.[8,9,24]

The major component of a human finger, by volume, is soft tissue (~56%),[25] resulting in an effective modulus close to 100 kPa.[26,27] In order to achieve this same softness, we crosslink PDMS in a 1×1×5 cm mold at a 30:1 elastomer:crosslinker ratio. In addition, two more features in the human finger impart significant mechanical differences. Human fingers have a bone at the fingertip, the distal phalanx,[26–28, 8–10]which we mimic with an acrylic “bone” within our PDMS network. The stratum corneum, the stiffer, glassier outer layer of skin,[29] is replicated with the surface of the mock finger glassified, or further crosslinked, after 8 hours of UV-Ozone treatment.30 This treatment also modifies the surface properties of the native PDMS to align with those of a human finger more closely: it minimizes the viscoelastic tack at the surface, resulting in a comparable non-sticky surface. Stabilizing after one day after treatment, the mock finger surface obtains a moderate hydrophilicity (~60º), as is typically observed for a real finger.[11,31]

The initial contact area formed before a friction trace is collected is a rectangle of 1×1 cm. While this shape is not entirely representative of a human finger with curves and ridges, human fingers flatten out enough to reduce the effects of curvature with even very light pressures.[31–33] This implies that for most realistic finger pressures, the contact area is largely load-independent, which is more accurately replicated with a rectangular mock finger.

Lastly, we consider the role of fingerprint ridges. A key finding of our previous work is that while fingerprints enhanced frictional dynamics at certain conditions, key features were still maintained with a flat finger.[11] Furthermore, for some loading conditions, the more amplified signals could also result in more similar friction traces for different surfaces. We have observed good agreement between these friction traces and human experiments.[8,9,22,34]”

Page 3-4, Materials and Methods

“Mock Finger Preparation

Friction forces across all six surfaces were measured using a custom apparatus with a polydimethylsiloxane (PDMS, Dow Sylgard 184) mock finger that mimics a human finger’s mechanical properties and contact mechanics while exploring a surface relatively closely.[8,9] PDMS and crosslinker were combined in a 30:1 ratio to achieve a stiffness of 100 kPa comparable to a real finger, then degassed in a vacuum desiccator for 30 minutes. We are aware that the manufacturer recommended crosslinking ratio for Sylgard 184 is 10:1 due to potential uncrosslinked liquid residues,[35] but further crosslinking concentrated at the surface prevents this. The prepared PDMS was then poured into a 1×1×5 cm mold also containing an acrylic 3D-printed “bone” to attach applied masses on top of the “fingertip” area contacting a surface during friction testing. After crosslinking in the mold at 60ºC for 1 hour, the finger was treated with UV-Ozone for 8 hours out of the mold to minimize viscoelastic tack.

Mechanical Testing

A custom device using our PDMS mock finger was used to collect macroscopic friction force traces replicating human exploration.[8,9] After placing a sample surface on a stage, the finger was lowered at a slight angle such that an initial 1×1 cm rectangle of “fingertip” contact area could be established. We considered a broad range of applied masses (M \= 0, 25, 75, and 100 g) added onto the deadweight of the finger (6 g) observed during a tactile discrimination task. The other side of the sensor was connected to a motorized stage (V-508 PIMag Precision Linear Stage, Physikinstrumente) to control both displacement (4 mm across all conditions) and sliding velocity (v \= 5, 10, 25, and 45 mm s^-1). Forces were measured at all 16 combinations of mass and velocity via a 250 g Futek force sensor (k \= 13.9 kN m^-1) threaded to the bone, and recorded at an average sampling rate of 550 Hz with a Keithley 7510 DMM digitized multimeter. Force traces were collected in sets of 4 slides, discarding the first due to contact aging. Because some mass-velocity combinations were near the boundaries of instability phase transitions, not all force traces at these given conditions exhibited similar profiles. Thus, three sets were collected on fresh spots for each condition to observe enough occurrences of multiple instabilities, at a total of nine traces per combination for each surface.”

Added References

(23) Infante, V. H. P. et al. The role of skin hydration, skin deformability, and age in tactile friction and perception of materials. Sci. Rep. 15, 9935 (2025).

(24) Nolin, A., Lo, C.-Y., Kayser, L. V. & Dhong, C. B. Transparent and Electrically Switchable Thin Film Tactile Actuators Based on Molecular Orientation. Preprint at https://doi.org/10.48550/arXiv.2411.07968 (2024).

(25) Murai, M., Lau, H.-K., Pereira, B. P. & Pho, R. W. H. A cadaver study on volume and surface area of the fingertip. J. Hand Surg. 22, 935–941 (1997).

(26) Abdouni, A. et al. Biophysical properties of the human finger for touch comprehension: influences of ageing and gender. R. Soc. Open Sci. (2017) doi:10.1098/rsos.170321.

(27) Cornuault, P.-H., Carpentier, L., Bueno, M.-A., Cote, J.-M. & Monteil, G. Influence of physico-chemical, mechanical and morphological fingerpad properties on the frictional distinction of sticky/slippery surfaces. J. R. Soc. Interface (2015) doi:10.1098/rsif.2015.0495.

(28) Qian, K. et al. Mechanical properties vary for different regions of the finger extensor apparatus. J. Biomech. 47, 3094–3099 (2014).

(29) Yuan, Y. & Verma, R. Measuring microelastic properties of stratum corneum. Colloids Surf. B Biointerfaces 48, 6–12 (2006).

(30) Fu, Y.-J. et al. Effect of UV-Ozone Treatment on Poly(dimethylsiloxane) Membranes: Surface Characterization and Gas Separation Performance. Langmuir 26, 4392–4399 (2010).

Comment 3, Part 2

The real finger has multiple layers with different moduli. In fact, the stratum corneum cells, which are the outer layer at the interface and determine the friction, have a much higher modulus than PDMS. The real finger has multiple layers with different moduli. In fact, the stratum corneum cells, which are the outer layer at the interface and determine the friction, have a much higher modulus than PDMS.

We have approximated the softness of the finger with 100 kPa crosslinked PDMS, which is close to what has been reported for the bulk of a human fingertip.[9,10] However, as mentioned in the Materials and Methods, there are two additional features of the mock finger that impart greater strength. The PDMS surrounds a rigid, acrylic bone comparable to the distal phalanx, which provides an additional layer of higher modulus.[8] Additionally, the 8-hour UV-Ozone treatment decreases the viscoelastic tack of the pristine PDMS by glassifying, or further crosslinking the surface of the finger,[12] therefore imparting greater stiffness at the surface similar to the contributions of the stratum corneum, along with a similar surface energy.[13] This technique is widely used in wearables,[14] soft robotics,[15] and microfluidics[16] to induce both these material changes. Additionally, the finger is used at least a day after UV-Ozone treatment is completed to generate a stable surface that is moderately hydrophilic, similar to the outermost layer of human skin.[17]

Comment 3, Part 3

In addition, the slanted position of the finger can cause non-uniform pressures across the finger. Both can contribute to making the PDMS finger have much more stick-slip than a real finger.

To ensure that there is minimal contribution from the slanted position of the finger, an initial contact area of 1×1 cm is established before sliding and recording friction measurements. As the PDMS finger is a soft object, the portion in contact with a surface flattens and the contact area remains largely unchanged during sliding. Any additional stick-slip after this alignment step is caused by contact aging at the interface, but the first trace we collect is always discarded to only consider stick-slip events caused by surface chemistry. We recognize that it is difficult to completely control the pressure distribution due to the planar interface, but this is also expected when humans freely explore a surface.

Comment 3, Part 4

In fact, if you look at the regime maps, there is very little space that has steady sliding. This does not represent well human exploration of surfaces. We do not tend to use a force and velocity that will cause extensive stick-slip (frequent regions of 100% stick-slip) and, in fact, the speeds used in the study are on the slow side, which also contributes to more stick-slip. At higher speeds and lower forces, all of the materials had steady sliding regions.”

We are not aware of published studies that extensively show that humans avoid stickslip regimes. In fact, we are aware familiar with literature where stiction spike formation is suppressed – a recent paper by AliAbbasi, Basdogan et. al. investigates electroadhesion and friction with NaCl solution-infused interfaces, resulting in significantly steadier forces.[18] We also directly showed evidence of instability formation that we observed during human exploration in Fig. 3B-C. These dynamic events are common, despite the lack of control of normal forces and sliding velocities. We also note that Reviewer 1, Comment 2, Part 2 was suggesting that we further explore possible trends from parameterizing the stiction spike.

We note that many studies have often not gone at the velocities and masses required for stiction spikes – even though these masses and velocities would be routinely seen in free exploration – this is usually due to constraints of their equipment.[19] Sliding events during human free exploration of surfaces can exceed 100 mm/s for rapid touches. However, for the surfaces investigated here, we observe that large regions of stick-slip can emerge at velocities as low as 5 mm/s depending on the applied load. The incidence of steady sliding appears more dependent on the applied mass, with almost no steady sliding observed at or above 75 g. Indeed, the force categorization along our transition zones is the main point of the paper.

Comment 3, Part 5

Further, on these very smooth surfaces, the friction and stiction are more complex and cannot dismiss considerations such as finger material property change with sweat pore occlusion and sweat capillary forces. Also, the vertical motion of both the PDMS finger and the instructed human subjects is not the motion that humans typically use to discriminate between surfaces.

We did not describe the task sufficiently. Humans were only given the instruction to slide their finger along a single axis from top to bottom of a sample, not vertical as in azimuthal to gravity. We have updated our wording in the manuscript to reflect this.

Page 4

“Participants could touch for as long as they wanted, but were asked to only use their dominant index fingers along a single axis to better mimic the conditions for instability formation during mechanical testing with the mock finger.”

Page 11

“The participant was then asked to explore each sample simultaneously, and ran over each surface in strokes along a single axis until the participant could decide which of the two had “more friction”.”

Comment 3, Part 6

Finally, fingerprints may not affect the shape and size of the contact area, but they certainly do affect the dynamic response and detection of vibrations.”

We are aware of the nuance. Our previous work on the role of fingerprints on friction experienced by a PDMS mock finger showed enhanced signals with the incorporation of ridges on the finger and used a rate-and-state model of a heterogenous, elastic body to find corresponding trends (though there is no existing model of friction that can accurately model experiments on mesoscale friction).[11] The key conclusion was that a flat finger still preserved key dynamic features, and the presence of stronger or more vibrations could result in more similar forces for different surfaces depending on the sliding conditions.

This is also in the context that we are seeking to provide a reasonable and experimentally accessible method to characterize surfaces, which will always be better as we get closer in replicating a true human finger. But our goal here was to replicate the finger sufficiently for use in human studies. We believe the more appropriate metric of success is if the mock finger is more successful than replacing traditional characterization experiments, like friction coefficient, roughness, surface energy, etc.

Comment 4

This all leads to the critical question, why are friction, normal force, and velocity not measured during the measured human exploration and in a systematic study using the real human finger? The authors posed an extremely interesting hypothesis that humans may alter their speed to feel the instability transition regions. This is something that could be measured with a real finger but is not likely to be correlated accurately enough to match regime boundaries with such a simplified artificial finger.

We are excited that our manuscript offers a tractable manner to test the hypothesis that tactile decision-making models use friction instabilities as evidence. However, we lay out the challenges and barriers, and how the scope of this paper will lead us in that direction. We also clarify that our goals are to provide a method to characterize samples to better design tactile interfaces in haptics or in psychophysical experiments and raise awareness that the common methods of sample characterization in touch by an average friction coefficient or roughness is fundamentally unsound. Throughout the paper, we have made changes to reflect that our study, at this point, is only correlative.

As discussed in the summary, and with additional detail here, to further support our findings through observation on humans would require answering:

(1) Which one, or combination of, of the multiple swipes that people make responsible for a tactile decision? (There is a need for a decision-making model)

(2) Establish what is, or may be, tactile evidence.

(3) Establish tactile decision-making models are similar or different than existing decision-making models.

(4) Design a task that does not require the use of subjective tactile descriptors, like “which one feels rougher”, which we have seen causes confusion in participants, which will likely require accounting for memory effects.

We elaborate these points below:

To successfully perform this experiment, we note that freely exploring humans make multiple strokes on a surface. Therefore, we would need to construct a decision-making model. It has not yet been demonstrated whether tactile decision making follows visual decision making, but perhaps to start, we can assume it does. Then, in the design of our decision-making paradigm, we immediately run into the problem: What is tactile evidence?

From Fig. 3C, we already can see that identifying evidence is challenging. Prior to this manuscript, people may have chosen the average force, or the highest force. Or we may choose the average friction force. Then, after deciding on the evidence, we need to find a method to manipulate the evidence, i.e., create samples or a machine that causes high friction, etc. We show that during the course of human touch, due to the dynamic nature of friction, the average can change a large amount and sample design becomes a central barrier to experiments. Others may suggest immobilizing the finger and applying a known force, but given how much friction changes with human exploration, there is no known method to make a machine recreate temporally and spatially varying friction forces during sliding onto a stationary finger. Finally, perhaps most importantly, in addition to mechanical challenges, a study by Liu, Colgate et al. showed that even if they recorded the friction (2D) of a finger exploring a surface and then replicated the same friction forces onto a finger, the participant could not determine which surface the replayed friction force was supposed to represent.[1] This supports that the efference copy is important, that the forces in response to expected motion are important to determine friction. Finally, there is no known method to design instabilities a priori. They must be found through experiments. Especially since if we were to introduce, say a bump or a trough, then we bring in confounding variables to how participants tell surfaces apart.

Furthermore, even if we had some consistent method to create tactile “evidence”, the paradigm also deserves some consideration. In our experience, the 3-AFC task we perform is important because the vocabulary for touch has not been established. That is, in 3-AFC, by asking to determine which one sample is unlike the others, we do not have to ask the participant questions like “which one is rougher” or “which one has less friction”. In contrast, 2-AFC, which is better for decision-making models because it does not include memory, requires the asking of a perceptual question like: “which one is rougher?”. In our ongoing work, taking two silane coatings, we found that participants could easily identify which surface is unlike the others above chance in a 3-AFC, but participants, even within their own trials, could not consistently identify one silane as perceptually “rougher” by 2-AFC. To us, this calls into question the validity of tactile descriptors, but is beyond the scope of this manuscript.

This is not our only goal, but in the context of human exploration, in this manuscript here, we believed it was important to identify a mechanical parameter that was consistent with how humans explore surfaces, but was also a parameter that could characterize to some consistent property of a surface – irrespective of whether a human was touching it. We thought that designing human decision-making models and paradigms around the friction coefficient would not be successful.

Given the scope of these challenges, we do not think it would be possible to establish these conceptual sequences in a single manuscript. However, we think that our manuscript brings an important step forward to approach this problem.

Reviewer 2 (Public review):

Summary:

In this paper, the authors want to test the hypothesis that frictional instabilities rather than friction are the main drivers for discriminating flat surfaces of different sub-nanometric roughness profiles.

They first produced flat surfaces with 6 different coatings giving them unique and various properties in terms of roughness (picometer scale), contact angles (from hydrophilic to hydrophobic), friction coefficient (as measured against a mock finger), and Hurst exponent.

Then, they used those surfaces in two different experiments. In the first experiment, they used a mock finger (PDMS of 100kPA molded into a fingertip shape) and slid it over the surfaces at different normal forces and speeds. They categorized the sliding behavior as steady sliding, sticking spikes, and slow frictional waves by visual inspection, and show that the surfaces have different behaviors depending on normal force and speed. In a second experiment, participants (10) were asked to discriminate pairs of those surfaces. It is found that each of those pairs could be reliably discriminated by most participants.

Finally, the participant's discrimination performance is correlated with differences in the physical attributes observed against the mock finger. The authors found a positive correlation between participants' performances and differences in the count of steady sliding against the mock finger and a negative correlation between participants' reaction time and differences in the count of stiction spikes against the mock finger. They interpret those correlations as evidence that participants use those differences to discriminate the surfaces.

Strengths:

The created surfaces are very interesting as they are flat at the nanometer scale, yet have different physical attributes and can be reliably discriminated.

We thank Reviewer 2 for their notes on our manuscript. The responses below address the reviewer’s comments and recommendations for revised work.

Weaknesses:

Comment 1

In my opinion, the data presented in the paper do not support the conclusions. The conclusions are based on a correlation between results obtained on the mock finger and results obtained with human participants but there is no evidence that the human participants' fingertips will behave similarly to the mock finger during the experiment. Figure 3 gives a hint that the 3 sliding behaviors can be observed in a real finger, but does not prove that the human finger will behave as the mock finger, i.e., there is no evidence that the phase maps in Figure 1C are similar for human fingers and across different people that can have very different stiffness and moisture levels.

We have made changes throughout the manuscript to acknowledge that our findings are correlative, clarifying this throughout, and incorporating into the discussion how our work may enable biomechanical measurements and tactile decision making models.

The mechanical characterization conducted with the mock finger seeks to extract significant features of friction traces of a set of surfaces to use as predictors of tactile discriminability. The goal is to find a consistent method to characterize surfaces for use in tactile experiments that can be replicated by others and used prior to any human experiments. However, in the overall response and in a response to a similar comment by Reviewer 1 (recreated below), we also explain why we believe experiments on humans to establish this fact is not yet reasonable.

First, we discuss the mock finger. The PDMS finger is treated to have comparable surface and bulk properties to a human finger. We have approximated the softness of the finger with 100 kPa crosslinked PDMS, which is close to what has been reported for the bulk of a human fingertip.[9,10] However, as mentioned in the Materials and Methods, there are two additional features of the mock finger that impart greater strength. The PDMS surrounds a rigid, acrylic bone comparable to the distal phalanx, which provides an additional layer of higher modulus.[8] Additionally, the 8-hour UV-Ozone treatment decreases the viscoelastic tack of the pristine PDMS by glassifying, or further crosslinking the surface of the finger,[12] therefore imparting greater stiffness at the surface similar to the contributions of the stratum corneum, along with a similar surface energy.[13] Additionally, the finger is used at least a day after UV-Ozone treatment is completed in order for the surface to return to moderate hydrophilicity, similar to the outermost layer of human skin.[17] We also discuss the shape of the contact formed. To ensure that there is minimal contribution from the slanted position of the finger, an initial contact area of 1×1 cm is established before sliding and recording friction measurements. As the PDMS finger is a soft object, the portion in contact with a surface flattens and the contact area remains largely unchanged during sliding. Any additional stick-slip after this alignment step is caused by contact aging at the interface, but the first trace we collect is always discarded to only consider stick-slip events caused by surface chemistry. We recognize that it is difficult to completely control the pressure distribution due to the planar interface, but this is also expected when humans freely explore a surface. Finally, we consider flat vs. fingerprinted fingers. Our previous work on the role of fingerprints on friction experienced by a PDMS mock finger showed enhanced signals with the incorporation of ridges on the finger and used a rate-and-state model of a heterogenous, elastic body to find corresponding trends.[11] The key conclusion was that a flat finger still preserved key dynamic features, and the presence of stronger or more vibrations could result in more similar forces for different surfaces depending on the sliding conditions. We note that we have subsequently used this flat mock finger in correlations with human psychophysics in previous work, where findings from our mechanical experiments were predictive of human performance.[4–7] We have added these details to the manuscript.

With this adequately similar mock finger, we collected friction traces at controlled conditions of normal force and velocity in order to extract the signals unique to each material that are not caused by the influence of human variability. For example, we observe the smallest regions of steady sliding on our phase maps (Fig. 1C) for short-chain alkylsilanes C4 and C5, while the increased intermolecular forces of other silanes increase the incidence of steady sliding. We have also previously shown that comparisons of similarly collected mechanical data is predictive of human performance, using the crosscorrelations between signals of two different materials.[4–7] While different participants produce different raw signals, we see that broad categories of stick-slip, i.e. instabilities, can be extracted (Fig. 3B-C) and used as a cue in a tactile discrimination task. As mentioned above, we have provided an additional section about the usefulness of our mock finger, as well as its structure, in the main manuscript.

Second, we lay out the challenges and barriers to demonstrating this in humans in the manner requested by the reviewer, and how the scope of this paper will lead us in that direction. We also clarify that our goals are to provide a method to characterize samples to better design tactile interfaces in haptics or in psychophysical experiments and raise awareness that the common methods of sample characterization in touch by an average friction coefficient or roughness is fundamentally unsound.

As discussed in the summary, and with additional detail here, to further support our findings through observation on humans would require answering:

(1) Which one, or combination of, of the multiple swipes that people make responsible for a tactile decision?

(2) Establish what is, or may be, tactile evidence.

(3) Establish tactile decision-making models are similar or different than existing decision-making models.

(4) Test the hypothesis, in these models, that friction instabilities are evidence, and not some other unknown metric.

(5) Design a task that does not require the use of subjective tactile descriptors, like “which one feels rougher”, which we see cause confusion in participants, which will likely require accounting for memory effects.

We elaborate these points below:

To successfully perform this experiment, we note that freely exploring humans make multiple strokes on a surface. Therefore, we would need to construct a decision-making model. It has not yet been demonstrated whether tactile decision making follows visual decision making, but perhaps to start, we can assume it does. Then, in the design of our decision-making paradigm, we immediately run into the problem: What is tactile evidence?

From Fig. 3C, we already can see that identifying evidence is challenging. Prior to this manuscript, people may have chosen the average force, or the highest force. Or we may choose the average friction force. Then, after deciding on the evidence, we need to find a method to manipulate the evidence, i.e., create samples or a machine that causes high friction, etc. We show that during the course of human touch, due to the dynamic nature of friction, the average can change a large amount and sample design becomes a central barrier to experiments. Others may suggest immobilizing the finger and applying a known force, but given how much friction changes with human exploration, there is no known method to make a machine recreate temporally and spatially varying friction forces during sliding onto a stationary finger. Finally, perhaps most importantly, in addition to mechanical challenges, a study by Liu, Colgate, et al. showed that even if they recorded the friction (2D) of a finger exploring a surface and then replicated the same friction forces onto a finger, the participant could not determine which surface the replayed friction force was supposed to represent.[1] This supports that the efference copy is important, that the forces in response to expected motion are important to determine friction. Finally, there is no known method to design instabilities a priori. They must be found through experiments, especially since if we were to introduce, say a bump or a trough, then we bring in confounding variables to how participants tell surfaces apart.

Furthermore, even if we had some consistent method to create tactile “evidence”, the paradigm also deserves some consideration. In our experience, the 3-AFC task we perform is important because the vocabulary for touch has not been established. That is, in 3-AFC, by asking to determine which one sample is unlike the others, we do not have to ask the participant questions like “which one is rougher” or “which one has less friction”. In contrast, 2-AFC, which is better for decision-making models because it does not include memory, requires the asking of a perceptual question like: “which one is rougher?”. In our ongoing work, taking two silane coatings, we found that participants could easily identify which surface is unlike the others above chance in a 3-AFC, but participants, even within their own trials, could not consistently identify one silane as perceptually “rougher” by 2-AFC. To us, this calls into question the validity of tactile descriptors, but is beyond the scope of the current manuscript.

This is not our only goal, but in the context of human exploration, in this manuscript here, we believed it was important to identify a mechanical parameter that was consistent with how humans explore surfaces, but was also a parameter that could characterize to some consistent property of a surface – irrespective of whether a human was touching it. We thought that designing human decision-making models and paradigms around the friction coefficient would not be successful.

Given the scope of these challenges, we do not think it would be possible to establish this conceptual sequence in a single manuscript.

See Reviewer 1, comment 3part 3 for changes to the manuscript

Comment 2

I believe that the authors collected the contact forces during the psychophysics experiments, so this shortcoming could be solved if the authors use the actual data, and show that the participant responses can be better predicted by the occurrence of frictional instabilities than by the usual metrics on a trial by trial basis, or at least on a subject by subject basis. I.e. Poor performers should show fewer signs of differences in the sliding behaviors than good performers.

To fully implement this, a decision-making model is necessary because, as a counter example, a participant could have generated 10 swipes of SFW and 1 swipe of a Sp, but the Sp may have been the most important event for making a tactile decision. This type of scenario is not compatible with the analysis suggested — and similar counterpoints can be made for other types of seemingly straightforward analysis.

While we are interested and actively working on this, the study here is critical to establish types of evidence for a future decision-making model. We know humans change their friction constantly during real exploration, so it is unclear which of these constantly changing values we should input into the decision making model, and the future challenges we anticipate are explained in Weaknesses, Comment 1.

Comment 3

The sample size (10) is very small.

We recognize that, with all factors being equal, this sample size is on the smaller end. However, we emphasize the degree of control of samples is far above typical, with minimal variations in sample properties such as surface roughness, and every sample for every trial was pristine. Furthermore, the sample preparation (> 300 individual wafers were used) became a factor. Although not typically appropriate, and thus not included in the manuscript, a post-hoc power analysis for our 100 trials of our pair that was closest to chance, P4, (53%, closest to chance at 33%) showed a power of 98.2%, suggesting that the study was appropriately powered.

Reviewer 2 (Recommendations for the authors):

Comment 1

Differences in SS and Sp (Table 2) are NOT physical or mechanical differences but are obtained by counting differences in the number of occurrences of each sliding behavior. It is rather a weird choice.

We disagree that differences in SS and Sp are not physical or mechanical, as these are well-established phenomena in the soft matter and tribology literature.[20–22] These are known as “mechanical instabilities” and generated due to the effects of two physical phenomena: the elasticity of the finger (which is constant in our mechanical testing) and the friction forces present (which change per sample type). The motivation behind using these different shapes is that the instabilities, in some conditions, can be invariant to external factors like velocity. This would be quite advantageous for human exploration because, unlike friction coefficient, which changes with nearly any factor, including velocity and mass, the instabilities being invariant to velocity would mean that we are accurately characterizing a unique identifier of the surface even though velocity may be variable.

This “weird choice” is the central innovation of this paper. This choice was necessary because we demonstrated that the common usage of friction coefficient is fundamentally flawed: we see that friction coefficient suggests that surface which are more different would feel more similar – indeed the most distinctive surfaces would be two surfaces that are identical, which is clearly spurious. Furthermore, Table 1 now includes the range of friction generated on a surface, the range of friction coefficients of a single surface is large – of order the differences in friction between two surfaces. This is expected in soft sliding systems and emphasizes our issue with the use of average friction coefficient in psychophysical design. One potential explanation for why we were able to see this is effect is because our surfaces have similar (< 0.6 nm variability) roughness, removing potential confounding factors from large scale roughness, and this type of low roughness control has not been widely used in tactile studies to the best of our knowledge.

Comment 2

Figures 2B-C: why are the x-data different than Table 2?

The x-data in Fig. 2B-C are the absolute differences in the number of occurrences measured for a given instability type or material property out of 144 pulls. Modeling the human participant results in our GLMMs required the independent variables to be in this form rather than percentages. We initially chose to list percent differences in Table 2 to highlight the ranges of differences instead of an absolute value, but have added both for clarity.

Our changes to the manuscript

Page 7

“To determine if humans can detect these three different instabilities, we selected six pairs of surfaces to create a broad range of potential instabilities present across all three types. These are summarized in Table 2, where the first column for each instability is the difference in occurrence of that instability formed between each pair, and the second is the percent difference.”

“Thus, when comparing C4 versus C4-APTMS, they have a difference in steady sliding of 20 out of a maximum 144 pulls, for a |ΔSS| of 13.9%. The absolute value is taken to compare total differences present, as the psychophysical task does not distinguish between sample order.”

Comment 3

We constructed a set of coated surfaces with physical differences which were imperceptible by touch but created different types of instabilities based on how quickly a finger is slid and how hard a human finger is pressed during sliding." Yet, in your experiment, participants could discriminate them, so this is incoherent.

To clarify the point, macroscopic objects can differ in physical shape and in chemical composition. What we meant was that the physical differences, i.e., roughness, were below a limit (Skedung et al.) that participants, without a coating, would not be able to tell these apart.[23] Therefore, the reason people could tell our surfaces apart was due to the chemical composition of the surface, and not any differences in roughness or physical effects like film stiffness (due to the molecular-scale thinness of the surface coatings, they are mechanically negligible). However, we concede that at the molecular scale, the traditional macroscopic distinction between physical and chemical is blurred.

We have made minor revisions to the wording in the abstract. We clarify that the surface coatings had physical differences in roughness that were smaller than 0.6 nm, which based purely on roughness, would not be expected to be distinguishable to participants. Therefore, the reason participants can tell these surfaces apart is due to differences in friction generated by chemical composition, and we were able to minimize contributions from physical differences in the sample our study.

Our changes to the manuscript

Page 1, Abstract

“Here, we constructed a set of coated surfaces with minimal physical differences that by themselves, are not perceptible to people, but instead, due to modification in surface chemistry, the surfaces created different types of instabilities based on how quickly a finger is slid and how hard a human finger is pressed during sliding.”

“In one experiment, we used a mechanical mock finger to quantify and classify differences in instability formation from different coated surfaces. In a second experiment, participants perform a discrimination task using the same coated surfaces. Using the data from these two experiments, we found that human discrimination response times were faster with surfaces where the mock finger produced more stiction spikes and discrimination accuracy was higher where the mock finger produced more steady sliding. Conversely, traditional metrics like surface roughness or average friction coefficient did not relate to tactile discriminability. In fact, the typical method of averaging friction coefficients led to a spurious correlation which erroneously suggests that distinct objects should feel identical and identical objects should feel distinct—similar to findings by others. Friction instabilities may offer a more predictive and tractable framework of fine touch perception than friction coefficients, which would accelerate the design of tactile interfaces.”

Reviewer 3 (Public review):

Strengths

The paper describes a new perspective on friction perception, with the hypothesis that humans are sensitive to the instabilities of the surface rather than the coefficient of friction. The paper is very well written and with a comprehensive literature survey.

One of the central tools used by the author to characterize the frictional behavior is the frictional instabilities maps. With these maps, it becomes clear that two different surfaces can have both similar and different behavior depending on the normal force and the speed of exploration. It puts forward that friction is a complicated phenomenon, especially for soft materials.

The psychophysics study is centered around an odd-one-out protocol, which has the advantage of avoiding any external reference to what would mean friction or texture for example. The comparisons are made only based on the texture being similar or not.

The results show a significant relationship between the distance between frictional maps and the success rate in discriminating two kinds of surface.

We thank Reviewer 3 for their notes and interesting discussion points on our manuscript. Below, we address the reviewer’s feedback and comments on related works.

Weaknesses:

Comment 1

The main weakness of the paper comes from the fact that the frictional maps and the extensive psychophysics study are not made at the same time, nor with the same finger. The frictional maps are produced with an artificial finger made out of PDMS which is a poor substitute for the complex tribological properties of skin.

A similar comment was made by Reviewers 1 and 2. We agree in part and have made changes throughout that our study is correlative, but presents an important step forward to these biomechanical measurements and corresponding decision making models.

We are not claiming that our PDMS fingers are superior to real fingers, but rather, we cannot establish standards in the field by using real human fingers that vary between subjects and researchers. We believe the mock finger we designed is a reasonable mimic of the human finger by matching surface energy, heterogeneous mechanical structure, and the ability to test multiple physiologically relevant pressures and sliding velocities.

We achieve a heterogeneous mechanical structure with the 3 primary components of stiffness of a human finger. The effective modulus of ~100 kPa, from soft tissue,[9,10] is obtained with a 30:1 ratio of PDMS to crosslinker. The PDMS also surrounds a rigid, acrylic bone comparable to the distal phalanx, which provides an additional layer of higher modulus.[8] Additionally, the 8-hour UV-Ozone treatment decreases the viscoelastic tack of the pristine PDMS by glassifying, or further crosslinking the surface of the finger,[12] therefore imparting greater stiffness at the surface similar to the contributions of the stratum corneum, along with a similar surface energy.[13] The finger is used at least a day after UV-Ozone treatment is completed in order for the surface to return to moderate hydrophilicity, similar to the outermost layer of human skin.[17] We also discuss the shape of the contact formed. To ensure that there is minimal contribution from the slanted position of the finger, an initial contact area of 1×1 cm is established before sliding and recording friction measurements. As the PDMS finger is a soft object, the portion in contact with a surface flattens and the contact area remains largely unchanged during sliding. We recognize that it is difficult to completely control the pressure distribution due to the planar interface, but this variation is also expected when humans freely explore a surface. Finally, we consider flat vs. fingerprinted fingers. Our previous work on the role of fingerprints on friction experienced by a PDMS mock finger showed enhanced signals with the incorporation of ridges on the finger and used a rate-andstate model of a heterogenous, elastic body to find corresponding trends.[11] The key conclusion was that a flat finger still preserved key dynamic features, and the presence of stronger or more vibrations could result in more similar forces for different surfaces depending on the sliding conditions. We note that we have subsequently used the controlled mechanical data collected with this flat mock finger in correlations with human psychophysics in previous work, where findings from our mechanical experiments were predictive of human performance.[4–7] Ultimately, we see from our prior work and here that, despite the drawbacks of our mock finger, it outperforms other standard characterization technique in providing information about the mesoscale that correlates to tactile perception. We have added these details to the manuscript.

We also note that an intermediate option, replicating real fingers, even in a mold, may also inadvertently limit trends from characterization to a specific finger. One of the main – and severe – limitations of using a human finger is that all fingers are different, meaning any study focusing on a particular user may not apply to others or be recreated easily by other researchers. We cannot set a standard for replication around a real human finger as that participant may no longer be available, or willing to travel the world as a “standard”. Furthermore, the method in which a single person changes their pressures and velocities as they touch a surface is highly variable. We also note that in the Summary Response, we noted that a study by Colgate et al. (IEEE ToH 2024) demonstrated that efference copies may be important, and thus constraining a human finger and replaying the forces recorded during free exploration will not lead to the participant identifying a surface with any consistency. Thus, it is important to allow humans to freely explore surfaces, but creates nearly limitless variability in friction forces.

This is also against the backdrop that we are seeking to provide a method to characterize surfaces. Indeed, the more features we replicate in the mock finger to a human finger, the more likely it is that the mechanical data will correlate to human performance. However, we have used this technique several times to achieve stronger correlations to human data than other available techniques. We believe the metric of success should be in comparison to the available characterization technique, rather than a 1:1 reconstruction of forces of an arbitrary human finger. Indeed, a 1:1 reconstruction of forces of an arbitrary human finger would be limited to the finger of a single individual, perhaps even to that individual on a given day.

See Reviewer1 weaknesses, comment 2 part 2 for changes to the manuscript

Comment 2

The evidence would have been much stronger if the measurement of the interaction was done during the psychophysical experiment. In addition, because of the protocol, the correlation is based on aggregates rather than on individual interactions.

We agree that this would have helped further establish our argument, but in the overall statement and in other reviewer responses, we describe the significant challenges to establishing this.

To fully implement this, a decision-making model is necessary because, as a counter example, a participant could have generated 10 swipes of SFW and 1 swipe of a Sp, but the Sp may have been the most important event for making a tactile decision. We also clarify that our goals are to provide a method to characterize samples to better design tactile interfaces in haptics or in psychophysical experiments.

As discussed in the summary, and expanded on here, in our view, to develop a decision-making model, the challenges are as follows:

(1) Which one, or combination of, of the multiple swipes that people make responsible for a tactile decision?

(2) Establish what is, or may be, tactile evidence.

(3) Establish tactile decision-making models are similar or different than existing decision-making models.

(4) Test the hypothesis, in these models, that friction instabilities are evidence, and not some other unknown metric.

(5) Design a task that does not require the use of subjective tactile descriptors, like “which one feels rougher”, which we see cause confusion in participants, which will likely require accounting for memory effects.

(6) Design samples that vary in the amount of evidence generated, but this evidence cannot be controlled directly. Rather, the samples indirectly vary evidence by how likely it is for a human to generate different types of friction instabilities during standard exploration.

We elaborate these points below:

To successfully perform this experiment, we note that freely exploring humans make multiple strokes on a surface. Therefore, we would need to construct a decision-making model. It has not yet been demonstrated whether tactile decision making follows visual decision making, but perhaps to start, we can assume it does. Then, in the design of our decision-making paradigm, we immediately run into the problem: What is tactile evidence?

From Fig. 3C, we already can see that identifying evidence is challenging. Prior to this manuscript, people may have chosen the average force, or the highest force. Or we may choose the average friction force. Then, after deciding on the evidence, we need to find a method to manipulate the evidence, i.e., create samples or a machine that causes high friction, etc. We show that during the course of human touch, due to the dynamic nature of friction, the average can change a large amount and sample design becomes a central barrier to experiments. Others may suggest to immobilize the finger and applying a known force, but given how much friction changes with human exploration, there is no known method to make a machine recreate temporally and spatially varying friction forces during sliding onto a stationary finger. Finally, perhaps most importantly, in addition to mechanical challenges, a study by Liu, Colgate et al. showed that even if they recorded the friction (2D) of a finger exploring a surface and then replicated the same friction forces onto a finger, the participant could not determine which surface the replayed friction force was supposed to represent.[1] This supports that the efference copy is important, that the forces in response to expected motion are important to determine friction. Finally, there is no known method to design instabilities a priori. They must be found through experiments, especially since if we were to introduce, say a bump or a trough, then we bring in confounding variables to how participants tell surfaces apart.

Furthermore, even if we had some consistent method to create tactile “evidence”, the paradigm also deserves some consideration. In our experience, the 3-AFC task we perform is important because the vocabulary for touch has not been established. That is, in 3-AFC, by asking to determine which one sample is unlike the others, we do not have to ask the participant questions like “which one is rougher” or “which one has less friction”. In contrast, 2-AFC, which is better for decision-making models because it does not include memory, requires the asking of a perceptual question like: “which one is rougher?”. In our ongoing work, taking two silane coatings, we found that participants could easily identify which surface is unlike the others above chance in a 3-AFC, but participants, even within their own trials, could not consistently identify one silane as perceptually “rougher” by 2-AFC. To us, this calls into question the validity of tactile descriptors, but is beyond the scope of the current manuscript.

This is not our only goal, but in the context of human exploration, in this manuscript here, we believed it was important to identify a mechanical parameter that was consistent with how humans explore surfaces, but was also a parameter that could characterize to some consistent property of a surface – irrespective of whether a human was touching it. We thought that designing human decision-making models and paradigms around the friction coefficient would not be successful.

Given the scope of these challenges, we do not think it would be possible to establish this conceptual sequence in a single manuscript.

Comment 3

The authors compensate with a third experiment where they used a 2AFC protocol and an online force measurement. But the results of this third study, fail to convince the relation.

With this experiment, our central goal was to demonstrate that the instabilities we have identified with the PDMS finger also occur with a human finger. Several instances of SS, Sp, and SFW were recorded with this setup as a participant touched surfaces in real time.

Comment 4

No map of the real finger interaction is shown, bringing doubt to the validity of the frictional map for something as variable as human fingers.

Real fingers change constantly during exploration, and friction is state-dependent, meaning that the friction will depend on how the person was moving the moment prior. Therefore, a map is only valid for a single human movement – even if participants all were instructed to take a single swipe and start from zero motion, humans are unable to maintain constant velocities and pressures. Clearly, this is not sustainable for any analysis, and these drawbacks apply to any measured parameter, whether instabilities suggested here, or friction coefficients used throughout. We believe the difficulty of this approach emphasizes why a standard map of characterization of a surface by a mock finger, even with its drawbacks, is a viable path forward.

Reviewer 3 (Recommendations for the authors):

Comment 1

It would be interesting to comment on a potential connection between the frictional instability maps and Schalamack waves.

Schallamach waves are a subset of slow frictional waves (SFW). Schallamach waves are very specifically defined in the field. They occur when pockets of air that form between a soft sliding object and rigid surface which then propagate rear-to-front (retrograde waves) relative to motion of the sliding motion and form buckles due to adhesive pinning. Wrinkles then form at the detached portion of the soft material, until the interface reattaches and the process repeats.[24] There is typically a high burden of proof to establish a Schallamach wave over a more general slow frictional wave. We note that it would be exceedingly difficult to design samples that can reliably create subsets of SFW, but we are aware that this may be an interesting question at a future point in our work.

Comment 2

The force sensors look very compliant, and given the dynamic nature of the signal, it is important to characterize the frequency response of the system to make sure that the fluctuations are not amplified.

Thank you for noticing. We mistyped the sensor spring constant as 13.9 N m^-1 instead of kN m^-1. However, below we show how the instabilities are derived from the mechanics at the interface due to the compliance of the finger. The “springs” of the force sensor and PDMS finger are connected in parallel. Since k_sensor = 13.9 kN m^-1, the spring constant of the system overall reflects the compliance of the finger, and highlights the oscillations arising solely from stick-slip. A sample calculation is shown below.

Author response image 1.

Fitting a line to the initial slope of the force trace for C6 gives the equation y = 25.679x – 0.2149. The slope here represents force data over time data, and is divided by the velocity (25 mm/s) to determine the spring constant of the system k_total == 1027.16 N/m. This value is lower than k_sensor = 13.9 kN/m, indicating that the “springs” representing the force sensor and PDMS finger are connected in parallel:

. The finger is the compliant component of the system, with k_finger = 1.11 kN/m, and of course, real human fingers are also compliant so this matches our goals with the design of the mock finger.

Our changes to the manuscript

(Page 4) (k = 13.9 kN m¹)

Comment 3

The authors should discuss about the stochastic nature of friction: - Wiertlewski, Hudin, Hayward, IEEE WHC 2011 Greenspon, McLellan, Lieber, Bensmaia, JRSI 2020.

We believe that, given the references, this comment on “stochastic” refers to the macroscopically-observable fluctuations (i.e., the mechanical “noise” which is not due to instrument noise) in friction arising from the discordant network of stick-slip phenomena occurring throughout the contact zone, and not the stochastic nature of nanoscale friction that occurs thermal fluctuations nor due to statistical distributions in bond breaking associated with soft contact.

We first note that our small-scale fluctuations do not arise from a periodic surface texture that dominates in the frequency regime. However, even on our comparatively smooth surfaces, we do expect fluctuations due to nanoscale variation in contact, generation of stick-slip across at microscale length scales that occur either concurrently or discordantly across the contact zone, and the nonlinear dependence of friction to nearly any variation in state and composition.[11]

Perhaps the most relevant to the manuscript is that a major advantage of analysis by friction is that it sidesteps these ever-present microscale fluctuations, leading to more clearly defined classifiers or categories during analysis. Wiertlewski et. al. showed repeated measurements in their systems ultimately gave rise to consistent frequencies[25] (we think their system was in a steady sliding regime and the patterning gave rise to underlying macroscopic waves). These consistent frequencies, at least in soft systems and absent obvious macroscopic patterned features, would be expected to arise from the instability categories and we see them throughout.

Comment 4

It is stated that "we observed a spurious, negative correlation between friction coefficient and accuracy".

What makes you qualify that correlation as spurious?

We mean this as in the statistical definition of “spurious”.

This correlation would indicate that by the metric of friction coefficient, more different surfaces are perceived more similarly. Thus, two very different surfaces, like Teflon and sandpaper, by friction coefficient would be expected to feel very similar. Two nearly identical surfaces would be expected to feel very different – but of course, humans cannot consistently distinguish two identical surfaces. This finding is counterintuitive and refutes that friction coefficient is a reliable classifier of surfaces by touch. We do not think it is productive to determine a mechanism for a spurious correlation, but perhaps one reason we were able to observe this is because our study, to the best of our knowledge, is unique for having samples that are controlled in their physical differences in roughness and surface features.

See response to Reviewer 1 weaknesses, comment 1 for changes to the manuscript

Comment 5

The authors should comment on the influence of friction on perceptual invariance. Despite inducing radially different frictional behavior for various conditions, these surfaces are stably perceived. Maybe this is a sign that humans extract a different metric?

We agree – we are excited that frictional instabilities may offer a more stable perceptual cue because they are not prone to fluctuations (as discussed in Comment 3) and instability formation, in many conditions, is invariant to applied pressures and velocities – thus forming large zones where a human may reasonable encounter a given instability.

Raw friction is highly prone to variation during human exploration (in alignment with Recommendations for the authors, Comment 3), but ongoing work seeks to explain tactile constancy, or the ability to identify objects despite these large changes in force. Very recently published work by Fehlberg et. al. identified the role of modulating finger speed and normal force in amplifying the differences in friction coefficient between materials in order to identify them,[26] and we postulate that their work may be streamlined and consistent with the idea of friction instabilities, though we have not had a chance to discuss this in-depth with the authors yet.

We think that the instability maps show a viable path forward to how surfaces are stably perceived, and instabilities themselves show a potential mechanism: mathematically, instabilities for given conditions can be invariant to velocity or mass, creating zones where a certain instability is encountered. This reduces the immense variability of friction to a smaller, more stable classification of surfaces (e.g., a 30% SS surface or a 60% SS surface). A given surface will typically produce the same instability at a specific condition (we found some boundaries of experimental parameters are very condition sensitive, but many conditions are not), whereas a single friction trace which is highly prone to variation is not a stable metric.

Added Reference

(53) M. Fehlberg, E. Monfort, S. Saikumar, K. Drewing and R. Bennewitz, IEEE Trans. Haptics, 2024, 17, 957–963.

References

(1) Liu, Z., Kim, J.-T., Rogers, J. A., Klatzky, R. L. & Colgate, J. E. Realism of Tactile Texture Playback: A Combination of Stretch and Vibration. IEEE Trans. Haptics 17, 441–450 (2024).

(2) Waters, I., Alazmani, A. & Culmer, P. Engineering Incipient Slip Into Surgical Graspers to Enhance Grasp Performance. IEEE Transactions on Medical Robotics and Bionics 2, 541–544 (2020).

(3) Gueorguiev, D., Bochereau, S., Mouraux, A., Hayward, V. & Thonnard, J.-L. Touch uses frictional cues to discriminate flat materials. Sci Rep 6, 25553 (2016).

(4) Carpenter, C. W. et al. Human ability to discriminate surface chemistry by touch. Mater. Horiz. 5, 70– 77 (2018).

(5) Nolin, A. et al. Predicting human touch sensitivity to single atom substitutions in surface monolayers for molecular control in tactile interfaces. Soft Matter 17, 5050–5060 (2021).

(6) Nolin, A. et al. Controlling fine touch sensations with polymer tacticity and crystallinity. Soft Matter 18, 3928–3940 (2022).

(7) Swain, Z. et al. Self-Assembled Thin Films as Alternative Surface Textures in Assistive Aids with Users Who are Blind. J. Mater. Chem. B (2024) doi:10.1039/D4TB01646G.

(8) Qian, K. et al. Mechanical properties vary for different regions of the finger extensor apparatus. J Biomech 47, 3094–3099 (2014).

(9) Abdouni, A. et al. Biophysical properties of the human finger for touch comprehension: influences of ageing and gender. Royal Society Open Science (2017) doi:10.1098/rsos.170321.

(10) Cornuault, P.-H., Carpentier, L., Bueno, M.-A., Cote, J.-M. & Monteil, G. Influence of physicochemical, mechanical and morphological fingerpad properties on the frictional distinction of sticky/slippery surfaces. Journal of The Royal Society Interface (2015) doi:10.1098/rsif.2015.0495.

(11) Dhong, C. et al. Role of fingerprint-inspired relief structures in elastomeric slabs for detecting frictional differences arising from surface monolayers. Soft Matter 14, 7483–7491 (2018).

(12) Fu, Y.-J. et al. Effect of UV-Ozone Treatment on Poly(dimethylsiloxane) Membranes: Surface Characterization and Gas Separation Performance. Langmuir 26, 4392–4399 (2010).

(13) Yuan, Y. & Verma, R. Measuring microelastic properties of stratum corneum. Colloids Surf B Biointerfaces 48, 6–12 (2006).

(14) Yu, G. et al. A wearable pressure sensor based on ultra-violet/ozone microstructured carbon nanotube/polydimethylsiloxane arrays for electronic skins. Nanotechnology 29, 115502 (2018).

(15) Zheng, L. et al. Dual-Stimulus Smart Actuator and Robot Hand Based on a Vapor-Responsive PDMS Film and Triboelectric Nanogenerator. ACS Appl. Mater. Interfaces 11, 42504–42511 (2019).

(16) Ma, K., Rivera, J., Hirasaki, G. J. & Biswal, S. L. Wettability control and patterning of PDMS using UV–ozone and water immersion. Journal of Colloid and Interface Science 363, 371–378 (2011).

(17) Mavon, A. et al. Sebum and stratum corneum lipids increase human skin surface free energy as determined from contact angle measurements: A study on two anatomical sites. Colloids and Surfaces B: Biointerfaces 8, 147–155 (1997).

(18) AliAbbasi, E. et al. Effect of Finger Moisture on Tactile Perception of Electroadhesion. IEEE Trans. Haptics 17, 841–849 (2024).

(19) Corniani, G. et al. Sub-surface deformation of individual fingerprint ridges during tactile interactions.

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(20) Israelachvili, J. N. Intermolecular and Surface Forces. (Academic Press, 2011).

(21) Das, S. et al. Stick–slip friction of gecko-mimetic flaps on smooth and rough surfaces. J R Soc Interface 12, 20141346 (2015).

(22) Persson, B. N. J., Albohr, O., Creton, C. & Peveri, V. Contact area between a viscoelastic solid and a hard, randomly rough, substrate. The Journal of Chemical Physics 120, 8779–8793 (2004).

(23) Skedung, L. et al. Feeling Small: Exploring the Tactile Perception Limits. Sci Rep 3, 2617 (2013).

(24) Viswanathan, K., Sundaram, N. K. & Chandrasekar, S. Stick-slip at soft adhesive interfaces mediated by slow frictional waves. Soft Matter 12, 5265–5275 (2016).

(25) Wiertlewski, M., Hudin, C. & Hayward, V. On the 1/f noise and non-integer harmonic decay of the interaction of a finger sliding on flat and sinusoidal surfaces. in 2011 IEEE World Haptics Conference 25–30 (2011). doi:10.1109/WHC.2011.5945456.

(26) Fehlberg, M., Monfort, E., Saikumar, S., Drewing, K. & Bennewitz, R. Perceptual Constancy in the Speed Dependence of Friction During Active Tactile Exploration. IEEE Transactions on Haptics 17, 957–963 (2024).

Author response:

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

Introduction to the revised manuscript:

We thank all three reviewers for their time and insightful comments on our original submission. We are submitting a substantially revised manuscript that includes several new experiments, analyses, discussion points, and clarifications that we believe address all of the main concerns of the reviewers.

To address the request of Reviewers 2 and 3 to reinforce key findings in a more physiologically intact preparation, we performed recordings of YH-HET SST neurons in brain slices and found that these neurons show impairments in AP generation similar to those observed in YH-HET SST cultured neurons. These data are summarized in a new figure (Fig. 9). Along these lines, we performed additional recordings in cultured neurons at room temperature compared with physiological temperature and found that WT and YH-HET PV neuronal properties were similarly altered by temperature increases, suggesting that our YH variant-induced neuronal phenotypes are not temperature dependent. These data are shown in a new supplemental figure (Supplemental Fig. 4-3). To address concerns of Reviewer 1 regarding our KNa and NaP current recordings, we performed new experiments to further assess the specificity of the VU170 blocker in KNa KO neurons (summarized in Supplemental Fig. 5-2) and to better characterize the time course over which TTX blocks the persistent Na+ current and the KNa current (summarized in Supplemental Fig. 7-1). These latter two experiments provide further clarity and confidence in the accuracy of our measurements of both KNa and NaP currents. Lastly, to address the concern of Reviewer 3 regarding statistical analyses of the modeling data, we’ve added a new table with the results of a repeated measures ANOVA analysis (Supplemental Table 6), and two new figures illustrating the relative changes in each neuron group compared to their controls (Supplemental Figures 6-2 and 7-2). 

In addition to the new experiments and analyses, we’ve added three new paragraphs to the Discussion section. As the hyperexcitability phenotype in YH-HET PV neurons is somewhat unexpected, we’ve added a paragraph comparing our findings with those found in PV neurons in another KCNT1 GOF model. We’ve also added a paragraph to speculate on the contribution of YH-HET variant-induced alterations in SST and PV neurons to network behavior and seizure propensity. Lastly, we’ve added a paragraph to include the additional limitations and caveats of our study requested by the reviewers.  

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This manuscript reports the effects of a heterozygous mutation in the KCNT1 potassium channels on the properties of ion currents and the firing behavior of excitatory and inhibitory neurons in the cortex of mice expressing KCNT1-Y777H. In humans, this mutation as well as multiple other heterozygotic mutations produce very severe early-onset seizures and produce a major disruption of all intellectual function. In contrast, in mice, this heterozygous mutation appears to have no behavioral phenotype or any increased propensity to seizures.

Regarding the last sentence above, we wanted to clarify a point that we neglected to emphasize in the initial submission. In the Results section from our previous paper (Shore et al., 2020), we failed to observe seizures in 14 heterozygous mice, whereas 23/25 homozygous mice showed seizures by video-EEG. However, in the fifth paragraph of the Discussion section from that paper, we further stated that “during the preparation and review of [that] article, we observed seizures in two Kcnt1-Y777H heterozygous mice, one during a widefield Ca2+ imaging experiment and the other during a video-EEG experiment”. Thus, we concluded that “heterozygous expression can result in seizures in a rodent model, but apparently at a much lower frequency than that observed with homozygous expression”. To emphasize these findings, we’ve added a sentence to the Introduction in this manuscript about the occurrence of infrequent seizures in Kcnt1-Y777H heterozygous mice, along with a reference to the Discussion of our previous paper.

A relevant phenotype is, however, evident in mice with the homozygous mutation, and the authors have previously published the results of similar experiments with the homozygotes. As perhaps expected, the neuronal effects of the heterozygous mutation presented in this manuscript are generally similar but markedly smaller than the previously published findings on homozygotes. There are, however, some interesting differences, particularly on PV+ interneurons, which appear to be more excitable than wild type in the heterozygotes but more excitable in the heterozygotes. This raises the interesting question (which could be more explicitly discussed by the authors) as to whether the reported changes represent homeostatic events that suppress the seizure phenotype in the mouse heterozygotes or simply changes in excitability that do not reach the threshold for behavioral outcomes.

That is an interesting question. We have added a new paragraph to the Discussion speculating about whether the alterations in SST and PV excitability suppress seizures or do not reach the threshold for behavioral outcomes. This seems to be requested by the second reviewer as well in Weaknesses point #2.

Strengths and Weaknesses:

(1) The authors find that the heterozygous mutation in PV+ interneurons increases their excitability, a result that is opposite from their previous observation in neurons with the corresponding homozygous mutation.

We would like to provide a minor clarification to the above statement that, in this manuscript, we show that “the heterozygous mutation in PV+ interneurons increases their excitability, a result that is opposite from their previous observation in neurons with the corresponding homozygous mutation”. In our previous manuscript, we assessed YH-HOM phenotypes in NFS and FS GABAergic neurons, but did not specifically mark PV neurons. Although the YH-HOM FS neurons showed an increase in rheobase and a decrease in AP firing, the magnitudes of these effects were far less than those observed in the NFS population. More importantly, the FS GABAergic population likely consists of PV- and SST-expressing neurons; thus, we can not directly compare the results from the NFS and FS groups to the PV and SST groups, respectively (please see our response to Weaknesses point #3, Reviewer #2). We apologize for the confusion.

They propose that this results from the selective upregulation of a persistent sodium current INaP in the PV+ interneurons. While the observations are very interesting, there are three issues concerning this interpretation that should be addressed:

A) The protocol for measuring the INaP current could potentially lead to results that could be (mis)interpreted in different ways in different cells. First, neither K currents nor Ca currents are blocked in these experiments. Instead, TTX is applied to the cells relatively rapidly (within 1 second) and the ramp protocol is applied immediately thereafter. It is stated that, at this time, Na currents and INaP are fully blocked but that any effects on Na-activated K currents are minimal. In theory, this would allow the pre- to post-difference current to represent a relatively uncontaminated INaP. This would, however, only work if activation of KNa currents following Na entry is very slow, taking many seconds. A good deal of literature has suggested that the kinetics of activation of KNa currents by Na influx vary substantially between cell types, such that single action potentials and single excitatory synaptic events rapidly evoke KNa currents in some cell types. This is, of course, much faster than the time of TTX application. Most importantly, the kinetics of KNa activation may be different in different neuronal types, which would lead to errors that could produce different estimates of INaP in PV+ interneurons vs other cell types.

First, we’d like to point out that we did not want to block K+ currents (which would also block KNa) when measuring INaP for these experiments, because our hypothesis was that the increased KNa current in YH-HET PV neurons was somehow causing an increase in INaP, and it is possible that this increase depends on an intact KNa. Thus, we decided to use a method based on the observation in our experiments, and previously made by others (Budelli et al., 2009), that the reduction of outward current after TTX addition is slow relative to the rapid reduction in Na+ current. We understand and agree with the reviewer that, if KNa currents were blocked more quickly by TTX in some neuron types than others, then our estimate of INaP using this method would be contaminated in these neuron types, which would lead to inaccurate measurements. To assess this possibility among the main neuron types used in this study, we performed new experiments in which we monitored the time course of INaP block and subsequent IKNa loss following TTX application in PV and SST neurons during slow voltage ramps. We note that action potentials are not present in the slow voltage ramps due to inactivation of the transient Na+ current. These new experiments show that, in SST and PV (both WT and Het) neurons, the block of INaP is nearly complete at the 6s time point, whereas the decay in IKNa is far slower (V50 of ≈ 25s), and importantly, these results do not differ substantially by cell type or genotype. These data suggest that our measurements of INaP are not significantly contaminated by IKNa, and that this method allows for the effective separation of these two currents. These data have been added as a supplemental figure (Supplemental Fig. 7-1) and are briefly described and referenced in the Results section.

B) As the authors recognize, INaP current provides a major source of cytoplasmic sodium ions for the activation. An expected outcome of increased INaP is, therefore, further activation of KNa currents, rather than a compensatory increase in an inward current that counteracts the increase in KNa currents, as is suggested in the discussion.

We agree that the increase in INaP could theoretically further increase IKNa, as veratridine was previously shown to increase IKNa (Hage & Salkoff, 2012). However, we do not believe that this would necessarily be the case, because as the reviewer notes in their next comment, there is insufficient information on the relative locations of the INaP and KCNT1 channels, as well as the kinetics of sodium transfer to KCNT1 channels, and even less is known in the context of KCNT GOF neurons. Thus, there are a couple of plausible reasons that increased INaP may not alter KNa currents in YH-HET PV neurons: (1) In YH-HET PV neurons, the particular sodium channels that are responsible for the increased INaP may not be located within close proximity to the KCNT1 channels. (2) Homeostatic mechanisms that alter the AIS length, or move the AIS further from the soma, in response to altered neuronal excitability are well described (Grubb & Burrone, 2010; Kuba et al., 2010); thus, it is possible that in YH-HET PV neurons, the length or location of the AIS is altered, leading to uncoupling of the sodium channels that are responsible for the increased INaP to the KCNT1 channels.

C) Numerical simulations, in general, provide a very useful way to evaluate the significance of experimental findings. Nevertheless, while the in-silico modeling suggests that increases in INaP can increase firing rate in models of PV+ neurons, there is as yet insufficient information on the relative locations of the INaP channels and the kinetics of sodium transfer to KNa channels to evaluate the validity of this specific model.

We completely agree; thus, we have described each of these limitations in the Discussion. We state that the model neurons may “lack more detailed features of ion channels, such as post-translational modifications and subcellular localizations”, and that our KCNT1 model conductance is “hampered by an incomplete understanding of the relationship between Na+ influx, membrane voltage, and channel gating in neurons”.  

(2) The greatest effect of TTX application would be expected to be the elimination of large transient inward sodium currents. Why are no such currents visible in the control (pre-TTX) or the difference currents (Fig. 2)? Is it possible I missed something in the methods?

We apologize for the confusion and our mistake in failing to mention this important feature of the displayed traces. To include all of the representative traces in the figures, and prevent overlap of the traces, we removed the large inward sodium currents using the masking tool in Adobe Illustrator in Figure 2 and Supplemental Figure 5-1. We have added that information to the relevant figure legends. We have also provided unmasked images of the representative traces from Figure 2 and Supplemental Figure 5-1 to illustrate the large transient inward sodium currents, and the significant reduction of these currents with TTX treatment.

(3) As expected, the changes in many of the measured parameters are smaller in the present study with heterozygotes than those previously reported for the homozygous mutation. Some of the statements on the significance of some of the present findings need to be stated more clearly. For example, in the results section describing Fig. 2, it is stated that "In glutamatergic and NFS GABAergic YH-HET neurons, the overall KNa current was increased ...as measured by a significant effect of genotype ...." Later in the same paragraph it is stated that the increases in KNa current are not significant. Apparently, different tests lead to different conclusions. Both for the purpose of understanding the pathophysiological effects of changes in KNa current and for making further numerical simulations, more explicit clarifying statements should be made.

We apologize for the confusion on the description of these statistics. The results come from the same test, which is a Generalized Linear Mixed Model (GLMM). The factors in our GLMM were voltage step, genotype, and a voltage step x genotype interaction term. The overall effect of genotype is significant in glutamatergic neurons, but pairwise tests at each voltage step show no significant effect of genotype at any given voltage. This is somewhat analogous to running a traditional ANOVA on multiple groups and finding a significant ANOVA p-value but no significant post-hoc multiple comparisons tests, and is not uncommon. Our interpretation of this is that heterozygous expression of the YH variant in glutamatergic neurons likely increases KNa currents across positive potentials (as was seen with the YH-HOM glutamatergic neurons), but only a small amount at each positive step; thus, we lack the statistical power to determine any particular voltage step where this occurs.

(4) The effects of the KCNT1 channel blocker VU170 on potassium currents are somewhat larger and different from those of TTX, suggesting that additional sources of sodium may contribute to activating KCNT1, as suggested by the authors. Because VU170 is, however, a novel pharmacological agent, it may be appropriate to make more careful statements on this. While the original published description of this compound reported no effect on a variety of other channels, there are many that were not tested, including Na and cation channels that are known to activate KCNT1, raising the possibility of off-target effects.

We agree and thank the reviewer for making this point. To address this question, we measured KNa currents in WT vs. Kcnt1/Kcnt2-dKO neurons using VU170 to illustrate the extent of outward current due to off-target effects of the drug. These data have been included as a supplemental figure (Supplemental Fig. 5-2). We have also added several sentences to the Results section referencing this figure. Interestingly, in Kcnt1/Kcnt2-dKO neurons, VU170 seems to be quite specific across the negative potentials, as no outward currents are apparent until approximately -10 mV onward, whereas across positive potentials, there is a VU170-senstive outward current reaching ~1 nA by +50 mV. We have also included a note of caution in interpreting these data and added the possibility of off-target effects of VU170 as an alternative explanation for the differences observed on KNa currents between TTX and VU170 to the Discussion section.

(5) The experiments were carried out at room temperature. Is it possible that different effects on firing patterns in heterozygotes and homozygotes would be observed at more physiological temperatures?

Yes, it is reasonable to assume that an increased temperature would affect neuronal firing patterns in cultured neurons, as temperature differences have been shown to alter synaptic transmission and neuronal function, as assessed in both cultured neuron and slice recordings. All of our recordings were performed at room temperature in this study, and although they are valid with regard to between-group comparisons, this additional caveat is worth mentioning. We have added this to the paragraph describing study limitations in the Discussion section.

To better understand the effects of temperature in our recordings, we have now compared membrane and AP generation parameters at room temperature (~22°C) and at a more physiological temperature (35°C) in a before-after study of 16 WT neurons, including both glutamatergic and GABAergic neuron types. Not surprisingly, we found robust alterations in all parameters assessed, excluding resting membrane potential and capacitance. We further assessed the effect of temperature on WT and YH-HET PV neurons, as the PV neurons expressing the YH variant showed the most unexpected phenotypes in our study. In our room temperature recordings, we showed that the YH-HET variant decreased the rheobase current, increased the AP amplitude, and increased the AP firing. In our before-after comparison (22°C-35°C) of PV neurons (WT; n=11, YH-Het; n=10), the WT and YH-HET neurons showed the same temperature-dependent effects on these parameters, including increased rheobase, decreased AP amplitude, and a higher maximal firing rate, at 35°C compared to those at 22°C. These data have been added to the manuscript as a supplemental figure (Supplemental Fig. 4-3) and are briefly referenced and described in the Results section.     

Moreover, in our original manuscript, we showed that the effects of the homozygous YH variant on glutamatergic and NFS GABAergic neuron excitability were highly similar between cultured recordings at room temperature (~22°C) and slice recordings at 32°C. Taken together, these data suggest that the reported neurophysiological phenotypes downstream of the YH variant are likely not temperature dependent. 

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shore et al. investigate the consequent changes in excitability and synaptic efficacy of diverse neuronal populations in an animal model of juvenile epilepsy. Using electrophysiological patch-clamp recordings from dissociated neuronal cultures, the authors find diverging changes in two major populations of inhibitory cell types, namely somatostatin (SST)- and parvalbumin (PV)-positive interneurons, in mice expressing a variant of the KCNT1 potassium channel. They further suggest that the differential effects are due to a compensatory increase in the persistent sodium current in PV interneurons in pharmacological and in silico experiments.

Strengths:

(1) Heterozygous KCNT1 gain of function variant was used which more accurately models the human disorder.

(2) The manuscript is clearly written, and the flow is easy to follow. The authors explicitly state the similarities and differences between the current findings and the previously published results in the homozygous KCNT1 gain of function variant.

(3) This study uses a variety of approaches including patch clamp recording, in silico modeling, and pharmacology that together make the claims stronger.

(4) Pharmacological experiments are fraught with off-target effects and thus it bolsters the authors' claims when multiple channel blockers (TTX and VU170) are used to reconstruct the sodium-activated potassium current. Having said that, it would be helpful to see the two drug manipulations used in the same experiment. Notably, does the more selective blocker VU170 mimic the results of TTX for NFS GABAergic cells in Figure 2? And does it unmask a genotype difference for FS GABAergic cells like the one seen in PV interneurons in Figure 5C3.

To illustrate the two drug manipulations in the same experiment, we recorded from WT SST and PV neurons (5 neurons/group) and blocked KNa currents first using TTX and then VU170, following wash out between the two drugs, in the same neurons. Below, we have plotted the points at each voltage step for each SST and PV neuron, and for each drug treatment, on the same graph to show how they vary directly. At each voltage step, lines connect the points representing the TTX-sensitive and VU-sensitive currents for each neuron to show the individual effects (left-most graphs). Summary data are shown across all voltages (middle graphs) and across negative voltages (right-most graphs).

Author response image 1.

We have not used VU170 on FS and NFS populations of GABAergic neurons. However, for reasons that are explained more extensively below in response to Weaknesses #3, we would not predict KNa currents recorded from SST- and PV-GABAergic neurons to mimic those of NFS- and FS-GABAergic neurons, respectively.

Weaknesses:

(1) This study relies on recordings in dissociated cortical neurons. Although specific WT interneurons showed intrinsic membrane properties like those reported for acute brain slices, it is unclear whether the same will be true for those cells expressing KCNT1 variants. This reviewer highly recommends confirming some of the key findings using an ex vivo slice preparation. This is especially important given the discrepant result of reduced excitability of PV cells reported by Gertler et al., 2022 (cited here in the manuscript but not discussed in this context) in acute hippocampal slices for a different KCNT1 gain of function variant.

We thank the reviewer for this suggestion. To test whether SST-expressing YH-HET neurons show similar impairments to those observed in culture, we crossed the FVB-Tg(GadGFP)45704Swn/J transgenic mouse line (Jackson Labs #003718), also known as the GIN line, to the Kcnt1-YH line. Mice from the GIN line express eGFP in a subpopulation of SST-expressing neurons in the hippocampus and cortex. We performed slice recordings of cortical layer 2/3, GFP-expressing neurons from P21-30, WT and YH-HET GIN mice. Although the input resistance was not significantly decreased, the rheobase was higher in the YH-HET neurons, and they fired fewer APs across increasing current steps, than WT neurons, supporting the main findings from the SST-expressing neurons in culture. These data have been added to the manuscript in a new figure (Fig. 9).

Regarding the previously published results on the effect of KCNT1 GOF on PV neuron excitability by Gertler et al., we have written a new paragraph in the Discussion section (last paragraph of the section, “Neuron-type-dependent KCNT1 GOF effects”) that discusses the differences between the findings by Gertler et al. and the current study. 

To further investigate the effects of heterozygous YH variant expression on SST- vs. PV-expressing neuron excitability in ex vivo slice recordings, we are now crossing a cre-inducible, Td-Tomato Red reporter line (Ai9) to the Kcnt1-YH line. After obtaining Ai9Tg/Tg; Kcnt1m/+ mice, we will cross these to Sst-Cre and Pvalb-Cre lines to be able to record from marked SST and PV, WT and YH-HET neurons in slice. We plan on submitting results from these recordings as an eLife Research Advances article linked to this article.

(2) It is unclear how different pieces of results fit together to form a story about the disease pathophysiology.

We have added a paragraph to the Discussion to speculate on how these various GABAergic subtype-specific effects downstream of the YH variant may contribute to overall network/brain pathology and seizure propensity in heterozygous mice.

For example, hyperexcitability of PV cells would suggest more inhibition which would counter seizure propensity. However, spontaneous inhibitory postsynaptic currents show no change in pyramidal neurons. Moreover, how do the authors reconcile that the reductions in synaptic inputs onto interneurons in Figure 3B with the increases in Figure 8? This should be discussed.

Generally, network and synaptic alterations downstream of the heterozygous variant were quite minimal compared with those of the homozygous variant. Although there were reductions in the frequency of synaptic inputs onto inhibitory neurons, the changes were relatively small. Thus, we concluded that the neuronal effects downstream of the heterozygous YH variant were below some threshold to result in broader network effects on synaptic activity and connectivity similar to those in the homozygous YH model. The discrepancies between our GABAergic vs. FS/NFS vs. VIP/SST/PV data will be discussed in more detail in response to Weakness #3.   

(3) Similarly, the results in this work are not entirely internally consistent. For example, given the good correspondence between FS and NFS GABAergic cells with PV and SST expression, why are FS GABAergic cells hyperexcitable in Figure 1? If anything, there is a tendency to show reduced excitability like the NFS GABAergic cells.

In our neuron cultures, 76-80% of Neu-N-expressing neurons are GFP+ (from the CamKII-eGFP virus used to mark glutamatergic neurons), and of the remaining ~20-24%, the majority are GABAergic (verified using the Dlx5/6-mRuby virus to mark GABAergic neurons and using electrophysiology to assess AP parameters and analyze evoked responses). In our original experiments, recordings sampled from this larger GABAergic population were used (Fig. 3), or this population was sorted almost equally into FS and NFS (Figs. 1 and 2).

In later experiments, we isolated and cultured neurons from VIP-Cre, SST-Cre, and PV-Cre mouse lines and marked these neuron types in vitro with a Cre-inducible mCherry virus. In the VIP-Cre cultures, ~6% of the GFP- population, or 1.2% of the Neu-N-population, was mCherry+. In the SST-Cre cultures, ~20.5% of the GFP- population, or 4.7% of the Neu-N-population, was mCherry+. In the PV-Cre cultures, less than 1% of the Neu-N-population was mCherry+, which is not surprising considering the relatively late onset of PV expression compared with those of VIP and SST. Thus, we would estimate that we are marking and recording from less than 30% of the total GABAergic population in these in vitro experiments, rather than the 80-90% that these three populations would sum to in vivo.  

Furthermore, using our original criteria for sorting GABAergic neurons into FS and NFS subtypes, all VIP recorded neurons were of the NFS type, PV of the FS type, whereas SST were of the FS (38%) and NFS (62%) types, which is not far off from the significant fraction of SST neurons that have been shown to be fast-spiking in slice experiments (Kvitsiani et al., 2013; Urban-Ciecko & Barth, 2016). Therefore, the FS group consists of both PV and SST neurons, and the NFS group consists of both VIP and SST neurons, and likely also contains immature PV neurons that have not yet developed a fast-spiking phenotype. Taken together, this suggests that the data from these two sets of experiments (FS/NFS vs. VIP/SST/PV) are not directly comparable.

Also, why do the WT I-V curves look so different between Figures 2 and 5? This reviewer suggests at least a brief explanation in the discussion.

As to the differences in appearance between the WT I-V curves in Figures 2 and 5, those plots are from different neuron types (Fig. 2: Glutamatergic, FS GABAergic, and NFS GABAergic vs. Fig. 5: VIP-, SST-, and PV-expressing), and the KNa currents are isolated using different methods (Fig. 2: TTX-subtraction vs. Fig. 5: VU170-subtraction). TTX blocks an inward Na+ current, which is apparent across subthreshold voltages in Fig. 2C1-3, whereas VU170 does not block this current, making it not apparent in Fig. 5C1-3. Also, the bottom three panels in Fig. 2C1-3 show the KNa current from -80 to 0 mV, whereas those in Fig. 5C1-3 show from -80 to -30 mV, to better illustrate the areas spanning KNa current increases, so their appearance is not directly comparable.

(4) Given the authors' claim that the KCNT1 activation curve is a major contributor to the observed excitability differences in specific GABA cell subtypes, it would be helpful to directly measure the activation curve in the variants experimentally as was done for WT KCNT1 in Figure 6A and use the derived kinetics in the compartmental model.

We apologize for the confusion. Although the activation curves among different GABAergic subtypes from WT KCNT1 are distinct, and we believe that these varying kinetics contribute to the neuron-type-specific phenotypes of KCNT1 GOF, we didn’t intend to suggest that the heterozygous Y777H variant itself causes neuron-type-specific alterations to the activation curves of the GABAergic subtypes. To clarify this point, below, we show the high similarity of the activation curves between WT KCNT1 and YH-HET KCNT1 in each of the GABAergic subtypes.

Author response image 2.

Reviewer #3 (Public Review):

Summary:

The present manuscript by Shore et al. entitled Reduced GABAergic Neuron Excitability, Altered Synaptic Connectivity, and Seizures in a KCNT1 Gain-of-Function Mouse Model of Childhood Epilepsy" describes in vitro and in silico results obtained in cortical neurons from mice carrying the KCNT1-Y777H gain-of-function (GOF) variant in the KCNT1 gene encoding for a subunit of the Na+-activated K+ (KNa) channel. This variant corresponds to the human Y796H variant found in a family with Autosomal Dominant Nocturnal Frontal lobe epilepsy. The occurrence of GOF variants in potassium channel encoding genes is well known, and among potential pathophysiological mechanisms, impaired inhibition has been documented as responsible for KCNT1-related DEEs. Therefore, building on a previous study by the same group performed in homozygous KI animals, and considering that the largest majority of pathogenic KCNT1 variants in humans occur in heterozygosis, the Authors have investigated the effects of heterozygous Kcnt1-Y777H expression on KNa currents and neuronal physiology among cortical glutamatergic and the 3 main classes of GABAergic neurons, namely those expressing vasoactive intestinal polypeptide (VIP), somatostatin (SST), and parvalbumin (PV), crossing KCNT1-Y777H mice with PV-, SST- and PV-cre mouse lines, and recording from GABAergic neurons identified by their expression of mCherry (but negative for GFP used to mark excitatory neurons).

The results obtained revealed heterogeneous effects of the variant on KNa and action potential firing rates in distinct neuronal subpopulations, ranging from no change (glutamatergic and VIP GABAergic) to decreased excitability (SST GABAergic) to increased excitability (PV GABAergic). In particular, modelling and in vitro data revealed that an increase in persistent Na current occurring in PV neurons was sufficient to overcome the effects of KCNT1 GOF and cause an overall increase in AP generation.

Strengths:

The paper is very well written, the results clearly presented and interpreted, and the discussion focuses on the most relevant points.

The recordings performed in distinct neuronal subpopulations are a clear strength of the paper. The finding that the same variant can cause opposite effects and trigger specific homeostatic mechanisms in distinct neuronal populations is very relevant for the field, as it narrows the existing gap between experimental models and clinical evidence.

Weaknesses:

My main concern is in the epileptic phenotype of the heterozygous mice investigated. In fact, in their previous paper the Authors state that "...Kcnt1-Y777H heterozygous mice did not exhibit any detectable epileptiform activity" (first sentence on page 4). However, in the present manuscript, they indicate twice in the discussion section that these mice exhibit "infrequent seizures". This relevant difference needs to be clarified to correctly attribute to the novel pathophysiological mechanism a role in seizure occurrence. Were such infrequent seizures clearly identified on the EEG, or were behavioral seizures? Could the authors quantify this "infrequent" value? This is crucial also to place in the proper perspective the Discussion statement regarding "... the increased INaP contribution to ... network hyperexcitability and seizures".

We apologize for the confusion. Indeed, in the Results section from our previous paper, we failed to observe seizures in 14 heterozygous mice, whereas 23/25 homozygous mice showed seizures by video-EEG. However, in the fifth paragraph of the Discussion section from that paper, we further stated that “during the preparation and review of [that] article, we observed seizures in two Kcnt1-Y777H heterozygous mice, one during a widefield Ca2+ imaging experiment and the other during a video-EEG experiment”. Thus, we concluded that “heterozygous expression can result in seizures in a rodent model, but apparently at a much lower frequency than that observed with homozygous expression”. To emphasize these findings, we’ve added a sentence to the Introduction in this manuscript about the occurrence of infrequent seizures in Kcnt1-Y777H heterozygous mice, along with a reference to the Discussion of our previous paper.

Of the two observed seizures, one seizure was captured in the Weston Lab at the University of Vermont from a Kcnt1-Y777H heterozygous mouse expressing a calcium indicator (after it was bred to the Snap25-GCaMP6s line) during a Ca2+ widefield imaging experiment, and it was accompanied by a time-locked video of the seizure event. The other seizure was recorded as a control during a drug study using video-EEG. This Kcnt1-Y777H heterozygous mouse had multiple tonic seizures, as evidenced by EEG traces and the accompanying video, which were recorded and analyzed in the Frankel Lab at Columbia University. The seizures from heterozygous mice have not been officially quantified, as they have only been rarely observed across multiple different experiments using heterozygous mice at multiple institutions, making quantification quite difficult.

Lastly, regarding attributing the role of the identified pathological mechanisms to seizure occurrence mentioned by the reviewer, we have added a paragraph to the Discussion to speculate on how the various GABAergic subtype-specific effects downstream of the YH variant may contribute to the general lack of network/brain pathology and seizure generation in heterozygous mice.  

Also, some statistical analysis seems to be missing. For example, I could not find any for the data shown in Fig. 6. Thus, the following statement: "the model PV neurons responded to KCNT1 GOF with decreased AP firing and an increased rheobase" requires proper statistical evaluation.

We thank the reviewer for this suggestion. We were initially hesitant to apply a formal statistical analysis to the modeling data because it differs in important ways from the experimental data. However, we have now provided statistical analyses of these data, with some caveats. Because we applied each KCNT1 GOF level (40, 35, and 30 mM) to the same set of neurons for each data set, we performed repeated measures ANOVA analyses to assess differences due to GOF in each subtype. We note that some changes are statistically significant, but may not be physiologically relevant. For example, there are changes in input resistance and rheobase in VIP neurons only at the higher GOF level (30 mM), but the magnitude of each change is quite small relative to those in SST neurons (Rin: 1.7 MΩ in VIP vs. 23.2 MΩ in SST, rheo: 1.7 pA in VIP vs. 52.5 pA in SST), and likely as a consequence, there are no downstream effects on the AP firing rate at either GOF level in VIP neurons. It is important to examine the magnitude of the effects and interpret them in the context of the changes in other neuron types and in the experimental data, thus, we’ve provided two new figures to better illustrate the relative changes in each neuron type (Supplemental Figures 6-2 and 7-2). We have also added these statistical results to Figures 6E2, 6F2, 6G2, and 7E, and Supplemental Fig. 6-1, and we have described them in the Results section. A summary of the statistics has also been added in Supplemental Table 6.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

In addition to addressing the weaknesses highlighted in the public review, this reviewer recommends using a KCNT1 agonist such as loxapine to see if activating the potassium channel mimics the KCNT1 GOF in SST and PV cells.

Although we appreciate this suggestion, we’re not sure whether treating GABAergic subtypes with loxapine would provide much clarity in the absence of many supporting experiments. First, the amount of channel activation and any changes in kinetics caused by loxapine would need to be measured and compared to the YH-HET GOF effects in order to interpret the results. In addition, the aforementioned caveat about off-target effects of small molecules would also have to be considered, as loxapine inhibits many other channels at nanomolar concentrations.

More importantly, we hypothesize that several of the GABAergic subtype-specific effects of KCNT1 GOF result from homeostatic or adaptive mechanisms due to long-term increases in KNa currents. For instance, PV-expressing YH-HET neurons had a lower rheobase, increased AP amplitude, and increased AP firing frequency, effects that we believe are due, not to increased KNa currents themselves, but to a compensatory increase in a persistent Na+ current. For the SST neurons, we hypothesize that the increased capacitance and soma size, together with the increased electrical coupling, exacerbate the hypoexcitability phenotype downstream of the YH variant. Thus, we would not necessarily expect that opening KCNT1 channels by acute loxapine treatment would mimic many of these effects.

Indeed, in a previous study using a different KCNT1 GOF mouse model, loxapine treatment mimics KCNT1 GOF effects in some neuron types (reduced AP firing frequency in loxapine-treated, WT PV neurons mimics that observed in heterozygous KCNT1 GOF PV neurons), but not in others (reduced AP firing frequency in loxapine-treated, WT pyramidal neurons does not mimic the unaltered AP firing frequency observed in heterozygous and homozygous KCNT1 GOF pyramidal neurons) (Gertler et al., 2022).  

Related to this suggestion by the reviewer, we are currently performing studies using a KCNT1 blocker in WT and Kcnt1-KO neurons to better understand the role of KCNT1 among cortical neuronal subtypes that will be published in a future manuscript.

Reviewer #3 (Recommendations For The Authors):

Though I realize that primary cultures allow for efficient identification of neuronal subclasses, it would have been useful to show that similar changes also occur in neurons with conserved in vivo connectivity, such as those recorded from brain slices.

We thank the reviewer for this suggestion. We have added an additional figure (Fig. 9) showing that the hypoexcitability phenotype observed in SST neurons in culture recordings is conserved in SST neurons in slice recordings from GIN mice, which express GFP predominately in SST-expressing neurons.

In addition, further experiments in PV neurons from Kcnt1-Y777H homozygous mice would provide evidence for a gene-dosage role in the changes found in heteros.

For this manuscript, we chose to focus our efforts on understanding the effects of heterozygous Kcnt1 variant expression in various neuronal subtypes with the goal of better modeling GOF variant effects in human disease. However, we’re very interested in investigating the effects of homozygous expression of the YH variant on each of the GABAergic subtypes to compare with those found in this study, but this requires more rounds of breeding to get homozygous mice with GABAergic subtype-specific expression of cre recombinase. We look forward to reporting the results from these experiments in a future manuscript.

Also, when addressing the issue regarding the different effects of the same GOF variant on the excitability of distinct neuronal populations in the Discussion or Introduction sections, the authors may want to cite the recent work on KCNQ2 and KCNQ3 by the Tzingounis group (https://pubmed.ncbi.nlm.nih.gov/37607817/).

We thank the reviewer for bringing this manuscript to our attention. We have added this citation to a new paragraph in the Discussion section regarding neuron-type specific effects of ion channel variants (the last paragraph focusing on the effects in PV neurons).

Budelli, G., Hage, T. A., Wei, A., Rojas, P., Jong, Y. J., O'Malley, K., & Salkoff, L. (2009). Na+-activated K+ channels express a large delayed outward current in neurons during normal physiology. Nat Neurosci, 12(6), 745-750. https://doi.org/10.1038/nn.2313

Gertler, T. S., Cherian, S., DeKeyser, J. M., Kearney, J. A., & George, A. L., Jr. (2022). K(Na)1.1 gain-of-function preferentially dampens excitability of murine parvalbumin-positive interneurons. Neurobiol Dis, 168, 105713. https://doi.org/10.1016/j.nbd.2022.105713

Grubb, M. S., & Burrone, J. (2010). Activity-dependent relocation of the axon initial segment fine-tunes neuronal excitability. Nature, 465(7301), 1070-1074. https://doi.org/10.1038/nature09160

Hage, T. A., & Salkoff, L. (2012). Sodium-activated potassium channels are functionally coupled to persistent sodium currents. J Neurosci, 32(8), 2714-2721. https://doi.org/10.1523/JNEUROSCI.5088-11.2012

Kuba, H., Oichi, Y., & Ohmori, H. (2010). Presynaptic activity regulates Na(+) channel distribution at the axon initial segment. Nature, 465(7301), 1075-1078. https://doi.org/10.1038/nature09087

Kvitsiani, D., Ranade, S., Hangya, B., Taniguchi, H., Huang, J. Z., & Kepecs, A. (2013). Distinct behavioural and network correlates of two interneuron types in prefrontal cortex. Nature, 498(7454), 363-366. https://doi.org/10.1038/nature12176

Shore, A. N., Colombo, S., Tobin, W. F., Petri, S., Cullen, E. R., Dominguez, S., Bostick, C. D., Beaumont, M. A., Williams, D., Khodagholy, D., Yang, M., Lutz, C. M., Peng, Y., Gelinas, J. N., Goldstein, D. B., Boland, M. J., Frankel, W. N., & Weston, M. C. (2020). Reduced GABAergic neuron excitability, altered synaptic connectivity, and seizures in a KCNT1 gain-of-function mouse model of childhood epilepsy. Cell Rep.

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Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

This manuscript by Tesmer and colleagues uses fiber photometry recordings, sophisticated analysis of movement, and deep learning algorithms to provide compelling evidence that activity in hypothalamic hypocretin/orexin neurons (HONs) correlates with net body movement over multiple behaviors. By examining projection targets, the authors show that hypocretin/orexin release differs in projection targets to the locus coeruleus and substantia nigra, pars compacta. Ablation of HONs does not cause differences in the power spectra of movements. The movement-tracking ability of HONs is independent of HON activity that correlates with blood glucose levels. Finally, the authors show that body movement is not encoded to the same extent in other neural populations.

Strengths:

The major strengths of the study are the combination of fiber photometry recordings, analysis of movement in head-fixed mice, and sophisticated classification of movement using deep learning algorithms. The experiments seem to be well performed, and the data are well presented, visually. The data support the main conclusions of the manuscript.

We thank the reviewer for their supportive feedback.

Weaknesses:

The weaknesses are minor, mostly consisting of writing and data visualization throughout the manuscript. To some degree, it is already known that hypocretin/orexin neurons correlate with movement and arousal, although this manuscript studies this correlation with unprecedented sophistication and scale. It is also unfortunate that most of the experiments throughout the study were only performed in male mice. Taken together, this study is likely to be impactful to the field and our understanding of HONs across behavioral states.

We agree that disentangling movement from arousal is an important aspect, and in the revised manuscript, we now include new data and analyses towards this (pupillometry to directly assess arousal, and multivariate analysis to assess contributions of arousal vs movemement to HON activity). In addition, we now implement many of the reviewer’s recommendations regarding writing, data presentation, and visual clarity (see our replies in the “recommendations for authors” section).

Reviewer #1 (Recommendations for the authors):

Some recommendations for the authors:

(1) The first sentence of the Introduction states: "Neural activity related to body movement recently received much attention." I would rephrase or clarify this statement, as neuroscientists have been studying neural activity related to body movement for decades.

The reviewer is correct. Our intention was to highlight the resurgence of movementrelated neurosciences enabled by modern techniques such as deep learning applied to video data (e.g. DeepLabCut, etc). The passage has been updated for clarity.

(2) The Introduction also states that HONs orchestrate "consciousness and arousal." I would delete the word "consciousness," as consciousness represents a lofty, global concept that is challenging to define and quantify in humans, let alone mice.

We used the word consciousness to be consistent with current literature on the function of the mouse hypothalamus (e.g. Nat Neurosci 2016 Feb;19(2):290-8). But we agree it is not necessary here, and so we followed the advice to delete it.

(3) The authors state that HON dynamics were recorded while mice were head-fixed while on a running wheel. For clarity, it would be helpful to visualize this head-fixation in Figures 1A and 5B. It would also be helpful to clarify how certain behaviors (e.g. grooming, chewing) were performed and recorded while the mouse was head-fixed.

In the revised manuscript, updated graphics with a head-fixed mouse have now been added to relevant figures. Representative RGB frames (colors representing sequential frames) of each behaviour have been added to Figure 2A.

(4) In the legend for Figure 1A, the reference to Gonzalez et al. 2016 seems out of place (at least the reader should be informed why the text is referring to this previous study). Additionally, because the references are ordered by number instead of alphabetically, it would be more helpful to refer to a numbered reference rather than a name.

Gonzalez et al. 2016 references the source of the AAV construct used in this figure. This has been moved to the methods. Following eLife formatting guidelines, references will be alphabetized upon publication.

(5) In Figure 3F, it would be helpful to show visual validation that the HON-DTR method indeed ablates all HONs. This is depicted conceptually, but representative figures would be much more convincing.

A representative histological slice is now included for both wild type (WT) and HON-DTR mice in the new Figure 4B.

Reviewer #2 (Public review):

Summary:

Despite several methodological strengths, the major and highly significant drawback is the confound of arousal with movement. This confound is not resolved, so the results could be explained by previously established relationships between orexin and arousal/wakefulness.

This an excellent point, and we agree. To address this directly in the revised manuscript, we now include new data and analyses towards this (pupillometry to directly assess arousal, and multivariate analysis to assess contributions of arousal vs movemement to HON activity).

Strengths:

The authors show that orexin neuron activity is associated with body movement and that this information is conveyed irrespective of the fasted state. They also report differences in different orexin target brain regions for orexin release during movement. This paper contains an impressive array of cutting-edge techniques to examine a very important brain system, the orexin-hypocretin system. The authors offer an original perspective on the function of this system. The authors showed that orexin neuron activity scales to some degree with the magnitude of body movement change; this is unaffected by a fasted state and seems to be somewhat unique to orexin neurons.

The investigation of other genetically defined subcortical neuron populations to determine the specificity of findings is also a strength, as is the ability to quantify movement and use deep learning to classify specific behaviors adds sophistication to analysis. The authors also show heterogeneity in orexin projections to specific target nuclei, which is interesting.

The authors "speculate that narcolepsy-cataplexy, caused by HON loss-of-function, is perhaps explained by oscillations into unwanted sleep-states and motor programs due to impaired control loops for wakefulness and movement". This is quite an interesting aspect of their work and deserving of further study.

We thank the reviewer for their supportive feedback.

Weaknesses:

Despite the strengths, there are several major and minor weaknesses that detract significantly from the study.

My main concern with this work is the confound of arousal with movement so that correlations with one might reflect a relationship instead with the other. The orexin system is well known to play an important role in arousal, with elevated activity of orexin neurons reported for waking and high arousal. Orexin signaling has also been strongly associated with motivation, which also is associated with arousal and movement. The authors offer no compelling evidence that the relationships they describe between different movements and orexin signaling do not simply reflect the known relationship between arousal and motivation.

The authors could address this concern by including classical arousal measurements, eg, cortical EEG recorded simultaneously with movements. Often, EEG arousal occurs independently of movement, so this could provide one approach to disentangling this confound. The idea that orexin signaling plays a role in arousal rather than movement is supported by their finding that orexin lesions using the orexin-DTR mouse model did not impact movements. In contrast, prior lesion and pharmacologic studies have found that decreased orexin signaling significantly decreases arousal and waking.

Another way they could test their idea would be to paralyze and respirate animals so that orexin activity could be recorded without movement. Alternatively, animals could be trained to remain motionless to receive a reward. Thus, there are several ways to test the overall hypothesis of this work that have not been examined here.

The authors propose that "a simple interpretation of their results is that, via HON movement tracking, the brain creates a "wake up" signal in proportion to movement". This seems to argue for the role of the orexin system in arousal and motivation rather than in movement per se.

Thank you. We agree that disentangling between arousal and movement is indeed critical. A classic approach is a multivariate analysis, wherein multiple simultaneously recorded “predictors” of HON activity – such as arousal and movement - can be directly compared. While EEG arousal is an option, another well-accepted metric for arousal is pupil diameter. Using n = 7 mice, we now simultaneously record HON activity, movement, running speed, pupil size fluctuations, and ocular movements:

We then fit a partial least squares multivariate regression (a regression type more robust to collinearity) using the movement metric, pupil size, and ocular movements as predictors of orexin neuron activity. Consistent with previous publications, we found that pupil size alone has a positive correlation with hORX.GCaMP6s (~0.45). However, using a drop-one feature analysis in multivariate regression, we found that movement had the highest % contribution to statistically explaining orexin neuron activity. Here are the new results (which we now added as Fig. 7A-B).

Author response image 1.

Furthermore, we also expanded this analysis to incorporate the different frequencies found in HON dynamics, using empirical mode decomposition. We found that pupil size had a maximum correlation at lower HON frequencies than the movement metric, while ocular movements were maximally correlated in higher frequencies (now added as Fig. 7D,E).

Overall, this analysis suggests that – while HONs encode both movement and arousal – arousal and movement do not always co-fluctuate at the same timescales, and their impacts on HONs can be disentangled in a number of ways. We now mention this in revised text on page 5.

There are several studies that have examined the effect of orexin antagonist treatment in rodents on locomotor and other motor activities. These studies have largely found no consistent effect of antagonizing orexin signaling, especially at the OxR1 receptor, on simple motor activity. These studies are not referenced here but should be taken into account in the authors' conclusions.

We agree. Prior studies found that orexin antagonism – or optogenetic silencing of HONs – evokes either reduced locomotion, or no effect on locomotor movements. We now added text and references to paragraph 4 of Discussion, summarising this.

Figure 3, panel F: I understand HON-DTR is a validated model but a picture of HONs ablation is necessary, including pictures of HONs outputs ablation within the SNc and LC.

A representative histological slice is now included for both wild type (WT) and HON-DTR mice in the new Figure 4B. Because HONs are only found in the hypothalamus, somatic deletion of HONs in this region will result in axonal degradation in output regions.

The discussion lacks a more extensive paragraph on the distinct signal and role of Ox>SNc and Ox-LC projections.

We now added sentences discussing potential implications of this to Discussion (middle of paragraph 4).

Reviewer #2 (Recommendations for the authors):

Minor weaknesses

A very important movement in rodents is head orientation, especially given the limitation in ocular movement. However, this paper used a fixed head model which obviated this movement and did not attempt to analyze ocular movements.

Analysing ocular movements is something we had not considered but is very easy to check using pupillometry. In n = 7 mice, we recorded both orexin neurons, and ocular movements captured through an infrared camera under constant lighting. Ocular movements had a small positive correlation with orexin neuron photometry (r = ~0.26). See response to the public review above.

Author response image 2.

The "HON" abbreviation is not commonly used for orexin neurons, and I suggest replacing that with a more well-known abbreviation.

To the best of our knowledge, there is no universally agreed or best-known abbreviation for hypocretin/orexin neurons (we agree it would be nice if there was one!). “HONs” is a simple first letter abbreviation of hypocretin/orexin neurons, which acknowledges the two names for this peptide given by the original discoverers (de Lecea et al, and Sakurai et al, in 1998). Although this may not be the perfect abbreviation, we have kept it for now, also to be consistent with the large number (>10) of other published studies that recently used this abbreviation.

The graphs showing Pearson's r values do not demonstrate a very strong correlation between neural activity and movement change; they also lack validation of genetic expression/ablation in some cases. The results would more strongly support the conclusions if statistically significant correlations could be demonstrated between activity and movement.

We agree that a correlation of ~0.68 is probably not worthy of a “very strong” classification. While there is no universal ruleset for categorizing the strength of a correlation, we have toned down our language throughout the manuscript.

Comment regarding statistical testing of correlations: we are cautious to stand behind correlation significance testing for large sample sizes (~48’000 photometry & video samples in a 40-minute session). In our case, correlations were always extremely significant p<0.0001. The reason for this is that correlation p-values become “too big to fail” (see Lin et al. 2013) with inflated sample size. We therefore refrain from commenting on p-values and rather report between or within-subjects statistical tests, or tests against zero. See four example experiments below.

Author response image 3.

Citation: Lin, M., Lucas, H. C., Jr & Shmueli, G. Research Commentary—Too Big to Fail: Large Samples and the p-Value Problem. Information Systems Research 24, 906–917 (2013).

The rationale for looking at running speed, general movement, and specific types of nonlocomotor movements could be clarified and explained more thoroughly in the introduction. Why is it important to distinguish between locomotion (represented here with running) and all other movements? Presumably, this is because orexin is known to regulate arousal/locomotion. What evidence is there for orexin's role in other types of movements, which are being grouped together in Figure 1? This could be laid out in more detail in the Introduction. Relatedly, it is not very clear in the text whether the correlation between movement and orexin neuron activity includes movement related to running.

The main focus of our paper is on movement in general (i.e. video pixel difference, described in Results and Methods). This movement metric includes everything captured by the video, it is agnostic to the type of movement or behaviour.  To connect this to some of the specific innate movements/behaviours typically studied in mouse literature (running, grooming, sniffing, etc), we also performed plots in Figure 2. We attempted to explain this better in revised section 1 of Results.

What exactly is being correlated in Figure 1C (and throughout the rest of the paper?) Is this the average signal correlated with the average movement change over the entire recording time? This could be more explicitly stated in methods/results. The correlations themselves/p-values could be shown in addition to/instead of Pearson's r values. Are the correlations themselves significant? This would strengthen the claim that orexin activity is strongly coupled to the magnitude of body movement change. As another example, in Figure 2D, there are no statistics reported on the correlation between movement metric and average neural signal. In Figure 6G, orexin neuron activity is more strongly correlated with movement than MVe glut neurons, but are either of these correlations significant? The correlation between MVe glut activity and movement overall seems similar to that of orexin neurons, and may be worth noting more explicitly.

Throughout the paper, we have recorded both neural activity (photometry) and movement at 20 Hz. This would generate, for example, 48’000 samples of photometry and movement from a 40-minute session. All the samples were used to calculate a pearson’s r between variables. To clarify this, we now added the subtext “wholesession” to relevant figures, as well as a clarification in the methods.

Individual experiment correlations for orexin neurons and MVe glut neurons were always significant p<0.0001, even after a Bonferroni multiple comparisons correction was applied to each population. See the “too big to fail” nature of correlation hypothesis testing above.

It could be made clearer at the end of Figure 2 that orexin neuron activity is tracking the magnitude of movement change (shown in Figure 2D), not that it is encoding different types of movement.

We intended for original Figure 2E to illustrate this concept, however this panel has caused a great deal of confusion to several readers and was perhaps ill conceived. We have replaced Figure 2E with a new panel more directly addressing the reviewer’s statement. We can construct three models where orexin neuron activity is predicted from the behavioral classification (sometimes called “one-hot” encoding) and/or the movement metric.

Model 1 predicts orexin neuron activity using only a categorical predictor of behavioral state. Model 2 only uses the movement metric, and model 3 allows a different movement-metric correlation within each behavioral state. We can compare these models using AIC (Akaike Information Criterion) which is a point estimate. While the most complex model 3 was the best, model 2 was much closer to model 3 than model 1. Similarly, model 2 was much better than model 1. From this we conclude that the magnitude of movement change is a more powerful predictor than behavioral state (“type of movement”). This is now Figure 2E.

It would be interesting to see the raw movement metric data as shown in Figures 1 and 2 in the DTR mice to show that ablating orexin neurons does not impair the movement profile seen in Figures 1 and 2.

The requested visualization has been added to Figure 4B.

Validation that orexin was selectively ablated in these mice would be ideal.

Histology (see response to public review) was added to a new Figure 4B.

Figure 4A - OxLight expression in SNc does not look very robust.

Please note this is a membrane-targeted indicator, the staining this produces is thus much weaker than cyctosolic indicators such as calcium indicator GCaMP.

Figure 4 - It would be beneficial to see the same correlations that were done in Figures 1 and 2 to show OxLight activity vs. movement metric. Are they correlated?

Individual traces had significant correlations with OxLight and movement, and the population averages revealed similar trends:

Author response image 4.

Figure 6B - Targeting of MVe neurons does not look very specific. The sample size for orexintargeted mice should be re-stated in the figure legend for clarity.

Legend has been updated to clarify n = 15 for orexin targeted mice.

Some citations didn't seem to match what was being referenced in the text. Similarly, in the legend for Figure 1C, the statistics do not match what is reported in the text. In Figure 1, the sample size is not noted in the text. When referring to running in Figure 1, is this referring to running speed? Perhaps the language could be more consistent.

These typos (due to a rounding error) in the legend and text have been corrected. Sample size has been added to the text, and we have changed Figure 1D to clarify we are referring to running speed. We moved some citations to improve clarity.

Methods - where were Cre mice obtained from?

Sources now better referenced in Methods (JAX or Parlato et al).

Figure 1, panel C: The authors compared Pearson's r-coefficient results for each animal and for each variable. However, it would be interesting to show the correlation curves for each variable. However, it would be interesting to show the correlation curves for each variable as well here. Also, there is mention of a strong correlation but it is unclear whether these correlations are significant.

See below for an example mouse.

Author response image 5.

Figure 3, panel F: I understand HON-DTR is a validated model but a picture orexin ablation is necessary, including pictures of orexin fibers ablation within the SNc and LC.

See our reply to the public review above.

Figure 5, Panel A: Same comment as Figure 1, panel C.

We have similarly clarified the panel and legend.

Page 4: The authors mention "Within the 1st and 4th quartile of blood glucose, movement-HON correlations were not significantly different. Please add the figures.

The requested plot has been added to Figure 6, panel G.

Reviewer #3 (Public review):

Summary

The study presents an investigation into how hypothalamic orexin neurons (HONs) track body movement with high precision. Using techniques including fiber photometry, video-based movement metrics, and empirical mode decomposition (EMD), the authors demonstrate that HONs encode net body movement consistently across a range of behaviors and metabolic states. They test the ability of HONs to track body movement to that of other subcortical neural populations, from which they distinguish HONs activity from other subcortical neural populations.

Strengths:

The study characterizes HONs activity as key indicators of movement and arousal, and this method may have potential implications for understanding sleep disorders, energy regulation, and brain-body coordination. Overall, I think this is a very interesting story, with novel findings and implications about sensorimotor systems in animals. The manuscript is clearly written and the evidence presented is rigorous. The conclusions are well supported by experimental data with clear statistical analyses.

We thank the reviewer for their supportive feedback.

Weaknesses/suggestions:

There are a couple of issues I think the authors could address to make the paper better and more complete:

(1) The study primarily focuses on steady-state behaviors. It would be interesting if the authors' current dataset allows analyses of HON dynamics during transitions between behavioral states (e.g., resting to running or grooming to sniffing). This could provide additional insights into how HONs adapt to rapid changes in body movement.

This is a fantastic idea, and easy to check using our classification CNN. We identified the six most frequent behavioral transitions and plotted them in Figure 2H. HONs show rapid dynamics in activity aligned with behavioral changes.

These changes are very similar to the movement magnitude along these transitions, which is now also plotted in Figure 2G.

(2) Given the established role of HONs in arousal and wakefulness, the study could further investigate how movement-related HON dynamics interact with arousal states. For example, does HON encoding of movement differ during sleep versus wakefulness?

To further investigate how movement encoding interacts with arousal, we now include quantification and analysis of pupil-linked arousal (see new Figure 7). We agree it would be interesting to look at what happens during sleep, especially REM sleep when some HONs are thought to be active where there is no/little body movement, but this is beyond the scope of the present study.

(3) Although HON ablation experiments suggest that HONs do not shape movement frequency profiles. It would be more compelling if the authors could investigate whether HONs contribute to specific types of movements (e.g., fine motor vs. gross motor movements) or modulate movement initiation thresholds.

We performed this analysis using the k-means classifier for small/large movements. Consistent with previous results, we found no significant effect (p = 0.2767) of genotype on the frequency of identified small (fine) or large (gross) movement clusters. This plot has been added to Figure 4E.

(4) The heterogeneous movement-related orexin dynamics observed in the LC and SNc raise intriguing questions about the circuit-level mechanisms underlying these differences. Optogenetic or chemogenetic manipulation of these projections could validate the functional implications of these dynamics.

We agree. We now discuss some implications of this in revised Discussion (paragraph 4). Please note that previous work already demonstrated that orexin action in the SNc can produce locomotion (referenced in the paragraph), though we agree that further work would be valuable.

Reviewer #3 (Recommendations for the authors):

Additional feedback:

(1) Figure 1C: the individual data points are hard to track or see. Consider using a larger marker face to help data visualization. Similar issues can be found in Figures 2C, 2E, 5E, 6C, 6F, and 6G.

Thickness of the lines and scatterplots have been increased.

(2) First Section of Results: the authors claim to use a deep-learning network to automatically classify video recordings into five distinct behaviors. However, several issues need to be addressed here:

a. In Results, the corresponding sentence lacks a reference to the Methods Section.

Reference has been added to the text.

b. In Methods, the description of the CNN model is quite limited, lacking many basic, necessary components including necessary references to published papers, the model training, characterization (only an overall accuracy is not enough), as well as dataset definition, preparation, augmentation (if any), etc.

We have expanded the methods section regarding the CNN model.

(3) First Section of Results: in the second paragraph, the authors claim that "Overall, these results reveal HON population activity precisely tracks a general degree of body movement across recorded behaviors." This is not accurate. To indicate that HONs activity tracks the general degree of body movement across behavior states, they need to further show that behavioral states with similar levels of movement metrics can be differentiated via HON activities. However, as they showed in Figure 2D, some behaviors with similar values of movement metric do not seem to be easily discerned by HON activity levels.

We agree with you, and this is also what we originally intended to convey – now reworded for clarity.

(4) Technical issue: Figures 3B, 3C, 3G, using local regression to plot the solid lines makes them touch negative values, which does not make sense for "power proportion" (this quantity is always non-negative).

This is a good point. To fix this, we first log-transformed the power metric, then performed a local regression, and used the link function to transform the model predictions back to %-units for visualization. This has been noted in the methods.

(5) Figure 3G: For a better comparison, consider combining the two plots into a single plot.

The two plots have been merged as shown in Figure 4C.

(6) Figure 5E: For a better data visualization, the current pair of plots can be consolidated into one single plot where the x-axis is Move and the y-axis is dGlu. In this way, it is easier to understand and the orthogonality as claimed in the manuscript can be more apparent.

The requested plot has been added as Figure 6F.

Author Response

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

eLife assessment

This study presents a valuable finding for the treatment of PCCs by sequencing 16 tumor specimens from five patients with pheochromocytomas by single-cell transcriptomics and proposing a new molecular classification criterion based on the sequencing results and characterization of tumor microenvironmental features. The evidence supporting the claims of the authors is solid, although the inclusion of more patient samples would strengthen the study's conclusions. The work will be of interest to clinicians or medical biologists working on rare pheochromocytomas (PCCs).

Firstly, we sincerely appreciate the positive feedback from the editor and extend our gratitude to the three reviewers for their meticulous review and valuable comments. Our detailed responses to each recommendation are outlined below.

Response to reviewers’ recommendations

Reviewer #1 (Recommendations for The Authors):

1) Transcriptomal clonal dynamics of different PCCs is well written. However for conclusion sample size needs to be more.

Acknowledging the rarity of PCCs with an incidence of approximately 0.2 to 0.6 cases per 100,000 person-years (Farrugia & Charalampopoulos, 2019; Neumann et al, 2019), our study recognizes the limitation in sample size, as discussed in the limitations section (Page 22). In response to this concern, we are committed to undertaking further research with an expanded sample size to bolster the robustness of our conclusions, seeking a more comprehensive understanding of tumor microenvironment characterization and molecular classification in PCCs. We appreciate the valuable guidance provided by the reviewer.

2) Clinical, biochemistry data of 5 cases can be analysed. Any findings in different categories as per postulated classification can be noted for further studies. Example: epinephrine levels

We have now included the clinical information of 5 PCC patients, encompassing signs and symptoms, the tumor size, and laboratory test results in the revised manuscript as Supplemental Table S3 (Page 11-12). Notably, our analysis revealed that the kinase-type PCC patient (P4) exhibited higher blood pressures and plasma levels of catecholamine metabolites (3-methoxytyramine and normetanephrine) compared to metabolism-type PCC patients (P1-P3, and P5). This observation aligns with the elevated expression of phenylethanolamine N-methyltransferase (PNMT), an enzyme involved in the biosynthesis of catecholamine and linked to hypertension, in P4, as identified in the scRNA-seq data (Figure 4B and 4D) (Kennedy et al, 1993; Konosu-Fukaya et al, 2018; Nguyen et al, 2015). As suggested, we plan to conduct further research to explore the correlation of our molecular classification with plasma levels of catecholamine metabolites, and the relevant points have been discussed in the revision (Page 20).

We would like to take this chance to again thank the reviewer for the careful review and very helpful guidance about how to improve our study.

References for Reviewer #1:

Farrugia FA, Charalampopoulos A (2019) Pheochromocytoma. Endocrine regulations 53: 191-212 Neumann HPH, Young WF, Jr., Eng C (2019) Pheochromocytoma and Paraganglioma. The New England journal of medicine 381: 552-565

Kennedy B, Elayan H, Ziegler MG (1993) Glucocorticoid hypertension and nonadrenal phenylethanolamine N-methyltransferase. Hypertension (Dallas, Tex : 1979) 21: 415419

Konosu-Fukaya S, Omata K, Tezuka Y, Ono Y, Aoyama Y, Satoh F, Fujishima F, Sasano H, Nakamura Y (2018) Catecholamine-Synthesizing Enzymes in Pheochromocytoma and Extraadrenal Paraganglioma. Endocrine pathology 29: 302309

Nguyen P, Khurana S, Peltsch H, Grandbois J, Eibl J, Crispo J, Ansell D, Tai TC (2015) Prenatal glucocorticoid exposure programs adrenal PNMT expression and adult hypertension. The Journal of endocrinology 227: 117-127

Reviewer #2 (Recommendations for The Authors):

1) Please revise all references to "malignant potential", "malignant behavior", etc. throughout the article, including the abstract and introduction, and replace them with the word "metastasis" as appropriate. Since all PCCs are malignant non-epithelial neuroendocrine neoplasms originating from the paraganglia, which are themselves malignant tumors, it is unacceptable to describe them as "malignant potential" or "malignant potential". Please review the 2022 WHO/IARC classification and description of pheochromocytoma/paraganglioma (reference: Mete O, Asa SL, Gill AJ, Kimura N, de Krijger RR, Tischler A. Overview of the 2022 WHO Classification of Paragangliomas and Pheochromocytomas. Endocr Pathol. 2022;33(1):90-114. doi:10.1007/s12022-022-09704-6).

As suggested, we have replaced all occurrences of “malignant potential” or “malignant behavior” with “metastasis” throughout the revised manuscript. We have also included a citation to the 2022 WHO/IARC classification for further clarity.

• Similarly, it is not advisable to use the PASS score to predict "malignant" PCC; this type of scoring system evaluates the "metastasis risk" or the "metastasis potential" of PCC.

We appreciate the reviewer for this insight and have revised our statements accordingly.

• Also, "MALIGNANT CHAFFIN CELLS" needs to be modified; in fact, it is the "tumor cell of PCC" that the authors are trying to express.

As suggested, we have amended the term “malignant chromaffin cells” to “PCC cells” in the revised manuscript (Page 9-10).

2) How does the PASS score specifically relate to intra-tumor heterogeneity as reflected by scRNA-seq? In fact, the PASS score evaluates the histological or pathological invasiveness of PCC, and different sections of the same tumor tissue may have different histological manifestations, which may affect the score; however, scRNA-seq analyzes the cellular composition of the tumor, which is not the same as the information reflected by the PASS score. Both represent different levels and dimensions of intra-tumor heterogeneity and should be analyzed together. Please specifically list, one by one, the proportion of each item score of the PASS system and cell type of scRNA-seq for each sample and the results of the comparisons with each other to better present the conclusions.

As suggested, we have included the proportion of each item score from the PASS system in the revised manuscript as Supplemental Table S2 (Page 8). Integrating this data with the cell type composition of each sample from Figure 2B, our analysis suggests that intra-tumor heterogeneity, as assessed by the PASS system, is more extensive compared to scRNA-seq. We concur with the reviewer’s judgement that scRNA-seq analysis and PASS score represent different levels and dimensions of intratumor heterogeneity, and we have adjusted our claim throughout the revised manuscript accordingly (Page 8, 9, and 19).

3) Where is the specific mutation site of the VHL gene in patient 5? Please advise.

The VHL gene mutation site, c.499C>T (missense mutation), in patient 5 was identified through whole exome sequencing (WES) analysis. We have now added the information to Supplemental Table S1 in the revised manuscript (Page 6).

4) Please revise Supplementary Figure 1, the scale should not appear in the picture of the staining result of P5.

As suggested, we have adjusted the position of the scale bar.

Author response image 1.

Hematoxylin-eosin staining and immunohistochemistry staining of CGA marker in formalin-fixed paraffin-embedded PCC tissue sections matched to scRNA-seq specimens. Scale bar, 100 μm.

5) What were the clinical presentation and biochemical findings in the five patients?

The information regarding tumor sizes, signs and symptoms, and plasma levels of catecholamine metabolites [3-methoxytyramine (3-MT), metanephrine (MN), and normetanephrine (NMN)] has been added to the revised manuscript as Supplemental Table S3 (Page 11-12).

• Were there any preoperative symptoms of hypertension?

With the exception of P2, preoperative symptoms of hypertension were observed in all PCC patients. The information has been added to the revised manuscript as Supplemental Table S3 (Page 11-12).

• What was the size and catecholamine secretion phenotype of each tumor? What was the relationship between these data and the scRNA-seq results?

The secretion phenotype showed that the kinase-type PCC patient (P4) exhibited higher plasma levels of catecholamine metabolites (3-methoxytyramine and normetanephrine) compared to metabolism-type PCC patients (P1-P3, and P5). This observation aligns with the elevated expression of phenylethanolamine Nmethyltransferase (PNMT), an enzyme involved in the biosynthesis of catecholamine and linked to hypertension, in P4, as identified in the scRNA-seq data (Figure 4B and 4D) (Kennedy et al, 1993; Konosu-Fukaya et al, 2018; Nguyen et al, 2015). Meanwhile, we have not observed the correlation between tumor sizes and molecular classification. We have now included tumor sizes and laboratory test results of 5 PCC patients in the revised manuscript as Supplemental Table S3 (Page 11-12), and the relevant points have been discussed in the revision (Page 20).

6) Please revise Figure 1A, the meaning shown in the figure appears to dissociate the tissues of the patient's normal adrenal glands, which can be misleading.

We appreciate the reviewer for raising this concern. The schematic in Figure 1A has been revised accordingly.

Author response image 2.

(1A) Schematic of the experimental pipeline. 11 tumor specimens and 5 adjacent normal adrenal medullary specimens were isolated from 5 PCC patients, dissociated into single-cell suspensions, and analyzed using 10x Genomics Chromium droplet scRNA-seq.

• Please revise the figure note for Figure 1B, where the symbol (B) appears twice.

As suggested, we have revised the figure legends for Figure 1B and 1C (Page 42).

7) Please indicate in the figure legends and text what exactly is meant by "adjacent specimens"? medulla? cortex? normal tissue? I believe the authors mean adjacent normal adrenal medullary tissue, please check the article.

As suggested, we have revised the term “adjacent specimens” to “adjacent normal adrenal medullary tissues” throughout the revised manuscript.

8) Please review the pathologic diagnostic criteria of this study in light of the 2022 WHO/IARC guidelines for pathologic diagnosis: "For the pathological diagnosis, the inclusion criteria were neuroendocrine neoplasm originating from the adrenal medulla and retroperitoneal origin, i.e. pheochromocytoma and paraganglioma, with consistent morphologic and immunohistochemical confirmation in relevant cases and positivity for chromogranin A and synaptophysin. The exclusion criteria were adrenocortical neoplasm and metastatic tumors." It is not rigorous enough to diagnose a tumor as PCC based on positive CgA immunohistochemical staining results alone.

We have revised the statements about pathologic diagnostic criteria in accordance with the suggestion and have cited the reference (Page 6).

We would like to express our gratitude to the reviewer for the thorough review and invaluable guidance provided to enhance the quality of our study.

References for Reviewer #2:

Kennedy B, Elayan H, Ziegler MG (1993) Glucocorticoid hypertension and nonadrenal phenylethanolamine N-methyltransferase. Hypertension (Dallas, Tex: 1979) 21: 415419

Konosu-Fukaya S, Omata K, Tezuka Y, Ono Y, Aoyama Y, Satoh F, Fujishima F, Sasano H, Nakamura Y (2018) Catecholamine-Synthesizing Enzymes in Pheochromocytoma and Extraadrenal Paraganglioma. Endocrine pathology 29: 302309

Nguyen P, Khurana S, Peltsch H, Grandbois J, Eibl J, Crispo J, Ansell D, Tai TC (2015) Prenatal glucocorticoid exposure programs adrenal PNMT expression and adult hypertension. The Journal of endocrinology 227: 117-127

Reviewer #3 (Recommendations For The Authors):

I have several concerns and suggestions, which if addressed would improve the manuscript.

1) The statements of “plasmas” in the manuscript and figures are confusing, which should be revised as “plasma cells”.

As suggested, we have revised the terminology from “plasmas” to “plasma cells” throughout the revised manuscript and figures.

2) The marker genes used for defining plasma cells (IGHG1 and IGLC2) showed low expressing percentage in Figure 1D. Please consider providing other genes as the marker of plasma cells.

As suggested, we performed additional analysis to pinpoint marker genes for accurate definition of plasma cells. Applying stricter statistical criteria (cut-off pvalue < 0.05, log2 fold change ≥ 1.5, and expressing percentage ≥ 0.6), we identified XBP1 (a transcription factor playing key roles in the final stages of plasma cell development) and IGKC (a type of light-chain immunoglobulins) (Todd et al, 2009; Poulsen et al, 2002) as top significant differentially expressed genes (DEGs) suitable for defining plasma cells. These data are now presented as Figure 1D in the revised manuscript (Page 7).

Author response image 3.

(1D) Dot plot of representative marker genes for each cell type. The color scale represents the average marker gene expression level; dot size represents the percentage of cells expressing a given marker gene.

3) The statement “Our clustering and cell type annotation analysis identified diverse adrenal cells, stromal cells, and immune cells within the PCC microenvironment” seems not be exhibited in Figure 1, so the clustering result of adrenal cells, stromal cells, and immune cells need to be added.

As suggested, we performed clustering analysis for adrenal cells, stromal cells, and immune cells (including lymphocytes and myeloid cells), and visualized by the Uniform Manifold Approximation and Projection (UMAP) plot. These data have been added to the revised manuscript as Supplemental Figure S3 (Page 8).

Author response image 4.

Integration Analysis across 5 PCC Patients Revealing the Cell Type Composition of the PCC Microenvironment. UMAP plot depicting the distribution of adrenal cells, stromal cells, and immune cells (including lymphocytes and myeloid cells) within the PCC microenvironment.

4) Given the classification of “metabolism-type PCCs” and “kinase-type PCCs” have not been presented in Figure 2D, the statement “Combined with our findings of a higher proportion of neutrophils and monocyts/macrophages in metabolism-type as compared with kinase-type” in Result 6 should be supported by using additional data.

As suggested, we performed additional analysis to evaluate the proportion of neutrophils and monocytes/macrophages in metabolism-type and kinasetype PCC patients. These data have been added to the revised manuscript as Supplemental Figure S4 (Page 14).

Author response image 5.

The frequency distribution of cell types within the microenvironment of metabolism-type and kinase-type PCC patients.

5) What makes the difference of scRNA-seq analysis and multispectral immunofluorescent staining in judging the immune escape of PCCs? Please provide an explanation.

We appreciate the reviewer's concern. scRNA-seq lacks spatial details, and multispectral immunofluorescent staining is constrained in the number of detected proteins. To address this, we employed both methods for analysis. scRNA-seq revealed limited communication between tumor and T cells, with lower HLA-I expression in kinase-type PCCs compared to metabolism-type PCCs. This was supported by multispectral staining using antibodies against CD4+ T cells, CD8+ T cells, M1 macrophages, or M2 macrophages markers, indicating sparse immune cell infiltration around tumor cells, mainly in the stroma (Figure 7A and 7B). This dual approach strengthens our understanding of immune escape in both PCC types. The explanation has been added to the revised manuscript (Page 21).

6) Figure 7G missed the scale bar for the staining results of marker proteins. Please add the scale bar into the figure.

As suggested, we have added to the scale bar accordingly.

7) In the method part of the manuscript, the authors should describe the minimum and maximum number used for quality control of the number of genes and the percentage of mitochondrial genes.

For quality control, we established a minimum threshold of no less than 200 genes and a maximum threshold of no more than 5000 genes. Additionally, the quality control process included a maximum threshold of 30% for mitochondrial genes. These specific criteria have been added to the methods section of the revised manuscript (Page 25-26).

We express our gratitude to the reviewer for their supportive recommendations and invaluable guidance on enhancing the rigor of our data.

References for Reviewer #3:

Todd DJ, McHeyzer-Williams LJ, Kowal C, Lee AH, Volpe BT, Diamond B, McHeyzer-Williams MG, Glimcher LH (2009) XBP1 governs late events in plasma cell differentiation and is not required for antigen-specific memory B cell development. The Journal of experimental medicine 206: 2151-2159

Poulsen TS, Silahtaroglu AN, Gisselø CG, Tommerup N, Johnsen HE (2002) Detection of illegitimate rearrangements within the immunoglobulin light chain loci in B cell malignancies using end sequenced probes. Leukemia 16: 2148-2155

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Li et al. investigates the metabolism-independent role of nuclear IDH1 in chromatin state reprogramming during erythropoiesis. The authors describe accumulation and redistribution of histone H3K79me3, and downregulation of SIRT1, as a cause for dyserythropoiesis observed due to IDH1 deficiency. The authors studied the consequences of IDH1 knockdown, and targeted knockout of nuclear IDH1, in normal human erythroid cells derived from hematopoietic stem and progenitor cells and HUDEP2 cells respectively. They further correlate some of the observations such as nuclear localization of IDH1 and aberrant localization of histone modifications in MDS and AML patient samples harboring IDH1 mutations. These observations are intriguing from a mechanistic perspective and they hold therapeutic significance, however there are major concerns that make the inferences presented in the manuscript less convincing.

(1) The authors show the presence of nuclear IDH1 both by cell fractionation and IF, and employ an efficient strategy to knock out nuclear IDH1 (knockout IDH1/ Sg-IDH1 and rescue with the NES tagged IDH1/ Sg-NES-IDH1 that does not enter the nucleus) in HUDEP2 cells. However, some important controls are missing.

A) In Figure 3C, for IDH1 staining, Sg-IDH1 knockout control is missing.

Thanks for the reviewer’s suggestion. We have complemented the staining of Sg-IDH1 knockout cells, and made corresponding revision in Figure 3C in the revised manuscript.

B) Wild-type IDH1 rescue control (ie., IDH1 without NES tag) is missing to gauge the maximum rescue that is possible with this system.

Thanks for the reviewer’s suggestion. We have overexpressed wild-type IDH1 in the IDH1-deficient HUDEP2 cell line and detected the phenotype. The results are presented in Supplementary Figure 9 in the revised manuscript. As shown in Supplementary Figure 9A, IDH1 deficiency resulted in reduced cell number in HUDEP2 cells, a phenotype that was rescued by overexpression of wild-type IDH1 but not by NES-IDH1. Given IDH1's well-established role in redox homeostasis through catalyzing isocitrate to α-KG conversion, we hypothesized that both wild-type IDH1 and NES-IDH1 overexpression would significantly restore α-KG levels compared to the IDH1-deficient group. Supplementary Figure 9B demonstrates that IDH1 depletion resulted in a dramatic decrease in α-KG levels, whereas overexpression of either wild-type IDH1 or NES-IDH1 almost completely restored α-KG levels, as anticipated. These results suggest that wild-type IDH1 overexpression can restore metabolic regulatory functions as effectively as NES-IDH1 overexpression. To investigate whether apoptosis contributes to the impaired cell expansion caused by IDH1 deficiency, we performed Annexin V/PI staining to quantify apoptotic cells. As shown in Supplementary Figure 9C and D, flow cytometry analysis revealed no significant changes in apoptosis rates following either IDH1 depletion or ectopic expression of wild-type IDH1 or NES-IDH1 in IDH1 deficient HUDEP2 cells.

Flow cytometric analysis demonstrated that IDH1 deficiency triggered S-phase accumulation at day 8, indicative of cell cycle arrest. Whereas ectopic expression of wild-type IDH1 significantly rescued this cell cycle defect, overexpression of NES-IDH1 failed to ameliorate the S-phase accumulation phenotype induced by IDH1 depletion, as presented in Supplementary Figure 9E and F. Although NES-IDH1 overexpression rescued metabolic regulatory function defect, it failed to alleviate the cell cycle arrest induced by IDH1 deficiency. In contrast, wild-type IDH1 overexpression fully restored normal cell cycle progression. This functional dichotomy demonstrates that nuclear-localized IDH1 executes critical roles distinct from its cytoplasmic counterpart, and overexpression of wild-type IDH1 could efficient restore the functional impairment induced by depletion of nuclear localized IDH1.

(2) Considering the nuclear knockout of IDH1 (Sg-NES-IDH1 referenced in the previous point) is a key experimental system that the authors have employed to delineate non-metabolic functions of IDH1 in human erythropoiesis, some critical experiments are lacking to make convincing inferences.

A) The authors rely on IF to show the nuclear deletion of Sg-NES-IDH1 HUDEP2 cells. As mentioned earlier since a knockout control is missing in IF experiments, a cellular fractionation experiment (similar to what is shown in Figure 2F) is required to convincingly show the nuclear deletion in these cells.

We sincerely thank the reviewer for raising this critical point. As suggested, we have performed additional IF experiments and cellular fractionation experiments to comprehensively address the subcellular localization of IDH1.

The results of IF staining were shown in Figure 3C of the revised manuscript. In Control HUDEP2 cells, endogenous IDH1 was detected in both the cytoplasm and nucleus. This dual localization may reflect its dynamic roles in cytoplasmic metabolic processes and potential nuclear functions under specific conditions. In Sg-IDH1 cells (IDH1 knockout), IDH1 signal was undetectable, confirming efficient depletion of the protein. In Sg-NES-IDH1 cells (overexpressing NES-IDH1 in IDH1 deficient cells), IDH1 predominantly accumulated in the cytoplasm, consistent with the disruption of its nuclear export signal. The dual localization of IDH1 that was determined by IF staining experiment were then further confirmed by cellular fractionation assays, as shown in Figure 3D.

B) Since the authors attribute nuclear localization to a lack of metabolic/enzymatic functions, it is important to show the status of ROS and alpha-KG in the Sg-NES-IDH1 in comparison to control, wild type rescue, and knockout HUDEP2 cells. The authors observe an increase of ROS and a decrease of alpha-KG upon IDH1 knockdown. If nuclear IDH1 is not involved in metabolic functions, is there only a minimal or no impact of the nuclear knockout of IDH1 on ROS and alpha-KG, in comparison to complete knockout? These studies are lacking.

We appreciate the insightful suggestions of the reviewers and agree that the detection of ROS and alpha-KG is useful for the demonstration of the non-canonical function of IDH1. We examined alpha-KG concentrations in control, IDH1 knockout and nuclear IDH1 knockout HUDEP2 cell lines. The results showed a significant decrease in alpha-KG content after complete knockout of IDH1, whereas there was no significant change in nuclear knockout IDH1 (Supplementary Figure 9B). As to the detection of ROS level, the commercial ROS assay kits that we can get are detected using PE (Excitation: 565nm; Emission: 575nm) and FITC (Excitation: 488nm; Emission: 518nm) channels in flow cytometry. We constructed HUDEP2 cell lines of Sg-IDH1 and Sg-NES-IDH1 to express green fluorescent protein (Excitation: 488nm; Emission: 507nm) and Kusabira Orange fluorescent protein (Excitation: 500nm; Emission: 561nm) by themselves. Unfortunately, due to the spectral overlap of the fluorescence channels, we were unable to detect the changes in ROS levels in these HUDEP2 cell lines using the available commercial kit.

(3) The authors report abnormal nuclear phenotype in IDH1 deficient erythroid cells. It is not clear what parameters are used here to define and quantify abnormal nuclei. Based on the cytospins (eg., Figure 1A, 3D) many multinucleated cells are seen in both shIDH1 and Sg-NES-IDH1 erythroid cells, compared to control cells. Importantly, this phenotype and enucleation defects are not rescued by the administration of alpha-KG (Figures 1E, F). The authors study these nuclei with electron microscopy and report increased euchromatin in Figure 4B. However, there is no discussion or quantification of polyploidy/multinucleation in the IDH1 deficient cells, despite their increased presence in the cytospins.

A) PI staining followed by cell cycle FACS will be helpful in gauging the extent of polyploidy in IDH1 deficient cells and could add to the discussions of the defects related to abnormal nuclei.

We appreciate the reviewer’s insightful suggestion. Since PI dye is detected using the PE channel (Excitation: 565nm; Emission: 575nm) of the flow cytometer and the HUDEP2 cell line expresses Kusabira orange fluorescent protein (Excitation: 500nm; Emission: 561nm), we were unable to use PI staining to detect the cell cycle. Edu staining is another commonly used method to determine cell cycle progression, and we performed Edu staining followed by flow cytometry analysis on Control, Sg-IDH1 and Sg-NES-IDH1 HUDEP2 cells, respectively. The results showed that complete knockdown of IDH1 resulted in S-phase block and increased polyploidy in HUDEP2 cells on day 8 of erythroid differentiation, and overexpression of IDH1-NES did not reverse this phenotype (Supplemental Figure 9E-F). Moreover, we have added a discussion of abnormal nuclei being associated with impaired erythropoiesis.

B) For electron microscopy quantification in Figures 4B and C, how the quantification was done and the labelling of the y-axis (% of euchromatin and heterochromatin) in Figure 4 C is not clear and is confusingly presented. The details on how the quantification was done and a clear label (y-axis in Figure 4C) for the quantification are needed.

Thanks for the reviewer's suggestion. In this study, we calculated the area of nuclear, heterochromatin and euchromatin by using Image J software. We addressed the quantification strategy in the section of Supplementary methods of the revised Supplementary file. In addition, the y-axis label in Figure 4C was changed to “the area percentage of euchromatin and heterochromatin’’.

C) As mentioned earlier, what parameters were used to define and quantify abnormal nuclei (e.g. Figure 1A) needs to be discussed clearly. The red arrows in Figure 1A all point to bi/multinucleated cells. If this is the case, this needs to be made clear.

We thank the reviewer for their suggestion. In our present study, nuclear malformations were defined as cells exhibiting binucleation or multinucleation based on cytospin analysis. A minimum of 300 cells per group were evaluated, and the proportion of aberrant nuclei was calculated as (number of abnormal cells / total counted cells) × 100%.

(4) The authors mention that their previous study (reference #22) showed that ROS scavengers did not rescue dyseythropoiesis in shIDH1 cells. However, in this referenced study they did report that vitamin C, a ROS scavenger, partially rescued enucleation in IDH1 deficient cells and completely suppressed abnormal nuclei in both control and IDH1 deficient cells, in addition to restoring redox homeostasis by scavenging reactive oxygen species in shIDH1 erythroid cells. In the current study, the authors used ROS scavengers GSH and NAC in shIDH1 erythroid cells and showed that they do not rescue abnormal nuclei phenotype and enucleation defects. The differences between the results in their previous study with vitamin C vs GSH and NAC in the context of IDH1 deficiency need to be discussed.

We appreciate the reviewer’s insightful observation. The apparent discrepancy between the effects of vitamin C (VC) in our previous study and glutathione (GSH)/N-acetylcysteine (NAC) in the current work can be attributed to divergent molecular mechanisms beyond ROS scavenging. A growing body of evidence has identified vitamin C as a multifunctional regulator. In addition to acting as an antioxidant maintaining redox homeostasis, VC also acts as a critical epigenetic modulator. VC have been identified as a cofactor for α-ketoglutarate (α-KG)-dependent dioxygenases, including TET2, which catalyzes 5-methylcytosine (5mC) oxidation to 5-hydroxymethylcytosine (5hmC) [1,2]. Structural studies confirm its direct interaction with TET2’s catalytic domain to enhance enzymatic activity in vitro [3]. The biological significance of the epigenetic modulation induced by vitamin C is illustrated by its ability to improve the generation of induced pluripotent stem cells and to induce a blastocyst-like state in mouse embryonic stem cells by promoting demethylation of H3K9 and 5mC, respectively [4,5]. In contrast, GSH and NAC are canonical ROS scavengers lacking intrinsic epigenetic-modifying activity. While they effectively neutralize oxidative stress (as validated by reduced ROS levels in our current data, Supplemental Figure 7), their inability to rescue nuclear abnormalities or enucleation defects in IDH1 deficient cells suggests that IDH1 deficiency-driven dyserythropoiesis is not solely ROS-dependent.

References:

(1) Blaschke K, Ebata KT, Karimi MM, Zepeda-Martínez JA, Goyal P, et al. Vitamin C induces Tet-dependent DNA demethylation and a blastocyst-like state in ES cells. Nature. 20138;500(7461): 222-226.

(2) Minor EA, Court BL, Young JI, Wang G. Ascorbate induces ten-eleven translocation (Tet) methylcytosine dioxygenase-mediated generation of 5-hydroxymethylcytosine. J Biol Chem. 2013;288(19): 13669-13674.

(3) Yin R, Mao S, Zhao B, Chong Z, Yang Y, et al. Ascorbic acid enhances Tet-mediated 5-methylcytosine oxidation and promotes DNA demethylation in mammals. J Am Chem Soc. 2013;135(28):10396-10403.

(4) Esteban MA, Wang T, Qin B, Yang J, Qin D, et al. Vitamin C enhances the generation of mouse and human induced pluripotent stem cells. Cell Stem Cell. 2010;6(1):71-79.

(5) Chung T, Brena RM, Kolle G, Grimmond SM, Berman BP, et al. Vitamin C promotes widespread yet specific DNA demethylation of the epigenome in human embryonic stem cells. Stem Cells. 2010;28(10):1848-1855.

(5) The authors describe an increase in euchromatin as the consequential abnormal nuclei phenotype in shIDH1 erythroid cells. However, in their RNA-seq, they observe an almost equal number of genes that are up and down-regulated in shIDH1 cells compared to control cells. If possible, an RNA-Seq in nuclear knockout Sg-NES-IDH1 erythroid cells in comparison with knockout and wild-type cells will be helpful to tease out whether a specific absence of IDH1 in the nucleus (ie., lack of metabolic functions of IDH) impacts gene expression differently.

Thanks for the reviewer's suggestion. ATAC-seq showed an increase in chromatin accessibility after IDH1 deletion, but the number of up-regulated genes was slightly larger than that of down-regulated genes, which may be caused by the metabolic changes affected by IDH1 deletion. In order to explore the effect of chromatin accessibility changes on gene expression after IDH1 deletion, we analyzed the changes in differential gene expression at the differential ATAC peak region (as shown in Author response image 1), and the results showed that the gene expression at the ATAC peak region with increased chromatin accessibility was significantly up-regulated. This may explain the regulation of chromatin accessibility on gene expression.

Author response image 1.

Box plots of gene expression differences of differential ATAC peaks located in promoter for the signal increasing and decreasing groups.

(6) In Figure 8, the authors show data related to SIRT1's role in mediating non-metabolic, chromatin-associated functions of IDH1.

A) The authors show that SIRT1 inhibition leads to a rescue of enucleation and abnormal nuclei. However, whether this rescues the progression through the late stages of terminal differentiation and the euchromatin/heterochromatin ratio is not clear.

Thanks for the reviewer's suggestion. As shown in Supplementary Figure 14 and 15 in the revised Supplementary Data, our data showed that both the treatment of SRT1720 on normal erythroid cells and treatment of IDH1-deficient erythroid cells with SIRT1 inhibitor both have no effect on the terminal differentiation.

(7) In Figure 4 and Supplemental Figure 8, the authors show the accumulation and altered cellular localization of H3K79me3, H3K9me3, and H3K27me2, and the lack of accumulation of other three histone modifications they tested (H3K4me3, H3K35me4, and H3K36me2) in shIDH1 cells. They also show the accumulation and altered localization of the specific histone marks in Sg-NES-IDH1 HUDEP2 cells.

A) To aid better comparison of these histone modifications, it will be helpful to show the cell fractionation data of the three histone modifications that did not accumulate (H3K4me3, H3K35me4, and H3K36me2), similar to what was shown in Figure 4E for H3K79me3, H3K9me3, and H3K27me2).

We appreciate the reviewer’s insightful suggestion. We collected erythroblasts on day 15 of differentiation from cord blood-derived CD34⁺ hematopoietic stem cells to erythroid lineage and performed ChIP assay. As shown in Author response image 2, the results showed that the concentration of bound DNA of H3K9me3, H3K27me2 and H3K79me3 was too low to meet the sequencing quality requirement, which was consistent with that of WB. In addition, we tried to perform ChIP-seq for H3K79me3, and the results showed that there was no marked peak signal.

Author response image 2.

ChIP-seq analysis show that there was no marked peak signal of H3K79me3 on D15. (A) Quality control of ChIP assay for H3K9me3, H3K27me2, and H3K79me3. (B) Representative peaks chart image showed normalized ChIP signal of H3K79me3 at gene body regions. (C) Heatmaps displayed normalized ChIP signal of H3K79me3 at gene body regions. The window represents ±1.5 kb regions from the gene body. TES, transcriptional end site; TSS, transcriptional start site.

C) Among the three histone marks that are dysregulated in IDH1 deficient cells (H3K79me3, H3K9me3, and H3K27me2), the authors show via ChIP-seq (Fig5) that H3K79me3 is the critical factor. However, the ChIP-seq data shown here lacks many details and this makes it hard to interpret the data. For example, in Figure 5A, they do not mention which samples the data shown correspond to (are these differential peaks in shIDH1 compared to shLuc cells?). There is also no mention of how many replicates were used for the ChIP seq studies.

We thank the reviewer for pointing this out. We apologize for not clearly describing the ChIP-seq data for H3K9me3, H3K27me2 and H3K79me3 and we have revised them in the corresponding paragraphs. Since H3 proteins gradually translocate from the nucleus to the cytoplasm starting at day 11 (late Baso-E/Ploy-E) of erythroid lineage differentiation, we performed ChIP-seq for H3K9me3, H3K27me2 and H3K79me3 only for the shIDH1 group, and set up three independent biological replicates for each of them.

Reviewer #2 (Public Review):

Li and colleagues investigate the enzymatic activity-independent function of IDH1 in regulating erythropoiesis. This manuscript reveals that IDH1 deficiency in the nucleus leads to the redistribution of histone marks (especially H3K79me3) and chromatin state reprogramming. Their findings suggest a non-typical localization and function of the metabolic enzyme, providing new insights for further studies into the non-metabolic roles of metabolic enzymes. However, there are still some issues that need addressing:

(1) Could the authors show the RNA and protein expression levels (without fractionation) of IDH1 on different days throughout the human CD34+ erythroid differentiation?

We sincerely appreciate the reviewer’s constructive feedback. To address this point, we have now systematically quantified IDH1 expression dynamics across erythropoiesis stages using qRT-PCR and Western blot analyses. As quantified in Supplementary fige 1, IDH1 expression exhibited a progressive upregulation during early erythropoiesis and subsequently stabilized throughout terminal differentiation.

(2) Even though the human CD34+ erythroid differentiation protocol was published and cited in the manuscript, it would be helpful to specify which erythroid stages correspond to cells on days 7, 9, 11, 13, and 15.

We sincerely thank the reviewer for raising this important methodological consideration. Our research group has previously established a robust platform for staged human erythropoiesis characterization using cord blood-derived CD34⁺ hematopoietic stem cells (HSCs) [6-9]. This standardized protocol enables high-purity isolation and functional analysis of erythroblasts at defined differentiation stages.

Thanks for the reviewer’s suggestion. Our previous work (Jingping Hu et.al, Blood 2013. Xu Han et.al, Blood 2017.Yaomei Wang et.al, Blood 2021.) have isolation and functional characterization of human erythroblasts at distinct stages by using Cord blood. These works illustrated that using cord blood-derived hematopoietic stem cells and purification each stage of human erythrocytes can facilitate a comprehensive cellular and molecular characterization.

Following isolation from cord blood, CD34⁺ cells were cultured in a serum-free medium and induced to undergo erythroid differentiation using our standardized protocol. The process of erythropoiesis was comprised of 2 phases. During the early phase (day 0 to day 6), hematopoietic stem progenitor cells expanded and differentiated into erythroid progenitors, including BFU-E and CFU-E cells.

During terminal erythroid maturation (day 7 to day 15), CFU-E cells progressively transitioned through defined erythroblast stages, as validated by daily cytospin morphology and expression of band 3/α4 integrin. The stage-specific composition was quantitatively characterized as follows:

Author response table 1.

The composition of erythroblast during terminal stage erythropoiesis.

This differentiation progression from proerythroblasts (Pro-E) through basophilic (Baso-E), polychromatic (Poly-E), to orthochromatic erythroblasts (Ortho-E) recapitulates physiological human erythropoiesis, confirming the validity of our differentiation system for mechanistic studies.

Reference:

(6) Li J, Hale J, Bhagia P, Xue F, Chen L, et al. Isolation and transcriptome analyses of human erythroid progenitors: BFU-E and CFU-E. Blood. 2014;124(24):3636-3645.

(7) Hu J, Liu J, Xue F, Halverson G, Reid M, et al. Isolation and functional characterization of human erythroblasts at distinct stages: implications for understanding of normal and disordered erythropoiesis in vivo. Blood. 2013;121(16):3246-3253.

(8) Wang Y, Li W, Schulz VP, Zhao H, Qu X, et al. Impairment of human terminal erythroid differentiation by histone deacetylase 5 deficiency. Blood. 2021;138(17):1615-1627.

(9) Li M, Liu D, Xue F, Zhang H, Yang Q, et al. Stage-specific dual function: EZH2 regulates human erythropoiesis by eliciting histone and non-histone methylation. Haematologica. 2023;108(9):2487-2502.

(3) It is important to mention on which day the lentiviral knockdown of IDH1 was performed. Will the phenotype differ if the knockdown is performed in early vs. late erythropoiesis? In Figures 1C and 1D, on which day do the authors begin the knockdown of IDH1 and administer NAC and GSH treatments?

We sincerely appreciate the reviewer’s inquiry regarding the experimental timeline. The day of getting CD34⁺ cells was recorded as day 0. Lentivirus of IDH1-shRNA and Luciferase -shRNA was transduced in human CD34⁺ at day 2. Puromycin selection was initiated 24h post-transduction to eliminate non-transduced cells. IDH1-KD cells were then selected for 3 days. The knock down deficiency of IDH1 was determined on day 7. NAC or GSH was added to culture medium and replenished every 2 days.

(4) While the cell phenotype of IDH1 deficiency is quite dramatic, yielding cells with larger nuclei and multi-nuclei, the authors only attribute this phenotype to defects in chromatin condensation. Is it possible that IDH1-knockdown cells also exhibit primary defects in mitosis/cytokinesis (not just secondary to the nuclear condensation defect)?), given the function of H3K79Me in cell cycle regulation?

We appreciate the reviewer’s insightful suggestion. We performed Edu based cell cycle analysis on Control, Sg-IDH1 and Sg-NES-IDH1 HUDEP2 cells, respectively. The results showed that IDH1 deficiency resulted in S-phase block and increased polyploidy in HUDEP2 cells on day 8 of erythroid differentiation. NES-IDH1 overexpression failed to rescue these defects, indicating nuclear IDH1 depletion as the primary driving factor (Figure 3E,F). Recent studies have established a clear link between cell cycle arrest and nuclear malformation. Chromosome mis-segregation, nuclear lamina disruption, mechanical stress on the nuclear envelope, and nucleolar dysfunction all contribute to nuclear abnormalities that trigger cell cycle checkpoints [10,11]. Based on all these findings, it reasonable for us to speculate that the cell cycle defect in IDH1 deficient cells might caused by the nuclear malfunction.

Reference:

(10) Hong T, Hogger AC, Wang D, Pan Q, Gansel J, et al. Cell Death Discov. CDK4/6 inhibition initiates cell cycle arrest by nuclear translocation of RB and induces a multistep molecular response. 2024;10(1):453.

(11) Hervé S, Scelfo A, Marchisio GB, Grison M, Vaidžiulytė K, et al. Chromosome mis-segregation triggers cell cycle arrest through a mechanosensitive nuclear envelope checkpoint. Nat Cell Biol. 2025;27(1):73-86. 

(5) Why are there two bands of Histone H3 in Figure 4A?

We sincerely appreciate the reviewer's insightful observation regarding the dual bands of Histone H3 in our original Figure 4A. Upon rigorous investigation, we identified that the observed doublet pattern likely originated from the inter-batch variability of the original commercial antibody. To conclusively resolve this technical artifact, we have procured a new lot of Histone H3 antibody and repeated the western blot experimental under optimized conditions, and the results demonstrates a single band of H3.

(6) Displaying a heatmap and profile plots in Figure 5A between control and IDH1-deficient cells will help illustrate changes in H3K79me3 density in the nucleus after IDH1 knockdown.

Thank you for your suggestion. As presented in Author response image 2, we performed ChIP assays on erythroblasts collected at day 15. However, the concentration of H3K79me3-bound DNA was insufficient to meet the quality threshold required for reliable sequencing. Consequently, we are unable to generate the requested heatmap and profile plots due to limitations in data integrity from this experimental condition.

Reviewer #3 (Public Review):

Li, Zhang, Wu, and colleagues describe a new role for nuclear IDH1 in erythroid differentiation independent from its enzymatic function. IDH1 depletion results in a terminal erythroid differentiation defect with polychromatic and orthochromatic erythroblasts showing abnormal nuclei, nuclear condensation defects, and an increased proportion of euchromatin, as well as enucleation defects. Using ChIP-seq for the histone modifications H3K79me3, H3K27me2, and H3K9me3, as well as ATAC-seq and RNA-seq in primary CD34-derived erythroblasts, the authors elucidate SIRT1 as a key dysregulated gene that is upregulated upon IDH1 knockdown. They furthermore show that chemical inhibition of SIRT1 partially rescues the abnormal nuclear morphology and enucleation defect during IDH1-deficient erythroid differentiation. The phenotype of delayed erythroid maturation and enucleation upon IDH1 shRNA-mediated knockdown was described in the group's previous co-authored study (PMID: 33535038). The authors' new hypothesis of an enzyme- and metabolism-independent role of IDH1 in this process is currently not supported by conclusive experimental evidence as discussed in more detail further below. On the other hand, while the dependency of IDH1 mutant cells on NAD+, as well as cell survival benefit upon SIRT1 inhibition, has already been shown (see, e.g, PMID: 26678339, PMID: 32710757), previous studies focused on cancer cell lines and did not look at a developmental differentiation process, which makes this study interesting.

(1) The central hypothesis that IDH1 has a role independent of its enzymatic function is interesting but not supported by the experiments. One of the author's supporting arguments for their claim is that alpha-ketoglutarate (aKG) does not rescue the IDH1 phenotype of reduced enucleation. However, in the group's previous co-authored study (PMID: 33535038), they show that when IDH1 is knocked down, the addition of aKG even exacerbates the reduced enucleation phenotype, which could indicate that aKG catalysis by cytoplasmic IDH1 enzyme is important during terminal erythroid differentiation. A definitive experiment to test the requirement of IDH1's enzymatic function in erythropoiesis would be to knock down/out IDH1 and re-express an IDH1 catalytic site mutant. The authors perform an interesting genetic manipulation in HUDEP-2 cells to address a nucleus-specific role of IDH1 through CRISPR/Cas-mediated IDH1 knockout followed by overexpression of an IDH1 construct containing a nuclear export signal. However, this system is only used to show nuclear abnormalities and (not quantified) accumulation of H3K79me3 upon nuclear exclusion of IDH1. Otherwise, a global IDH1 shRNA knockdown approach is employed, which will affect both forms of IDH1, cytoplasmic and nuclear. In this system and even the NES-IDH1 system, an enzymatic role of IDH1 cannot be excluded because (1) shRNA selection takes several days, prohibiting the assessment of direct effects of IDH1 loss of function (only a degron approach could address this if IDH1's half-life is short), and (2) metabolic activity of this part of the TCA cycle in the nucleus has recently been demonstrated (PMID: 36044572), and thus even a nuclear role of IDH1 could be linked to its enzymatic function, which makes it a challenging task to separate two functions if they exist.

We appreciate the reviewer’s emphasis on rigorously distinguishing between enzymatic and enzymatic independent roles of IDH1. In our revised manuscript, we have removed all assertions of a "metabolism-independent" mechanism. Instead, we focus on demonstrating that nuclear-localized IDH1 contributes to chromatin state regulation during terminal erythropoiesis (e.g., H3K79me3 accumulation). While we acknowledge that nuclear IDH1’s enzymatic activity may still play a role [12], our data emphasize its spatial association with chromatin remodeling. We now explicitly state that nuclear IDH1’s function may involve both enzymatic and structural roles, and further studies are required to dissect these mechanisms.

Reference:

(12) Kafkia E, Andres-Pons A, Ganter K, Seiler M, Smith TS, et al.Operation of a TCA cycle subnetwork in the mammalian nucleus. Sci Adv. 2022;8(35):eabq5206.

(2) It is not clear how the enrichment of H3K9me3, a prominent marker of heterochromatin, upon IDH1 knockdown in the primary erythroid culture (Figure 4), goes along with a 2-3-fold increase in euchromatin. Furthermore, in the immunofluorescence (IF) experiments presented in Figure 4Db, it seems that H3K9me3 levels decrease in intensity (the signal seems more diffuse), which seems to contrast the ChIP-seq data. It would be interesting to test for localization of other heterochromatin marks such as HP1gamma. As a related point, it is not clear at what stage of erythroid differentiation the ATAC-seq was performed upon luciferase- and IDH1-shRNA-mediated knockdown shown in Figure 6. If it was done at a similar stage (Day 15) as the electron microscopy in Figure 4B, then the authors should explain the discrepancy between the vast increase in euchromatin and the rather small increase in ATAC-seq signal upon IDH1 knockdown.

Thank you for raising this important point. We agree that while H3K9me3 and H3K27me2 modifications are detectable in the nucleus, their functional association with chromatin in this context remains unclear. Our ChIP-seq data did not reveal distinct enrichment peaks for H3K9me3 or H3K27me2 (unlike the well-defined H3K79me3 peaks), suggesting that these marks may not be stably bound to specific chromatin regions under the experimental conditions tested. However, we acknowledge that the absence of clear peaks in our dataset does not definitively rule out chromatin interactions, as technical limitations or transient binding dynamics could influence these results. To avoid over-interpretation, we have removed speculative statements about the chromatin-unbound status of H3K9me3 and H3K27me2 from the revised manuscript. This revision aligns with our broader effort to present conclusions strictly supported by the current data while highlighting open questions for future investigation.

(3)The subcellular localization of IDH1, in particular its presence on chromatin, is not convincing in light of histone H3 being enriched in the cytoplasm on the same Western blot. H3 would be expected to be mostly localized to the chromatin fraction (see, e.g., PMID: 31408165 that the authors cite). The same issue is seen in Figure 4A.

We sincerely appreciate the reviewer's insightful comment regarding the subcellular distribution of histone H3 in our study. We agree that histone H3 is classically associated with chromatin-bound fractions, and its cytoplasmic enrichment in our Western blot analyses appears counterintuitive at first glance. However, this observation is fully consistent with the unique biology of terminal erythroid differentiation, which involves drastic nuclear remodeling and histone release - a hallmark of terminal stage erythropoiesis. Terminal erythroid differentiation is characterized by progressive nuclear condensation, chromatin compaction, and eventual enucleation. During this phase, global chromatin reorganization leads to the active eviction of histones from the condensed nucleus into the cytoplasm. This process has been extensively documented in erythroid cells, with studies demonstrating cytoplasmic accumulation of histones H3 and H4 as a direct consequence of nuclear envelope breakdown and chromatin decondensation preceding enucleation [13-16]. Our experiments specifically analyzed terminal-stage polychromatic and orthochromatic erythroblasts. At this stage, histone releasing into the cytoplasm is a dominant biological event, explaining the pronounced cytoplasmic H3 signal in our subcellular fractionation assays.

In summary, the cytoplasmic enrichment of histone H3 in our data aligns with established principles of erythroid biology and reinforces the physiological relevance of our findings. We thank the reviewer for raising this critical point, which allowed us to better articulate the unique aspects of our experimental system.

Reference:

(13) Hattangadi SM, Martinez-Morilla S, Patterson HC, Shi J, Burke K, et al. Histones to the cytosol: exportin 7 is essential for normal terminal erythroid nuclear maturation. Blood. 2014;124(12):1931-1940.

(14) Zhao B, Mei Y, Schipma MJ, Roth EW, Bleher R, et al. Nuclear Condensation during Mouse Erythropoiesis Requires Caspase-3-Mediated Nuclear Opening. Dev Cell. 2016;36(5): 498-510.

(15) Zhao B, Liu H, Mei Y, Liu Y, Han X, et al. Disruption of erythroid nuclear opening and histone release in myelodysplastic syndromes. Cancer Med. 2019;8(3):1169-1174. 

(16) Zhen R, Moo C, Zhao Z, Chen M, Feng H, et al.  Wdr26 regulates nuclear condensation in developing erythroblasts. Blood. 2020;135(3):208-219.

(4) This manuscript will highly benefit from more precise and complete explanations of the experiments performed, the material and methods used, and the results presented. At times, the wording is confusing. As an example, one of the "Key points" is described as "Dyserythropoiesis is caused by downregulation of SIRT1 induced by H3K79me3 accumulation." It should probably read "upregulation of SIRT1".

We sincerely thank the reviewer for highlighting the need for improved clarity in our experimental descriptions and textual precision. We fully agree that rigorous wording is essential to accurately convey scientific findings. Specific modifications have been made and are highlighted in Track Changes mode in the resubmitted manuscript.

The reviewer correctly identified an inconsistency in the original phrasing of one key finding. The sentence in question ("Dyserythropoiesis is caused by downregulation of SIRT1 induced by H3K79me3 accumulation") has been revised to:"Dyserythropoiesis is caused by the upregulation of SIRT1 mediated through H3K79me3 accumulation." This correction aligns with our experimental data showing that H3K79me3 elevation promotes SIRT1 transcriptional activation. We apologize for this oversight and have verified the consistency of all regulatory claims in the text.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) It will be helpful to mention/introduce the cells used for the study at the beginning of the results section. For example, for Figure 1A neither the figure legend nor the results text includes information on the cells used.

Thanks for the reviewer’s suggestion. The detail information of the cells that were used in our study have been provided in the revised manuscript.

(2) Important details for many figures are lacking. For example, in Figure 5, there is no mention of the replicates for ChIP-Seq studies. Also, the criteria used for quantifications of abnormal nuclei, % euchromatin vs heterochromatin, the numbers of biological replicates, and how many fields/cells were used for these quantifications are missing.

We thank the reviewer for emphasizing the importance of methodological transparency. It has been revised accordingly. The ChIP-Seq data in Figure 5 was generated from three independent biological replicates to ensure reproducibility. In this study, Image J software was used to calculate the area of nuclear, heterochromatin/euchromatin and to quantify the percentage of euchromatin and heterochromatin. A minimum of 300 cells per group were evaluated, and the proportion of aberrant nuclei was calculated as (number of abnormal cells / total counted cells) × 100%.

(3) It will be helpful if supplemental data are ordered according to how they are discussed in the text. Currently, the order of the supplemental data is hard to keep track of eg., the results section starts describing supplemental Figure 1, then the text jumps to supplemental Figure 5 followed by Supplemental Figure 3 (and so on).

Thanks for the reviewer’s suggestion. It has been revised accordingly.

(4) Overall, there are many incomplete sentences and typos throughout the manuscript including some of the figures e.g. on page 10 the sentence "Since the generation of erythroid with abnormal nucleus and reduction of mature red blood cells caused by IDH1 absence are notable characteristics of MDS and AML." is incomplete. On page 11, it reads "Histone post-modifications". This needs to be either histone modifications or histone post-translational modifications. In Figure 4C, the y-axis title is hard to understand "% of euchromatin and heterochromatin". Overall, the document needs to be proofread and revised carefully.

Thanks for the reviewer’s suggestion. We have made revision accordingly in the revised manuscript. The sentence "Since the generation of erythroid with abnormal nucleus and reduction of mature red blood cells caused by IDH1 absence are notable characteristics of MDS and AML." has been revised to “The production of erythrocytes with abnormal nuclei and the reduction of mature erythrocytes due to IDH1 deletion are prominent features of MDS and AML.”  “% of euchromatin and heterochromatin” has been modified to “Area ratio of euchromatin to heterochromatin”.

Reviewer #3 (Recommendations For The Authors):

The following critique points aim to help the authors to improve their manuscript:

(1) The authors reason (p. 10) that because mutant IDH1 has been shown to result in altered chromatin organization, this could be the case in their system, too. However, mutant IDH1 has an ascribed metabolic consequence, the generation of 2-HG, which further weakens the author's argument for an enzymatically independent role of IDH1 in their system. The same is true for the author's observation in Supplementary Figure 9B that in IDH1-mutant AML/MDS samples, H3K79me3 colocalized with the IDH1 mutants in the nucleus. Again, this speaks in favor of IDH1's role being linked to metabolism. The authors could re-write this manuscript, not so much emphasizing the separation of function between different subcellular forms of IDH1 but rather focusing on the chromatin changes and how they could be linked to the actual phenotype, the nuclear condensation and enucleation defect - if so, addressing the surprising finding of enrichment of both active and repressive chromatin marks will be important.

Thanks for the reviewer’s suggestion. We agree with the reviewers and editors all the data we present in the current are not robust enough to rigorously distinguish between enzymatic and enzymatic-independent roles of IDH1. In our revised manuscript, we have removed all assertions of a "metabolism-independent" mechanism. Instead, we focus on demonstrating that nuclear-localized IDH1 contributes to chromatin state regulation during terminal erythropoiesis (e.g., H3K79me3 accumulation).

(2) How come so many genes were downregulated by RNA-seq (about an equal number as upregulated genes) but not more open by ATAC-seq? The authors should discuss this result.

Thanks for the reviewer's suggestion. ATAC-seq showed an increase in chromatin accessibility after IDH1 deletion, but the number of up-regulated genes was slightly larger than that of down-regulated genes, which may be caused by the metabolic changes affected by IDH1 deletion. In order to explore the effect of chromatin accessibility changes on gene expression after IDH1 deletion, we analyzed the changes in differential gene expression at the differential ATAC peak region (as shown in the figure below), and the results showed that the gene expression at the ATAC peak region with increased chromatin accessibility was significantly up-regulated. This may explain the regulation of chromatin accessibility on gene expression.

(3) For the ChIP-seq analyses of H3K79me3, H3K27me2, and H3K9me3, the authors should not just show genome-wide data but also several example gene tracks to demonstrate the differential abundance of peaks in control versus IDH1 knockdown. Furthermore, the heatmap shown in Figure 5A should include broader regions spanning the gene bodies, to visualize the intergenic H3K27me2 and H3K9me3 peaks. Expression could very well be regulated from these intergenic regions as they could bear enhancer regions. ChIP-seq for H3K27Ac in the same setting would be very useful to identify those enhancers.

Thanks for the reviewer’s suggestion. It has been revised accordingly. We reanalyzed the ChIP-seq peak signal of H3K79me3, H3K27me2 and H3K9me3 in a wider region (±5Kb) at gene body, and the results showed that the H3K27me2 and H3K9me3 peak signals did not change significantly. Since H3K79me3 showed a higher peak signal and was mainly enriched in the promoter region, our subsequent analysis focusing on the impact of H3K79me3 accumulation on chromatin accessibility and gene expression might be more valuable.

Author response image 3.

ChIP-seq analysis show that the peak signal of H3K79me3,H3K27me2 and H3K9me3. (A) Heatmaps displayed normalized ChIP signal of H3K9me3, H3K27me2, and H3K79me3 at gene body regions. The window represents ±5 kb regions from the gene body. TES, transcriptional end site; TSS, transcriptional start site. (B) Representative peaks chart image showed normalized ChIP signal of H3K9me3, H3K27me2, and H3K79me3 at gene body regions.

(4) The absent or very mild delay (also no significance visible in the quantification plots) in the generation of orthochromatic erythroblasts on Day 13 upon IDH1 shRNA knockdown as per a4-integrin/Band3 flow cytometry does not correspond to the already quite prominent number of multinucleated cells at that stage seen by cytospin/Giemsa staining. Why do the authors think this is the case? Cytospin/Giemsa staining might be the better method to quantify this phenotype and the authors should quantify the cells at different stages in at least 100 cells from non-overlapping cytospin images.

Thanks for the reviewer’s suggestion. We have supplemented the cytpspin assay and the results were presented in Supplemental Figure 4.

(5) The pull-down assay in Figure 7E does not show a specific binding of H3K79me3 to the SIRT1 promoter. Rather, there is just more H3K79me3 in the nucleus, thus leading to generally increased binding. The authors should show that H3K79me3 does not bind more just everywhere but to specific loci. The ChIP-seq data mention only categories but don't show any gene lists that could hint at the specificity of H3K79me3 binding at genes that would promote nuclear abnormalities and enucleation defects.

We thank the reviewer for pointing this out. The GSEA results of H3K79me3 peak showed enrichment of chromatin related biological processes, and the list of associated genes is shown Figure 7B. In addition, we also displayed the changes in H3K79me3 peak signals, ATAC peak signals, and gene expression at gene loci of three chromatin-associated genes (SIRT1, KMT5A and NUCKS1).

(6) P. 12: "Representatively, gene expression levels and ATAC peak signals at SIRT1 locus were elevated in IDH1-shRNA group and were accompanied by enrichment of H3K9me3 (Figure 7F)." Figure 7F does not show an enrichment of H3K9me3, but if the authors found such, they should explain how this modification correlates with the activation of gene expression.

Thank you for bringing this issue to our attention. We sincerely apologize for the mistake in the description of Figure 7F on page 12. We have already corrected this error in the revised manuscript.

(7) Related to the mild phenotype by flow cytometry on Day 13, are the "3 independent biological replicates" from culturing and differentiating CD34 cells from 3 different donors? If all are from the same donor, experiments from at least a second donor should be performed to generalize the results.

In our current study, CD34⁺ cells were derived from different donors. 

(8) If the images in Supplementary Figure 4 are only the indicated cell type, then it is not clear how the data were quantified since only some cells in each image are pointed at and others do not seem to have as large nuclei. There is also no explanation in the legend what the colors mean (nuclei were presumably stained with DAPI, not clear what the cytoplasm stain is - GPA?).

We thank the reviewer for pointing this out. We have revised the manuscript accordingly. Specifically, the nuclei was stained with DAPI and the color was blue. The cell membrane was stained with GPA and the color was red. This staining method allows for clear visualization of the cell structure and helps to better understand the localization of the proteins of interest.

(9) It is not clear to this reviewer whether Figure 4F is a quantification of the Western Blot or of the IF data.

Figure 4F is a quantification of the Western Blot experiment.

(10) The authors sometimes do not describe experiments well, e.g., "treatment of IDH1-deficient erythroid cells with IDH1-EX527" (p. 13). EX-527 is a SIRT1 inhibitor, which the authors only explicitly mention later in that paragraph. It is unclear to this reviewer, why the authors call it IDH1-EX527.

Thank you for pointing out the unclear description in our manuscript. We apologize for the confusion caused by the unclear statement. We have revised the manuscript accordingly. The compound EX-527 is a SIRT1 inhibitor, and we have corrected the description to simply "EX-527" in the revised manuscript.

(11) The end of the introduction needs revising to be more concise; the last paragraph on p. 4 ("Recently, the decreased expression of IDH1...") partially should be integrated with the previous paragraph, and partially is repeated in the last paragraph (top paragraph on p. 5). The last sentence on p. 4, "These findings strongly suggest that aberrant expression of IDH1 is also an important factor in the pathogenesis of AML and MDS.", should rather read "increased expression of IDH1", to distinguish it from mutant IDH1 (mutant IDH1 is also aberrantly expressed IDH1).

We appreciated the reviewer for the helpful suggestion. Considering that the inclusion of this paragraph did not provide a valuable contribution to the formulation of the scientific question, we have removed it after careful consideration, and the revised manuscript is generally more logically smooth.

(12) Abstract and last sentence of the introduction: "innovative perspective" should be re-worded, as the authors present data, not a perspective. Maybe could use "evidence".

Thanks for the reviewer’s suggestion. It has been revised accordingly.

(13) "IDH1-mut AML/MDS" on p. 11. The authors should provide more information about these AML/MDS samples. The legend contains no information about them/their mutational status. How many samples did the authors look at? Do these cells contain mutations other than IDH1?

Thanks for the reviewer’s suggestion. The detail information of these AML/MDS samples are provide in supplemental table 1. In our current study, we collected ten AML/MDS samples and the majority of the samples only contain IDH1 mutations at different sites.

(14) The statement, "Taken together, these results indicated that IDH1 deficiency reshaped chromatin states and subsequently altered gene expression pattern, especially for genes regulated by H3K79me3, which was the mechanism underlying roles of IDH1 in modulation of terminal erythropoiesis." (p. 10), is not correct at that point in the manuscript as the authors have not yet introduced the RNA-seq data.

Thanks for the reviewer’s suggestion. The statement has been revised to “Taken together, these results indicated that IDH1 deficiency reshaped chromatin states by altering the abundance and distribution of H3K79me3, which was the mechanism underlying roles of IDH1 in modulation of terminal erythropoiesis”.

(15) For easier readability, the authors should present the data in order. For example, the supplemental data for IDH shRNA and siRNA should be presented together and not in Supplementary Figures 1 and 5. Supplementary Figure 3 is mentioned after Supplementary Figure 1, but before Supplementary Figure 2 - again, all data need to be presented in subsequent figures to be viewed together.

Thank you for your suggestion regarding the order of data presentation. We have reorganized the figures in the manuscript to improve readability. We apologize for any confusion caused by the previous arrangement and hope that the revised version meets your expectations.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

Summary:

The manuscript by Zhang et al describes the use of a protein language model (pLM) to analyse disordered regions in proteins, with a focus on those that may be important in biological phase separation. While the paper is relatively easy to read overall, my main comment is that the authors could perhaps make it clearer which observations are new, and which support previous work using related approaches. Further, while the link to phase separation is interesting, it is not completely clear which data supports the statements made, and this could also be made clearer.

We thank the reviewer for their thoughtful evaluation of our manuscript and for the supportive comments. As outlined in the responses below, we have made substantial revisions to clarify the novel observations presented in our study and to strengthen the connection between sequence conservation and phase separation.

Comment 1: With respect to putting the work in a better context of what has previously been done before, this is not to say that there is not new information in it, but what the authors do is somewhat closely related to work by others. I think it would be useful to make those links more directly.

We have addressed the specific comments as outlined below.

Comment 1a: Alderson et al (reference 71) analysed in detail the conservation of IDRs (via pLDDT, which is itself related to conservation) to show, for example, that conserved residues fold upon binding. This analysis is very similar to the analysis used in the current study (using ESM2 as a different measure of conservation). Thus, the result that "Given that low ESM2 scores generally reflect mutational constraint in folded proteins, the presence of region a among disordered residues suggests that certain disordered amino acids are evolutionarily conserved and likely functionally significant" is in some ways very similar to the results of that (Alderson et al) paper .

We thank the reviewer for the comment. However, we would like to clarify that our findings show subtle but important differences from those reported by Alderson et al. Specifically, Alderson et al. used AlphaFold2 predictions to identify IDRs that undergo disorder-to-order transitions, which the authors termed as conditionally folded IDRs. These regions could potentially be functionally important, assuming that function of IDRs necessitate folding.

We argue, however, that, the validity of this structure-function relationship for IDRs remains to be tested. In our opinion, The most direct way to evaluate the functional significance is via evaluating the evolutionary conservation.

As shown in Author response image 1, the correlation between pLDDT scores and the conservation score, while noticable, is significantly weaker than that between the ESM2 score and the conservation score.

Author response image 1.

Comparison of the correlation between AlphaFold2 pLDDT scores and conservation scores with the correlation between ESM2 scores and conservation scores. Calculations were performed using proteins in the MLO-hProt dataset. (A) Correlation between the mean AlphaFold2 pLDDT scores and conservation scores for various amino acids. Pearson correlation coefficients (r) are indicated in the figure legends. The four panels on the right present analogous correlation plots for amino acids grouped by structural order, as defined by their pLDDT scores. (B) Similar as in part A but for ESM2 scores.

Therefore, we believe that ESM2 score is a better indicator than AlphaFold2 pLDDT score for functional relevance.

Furthermore, for the human IDRs, we explicitly selected amino acids with pLDDT scores ≤ 70.

These would be classified as structureless, disordered amino acids, according to the study by Alderson et al. Nevertheless, as shown in Figures 2 and 3 of the main text, our analyses still identifies conserved regions. Therefore, these regions may function via distinct mechanisms than the disorder to order transition.

We now discuss the novelty of our work in the context of existing studies in the newly added Conclusions and Discussion: Related Work, as quoted below.

“Numerous studies have sought to identify functionally relevant amino acid groups within IDRs [cite]. For instance, using multiple sequence alignment, several groups have identified evolutionarily conserved residues that contribute to phase separation [cite]. Alderson et al. employed AlphaFold2 to detect disordered regions with a propensity to adopt structured conformations, suggesting potential functional relevance [alderson et al].

In contrast, our approach based on ESM2 is more direct: it identifies conserved residues without relying on alignment or presupposing that functional significance requires folding into stable 3D structures. Notably, many of the conserved residues identified in our analysis exhibit low pLDDT scores (Figure 2), implying potential functional roles independent of stable conformations.”

Comment 1b: Dasmeh et al, Lu et al and Ho & Huang analysed conservation in IDRs, including aromatic residues and their role in phase separation.

We thank the reviewer for bringing these works to our attention! We now explicitly discuss these studies in both the Discussion section as mentioned above and in the Introduction as quoted below.

“Evolutionary analysis of IDRs is challenging due to difficulties in sequence alignment [cite], though several studies have attempted alignment of disordered proteins with promising results [Dasmeh et al, Lu et al and Ho & Huang].”

Comment 1c: A number of groups have performed proteomewide saturation scans using pLMs, including variants of the ESM family, including Meier (reference 89, but cited about something else) and Cagiada et al (https://doi.org/10.1101/2024.05.21.595203) that analysed variant effects in IDRs using a pLM. Thus, I think statements such as "their applicability to studying the fitness and evolutionary pressures on IDRs has yet to be established" should possibly be qualified.

We added a new paragraph in the Introduction to discuss the application of protein language models to IDRs and cited the suggested references.

“While protein language models have been widely applied to structured proteins [cite], it is important to emphasize that these models themselves are not inherently biased toward folded domains. For example, the Evolutionary Scale Model (ESM2) [cite] is trained as a probabilistic language model on raw protein sequences, without incorporating any structural or functional annotations. Its unsupervised learning paradigm enables ESM2 to capture statistical patterns of residue usage and evolutionary constraints without relying on explicit structural information. Thus, the success of ESM2 in modeling the mutational landscapes of folded proteins [cite] reflects the model’s ability to learn sequence-level constraints imposed by natural selection — a property that is equally applicable to IDRs if those regions are also under functional selection. Indeed, protein language models are increasingly been used to analyze variant effects in IDRs [cite].”

Comment 2: On page 4, the authors write, "The conserved residues are primarily located in regions associated with phase separation." These results are presented as a central part of the work, but it is not completely clear what the evidence is.

We thank the reviewer this insightful comment. We realized that our wording is not as precise as we should have been. We meant to state that the regions associated with phase separation are significantly enriched in these conserved residues. This is a significant finding and indicates that phase separation could be a source of evolutionary pressure in dictating IDP sequence conservation. However, we do not intend to suggest that phase separation is the only evolutionary pressure.

The sentence has been revised to

“Notably, regions associated with phase separation are significantly enriched in these conserved residues.”

We further replaced the section title "Conserved, Disordered Residues Localize in Regions Driving Phase Separation" with "Regions Driving Phase Separation Are Enriched with Conserved, Disordered Residues" to further clarify our findings and avoid overinterpretation.

Finally, we revised the following sentence in the discussion

“Notably, these conserved, disordered residues are predominantly located in regions actively involved in phase separation, contributing to the formation of membraneless organelles.”

to

“Notably, regions actively involved in phase separation are enriched with these conserved, disordered residues, supporting their potential role in the formation of membraneless organelles.”

The submitted manuscript provides clear evidence supporting the enrichment of conserved residues in MLO-driving IDRs. Specifically, Figures 4A and 4C demonstrate that these IDRs exhibit a substantially higher fraction of conserved residues compared to other IDRs involved in phase separation.

In this analysis, the nMLO-hIDR group serves as a baseline, representing the distribution of conservation in disordered regions lacking MLO-related functions. In contrast, IDRs from MLOassociated groups show a pronounced lower shift in their median and interquartile ranges, indicating stronger evolutionary constraints. Within the dMLO cohort, the degree of conservation follows a distinct gradient: driving residues exhibit the highest levels of conservation, followed by participant residues, with non-participant residues showing values closer to the nMLO baseline. This pattern reflects the relative functional importance of each group in phase separation, with conservation levels corresponding to their roles in MLO scaffolding.

To further support this, we computed, for each IDR, the fraction of conserved amino acids. As shown in Figure S11B, for IDRs that actively contribute to phase separation, the fraction is indeed higher than those not involved in phase separation. This analysis is now included in SI.

During the revision, we explicitly evaluated whether conserved residues are preferentially located in regions associated with phase separation. To this end, for each protein in the MLO-hProt dataset, we calculated the probability p of finding conserved residues within regions contributing to phase separation. These regions include both "driving" and "participating" segments as defined in Figure 4 of the main text.

Figure S11A presents the distribution of p across all proteins. For comparison, we also include the distribution of 1− p, representing the probability of finding conserved residues in regions not associated with phase separation. On average, p exceeds 0.5, suggesting a tendency for conserved residues to be more frequently located in phase-separating regions. However, the difference between the two distributions is not statistically significant. This result may be due to the generally low density of conserved residues in IDRs, which makes the estimation of p challenging for individual proteins. Additionally, some conserved sites may be involved in functions unrelated to phase separation.

We added the following text to the Discussion section of the main text.

“We emphasize that the results presented in Figure 4 do not directly demonstrate that conserved residues are preferentially located in regions associated with phase separation. Although these regions are more enriched in conserved amino acids, their total sequence length can be smaller than that of non-phase-separating regions. As a result, the absolute number of conserved residues may still be higher outside phase-separating regions. To quantitatively assess this, we calculated, for each protein in the MLO-hProt dataset, the probability p of finding conserved residues within regions contributing to phase separation. These regions include both "driving" and "participating" segments, as defined in Figure 4 of the main text. Figure S11 shows the distribution of p across all proteins. For comparison, we also present the distribution of 1− p, which reflects the probability of finding conserved residues in non-phase-separating regions. While the average value of p exceeds 0.5, indicating a trend toward conserved residues being more frequently located in phase-separating regions, the difference between the two distributions is not statistically significant. Future studies with expanded datasets may be necessary to clarify this trend.”

Comment 3: It would be useful with an assessment of what controls the authors used to assess whether there are folded domains within their set of IDRs.

We acknowledge that our previous labeling may have caused some confusion. Protein sequences used in Figures 2 and 3 include both folded and disordered domains. Results presented in these figures were constructed using full-length protein sequences to highlight the similarities and differences in ESM2 scores between folded and disordered domains.

In contrast, the analyses presented in Figures 4 and 5 focus exclusively on IDRs to examine their role in phase separation.

To prevent further confusion, we have renamed the dataset used in Figures 2 and 3 as MLO-hProt, emphasizing that the analysis pertains to entire protein sequences. The term MLO-hIDR is now reserved for a new dataset that includes only disordered residues, as used in Figures 4 and 5, and corresponding SI Figures.

For the dMLO-IDR dataset, all except one amino acid (P40967, residue G592) are annotated as disordered in the MobiDB database (https://mobidb.org/). This database characterizes disordered regions based on a combination of predictive algorithms and experimental data. As illustrated in Figure S5A, 25.5% of the proteins in the dataset have direct experimental evidence supporting their disorderedness. These experimental annotations are derived from a diverse range of techniques (Figure S5B). For the remaining proteins, disorder was predicted by one or more computational tools. Although not all tools were applied to every protein, each protein in the dataset was identified as disordered by at least one method.

For human proteins, IDRs were identified based on AlphaFold2 pLDDT scores, using a threshold of 70. As established in prior studies [1, 2], the pLDDT score provides a quantitative measure of local structural confidence, with lower values indicating greater structural disorder. IDRs associated with conditional folding or disorder-to-order transitions generally exhibit high pLDDT values (e.g., >70).

Author response image 2 shows a violin plot of AlphaFold2 pLDDT scores for the various MLO-hIDR groups. The consistently low scores support the conclusion that these regions are structurally disordered.

We also cross-checked the MLO-hIDR regions against the MobiDB database. As shown in Figure S6, approximately 76% of the proteins in the dataset are predicted to contain disordered regions. Among the non-labeled segments with pLDDT scores ≤ 70, the majority are relatively short, with segments of 1–5 residues accounting for approximately 80%.

Author response image 2.

AlphaFold pLDDT scores of hIDRs in different MLO-related groups.

In addition to renaming the dataset, we also revised the manuscript to highlight the validation of disorderedness in section of Results: Regions Driving Phase Separation Are Enriched with Conserved, Disordered Residues.

“The presence of evolutionarily conserved disordered residues raises the question of their functional significance. To explore this, we identified disordered regions of MLO-hProt using a pLDDT score less than 70 and partitioned these regions into two categories: drivers (dMLO-hIDR), which actively drive phase separation, and clients (cMLO-hIDR), which are present in MLOs under certain conditions but do not promote phase separation themselves [cite]. Additionally, IDRs from human proteins not associated with MLOs, termed nMLO-hIDR, were included as a control. To enhance statistical robustness, we extended our dataset by incorporating driver proteins from additional species [cite], resulting in the expanded dMLO-IDR dataset. Beyond the pLDDT-based classification, the majority of residues in these datasets are also predicted to be disordered by various computational tools and supported by experimental evidence (Figures S5 and S6).”

Recommendation 1: The authors use the terms "evolutionary fitness of IDRs" (abstract and p. 5, for example), "fitness of amino acids" (p. 4), and "quantify the fitness of particular residues at specific sites" (p. 5). It is not clear what is meant by fitness in this context.

We thank the reviewer for pointing out the ambiguity in the term fitness. To enhance clarity, we have replaced “fitness" with “mutational tolerance" to more directly emphasize the evolutionary conservation of specific residues.

Recommendation 2: The authors write (p. 6) "Previous studies have demonstrated a strong correlation between ESM2 scores and changes in free energy related to protein structure stability". While that may be true, it might be worth noting that ESM2 scores report on the effects of mutations and function more broadly than stability because these models have previously been shown to capture conservation effects beyond stability.

We fully agree with the reviewer’s comment and have revised the main text accordingly. Specifically, the referenced sentence has been revised and relocated, as shown below.

“Our analysis demonstrated that HP1_α_’s structured domains consistently yield low ESM2 scores, reflecting strong mutational constraints characteristic of folded regions. These constraints are further evident in the local LLR predictions, as shown in Figure 2B, where we illustrate the folded region G120-T130. Given the functional importance of preserving the 3D of structured domains, mutations with greater detrimental effects are likely to disrupt protein folding substantially. This interpretation is consistent with previous studies reporting a significant correlation between ESM2 LLRs and changes in free energy associated with protein structural stability [cite].”

Recommendation 3: p. 10: The authors write "To exclude sequences that no longer qualify as homologs, we filtered for sequences with at least 20% identity to the reference". How did they decide on 20% and why? And over which residues are these 20% calculated.

We apologize for the earlier lack of clarity. Sequence alignment was performed using the full-length protein sequences, encompassing both folded and disordered regions. For each sequence, we calculated the percent identity by counting the number of positions, denoted as n, at which the amino acid matches the reference. The percent identity was then computed as n/N, where N represents the total length of the aligned reference sequence. This total includes residues in folded and disordered regions, as well as gap positions introduced during alignment.

We updated the Methods section of the main text to clarify.

“We performed multi-sequence alignment (MSA) analysis using HHblits from the HH-suite3 software suite [citations], a widely used open-source toolkit known for its sensitivity in detecting sequence similarities and identifying protein folds. HHblits builds MSAs through iterative database searches, sequentially incorporating matched sequences into the query MSA with each iteration. Sequence alignment was performed using the full-length protein sequences, encompassing both folded and disordered regions.

...

To refine alignment quality by focusing on closely related homologs, we filtered out sequences with ≤ 20% identity to the query, excluding weakly related sequences where only short segments show similarity to the reference. For each sequence, we calculated the percent identity by counting the number of positions, denoted as n, at which the amino acid matches the reference. The percent identity was then computed as n/N, where N represents the total length of the aligned reference sequence. This total includes residues in folded and disordered regions, as well as gap positions introduced during alignment.”

We selected a 20% sequence identity threshold to balance inclusion of true homologs with exclusion of distant matches that may not share functional relevance. To determine this cutoff, we compared identity thresholds of 0%, 10%, 20%, and 40% and examined the resulting distributions of conservation and ESM2 scores across aligned residues for MLO-hProt dataset (Author response image 3). Thresholds of 10%, 20%, and 40% produced qualitatively similar results, with a consistent correspondence between low ESM2 scores and high conservation. Lower thresholds introduced highly divergent sequences that added noise to the alignment, resulting in reduced overall conservation scores. In contrast, higher thresholds excluded homologs with potentially meaningful conservation, particularly in disordered regions where conservation scores tend to be relatively low.

Author response image 3.

Histograms of the ESM2 score and the conservation score, presented in a format consistent with Figure 3B of the main text. The conservation scores were computed using aligned sequences with identity thresholds of ≥0, ≥10%, ≥20%, and ≥40% (left to right). Contour lines represent different levels of −log_P_(CS,ESM2), where P is the joint probability density of conservation score (CS) and ESM2 score. Contours are spaced at 0.5-unit intervals, highlighting regions of distinct density.

Recommendation 4: In their description of "motif" searching algorithm (p. 20) I think that the search algorithm would give a different result whether the search is performed N->C or C->N (because the first residue (i) needs to have a score <0.5 but the last (j) could have a score >0.5 as long as the average is below 0.5. Is that correct? And if so, why did they choose an asymmetric algorithm? .

We thank the reviewer for highlighting the asymmetry in our motif-search algorithm.

To investigate this issue, we repeated the algorithm starting from the C-terminus and compared the resulting motifs with those obtained from the N-terminal scan. We found that the two sets of motifs overlap entirely: each motif identified from the C-terminal direction has a corresponding counterpart from the N-terminal scan. However, the motifs are not identical. The directionality of the search introduces additional amino acids—referred to here as peripheral residues—at the motif boundaries, which differ between the two sets.

As shown in Author response image 4, the number of peripheral residues is small relative to the total motif length.

To eliminate asymmetry and ambiguity, we have revised our method to perform bidirectional scans—from both the N- and C-termini—and define each motif as the overlapping region identified by both directions. This approach emphasizes the conserved core and avoids the inclusion of spurious terminal residues. The updated procedure is described in Methods: Motif Identification.

“To identify motifs within a given IDR, we implemented the following iterative procedure. Starting from either the N– or C–terminus of the sequence, we first locate the initial residue i whose ESM2 score falls within 0.5. From i, residues are sequentially appended…”

Author response image 4.

Number of peripheral residues and their relative length to the full-motif length identified from both sides. (A). The unique motifs identified from N-to-C terminal direction. (B) The unique motifs identified from C-to-N terminal direction.

“…in the direction toward the opposite terminus until the segment’s average ESM2 score exceeds 0.5; the first residue to breach this threshold is denoted j. The segment (i,i+1,..., j−1) is then recorded as a candidate motif. This process repeats starting from j until the end of the IDR is reached.

We perform this full procedure independently from both termini and designate the final motif as the intersection of the two candidate-motif sets. This bidirectional overlap strategy excludes terminal residues that might transiently satisfy the average-score criterion only due to adjacent low-scoring regions, thereby isolating the conserved core of each motif. All other residues—those not included in either directional pass—are classified as non-motif regions, minimizing peripheral artifacts.”

Accordingly, we have updated the Supplementary material: ESM2_motif_with_exp_ref.csv for the new identified motifs commonly exited from both N-terminal and C-terminal searches. Minor changes were observed in the set of motifs as being discussed, but these do not affect the main conclusions. Figures 5C, 5D, and S6 have been revised accordingly.

Reviewer #2:

Summary:

Unfortunately, I do not believe that the results can be trusted. ESM2 has not been validated for IDRs through experiments. The authors themselves point out its little use in that context. In this study, they do not provide any further rationale for why this situation might have changed. Furthermore, they mention that experimental perturbations of the predicted motifs in in vivo studies may further elucidate their functional importance, but none of that is done here. That some of the motifs have been previously validated does not give any credibility to the use of ESM2 here, given that such systems were probably seen during the training of the model.

We thank the reviewer for their detailed and thoughtful critique of our manuscript. We recognize the importance of careful model validation, especially in the context of IDRs, and appreciate the opportunity to clarify the scope and rationale of our study. Below, we respond point-by-point to the main concerns.

(1) The use of ESM2 is not validated for IDRs, and the authors provide no rationale for its applicability in this context.

We thank the reviewer for raising this important point.

First, we emphasize that ESM2 is a probabilistic language model trained entirely on amino acid sequences, without any structural supervision. The model does not receive any input about protein structure — folded or disordered — during training. Instead, it learns to estimate the likelihood of each amino acid at a given position, conditioned on the surrounding sequence context. This makes ESM2 agnostic to whether a sequence is folded or disordered; the model’s capacity to identify patterns of residue usage arises solely from the statistics of natural sequences.

As such, ESM2 is not inherently biased toward folded proteins, even though previous studies have demonstrated its usefulness in identifying conserved and functionally constrained residues in structured domains [3–9]. These findings support the broader utility of language models for uncovering evolutionary constraints — and by extension, suggest that similar signatures could exist in IDRs, particularly if they are under functional selection.

Indeed, if certain residues or motifs in IDRs are conserved due to their importance in biological processes (e.g., phase separation), we would expect such selection to be reflected in sequence-based features, which ESM2 is designed to detect. The model’s applicability to IDRs, then, is a natural extension of its core probabilistic architecture.

To further evaluate this, we carried out an independent in silico validation using multiple sequence alignments (MSAs). This analysis allowed us to compute the evolutionary conservation of individual amino acids without any reliance on ESM2. We then compared these conservation scores to ESM2 scores and found a strong correlation between the two. This provides direct, quantitative support for the idea that ESM2 is capturing biologically meaningful sequence constraints — even in disordered regions.

While we agree that experimental testing would ultimately provide the most compelling validation, we believe that our MSA-based comparison constitutes a strong and arguably ideal computational validation of the model’s predictions. It offers an orthogonal measure of evolutionary pressure that confirms the biological plausibility of ESM2 scores.

We added the following text in the introduction to highlight the applicability of ESM2 to IDRs.

“While protein language models have been widely applied to structured proteins, it is important to emphasize that these models themselves are not inherently biased toward folded domains. For example, the Evolutionary Scale Model (ESM2) [cite] is trained as a probabilistic language model on raw protein sequences, without incorporating any structural or functional annotations. It operates by estimating the likelihood of observing a given amino acid at a particular position, conditioned on the entire surrounding sequence context. This unsupervised learning paradigm enables ESM2 to capture statistical patterns of residue usage and evolutionary constraints without relying on explicit structural information. Thus, the success of ESM2 in modeling fitness landscapes of folded proteins reflects the model’s ability to learn sequence-level constraints imposed by natural selection — a property that is equally applicable to IDRs if those regions are also under functional selection. Indeed, protein language models are increasingly been used to analyze variant effects in IDRs [cite].”

(2) There is no experimental validation of the ESM2-based predictions in this study.

We agree that experimental validation would provide definitive support for the utility of ESM2 in IDRs, and we explicitly state this as a limitation in the revised manuscript as quoted below.

“Limitations: Despite the promising findings, our study has several limitations. Most notably, our analysis is purely computational, relying on ESM2-derived predictions and sequence-based conservation without accompanying experimental validation. While the strong correlation between ESM2 scores and evolutionary conservation provides compelling evidence that the identified motifs are functionally constrained, the precise biological roles of these motifs remain uncharacterized. ESM2 is well-suited for highlighting regions under selective pressure, but it does not provide mechanistic insights into how conserved motifs contribute to specific molecular functions such as phase separation, molecular recognition, or dynamic regulation. Determining these roles will require targeted experimental investigations, including mutagenesis and biophysical characterization.”

In addition, we revised the manuscript title from “Protein Language Model Identifies Disordered, Conserved Motifs Driving Phase Separation" to “Protein Language Model Identifies Disordered, Conserved Motifs Implicated in Phase Separation". This revision softens the original claim to better reflect the absence of direct experimental evidence for the motifs’ role in phase separation.

However, we also emphasize that the goal of our study is not to claim definitive predictive power, but rather to explore whether ESM2-derived mutational profiles align with known biological features of IDRs — and in doing so, to generate new, testable hypotheses.

In addition, while no in vivo experiments were performed, our study does include an in silico validation step, as detailed in the response to the previous comment. The strong correlation between ESM2 scores and conservation scores provides direct support for the utility of ESM2 in identifying residues under evolutionary constraint in disordered regions.

(3) The overlap between predicted motifs and known ones may be due totraining data leakage.

We respectfully clarify that training data leakage is not possible in this case, as ESM2 is trained using unsupervised learning on raw protein sequences alone. The model has no access to experimental annotations, functional labels, or knowledge of which motifs are involved in phase separation. It only models statistical sequence patterns derived from evolutionarily observed proteins.

Therefore, any agreement between ESM2-derived predictions and previously validated motifs arises not from memorization of experimental data, but from the model’s ability to learn meaningful sequence constraints from the natural distribution of proteins.

(4) The authors should revamp the study with a testable predictive framework.

We respectfully suggest that a full revamp is not necessary or appropriate in this context.

As outlined in our previous responses, we believe that certain misunderstandings about the nature and capabilities of ESM2 may have influenced the reviewer’s assessment.

Importantly, both Reviewer 1 and Reviewer 3 express strong support for the significance and novelty of this work, and recommend publication following minor revisions.

In this context, we believe the manuscript provides a useful contribution as a first step toward understanding disordered regions using language models, and that it has value even in the absence of direct experimental testing. We have now better positioned the manuscript in this light, clarified limitations, and suggested concrete next steps for follow-up research.

We hope these clarifications and revisions address the reviewer’s concerns, and we thank them again for helping us strengthen the framing, rigor, and clarity of our study.

Reviewer #3:

Summary:

This is a very nice and interesting paper to read about motif conservation in protein sequences and mainly in IDRs regions using the ESM2 language model. The topic of the paper is timely, with strong biological significance. The paper can be of great interest to the scientific community in the field of protein phase transitions and future applications using the ESM models. The ability of ESM2 to identify conserved motifs is crucial for disease prediction, as these regions may serve as potential drug targets. Therefore, I find these findings highly significant, and the authors strongly support them throughout the paper. The work motivates the scientific community towards further motif exploration related to diseases.

Strengths:

(1) Revealing conserved regions in IDRs by the ESM-2 language model.

(2) Identification of functionally significant residues within protein sequences, especially in IDRs.

(3) Findings supported by useful analyses.

We appreciate the reviewer’s thoughtful words and support for our work.

Weaknesses:

(1) Lack of examples demonstrating the potential biological functions of these conserved regions.

As detailed in the Response to Recommendation 6, we conducted additional analyses to connect the identified conserved regions with their biological functions.

(2) Very limited discussion of potential future work and of limitations.

We have substantially revised the Conclusions and Discussion section to provide a detailed analysis of the study’s limitations and to propose several directions for future research, as elaborated in our Response to Recommendation 5 below.

Recommendation 1: The authors describe the ESM2 score such that lower scores are associated with conserved residues, stating that "lower scores indicate higher mutational constraint and reduced flexibility, implying that these residues are more likely essential for protein function, as they exhibit fewer permissible mutational states." However, when examining intrinsically disordered regions (IDRs), which are known to drive phase separation, I observe that the ESM2 score is relatively high (Figure 3C, pLDDT < 50, and Supplementary Figure S2). Could the authors clarify how this relatively high score aligns with the conservation of motifs that drive phase separation?

We thank the reviewer for this insightful comment. We would like to clarify that most amino acids in the IDRs are not conserved, even for IDRs that contribute to phase separation. Only a small set of amino acids in these IDRs, which we term as motifs, are evolutionarily conserved with low ESM2 scores. Therefore, the ESM2 scores exhibit bimodal distribution at high and low values, as shown in Figures 4A and 4C of the manuscript. When averaged over all the amino acids, the mean ESM2 scores, plotted in Figure 3C, are relatively high due to dominant population of non-conserved amino acids.

Recommendation 2: The authors mention: "We first analyzed the relationship between ESM2 and pLDDT scores for human Heterochromatin Protein 1 (HP1, residues 1-191)". I appreciate this example as a demonstration of amino acid conservation in IDRs. However, it is questionable whether the authors could provide some more examples to support amino acid conservation particularly within the IDRs along with lower ESM2 score (e.g, Could the authors provide some additional examples of "conserved disordered" regions in various proteins which are associated with relatively low ESM2 score as appear in Figure 2A).

We thank the reviewer for this valuable suggestion. We want to kindly noted that the conserved residues on IDRs are prevalent as indicated in Figures 2D and 3B. To further illustrate the prevalence of “conserved disordered” regions, we generated ESM2 versus pLDDT score plots for the full dMLO–hProt dataset (82 proteins) in Figure S2. In these plots, residues with pLDDT ≤ 70 are highlighted in blue to denote structural disorder (dMLO-hIDR), and these disordered residues with ESM2 score ≤ 1.5 are shown in purple to indicate conserved disordered segments.

Recommendation 3: Could the authors plot a Violin conservation score plot for Figure 4A to emphasise the relationship between ESM2 scores and conservation scores of disordered residues?

We thank the reviewer for this suggestion. We included a violin plot illustrating the distribution of conservation scores for disordered residues across all four IDR groups, shown in Author response image 5. Consistent with the findings in Figure 4A, the phase separation drivers (dMLO-hIDR and dMLOIDR) exhibit a higher proportion of conserved amino acids compared to the client group (cMLOhIDR).

We also note that the nMLO-hIDR group may contain conserved residues due to functions unrelated to MLO formation, which could contribute to the higher observed levels of conservation in this group.

Author response image 5.

Violin plots illustrating the distribution of conservation scores for disordered residues across the nMLO–hIDR, cMLO–hIDR, dMLO–hIDR, and dMLO–IDR datasets. Pairwise statistical comparisons were conducted using two-sided Mann–Whitney U tests on the conservation score distributions (null hypothesis: the two groups have equal medians). P-values indicate the probability of observing the observed rank differences under the null hypothesis. Statistical significance is denoted as follows: ***: p < 0.001; **: p < 0.01; *:p < 0.05;

Recommendation 4: It will be appreciated if the authors could add to Figure 4 Violin plots, a statistical comparison between the different groups.

We thank the reviewer for this valuable suggestion. We included the p-values for Figures 4A and 4C to quantify the statistical significance of differences in the distributions.

Most comparisons are highly significant (p < 0.001), while the largest p-value (p = 0.089) between the conservation score of driving and non-participating groups (Figure 4C) still suggests a marginally significant trend.

Recommendation 5: Could the authors expand more on potential future research directions using ESM2, given its usefulness in identifying conserved motifs? Specifically, how do the authors envision conserved motifs will contribute to future discoveries/applications/models using ESM (e.g, discuss the importance of conserved motifs, especially in IDRs motifs, in protein phase transition prediction in relation to diseases).

We thank the reviewer for this insightful comment. To further assess the functional relevance of the conserved motifs, we incorporated pathogenic variant data from ClinVar [10, 11] to evaluate mutational impacts. As shown in Figure S12A and B, a substantial number of pathogenic variants in MLO-hProt proteins are associated with low ESM2 LLR values. This pattern holds for both folded and disordered residues.

Moreover, we observed that variants located within motifs are more frequently pathogenic compared to those outside motifs (Figure S12C). In the main text, motifs were defined only for driver proteins; however, the available variant data for this subset are limited (6 data points). To improve statistical power, we extended motif identification to include both client and driver human proteins, following the same methodology described in the main text. Consistent with previous findings, variants within motifs in this expanded set are also more likely to be pathogenic. These results further support the functional importance of both low ESM2-scoring residues and the conserved motifs in which they reside.

The following text was added in the Discussion section of the manuscript to discuss these results and outline future research directions.

“Several promising directions could extend this work, both to refine our mechanistic understanding and to explore clinical relevance. One avenue is testing the hypothesis that conserved motifs in scaffold proteins act as functional stickers, mediating strong intermolecular interactions. This could be evaluated computationally via free energy calculations or experimentally via interaction assays. Deletion of such motifs in client proteins may also reduce their partitioning into condensates, illuminating their roles in molecular recruitment.

To explore potential clinical implications, we analyzed pathogenicity data from Clin-Var [10, 11]. As shown in Figure S12A, single-point mutations with low LLR values—indicative of constrained residues—are enriched among clinically reported pathogenic variants, while benign variants typically exhibit higher LLR values. Moreover, mutations within conserved motifs are significantly more likely to be pathogenic than those in non-motif regions (Figure S12B). These findings highlight the potential of ESM2 as a first-pass screening tool for identifying clinically relevant residues and suggest that the conserved motifs described here may serve as priorities for future studies, both mechanistic and therapeutic.”

Moreover, the functional significance of conserved motifs, particularly their implications in disease and pathology, warrants further investigation. As an initial analysis, we incorporated ClinVar pathogenic variant data [citation] to assess mutational effects within our datasets. As illustrated in Figure R12A, single-point mutations with low LLR values are enriched among clinically reported pathogenic variants, whereas benign variants are more commonly associated with higher LLR values. Notably, mutations within conserved motifs are substantially more likely to be pathogenic compared to those in non-motif regions. These findings highlight the potential of ESM2 as a firstpass tool for identifying residues of clinical relevance. The conserved motifs identified here may be prioritized in future studies aimed at elucidating their biological roles and evaluating their viability as therapeutic targets.

Recommendation 6: The authors mention: "Our findings provide strong evidence for evolutionary pressures acting on specific IDRs to preserve their roles in scaffolding phase separation mechanisms, emphasizing the functional importance of entire motifs rather than individual residues in MLO formation." They also present a word cloud of functional motifs in Figure 5D. Although it makes sense that evolutionarily conserved motifs, especially within the IDRs regions, act as functional units, I think there is no direct evidence for such functionality (e.g., examples of biological pathways associated with IDRs and phase separation). Hence, there is no justification to write in the figure caption: "ESM2 Identifies Functional Motifs in driving IDRs" unless the authors provide some examples of such functionality. This will even make the paper stronger by establishing a clear connection to biological pathways, and hence these motifs can serve as potential drug targets.

We thank the reviewer for this insightful suggestion. We have replaced “functional motifs" with “conserved motifs" in the figure caption.

Identifying the precise biological pathways associated with the conserved motifs is a complex task and a comprehensive investigation lies beyond the scope of this study. Nonetheless, as an initial effort, we explored the potential functions of these motifs using annotations available in DisProt (https://disprot.org/).

DisProt is the leading manually curated database dedicated to IDPs, providing both structural and functional annotations. Expert curators compile experimentally validated data, including definitions of disordered regions, associated functional terms, and supporting literature references. Author response image 6 presents a representative DisProt entry for DNA topoisomerase 1 (UniProt ID: P11387), illustrating its structural and biological annotation.

For each motif, we located the corresponding DisProt entry and assigned a functional annotation based on the annotated IDR from which the motif originates. We emphasize that this functional assignment should be regarded as an approximation. Because experimental annotations often pertain to the entire IDR, regions outside the motif may also contribute to the reported function.

Nevertheless, the annotations provide valuable insights.

Author response image 6.

Screenshot of information provided by the DisProt database. Detailed annotations of biological functions and structural features, along with experimental references, are accessible via mouse click.

Approximately 50% of ESM2-predicted IDR motifs lack functional annotations. Among those that are annotated, motifs from the dMLO-IDR dataset are predominantly associated with “molecular condensate scaffold activity,” followed by various biomolecular binding functions (Author response image 7A). These findings support the role of these motifs in MLO formation.

For comparison, we applied the same identification procedure (described in Methods: Motif Identification) to motifs from the nMLO-hIDR dataset. In contrast to the dMLO-IDR motifs, these exhibit a broader range of annotated functions related to diverse cellular processes. Collectively, these results suggest that motifs identified by ESM2 are aligned with biologically relevant functions captured in current databases.

Finally, as illustrated in Figure S12 and discussed in the Response to Recommendation 5, variants occurring within identified motifs are more likely to be pathogenic than those in non-motif regions, further underscoring their functional importance.

Author response image 7.

Biological functions of ESM2-predicted motifs. (A) Distribution of biological functions associated with all identified motifs from dMLO-IDR driving groups. (B) Distribution of biological functions associated with all identified motifs from nMLO-hIDR groups.

Recommendation 7: In Figure 2C the authors present FE (I assume this is free energy), some discussion about the difference in the free energy referring to the "a" region is missing (i.e. both "Folded" and "Disordered" regions are associated with low ESM score but with low and high free energy (FE), respectively.

We thank the reviewer for the comments. FE indeed abbreviates free energy. To improve clarify and avoid confusion, we have updated all figure captions by replacing “FE” with “−logP” to explicitly denote the logarithm of probability in the contour density plots.

We used “a" in Figures 2C and 2D to refer to regions with low ESM2 scores, which appears a local minimum in both plots. Since most residues in folded regions are conserved, region a has lower free energy than region b in Figure 2C. On the other hand, as most residues in disordered regions are not conserved, as we elaborated in Response to Recommendation 1, region a has lower population and higher free energy than region b.

To avoid confusion, we have replaced “a" and “b" in Figure 2D with “I" and “II".

Recommendation 8: Figure S2: It would be useful to plot the same figure for structured and disordered regions as well.

We are not certain we fully understood this comment, as we believe the requested analysis has already been addressed. In Figure S2, we used the AlphaFold2 pLDDT score to represent the structural continuum of different protein regions, where residues with pLDDT > 70 (red and lightred bars) are classified as structured, while those with pLDDT ≤ 70 (blue and light-blue bars) are classified as disordered.

Minor suggestion 1: Could the authors clarify the meaning of the abbreviation "FE" in the colorbar of the contour line? I assume this is free energy.

We have updated all contour density plot figure captions by replacing “FE” with “−logP” to explicitly denote the logarithm of probability.

Minor suggestion 2: In Figure 2A - do the authors mean "Conserved folded" instead of just "Folded"? If so, could the authors indicate this?

We thank the reviewer for this comment. The ESM2 scores indeed suggest that, within folded regions, there may be multiple distinct groups exhibiting varying degrees of evolutionary conservation. However, as our primary focus is on IDRs, we chose not to investigate these distinctions further.

Figure 2A illustrates a randomly selected folded region based on AlphaFold2 pLDDT scores.

References

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(2) Alderson, T. R.; Pritišanac, I.; Kolaric, Ð.; Moses, A. M.; Forman-Kay, J. D. Systematic´ Identification of Conditionally Folded Intrinsically Disordered Regions by AlphaFold2. Proceedings of the National Academy of Sciences of the United States of America, 120, e2304302120.

(3) Brandes, N.; Goldman, G.; Wang, C. H.; Ye, C. J.; Ntranos, V. Genome-Wide Prediction of Disease Variant Effects with a Deep Protein Language Model. Nature Genetics 2023, 55, 1512–1522.

(4) Lin, Z. et al. Evolutionary-Scale Prediction of Atomic-Level Protein Structure with a Language Model. 2023.

(5) Zeng, W.; Dou, Y.; Pan, L.; Xu, L.; Peng, S. Improving Prediction Performance of General Protein Language Model by Domain-Adaptive Pretraining on DNA-binding Protein. Nature Communications 2024, 15, 7838.

(6) Gong, J. et al. THPLM: A Sequence-Based Deep Learning Framework for Protein Stability Changes Prediction upon Point Variations Using Pretrained Protein Language Model. Bioinformatics 2023, 39, btad646.

(7) Lin, W.; Wells, J.; Wang, Z.; Orengo, C.; Martin, A. C. R. Enhancing Missense Variant Pathogenicity Prediction with Protein Language Models Using VariPred. Scientific Reports 2024, 14, 8136.

(8) Saadat, A.; Fellay, J. Fine-Tuning the ESM2 Protein Language Model to Understand the Functional Impact of Missense Variants. Computational and Structural Biotechnology Journal 2025, 27, 2199–2207.

(9) Chu, S. K. S.; Narang, K.; Siegel, J. B. Protein Stability Prediction by Fine-Tuning a Protein Language Model on a Mega-Scale Dataset. PLOS Computational Biology 2024, 20, e1012248.

(10) Landrum, M. J.; Lee, J. M.; Riley, G. R.; Jang, W.; Rubinstein, W. S.; Church, D. M.; Maglott, D. R. ClinVar: Public Archive of Relationships among Sequence Variation and Human Phenotype. Nucleic Acids Research 2014, 42, D980–D985.

(11) Landrum, M. J. et al. ClinVar: Improving Access to Variant Interpretations and Supporting Evidence. Nucleic Acids Research 2018, 46, D1062–D1067.

Author response:

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

Reviewer 1:

(1) A major issue throughout the paper is that Hox expression analysis is done exclusively through quantitative PCR, with values ranging from 2-fold to several thousand-fold upregulation, with no antibody validation for any Hox protein (presumably they are all upregulated).

Thank you for your comment.

We tried to verify the stimulated Hox expression pattern by in situ hybridization. Although in early embryos (E9.5) we could detect clearly hox (i.e. Hox8 and Hox9 in Author response image 1) expression patterns in the neural tube by whole mount in situ hybridization, we failed to detect a clear pattern in the brain stem at E18.5 either in whole mount tissue or on sections. That’s one reason that we turned to single nuclear RNA-seq instead.

This is likely due to their low expression levels at late developmental stages and need to be detected by more sensitive method. However, we estimated that the stimulated expression levels of the representative Hox genes are at least comparable to the physiological levels at posterior spinal cord to evoke a functional effect.

Author response image 1.

Some Hox8 and Hox9 expression pattern in E9.5 embryos.

(2) In Figure 1, massive upregulation of most Hox genes in the brainstem is shown after e16.5 but the paper quickly focuses on analysis of PN nuclei. What are the other consequences of this broad upregulation of Hox genes in the brainstem? There is no discussion of the overall phenotype of the mice, the structure of the brainstem, the migration of neurons, etc. The very narrow focus on motor cortex projections to PN nuclei seems bizarre without broad characterization of the mice, and the brainstem in particular. There is only a mention of "severe motor deficits" from previous studies, but given the broad expression of Rnf220, the fact that is a global knockout, and the effects on spinal cord populations shown previously the justification for focusing on PN nuclei does not seem strong.

Thank you for your comment.

Although RNF220 is important for the dorsal-ventral patterning of the spinal cord as well as the hindbrain during embryonic development, the earlier neural patterning and differentiation are normal in the Rnf220+/- mice (Wang et al., 2022). However, these mice showed reduced survival and motility to various degree postnatally (Ma et al., 2019; Ma et al., 2021), likely suggesting a dosage dependent role of RNF220 in maintaining late neural development. As our microarray assay showed the deregulation of the Hox genes in the brain, we followed this direction in this study and narrowed down the affected region to the pons. Our single nuclear RNA-Seq (snRNA-seq) data further shows that the Hox de-regulation mainly occurred in 3 clusters of neurons. However, the pons is complex and contains tens of nuclei. And the current resolution of our data does not support to assign a clear identity to each of them. Although it is clear that more nuclei are likely affected, the PN (cluster7) is the only cluster we can identify to follow in the current study. 

As to general effect of RNF220 haploinsufficiency on the brainstem, we carried out Nissl staining assays and found no clear difference in neuronal cell organization between WT and Rnf220+/- pons (revised Figure 2-figure supplement 2).

(3) It is stated that cluster 7 in scRNA-seq corresponds to the PN nuclei. The modest effect shown on Hox3-5 expression in that data in Figure 1 is inconsistent with the larger effect shown in Figure 2.

Thank you for your comment.

Due to the low efficiency of snRNA-seq and the depth of the sequencing, the quantification of the Hox expression based on the snRNA-seq data is likely less accurate as the qRT-PCR. In addition, only mRNAs in the nuclear could be captured by snRNA-seq, while mRNAs in both the nuclear and cytoplasm were reversed-transcribed and examined for qRT-PCR assays in Figure 2A.

(4) Presumably, Hox genes are not the only targets of Rnf220 as shown in the microarray/RNA-sequencing data. There is no definitive evidence that any phenotypes observed (which are also not clear) are specifically due to Hox upregulation. The only assay the authors use to look at a Hox-dependent phenotype in the brainstem is the targeting of PN nuclei by motor cortex axons. This is only done in 2 animals and there are no details as to how the data was analyzed and quantified. The only 2 images shown are not convincing of a strong phenotype, they could be taken at slightly different levels or angles. At the very least, serial sections should be shown and the experiment repeated in more animals. There is also no discussion of how these phenotypes, if real, would relate to previous work by the Rijli group which showed very precise mechanisms of synaptic specificity in this system.

Thank you for your comments and suggestions.

The deregulation of Hox is the most obvious phenomena observed from the RNA-seq data, and we tried to assign its specific phenotypic effect in this study. As the roles of Hox in PN patterning and circuit formation is well established, we focused on the PN in the following study. Based on literature, we carried out the circuit analysis to examine the targeting of PN neurons by the motor cortex axons. A cohort of additional animals with different genotypes (n=10 for WT and n=9 for Rnf220+/-) were used to repeat the experiment and we got the same conclusion. More detailed information on data analysis and serial images were included in the revised manuscript and figure legends.

(5) The temporal aspect of this regulation in vivo is not clear. The authors show some expression changes begin at e16.5 but are also present at 2 months. Is the presumed effect on neural circuits a result of developmental upregulation at late embryonic stages or does the continuous overexpression in adult mice have additional influence? Are any of the Hox genes upregulated normally expressed in the brainstem, or PN specifically, at 2 months? Why perform single-cell sequencing experiments at 2 months if this is thought to be mostly a developmental effect? Similarly, the significance of the upregulated WRD5 in the pons and pontine nuclei at 2 months in Figure 3 is not clear.

Thank you for your comment.

The spatial and temporal expression pattern of Hox genes is established at early embryonic stages and then maintained throughout developmental stage in mammals. As we have shown, the de-repression of Hox genes is a long-lasting defect in Rnf220+/- mice beginning at late embryonic stages. Since the neuronal circuit is established after birth in mice, we speculated that the neuronal circuit defects from motor cortex to PN neurons were due to the long-lasting up-regulation of Hox genes in PN neurons. We could not distinguish the effect on neural circuit a result of Hox genes developmental upregulation or continuous overexpression in adult mice. An inducible knockout mouse model may help to answer this question in the future. The discussion on this point was included in the revised manuscript.

We carried out snRNA-seq analysis using pons tissues from adult mice aiming to identify the specific cell population with Hox up-regulation, which we failed to specify by in situ hybridization.

We repeated the related experiments in the original Figure 3 and some of the blot images were replaced and quantified.

(6) In Figure 3C, the levels of RNF220 in wt and het don't seem to be that different.

We repeated the experiments and changed the related image in the revised Figure 3C.

(7) Based on the single-cell experiments, and the PN nuclei focus, the rescue experiments are confusing. If the Rnf220 deletion has a sustained effect for up to 2 months, why do the injections in utero? If the focus is the PN nuclei why look at Hox9 expression and not Hox3-5 which are the only Hox genes upregulated in PN based on sc-sequencing? No rescue of behavior or any phenotype other than Hox expression by qPCR is shown and it is unclear whether upregulation of Hox9 paralogs leads to any defects in the first place. The switch to the Nes-cre driver is not explained. Also, it seems that wdr5 mRNA levels are not so relevant and protein levels should be shown instead (same for rescue experiments in P19 cells).

Thank you for your comments.

Since our data suggest that the upregulation of Hox genes expression is a long-lasting effect beginning at the late embryonic stage of E16.5, we conducted the rescue experiments by in utero injection of WDR5 inhibitor at E15.5 and examined the expression of Hox genes at E18.5. Although it is also necessary to examine whether the rescue effect by WDR5 inhibitor injection is also a long-lasting effect at adult stages, it is difficult to distinguish the embryos or pups when they were given birth. As a supplement, rescue assays with genetic ablation of Wdr5 gene were conducted and the results showed that genetic ablation of a single copy of Wdr5 allele could revere the upregulation of Hox genes by RNF220 haploinsufficiency in the hindbrains at P15.

Most of the upregulated Hox genes including both Hox9 and Hox3-5 were examined in our rescue experiments. Since this study focuses on the PN nuclei, the results of Hox3-5 genes were shown in the revised main Figure 6.

We conducted rescue experiments by deleting Wdr5 in neural tissue using Nestin-Cr_e mice because _Wdr5+/- mice is embryonic lethal. And the up-regulation of Hox genes could be also observed in the hindbrains of Rnf220fl/wt; Nestin-Cre mice. Although Rnf220fl/wt; Wdr5fl/wt; Nestin-Cre mice are viable and could survive to adult stages, developmental defects in the forebrains, including cerebral cortex and hippocampus, were observed in Rnf220fl/wt;Wdr5fl/wt;Nestin-Cre mice. Therefore, no rescue of behavior tests was conducted in this study. We believe that it is out of the scope of this study to discuss the role of WDR5 in the development of forebrains.

The potential defects due to the up-regulation of Hox9 paralogs awaits further investigations.

Wdr5 mRNA levels were firstly examined to confirm the genetic deletion or siRNA mediated knockdown of Wdr5 genes. We have carried out western blot to examine the WDR5 protein levels and the results were included in the revised Figure 3.

(8) What is the relationship between Retinoic acid and WRD5? In Figure 3E there is no change in WRD5 levels without RA treatment in Rnf KO but an increase in expression with RA treatment and Rnf KO. However, the levels of WRD5 do not seem to change with RA treatment alone. Does Rnf220 only mediate WDR5 degradation in the presence of RA? This does not seem to be the case in experiments in 293 cells in Figure 4.

Thank you for your comment.

We believe that the regulation of WDR5 and Hox expression by RNF220 is context dependent and precisely controlled in vivo, depending on the molecular and epigenetic status of the cell, which is fulfilled by RA treatment in P19 cells. In Figure 4, the experiment is based on exogenous overexpression assays, which might not fully reflect the situation in vivo.

(9) Why are the levels of Hox upregulation after RA treatment so different in Figure 5 and Figure Supplement 5?

In Figure.5C, the Hox expression levels were normalized against the control group in the presence of RA; while in Figure Supplement 5 they were normalized to the control group without RA treatment.

(10) In Figures 4B+C which lanes are input and which are IP? There is no quantitation of Figure 4D, from the blot it does look that there is a reduction in the last 2 columns as well. The band in the WT flag lane seems to have a bubble. Need to quantitate band intensities. Same for E, the effect does not seem to be completely reversed with MG132.

Thanks for pointing this out. The labels were included in the revised Figure 4B and 4C.

We repeated the experiments for Figure 4D and 4E. Some of bot images were replaced and quantified in the revised Figure 4D and 4E.

Reviewer 2:

(1) Figure 1E shows that Rnf220 knockdown alone could not induce an increase in Hox expression without RA, which indicates that Rnf220 might endogenously upregulate Retinoic acid signaling. The authors should test if RA signaling is downstream of Rnf220 by looking at differences in the expression of Retinaldehyde dehydrogenase genes (as a proxy for RA synthesis) upon Rnf220 knockdown.

Thank you for your comment and suggestion.

Two sequential reactions are required for RA synthesis from retinol, which catalyzed by alcohol dehydrogenases (ADHs)/ retinol dehydrogenase (RDH) and retinaldehyde dehydrogenase (RALDHs also known as ALDHs) respectively. When RA is no longer needed, it is catabolized by cytochrome enzymes (CYP26 enzymes) (Niederreither, et al.,2008; Kedishvili et al., 2016). Here, we test ADHs、ALDHs and CYP26 enzymes in E16.5 WT and Rnf220-/- embryos.

The results are as follows. ADH7 and ADH10 are slightly upregulated. ALDH1 and ALDH3 are upregulated and downregulated in Rnf220-/- embryos, respectively, but there is no significant change in the expression of ALDH2, which plays a key role in RA synthesis during embryonic development (Niederreither, et al.,2008). Furthermore, Cyp26a1 which responsible for RA catabolism was upregulated in Rnf220-/- embryos. Collectively, these data do not support a clear effect on RA signaling by RNF220.  

Author response image 2.

The effect of Rnf220 on RA synthesis and degradation pathways

(2) In Figure 2C-D further explanation is required to describe what criteria were used to segment the tissue into Rostral, middle, and caudal regions. Additionally, it is unclear whether the observed change in axonal projection pattern is caused due to physical deformation and rearrangement of the entire Pons tissue or due to disruption of Hox3-5 expression levels. Labeling of the tissue with DAPI or brightfield image to show the structural differences and similarities between the brain regions of WT and Rnf220 +/- will be helpful.

Thank you for your comment and suggestion.

More information on the quantification of the results shown in Figure 2C-D was included in our revised manuscript. We carried out Nissl staining assays using coronal sections of the brainstem and found that there is no significant difference in neuronal cell organization between WT and Rnf220+/- (revised Figure 2-figure supplement 2).

(3) Line 192-195. These roles of PcG and trxG complexes are inconsistent with their initial descriptions in the text - lines 73-74.

We are sorry for the mistake. We carefully revised the related descriptions to avoid such mistake. Thank you.

(4) In Figure 4D, the band in the gel seems unclear and erased. Please provide a different one. These data show that neither Rnf220 nor wdr5 directly regulates Hox gene expressions. The effect of double knockdown in the presence of RA suggests that they work together to suppress Hox gene expression via a different downstream target. This point should be addressed in the text and discussion section of the paper. example for the same data which shows a full band with lower intensity.

Thank you for your suggestion.

We repeated the experiment of Figure 4D and some of the blot images were replaced in the revised Figure 4D.

Indeed, in the presence of RA, knockdown of Rnf220 alone can upregulate the expression Hox genes (Figure 5C). Knockdown of Wdr5 could reverse the upregulation of Hox genes in RNF220 knockdown cells, suggesting that Rnf220 regulated Hox gene expression in a Wdr5 dependent manner. However, in the absence of RA, none of Rnf220 knockdown, Wdr5 knockdown or Rnf220 and Wdr5 double knockdown had a significant effect on the expression of Hox genes in P19 cells. It seems that RA signaling plays a crucial role for the regulation of RNF220 to WDR5 in P19 cells and discussion on this point was included in the revised manuscript.

(5) In Figure 4G the authors could provide some form of quantitation for changes in ubiquitination levels to make it easier for the reader. They should also describe the experimental procedures and conditions used for each of the pull-down and ubiquitination assays in greater detail in the methods section.

Thank you for your suggestion.

The quantitation and statistics for the original Figure 4G were included in the revised Figure 4. More information on the biochemical assays was included in the “Methods and Materials” section of our revised manuscript.

(6) Figure 5 shows that neither Rnf220 nor wdr5 directly regulate Hox gene expressions. The effect of double knockdown in the presence of RA suggests that they work together to suppress Hox gene expression via a different downstream target.

Thank you for your comment.

In fact, knockdown of Rnf220 alone can upregulate the expression Hox genes in the presence of RA (Figure 5C). Furthermore, knockdown of Wdr5 could reverse the upregulation of Hox genes in Rnf220 knockdown cells, which suggest that Rnf220 regulated Hox gene expression in a Wdr5 dependent manner. However, in the absence of RA, none of Rnf220 knockdown, Wdr5 knockdown or Rnf220 and Wdr5 double knockdown had a significant effect on the expression of Hox genes in P19 cells. It seems that RA signaling plays a crucial role for the regulation of RNF220 to WDR5 in P19 cells and discussion on this point was included in the revised manuscript.

(7) In Figure 6, while the reversal of changes in Hox gene expression upon concurrent Rnf220; Wdr5 inhibition highlights the importance of Wdr5 in this regulatory process, the mechanistic role of wdr5 and its functional consequences are unclear. To answer these questions, the authors need to: (i) Assay for activated and repressive epigenetic modifications upon double knockdown of Rnf220 and Wdr5 similar to that shown in Figure 3- supplement 1. This will reveal if wdr5 functions according to its intended role as part of the TrxG complex. (ii) The authors need to assay for changes in axon projection patterns in the double knockdown condition to see if Wdr5 inhibition rescues the neural circuit defects in Rnf220 +/- mice.<br />

Thank you for your suggestion.

Although it is also necessary to examine whether the rescue effect by WDR5 inhibitor injection in uetro is also a long-lasting effect for neuronal cirtuit at adult stages, it is difficult to distinguish the embryos or pups when they were given birth. Although Rnf220fl/wt;Wdr5fl/wt;Nestin-Cre mice are viable and could survive to adult stages, developmental defects in the forebrains, including cerebral cortex and hippocampus, were observed in Rnf220fl/wt;Wdr5fl/wt;Nestin-Cre mice. Therefore, no rescue effect on defects of behavior and neuronal circuit were examined in this study. Maybe, a PN nuclei specific inducible Cre mouse line could help toward this direction in the future.

We carried out ChIP-qPCR and tested activated and repressive epigenetic modifications upon double knockdown of Rnf220 and Wdr5 in P19 cell line and found Rnf220 and Wdr5 double knockdown recured Hox epigenetic modification to a certain degree (Figure 6-figure supplement 1).

References

Kedishvili, N.Y. 2016. Retinoic acid synthesis and degradation. Subcell Biochem, 81:127-161. DOI: 10.1007/978-94-024-0945-1_5, PMID: 2783050

Ma, P., Li, Y., Wang, H., Mao, B., Luo, Z.-G. 2021. Haploinsufficiency of the TDP43 ubiquitin E3 ligase RNF220 leads to ALS-like motor neuron defects in the mouse. Journal of Molecular Cell Biology, 13: 374-382. DOI: 10.1093/jmcb/mjaa072, PMID: 33386850

Ma, P., Song, N.-N., Li, Y., Zhang, Q., Zhang, L., Zhang, L., Kong, Q., Ma, L., Yang, X., Ren, B., Li, C., Zhao, X., Li, Y., Xu, Y., Gao, X., Ding, Y.-Q., Mao, B. 2019. Fine-Tuning of Shh/Gli Signaling Gradient by Non-proteolytic Ubiquitination during Neural Patterning. Cell Rep, 28: 541-553.e544. DOI: 10.1016/j.celrep.2019.06.017, PMID: 31291587

Niederreither, K., Dollé, P. 2008. Retinoic acid in development: towards an integrated view. Nat Rev Genet, 9: 541-53. DOI: 10.1038/nrg2340, PMID: 18542081

Wang, Y.-B., Song, N.-N., Zhang, L., Ma, P., Chen, J.-Y., Huang, Y., Hu, L., Mao, B., Ding, Y.-Q. 2022. Rnf220 is Implicated in the Dorsoventral Patterning of the Hindbrain Neural Tube in Mice. Front Cell Dev Biol, 10. DOI: 10.3389/fcell.2022.831365, PMID: 35399523

Author Response

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

Reviewer #1 (Public Review):

The paper from Hsu and co-workers describes a new automated method for analyzing the cell wall peptidoglycan composition of bacteria using liquid chromatography and mass spectrometry (LC/MS) combined with newly developed analysis software. The work has great potential for determining the composition of bacterial cell walls from diverse bacteria in high-throughput, allowing new connections between cell wall structure and other important biological functions like cell morphology or host-microbe interactions to be discovered. In general, I find the paper to be well written and the methodology described to be useful for the field. However, there are areas where the details of the workflow could be clarified. I also think the claims connecting cell wall structure and stiffness of the cell surface are relatively weak. The text for this topic would benefit from a more thorough discussion of the weak points of the argument and a toning down of the conclusions drawn to make them more realistic.

Thank you for your thorough and insightful review of our manuscript. We greatly appreciate your positive and constructive feedbacks on our methodology. We have carefully reviewed your comments and have responded to each point as follows:

Specific points:

1) It was unclear to me from reading the paper whether or not prior knowledge of the peptidoglycan structure of an organism is required to build the "DBuilder" database for muropeptides. Based on the text as written, I was left wondering whether bacterial samples of unknown cell wall composition could be analyzed with the methods described, or whether some preliminary characterization of the composition is needed before the high-throughput analysis can be performed. The paper would be significantly improved if this point were explicitly addressed in the main text. We apologize for not making it clearer. The prior knowledge of the peptidoglycan structure of an organism is indeed required to build the “DBuilder” database to accurately identify muropeptides; otherwise, the false discovery rate might increase. While peptidoglycan structures of certain organisms might not have been extensively studied, users still remain the flexibility to adapt the muropeptide compositions based on their study, referencing closely related species for database construction. We have addressed this aspect in the main text to ensure a clearer understanding.

“(Section HAMA platform: a High-throughput Automated Muropeptide Analysis for Identification of PGN Fragments) …(i) DBuilder... Based on their known (or putative) PGN structures, all possible combinations of GlcNAc, MurNAc and peptide were input into DBuilder to generate a comprehensive database that contains monomeric, dimeric, and trimeric muropeptides (Figure 1b)."

2) The potential connection between the structure of different cell walls from bifidobacteria and cell stiffness is pretty weak. The cells analyzed are from different strains such that there are many possible reasons for the change in physical measurements made by AFM. I think this point needs to be explicitly addressed in the main text. Given the many possible explanations for the observed measurement differences (lines 445-448, for example), the authors could remove this portion of the paper entirely. Conclusions relating cell wall composition to stiffness would be best drawn from a single strain of bacteria genetically modified to have an altered content of 3-3 crosslinks.

We understand your concern regarding the weak connection between cell wall structure and cell stiffness. We will make a clear and explicit statement in the main text to acknowledge that the cells analyzed are derived from different strains, introducing the possibility of various factors influencing the observed changes in physical measurements as determined by AFM. Furthermore, we greatly appreciate your suggestion to consider genetically modified strains to investigate the role of cross-bridge length in determining cell envelope stiffness. In this regard, we are in the process of developing a CRISPR/Cas genome editing toolbox for Bifidobacterium longum, and we plan on this avenue of investigation for future work.

Reviewer #2 (Public Review):

The authors introduce "HAMA", a new automated pipeline for architectural analysis of the bacterial cell wall. Using MS/MS fragmentation and a computational pipeline, they validate the approach using well-characterized model organisms and then apply the platform to elucidate the PG architecture of several members of the human gut microbiota. They discover differences in the length of peptide crossbridges between two species of the genus Bifidobacterium and then show that these species also differ in cell envelope stiffness, resulting in the conclusion that crossbridge length determines stiffness.

We appreciate your thoughtful review of our manuscript and your recognition of the potential significance of our work in elucidating the poorly characterized peptidoglycan (PGN) architecture of the human gut microbiota.

The pipeline is solid and revealing the poorly characterized PG architecture of the human gut microbiota is worthwhile and significant. However, it is unclear if or how their pipeline is superior to other existing techniques - PG architecture analysis is routinely done by many other labs; the only difference here seems to be that the authors chose gut microbes to interrogate.

We apologize if this could have been clearer. The HAMA platform stands apart from other pipelines by utilizing automatic analysis of LC-MS/MS data to identify muropeptides. In contrast, most of the routine PGN architecture analyses often use LC-UV/Vis or LC-MS platform, where only the automatic analyzing PGFinder software is supported. To our best knowledge, a comparable pipeline on automatically analyzing LC-MS/MS data was reported by Bern et al., which they used commercial Byonic software with an in-house FASTA database and specific glycan modifications. They achieved accurate and sensitive identification on monomer muropeptides, but struggled with cross-linked muropeptides due to the limitations of the Byonic software. We believe that our pipeline introducing the automatic and comprehensive analysis on muropeptide identification (particularly for Gram-positive bacterial peptidoglycans) would be a valuable addition to the field. To enhance clarity, we have adjusted the context as follows:

(Introduction) … Although they both demonstrated great success in identifying muropeptide monomers, the accurate identification of muropeptide multimers and other various bacterial PGN structures still remains unresolved. This is because deciphering the compositions requires MS/MS fragmentation, but it is still challenging to automatically annotate MS/MS spectra from these complex muropeptide structures."

I do not agree with their conclusions about the correlation between crossbridge length and cell envelope stiffness. These experiments are done on two different species of bacteria and their experimental setup therefore does not allow them to isolate crossbridge length as the only differential property that can influence stiffness. These two species likely also differ in other ways that could modulate stiffness, e.g. turgor pressure, overall PG architecture (not just crossbridge length), membrane properties, teichoic acid composition etc.

Regarding the conclusions drawn about the correlation between cross-bridge length and cell envelope stiffness, we understand your point and appreciate your feedback. We revisit this section of our manuscript and tone down the conclusions drawn from this aspect of the study. We also recognize the importance of considering other potential factors that could influence stiffness, as you mentioned above. In light of this, we mentioned the need for further investigations, potentially involving genetically modified strains, in the main text to isolate and accurately determine the impact of bridge length on cell envelope stiffness.

Reviewer #1 (Recommendations For The Authors):

Minor points:

1) One thing to consider would be testing the robustness of the analysis pipeline with one the well-characterized bacteria studied, but genetically modifying them to change the cell wall composition in predictable ways. Does the analysis pipeline detect the expected changes?

We appreciate the reviewer's suggestion and would like to provide a clear response. Regarding to testing the pipeline with genetically modified strains, our lab previously worked on genetically modified S. maltophilia (KJΔmrdA).1 Inactivation of mrdA turned out the increasing level of N-acetylglucosaminyl-1,6-anhydro-N-acetylmuramyl-L-alanyl-D-glutamyl-meso-diamnopimelic acid-D-alanine (GlcNAc-anhMurNAc tetrapeptide) in muropeptide profiles, which is the critical activator ligands for mutant strain ΔmrdA-mediated β-lactamase expression. In this case, our platform could provide rapid PGN analysis for verifying the expected change of muropeptide profiles (see Author response image 1). Besides, if the predictable changes involve genetically modifications on interpeptide bridges within the PGN structure, for example, the femA/B genes of S. aureus, which are encoded for the synthesis of interpeptide bridges,2 our current HAMA pipeline is capable of detecting these anticipated changes. However, if the genetically modifications involve the introduce of novel components to PGN structures, then it would need to create a dedicated database specific to the genetically modified strain.

Author response image 1.

2) Line 368: products catalyzed > products formed

The sentence has been revised.

“(Section Inferring PGN Cross-linking Types Based on Identified PGN Fragments) …Based on the muropeptide compositional analysis mentioned above, we found high abundances of M3/M3b monomer and D34 dimer in the PGNs of E. faecalis, E. faecium, L. acidophilus, B. breve, B. longum, and A. muciniphila, which may be the PGN products formed by Ldts.”

3) Lines 400-402: Is it possible the effect is related to porosity, not "hardness".

Thank you for the suggestion. The possibility of the slower hydrolysis rate of purified PGN in B. breve being related to porosity is indeed noteworthy. While this could be a potential factor, we would like to acknowledge the limited existing literature that directly addresses the relation between PGN architecture and porosity. It is plausible that current methods available for assessing cell wall porosity may have certain limitations, contributing to the scarcity of relevant studies. In light of this, we would like to propose a speculative explanation for the observed effect. It is plausible that the tighter PGN architecture resulting from shorter interpeptide bridges in B. breve could contribute to its harder texture. This speculation is grounded in the concept that a more compact PGN structure might lead to increased stiffness, aligning with our observations of higher cell stiffness in B. breve.

4) Lines 403-408: See point #2 above.

Thank you for the suggestion. We have explicitly addressed this point in the main text:

“(Section Exploring the Bridge Length-dependent Cell Envelope Stiffness in B. longum and B. breve) … Taken all together, we speculate that a tight peptidoglycan network woven by shorter interpeptide bridges or 3-3 cross-linkages could give bacteria stiffer cell walls. However, it is important to note that cell stiffness is a mechanical property that also depends on PGN thickness, overall architecture, and turgor pressure. These parameters may vary among different bacterial strains. Hence, carefully controlled, genetically engineered strains with similar characteristics will be needed to dissect the role of cross-bridge length in cell envelope stiffness.”

5) Lines 428-429: It is not clear to me how mapping the cell wall architecture provides structural information about the synthetic system. It is also not clear how antibiotic resistance can be inferred. More detail is needed here to flesh out these points.

Thank you for the suggestion. To provide further clarity on these important aspects, the context in the manuscript has been revised.

“(Discussion) …Importantly, our HAMA platform provides a powerful tool for mapping peptidoglycan architecture, giving structural information on the PGN biosynthesis system. This involves the ability to infer possible PGN cross-linkages based on the type of PGN fragments obtained from hydrolysis. For instance, the identification of 3-3 cross-linkage formed by L,D-transpeptidases (Ldts) is of particular significance. Unlike 4-3 cross-linkages, the 3-3 cross-linkage is resistant to inhibition by β-Lactam antibiotics, a class of antibiotics that commonly targets bacterial cell wall synthesis through interference with 4-3 cross-linkages. Therefore, by elucidating the specific cross-linkage types within the peptidoglycan architecture, our approach offers insights into antibiotic resistance mechanisms.”

6) Line 478: "maneuvers are proposed for" > "work is needed to generate". Also, delete "innovative". Also "in silico" > "in silico-based".

The sentence has been revised.

“(Discussion) …To achieve a more comprehensive identification of muropeptides, future work is needed to generate an expanded database, in silico-based fragmentation patterns, and improved MS/MS spectra acquisition.”

7) Line 485: "Its" > "It has potential"

The sentence has been revised.

“(Discussion) …It has potential applications in identifying activation ligands for antimicrobial resistance studies, characterizing key motifs recognized by pattern recognition receptors for host-microbiota immuno-interaction research, and mapping peptidoglycan in cell wall architecture studies.”

8) Figure 1 legend: Define Gb and Pb.

Gb and Pb are the abbreviations of glycosidic bonds and peptide bonds. We have revised the Figure legend 1 as follow:

“(Figure legend 1) …(b) DBuilder constructs a muropeptide database containing monomers, dimers, and trimers with two types of linkage: glycosidic bonds (Gb) and peptide bonds (Pb).”

9) Figure 2: It is hard to see what is going on in panel a and c with all the labels. Consider removing them and showing a zoomed inset with labels in addition to ab unlabeled full chromatogram.

We apologize for not making this clearer. The panel a and c in Figure 2 were directly generated by the Analyzer as a software screenshot of the peak annotations on chromatogram. Our intention was to present a comprehensive PGN mapping (approximately 70% of the peak area was assigned to muropeptide signals) using this platform. We understand the label density might affect clarity, so we have added the output tables of the whole muropeptide identifications as source data (Table 1–Source Data 1&2). Additionally, we have uploaded the Analyzer output files (see Additional Files), which can be better visualized in the Viewer program, and it also allows users zoom in for detailed labeling information.

10) Figure 3: It is worth pointing out what features of the MS/MS fingerprints are helping to discriminate between species.

Thank you for the suggestion. We have revised Figure 3 and the legend as follow:

“(Figure legend 3) …The sequence of each isomer was determined using in silico MS/MS fragmentation matching, with the identified sequence having the highest matching score. The key MS/MS fragments that discriminate between two isomers are labeled in bold brown.”

Author response image 2.

11) Figure 4 and 5 legend: Can you condense the long descriptions of the abbreviations - or at least only refer to them once?

Certainly, to enhance clarity and conciseness in the figure legends, we have revised Figure legend 5 as follow:

“(Figure legend 5) …(b) Heatmap displaying …. Symbols: M, monomer; D, dimer; T, trimer (numbers indicate amino acids in stem peptides). Description of symbol abbreviations as in Figure legend 4, with the addition of "Glycan-T" representing trimers linked by glycosidic bonds.”

Reviewer #2 (Recommendations For The Authors):

1. Please read the manuscript carefully for spelling errors.

We appreciate your careful review of our manuscript. We have thoroughly rechecked the entire manuscript for spelling errors and have made the necessary corrections to ensure the accuracy and quality of the text.

1. Line 46 - "multilayered" is likely only true for Gram-positive bacteria.

We thank reviewer #2 for bringing up this concern. Indeed, Gram-negative bacteria mostly possess single layer of peptidoglycan, but could be up to three layers in some part of the cell surface.3, 4 In order to reduce the confusion, we have rewritten the context as follow: “(Introduction) …PGN is a net-like polymeric structure composed of various muropeptide molecules, with their glycans linearly conjugated and short peptide chains cross-linked through transpeptidation.”

1. Methods section: It seems like pellets from a 10 mL bacterial culture were ultimately suspended in 1.5 L (750 mL water + 750 mL tris) - why such a large volume? And how were PG fragments subsequently washed (centrifugation? There is no information on this in the Methods).

We apologize for the mislabeling on the units. The accurate volume should be “1.5 mL (750 µL water + 750 µL tris)”. We have updated the correct volume in the Methods section (lines 99-100). For the washing process of purified PGN, we added 1 mL water, centrifuged at 10,000 rpm for 5 minutes, and removed supernatant. This information has added to the Methods section (lines 95-98).

1. Line 183 - why were 6 modifications chose as the cutoff? Please make rationale more clear.

We thank reviewer #2 for the comments. We set the maximum modification number of 6 in the assumption of one modification on each sugar of a trimeric muropeptide. A lower cutoff could effectively limit the identification of muropeptides with unlikely numbers of modifications, whereas a higher cutoff could allow for having multiple modifications on a muropeptide. In our hand, muropeptide modifications of E. coli are mostly N-deacetyl-MurNAc and anhydro-MurNAc, and modifications of gut microbes used here are mostly N-deacetyl-GlcNAc, anhydro-MurNAc, O-acetyl-MurNAc, loss of GlcNAc, and amidated iso-Glu. While we recommend starting data analysis with the cutoff of 6 modifications, users are free to adjust this based on their studies.

1. Line 339 - define donor vs. acceptor here (can be added in parentheses after explaining the relevant chemical reactions further above in the text)

Thank you for the suggestion. To provide greater clarity regarding the roles of the donor and acceptor substrates in the transpeptidation process, we have revised the content in the manuscript as follows:

“(Section Inferring PGN Cross-linking Types Based on Identified PGN Fragments) …In general, there are two types of PGN cross-linkage…. Transpeptidation involves two stem peptides which function as acyl donor and acceptor substrates, respectively. As the enzyme names imply, the donor substrates that Ddts and Ldts bind to are terminated as D,D-stereocenters and L,D-stereocenters, which structurally means pentapeptides and tetrapeptides. During D,D-transpeptidation, Ddts recognize D-Ala4-D-Ala5 of the donor stem (pentapeptide) and remove the terminal D-Ala5 residue, forming an intermediate. The intermediate then cross-links the NH2 group in the third position of the neighboring acceptor stem, forming a 4-3 cross-link.”

1. Line 366 following - can you calculate % crosslinks based on these numbers? What does "high abundance" of 3,3 crosslinks mean in this context? Is this the majority of PG?

Thank you for your questions. Calculating the percentage of crosslinks based on the muropeptide compositional numbers is a valid consideration. However, it's important to note that the muropeptides we analyzed were hydrolyzed by mutanolysin, and as such, deriving an accurate % crosslink value from these data might not provide a true representation of the crosslinking percentage within the PGN network. For a more precise determination of % crosslinks, methods such as solid-phase NMR on purified peptidoglycan would be required. Our research provides insights into the characterization of PGN fragments and allows us to infer potential PGN cross-linkage types and the enzymes involved based on the dominant muropeptide fragments. Regarding the phrase "high abundance" in the context, it indicates that the M3b/M4b monomer and D34 dimer muropeptides represent a significant portion of the hydrolysis products. These muropeptides are major constituents within the PGN fragments obtained from the enzymatic hydrolysis.

1. Line 375 - I am not sure PG is a meaningful diffusion barrier for drugs and signaling molecules, give that even larger proteins can apparently diffuse through the pores.

Thank you for raising this point. Peptidoglycan indeed possesses relatively wide pores that allow for the diffusion of larger molecules, including proteins.5 Research has provided a rough estimate of the porosity of the PGN meshwork, suggesting that it allows for the diffusion of proteins with a maximum molecular mass of around 50 kDa.6 Considering this, we acknowledge that PGN may not serve as a significant diffusion barrier for drugs and signaling molecules. The porosity of the PGN scaffold, which is defined by the degree of cross-linking, plays a role in influencing the transport of molecules to the cell membrane. Thus, while PGN may not serve as a strict diffusion barrier, its structural characteristics still impact bacterial cell mechanics and interactions. We have revised the manuscript to reflect this understanding:

“(Section Exploring the Bridge Length-dependent Cell Envelope Stiffness in B. longum and B. breve) …The porosity of the PGN scaffold, defined by the degree of cross-linking, influences the transport of larger molecules such as proteins. Therefore, modifications to PGN structure are anticipated to significantly affect bacterial cell mechanics and interactions.”

1. Line 400 - what does "slower hydrolysis rate" refer to, is this chemical hydrolysis or enzymatic (autolysins?). also, I am not sure hydrolysis rate of either modality allows for solid conclusions about how hard (line 402) the PG is.

Thank you for your comments. The hydrolysis rate here refers to the enzymatic hydrolysis, specifically the mutanolysin cleaving the β-N-acetylmuramyl-(1,4)-N-acetylglucosamine linkage. Indeed, there is no direct correlation between the hydrolysis rate and the hardness of PGN architecture, although the structure rigidity is a key determinant in protein digestion.7 Considering the enzymatic hydrolysis rate depending on the accessibility of the substrate to the enzyme, we proposed that the tighter PGN architecture could also lead to a slower hydrolysis rate. This speculation aligns with our observations of higher cell stiffness or more compact PGN structure of B. breve and its slower hydrolysis rate. We understand this is indirect proof, so the revised sentence now reads:

“(Section Exploring the Bridge Length-dependent Cell Envelope Stiffness in B. longum and B. breve) …Furthermore, B. breve also showed a slower enzymatic hydrolysis rate in purified PGNs, implying that the cell wall structure of B. breve is characterized by a compact PGN architecture.”

1. Line 424 - I am not convinced this pipeline can detect PG architectures that other pipelines cannot; likely, the difference between previous analyses and theirs is due to different growth conditions (3,3 crosslink formation is often modulated by environmental factors/growth stage). In the next sentence, it sounds like mutanolysin treatment is a novelty in PG analysis (which it is not).

We apologize if this could have been clearer and we have revised the paragraph to describe our study more accurately. We agree that different growth conditions could influence PGN architecture and other pipelines could manually identify the PGN architectures or automatically identify them if they are not too complex. Our original intention was to highlight the ability of the HAMA program to automatically identify unreported PGN structure. Here are the revised sentences:

“(Discussion) …We speculate that this finding may be influenced by the comprehensive mass spectrometric approaches we employed or by variations in growth conditions. Moreover, we utilized the well-established enzymatic method involving mutanolysin to cleave the β-N-acetylmuramyl-(1,4)-N-acetylglucosamine linkage, which preserves the original peptide linkage in intact PGN subunits.”

1. Line 440- 442: As outlined in more detail above: I don't think you can conclude something about the relationship between bridge length and envelope stiffness based on these data. Thank you for your valuable feedback. We agree that our data may not definitively support the direct conclusion about the relationship between bridge length and envelope stiffness in Bifidobacterium species. Instead, we will rephrase this section to accurately present the observed correlations without overgeneralizing:

“(Discussion) … Notably, our study suggested a potential correlation between the cell stiffness and the compactness of bacterial cell walls in Bifidobacterium species (Figure 5). B. longum, which predominantly harbors tetrapeptide bridges (Ser-Ala-Thr-Ala), exhibits a trend towards lower stiffness, whereas B. breve, characterized by PGN cross-linked with monopeptide bridges (Gly), demonstrates a trend towards higher stiffness. These findings suggested that it may be correlated between the increased rigidity and the more compact PGN architecture built by shorter cross-linked bridges.”

References: 1. Huang, Y.-W.; Wang, Y.; Lin, Y.; Lin, C.; Lin, Y.-T.; Hsu, C.-C.; Yang, T.-C., Impacts of Penicillin Binding Protein 2 Inactivation on β-Lactamase Expression and Muropeptide Profile in Stenotrophomonas maltophilia. mSystems 2017, 2 (4), 00077-00017.

1. Jarick, M.; Bertsche, U.; Stahl, M.; Schultz, D.; Methling, K.; Lalk, M.; Stigloher, C.; Steger, M.; Schlosser, A.; Ohlsen, K., The serine/threonine kinase Stk and the phosphatase Stp regulate cell wall synthesis in Staphylococcus aureus. Sci. Rep. 2018, 8 (1), 13693.

2. Labischinski, H.; Goodell, E. W.; Goodell, A.; Hochberg, M. L., Direct proof of a "more-than-single-layered" peptidoglycan architecture of Escherichia coli W7: a neutron small-angle scattering study. J. Bacteriol. 1991, 173 (2), 751-756.

3. Rohde, M., The Gram-Positive Bacterial Cell Wall. Microbiol. Spectr. 2019, 7 (3), gpp3-0044-2018.

4. Vollmer, W.; Höltje, J. V., The architecture of the murein (peptidoglycan) in gram-negative bacteria: vertical scaffold or horizontal layer(s)? J. Bacteriol. 2004, 186 (18), 5978-5987.

5. Vollmer, W.; Blanot, D.; De Pedro, M. A., Peptidoglycan structure and architecture. FEMS Microbiol. Rev. 2008, 32 (2), 149-167.

6. Li, Q.; Zhao, D.; Liu, H.; Zhang, M.; Jiang, S.; Xu, X.; Zhou, G.; Li, C., "Rigid" structure is a key determinant for the low digestibility of myoglobin. Food Chem.: X 2020, 7, 100094.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary

Type 1 diabetes mellitus (T1DM) progression is accelerated by oxidative stress and apoptosis. Eugenol (EUG) is a natural compound previously documented as anti-inflammatory, anti-oxidative, and anti-apoptotic. In this manuscript by Jiang et al., the authors study the effects of EUG on T1DM in MIN6 insulinoma cells and a mouse model of chemically induced T1DM. The authors show that EUG increases nuclear factor E2-related factor 2 (Nrf2) levels. This results in a reduction of pancreatic beta-cell damage, apoptosis, oxidative stress markers, and a recovery of insulin secretion. The authors highlight these effects as indicative of the therapeutic potential of EUG in managing T1DM.

Strengths

Relevant, timely, and addresses an interesting question in the field. The authors consistently observe enhanced beta cell functionality following EUG treatment, which makes the compound a promising candidate for T1DM therapy.

Weaknesses

(1) The in vivo experiments have too few biological replicates. With an n=3 (as all figure legends indicate) in complex mouse studies such as these, drawing robust conclusions becomes challenging. It is important to reproduce these results in a larger cohort, to validate the conclusions of the authors.

Thanks for your comments. In the figure legends of the first draft manuscript, n=3 means at least 3 biological replicates, and in the section of material and methods, n=30 means sample size. The number of mice in each group is 30 and there were 150 mice used in this study, and mice are assigned as follows for the whole in vivo experiments. The relative information has been added in the revised manuscript.

Author response image 1.

(2) Another big concern is the lack of quantifications and statistical analysis throughout the manuscript. Although the authors claim statistical significance in various experiments, the limited information provided makes it difficult to verify. The authors use vague and minimal descriptions of their experiments, which further reduces the reader's comprehension and the reproducibility of the experiments.

Thanks for your constructive suggestion. We conducted quantitative and statistical analysis of the entire manuscript through GraphPad Prism software again. Additionally, we have improved the experimental description in the revised manuscript.

(3) Finally, the use of Min6 cells as a model for pancreatic beta cells is a strong limitation of this study. Future studies should seek to reproduce these findings in a more translational model and use more relevant in vitro cell systems (eg. Islets).

Thanks for your professional comments. Mouse insulinoma cells (MIN6 cell line) are permanent cell lines isolated from mouse islet β cell tumors, which can reflect the functional changes of islet β cells. As mature islet cells, MIN6 cells have been widely used in the study of type 1 diabetes mellitus[1-4], so in this study, MIN6 cells were used as the cell model in vitro. In our future studies, we will try to conduct our findings using more relevant in vitro cell systems (eg. Islets).

References:

(1) WU M, CHEN W, ZHANG S, et al. Rotenone protects against β-cell apoptosis and attenuates type 1 diabetes mellitus [J]. Apoptosis, 2019, 24(11-12): 879-91.

(2) LUO C, HOU C, YANG D, et al. Urolithin C alleviates pancreatic β-cell dysfunction in type 1 diabetes by activating Nrf2 signaling [J]. Nutr Diabetes, 2023, 13(1): 24.

(3) LAKHTER A J, PRATT R E, MOORE R E, et al. Beta cell extracellular vesicle miR-21-5p cargo is increased in response to inflammatory cytokines and serves as a biomarker of type 1 diabetes [J]. Diabetologia, 2018, 61(5): 1124-34.

(4) LIN Y, SUN Z. Antiaging Gene Klotho Attenuates Pancreatic β-Cell Apoptosis in Type 1 Diabetes [J]. Diabetes, 2015, 64(12): 4298-311.

Reviewer #3 (Public Review):

Summary:

This study by Jiang et al. aims to establish the streptozotocin (STZ)-induced type 1 diabetes mellitus (T1DM) mouse model in vivo and the STZ-induced pancreatic β cell MIN6 cell model in vitro to explore the protective effects of Eugenol (EUG) on T1DM. The authors tried to elucidate the potential mechanism by which EUG inhibits the NRF2-mediated anti-oxidative stress pathway. Overall, this study is well executed with solid data, offering an intriguing report from animal studies for a potential new treatment strategy for T1DM.

Strengths:

The in vivo efficacy study is comprehensive and solid. Given that STZ-induced T1DM is a devastating and harsh model, the in vivo efficacy of this compound is really impressive.

Weaknesses:

(1) The Mechanism is linked with the anti-oxidant property of the compound, which is common for many natural compounds, such as flavonoids and polyphenol. However, rarely, this kind of compound has been successfully developed into therapeutics in clinical usage. Indeed, if that is the case, Vitamin C or Vitamin E could be used here as the positive control.

Thanks for your comments. In fact, many anti-oxidant drugs are used for the treatment of type 1 diabetes mellitus in the clinical. For example, lipoic acid was used to treat diabetic peripheral neuropathy[5]. Vitamin E could effectively eliminate free radicals, protect cell membranes, and significantly reduce the risk of cardiovascular disease in patients with SPACE or ICARE diabetes[6]. Glutathione played crucial roles in the detoxification and anti-oxidant systems of cells and has been used to treat acute poisoning and chronic liver diseases by intravenous injection[7]. Therefore, eugenol enhances the management of type 1 diabetes mellitus by modulating oxidative stress pathways and holds potential as a future therapeutic choice for clinical application. In the future relevant studies, we will try to use Vitamin C or Vitamin E as the positive control.

References:

(5) ZIEGLER D, PAPANAS N, SCHNELL O, et al. Current concepts in the management of diabetic polyneuropathy [J]. J Diabetes Investig, 2021, 12(4): 464-75.

(6) VARDI M, LEVY N S, LEVY A P. Vitamin E in the prevention of cardiovascular disease: the importance of proper patient selection [J]. J Lipid Res, 2013, 54(9): 2307-14.

(7) HONDA Y, KESSOKU T, SUMIDA Y, et al. Efficacy of glutathione for the treatment of nonalcoholic fatty liver disease: an open-label, single-arm, multicenter, pilot study [J]. BMC Gastroenterol, 2017, 17(1): 96.

Reviewer #1 (Recommendations For The Authors):

• For each of the figure panels the authors should indicate the exact number of biological replicates (how many mice or how many independent in vitro experiments). For IF panels, the number of mice, the number of histology slides per mouse, number of fields analyzed should be indicated.

Thanks for your constructive suggestion. These details had been added in the revised manuscript.

• The methods state n=30 and Figure 1 states n=3. N=3 is too little for such a complex in vivo study and would severely reduce the reliability of the in vivo experiments.

Thanks for your suggestion. In the figure legends of the first draft manuscript, n=3 means at least 3 biological replicates, and in the section of material and methods, n=30 means sample size. The number of mice in each group is 30 and there were 150 mice used in this study, and mice are assigned as follows for the whole in vivo experiments. The in vivo experimental data of Figure 1 were supplemented in the revised manuscript.

• Individual data points should be included in each of the graphs from this manuscript.

Thanks for your reminder. The revised manuscript have shown the individual data points in each of the graphs.

• The quantifications and statistics in the manuscript need improvement. Several experiments are missing quantifications and/or statistical tests (e.g. Figure 1J). Other experiments show a quantification but without any explanation of replicates (e.g. Figures 2B and 2G). None of the experiments show individual data points, and as in the previous comment, these should be included.

Thanks for your comments. In the revised manuscript, statistics and repetitions of experimental data have been supplemented, and individual data points were shown in each graph.

• What is the reason for intragastric administration? The previous studies on which the dosages were based used oral administration (gavage). (Discussed in methods 4.2).

Thanks for your professional comments. The intervention treatment of T1DM mice is conducted through two methods: oral administration[8] and oral gavage[9-11]. Due to limited experimental conditions, it is not feasible to feed a single mouse in a single cage, which makes it challenging to precisely control the actual daily intervention dose for each mouse when using oral administration. To ensure that each mouse receives an intervention dose according to its weight and expected dosage, we employ a method of gavage. In addition, oral gavage is more convenient and easier to operate than oral administration. Therefore, in vivo experiment of this study used eugenol gavage intervention as a treatment method. These details had been added in the revised manuscript.

References:

(8) ZHAO H, WU H, DUAN M, et al. Cinnamaldehyde Improves Metabolic Functions in Streptozotocin-Induced Diabetic Mice by Regulating Gut Microbiota [J]. Drug Des Devel Ther, 2021, 15: 2339-55.

(9) XING D, ZHOU Q, WANG Y, et al. Effects of Tauroursodeoxycholic Acid and 4-Phenylbutyric Acid on Selenium Distribution in Mice Model with Type 1 Diabetes [J]. Biol Trace Elem Res, 2023, 201(3): 1205-13.

(10) SUDIRMAN S, LAI C S, YAN Y L, et al. Histological evidence of chitosan-encapsulated curcumin suppresses heart and kidney damages on streptozotocin-induced type-1 diabetes in mice model [J]. Sci Rep, 2019, 9(1): 15233.

(11) YAO H, SHI H, JIANG C, et al. L-Fucose promotes enteric nervous system regeneration in type 1 diabetic mice by inhibiting SMAD2 signaling pathway in enteric neural precursor cells [J]. Cell Commun Signal, 2023, 21(1): 273.

• Urine volume cannot be specified per mouse (methods 4.4) unless the mice were single-housed or if the different groups were not mixed, both are not ideal study set-ups. Please clarify in the methods section.

Thanks for your constructive suggestion. After successful modeling of T1DM mice, the successful modeling mice were grouped based on method 4.2 as follows Control, T1DM, T1DM + EUG (5 mg/kg/day), T1DM + EUG (10 mg/kg/day), and T1DM + EUG (20 mg/kg/day). To ensure consistency among groups, each group consisted of 5 mice and had equal amounts of diet (100 g), drinking water (250 mL), and environmental conditions for feeding. The urine-soaked area of mice in each group was recorded to quantify the urine volume. The conditions are the same for each group. The description of Method 4.4 has been improved in the revised manuscript.

• OGTT (Figure 1H) of week 2 is missing. This is an important control time point, as it would show the effect of STZ before EUG treatment.

Thanks for your careful review. OGTT (Figure 1H) of week 2 has been added in the revised manuscript.

• In Figure 1J, the control group does not follow the expected ITT trajectory. If possible, add the 120-minute time point to see if the blood glucose levels return to baseline in the control group. The graph shows increased basal glucose levels in the experimental groups, but no differences in insulin tolerance. It also misses the AUC calculations. It is probably not significantly different, which should be noted in the text.

Thanks for your suggestion. T1DM primarily manifests as pancreatic β cell damage and the absolute reduction of insulin secretion, resulting in the disorder of glucose metabolism in vivo. The oral glucose tolerance test (OGTT) is a series of plasma glucose concentrations measured within 2 h after oral gavage of a certain amount of glucose. It is a standard method to evaluate an individual's blood glucose regulation ability and to understand the function of islet β cells. Insulin resistance means reducing the efficiency of insulin to promote glucose uptake and utilization for various reasons, and the body's compensatory secretion of excessive insulin leads to hyperinsulinemia to maintain the stability of blood glucose. The insulin resistance test (ITT) is commonly employed to detect insulin resistance in T2DM. However, it was found that the ITT experiment had little correlation with T1DM. Therefore, the ITT experiment of Figure 1J and related description have been removed from the revised manuscript.

• The staining and FACS data on the effects of STZ+EUG+/- ML385 are not convincing (Figure 6 and Figure 7) and do not seem to align with the bar graphs and the conclusions in the text. It would be good to include immunofluorescent staining for insulin to further validate the effects of STZ+EUG+/- ML385 on insulin expression.

Thanks for your comments.

(1) In the revised manuscript, between the statistical results and the pictures, so we re-conducted the statistics of the immunofluorescence results of NRF2 and HO-1, as follows：

(1) NRF2 immunofluorescence staining:

Author response image 2.

Group 1

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Group 2

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Group 3

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Group 4

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Group 5

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NRF2 immunofluorescence staining statistics:

(2) HO-1 immunofluorescence staining:

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Group 1

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Group 2

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Group 3

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Group 4

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Group 5

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HO-1 immunofluorescence staining statistics:

(2) The meanings represented by each quadrant of cell flow analysis are as follows: Q1 represents a group of necrotic cells, characterized by positive PI staining and negative Anenexin V staining; Q2 represents late apoptotic cells, with both PI and Anenexin V staining negative; Q3 represents early apoptotic cells, with both PI and Anenexin V staining positive; Q4 represents living cells, characterized by positive Anenexin V staining and negative PI staining. In the experiment, the number of apoptotic cells were calculated as the sum of late apoptotic cells in Q2 and early apoptotic cells in Q3. As shown in Figure 9F-G, these results were consistent with those observed in Figure 6G, 6J and Figure 7D-F.

(3) MIN6 cells, as mouse islet β cell line, has the function of secreting insulin. The intervention of STZ was an absolute decrease in the number of islet β cells, so the result of insulin immunofluorescence staining was only a decrease in the number of MIN6 cells in each cell group. In addition, the detection of insulin protein expression level is always through ELISA method to assess the secretion of insulin protein in the cell supernatant. Figure 6E is the ELISA results of insulin protein secretion in the cell supernatant.

• The experimental design for the in vitro experiments was unclear from the text. Consider including a schematic to show when cells were treated with STZ, EUG, and ML385.

Thanks for your suggestion. The experimental design for the in vitro experiments of this study has been added in Figure 6A of the revised manuscript.

• As stated in the Discussion, the use of the insulinoma line Min6 as a model instead of primary pancreatic beta cells is a clear limitation of the study. The mechanistic data would be stronger if validated on a more relevant system (eg. untransformed Islets).

Thanks for your comments. Mouse insulinoma cells (MIN6 cell line) are permanent cell lines isolated from mouse islet β cell tumors, which can reflect the functional changes of islet β cells. As mature islet cells, MIN6 cells have been widely utilized as an in vitro cellular model for diabetes research to investigate the functionality of β cells within pancreatic islets[1, 2, 12]. So in this study, MIN6 cells were used as the cell model in vitro. In our future studies, we will try to conduct our findings using more relevant in vitro cell systems (eg. Islets).

References:

(1) WU M, CHEN W, ZHANG S, et al. Rotenone protects against β-cell apoptosis and attenuates type 1 diabetes mellitus [J]. Apoptosis, 2019, 24(11-12): 879-91.

(2) LUO C, HOU C, YANG D, et al. Urolithin C alleviates pancreatic β-cell dysfunction in type 1 diabetes by activating Nrf2 signaling [J]. Nutr Diabetes, 2023, 13(1): 24.

(12) CHEN H, LOU Y, LIN S, et al. Formononetin, a bioactive isoflavonoid constituent from Astragalus membranaceus (Fisch.) Bunge, ameliorates type 1 diabetes mellitus via activation of Keap1/Nrf2 signaling pathway: An integrated study supported by network pharmacology and experimental validation [J]. J Ethnopharmacol, 2024, 322: 117576.

• The use of small molecule inhibitors such as ML385 can have unspecific effects. Genetic manipulation or the use of siRNAs to inhibit the NRF2 pathway would have been preferable for the in vitro experiments.

Thanks for your constructive suggestion. ML385 is a commonly used and stable inhibitor of the NRF2 and has been used in a variety of disease studies[13-15]. The MIN6 cells utilized in this study were cultured under challenging conditions and exhibited a sluggish growth rate. Owing to the cytotoxicity associated with siRNAs transfection reagents, a significant proportion of MIN6 cells succumbed following transfection. Consequently, small molecule inhibitors ML385 were employed in this investigation. In our future studies, we will try to conduct our findings using siRNAs.

References:

(13) DANG R, WANG M, LI X, et al. Edaravone ameliorates depressive and anxiety-like behaviors via Sirt1/Nrf2/HO-1/Gpx4 pathway [J]. J Neuroinflammation, 2022, 19(1): 41.

(14) WANG Z, YAO M, JIANG L, et al. Dexmedetomidine attenuates myocardial ischemia/reperfusion-induced ferroptosis via AMPK/GSK-3β/Nrf2 axis [J]. Biomed Pharmacother, 2022, 154: 113572.

(15) LI J, DENG S H, LI J, et al. Obacunone alleviates ferroptosis during lipopolysaccharide-induced acute lung injury by upregulating Nrf2-dependent antioxidant responses [J]. Cell Mol Biol Lett, 2022, 27(1): 29.

• The study proposes a mechanism in which EUG-induced disruption of KEAP1 and NRF2 interaction leads to NRF2 translocation to the nucleus and upregulation of proteins required to prevent oxidative stress. In Figure 6H it is unclear whether the nuclear NRF2 increases. Please add quantifications of the immunostainings.

Thanks for your reminder. Figure 6J shows the quantifications of the immunostainings of NRF2 in the revised manuscript.

• Some of the figure legends lack important information. In Figure 5A, 6E for instance, what is the protein expression normalized to?

Thanks for your constructive suggestion. Protein normalization refers to the standardization of proteins from different sources and with different properties, so as to facilitate the comparison of protein content and expression in different samples. In WB experiment, protein expression normalization is one of the essential steps. Western blot of nuclear protein generally cannot be performed using β-Actin as an internal reference. Lamin B was chosen because β-Actin is an intrinsic parameter not found in the nucleus. N-NRF2, as a nuclear protein, requires Lamin B as a reference for protein normalization. The lack important information of WB in Figure have been supplemented in figure legends of the revised manuscript.

• Please acknowledge previous literature on the effects of EUG/clove oil in diabetes models. The meta-analytical review by Carvalho et al. (DOI: 10.1016/j.phrs.2020.105315) should be cited and discussed.

Thanks for your suggestion. It has been cited and discussed in the revised manuscripts.

• Consider revising the text for grammar, language mistakes, and readability. The text is not always precise (e.g. in the explanation of gamma-H2AX in the results), does not explain terminology (e.g. the oxidative stress markers - line 204+205), or simplifies conclusions (e.g. "improved islet function" based on glucose tolerance test", line 129).

Thanks for your comments. The above problem has been solved in the revised manuscripts. In addition, we had send our manuscript to the professional English language editing company to improve our paper, and the editorial certificate had been submitted as a supplement document.

• In the current format, some figures are out of focus. Please make sure to upload a high-quality version for publication.

Thanks for your suggestion. A high quality version figures has been uploaded. Perhaps due to the excessive content of the file after upload, the file is compressed, and the figures is not focused. So, all figures in this study have been uploaded separately for download in the review system.

Reviewer #2 (Recommendations For The Authors):

Below are specific points of criticism on the experiments presented.

(1a) There is no comparison among eugenol treatments with regards to fasting weight, blood glucose, water intake, food intake, and, crucially, OGTT. All three treatments appear to show very similar effects but has this been statistically assessed? Shown statistical significance of ketonuria between no and high eugenol treatments seems exaggerated.

Thanks for your comments. EUG intervention has a dose-dependent effect on T1DM. According to Figure 1B-I, 20 mg/kg EUG has the best effect. Fasting body weight, blood glucose, water intake, food intake, and OGTT were statistically assessed in Figure 1 of the revised manuscript. In addition, we performed statistical analyse of ketonuria between no and high eugenol treatments again in the revised manuscript. In the revised manuscript, we have also made objective revisions to the expression of eugenol's efficacy.

(b) ITT is not used to detect T1DM (line 126).

Thanks for your suggestion. T1DM primarily manifests as pancreatic β cell damage and the absolute reduction of insulin secretion, resulting in the disorder of glucose metabolism in vivo. The oral glucose tolerance test (OGTT) is a series of plasma glucose concentrations measured within 2 h after oral gavage of a certain amount of glucose. It is a standard method to evaluate an individual's blood glucose regulation ability and to understand the function of islet β cells. Insulin resistance means reducing the efficiency of insulin to promote glucose uptake and utilization for various reasons, and the body's compensatory secretion of excessive insulin leads to hyperinsulinemia to maintain the stability of blood glucose. The insulin resistance test (ITT) is commonly employed to detect insulin resistance in T2DM. However, it was found that the ITT experiment had little correlation with T1DM. Therefore, the ITT experiment and related description have been removed in the revised manuscript.

(2) Here it is hard to reconcile the gradual increase of Ins protein levels in (STZ) and (STZ + increasing eugenol) samples with(a) results in 1 suggesting that the dose of eugenol does not significantly affect the outcome and(b) Ins expression, which is essentially undetectable in both STZ and STZ+EUG mice. A likely explanation is that EUG just postpones beta cell death. I assume that these analyses were done in week 10 but it is not stated.

Thanks for your professional suggestion. Perhaps because the file is compressed, the gray value of WB strip is not obvious, so the expression of INS is not seen clearly. In fact, the intervention of STZ resulted in a significant decrease in INS expression compared with the Control group, which could be alleviated by the treatment of EUG. However, due to the large difference in INS between the STZ group, EUG treatment, and the Control group, the gray values of INS in the STZ group and the STZ + EUG group were not clear. As mentioned in the method 4.12-4.13, our WB and PCR samples were from 10 week mice.

(3) The γH2Ax stainings provided are weak and do not fully correspond to the quantitation - the 5 mg/Kg EUG treatment appears less severe than the 10 mg/Kg. In contrast, changes in the PCD pathway are convincingly demonstrated.

Thanks for your reminder. γH2AX immunohistochemical staining is required to be located in the islets. It measured the number of β cells stained with brown, not the brown area. The ZOOM image of γH2AX staining showed that the EUG improvement effect of 10 mg/kg was better than that of 5 mg/kg. γH2AX, as a marker of DNA damage, exhibits nuclear localization and is absent in the cytoplasmic compartment. Therefore, in Figure 4C-D, we quantified the proportion of cells exhibiting brown staining. In Figure 4C, black arrows were employed to highlight the presence of brown-stained islet β cells.

(4) Is there a reason for looking at mRNA levels of Ho-1 but not KEAP1 or NQO-1 ? What is the expression of Nrf2 itself at the RNA level? Please give in the text what the abbreviations MDA, SOD, CAT GSH-Px stand for. Are these protein levels or activity assays? Units in the y-axis of graphs?

Thanks for your constructive suggestion.The required KEAP1 and NQO-1 primers have been synthesized, and the relevant data have been supplemented in the revised manuscript. The expression of Nrf2 itself at the RNA level is T-NRF2 (Total NRF2). The MDA, SOD, CAT and GSH-Px abbreviations stand for Malondialdehyde, Superoxide dismutase, Catalase, Glutathione peroxidase, and the relevant information, which have been supplemented in the revised manuscript. These are activity assays of serum, and units in the y-axis of graphs have been added in the revised manuscripts.

(5) The Ins levels in the culture medium of STZ + ML treated cells are much lower than the levels in STZ treated cells (6D). This is not consistent with the results of Ins cell content or Ins expression as stated (6B and D).

Thanks for your careful review. The experimental samples in Figure 6C in the revised manuscript represent the proteins extracted from cells of each group, while the experimental samples in Figure 6E represent the supernatant of cells from each group. ML385 is an inhibitor of NRF2, which effectively suppresses the NRF2 signaling pathway and aggravates MIN6 cell damage, resulting in lower INS expression observed in both the STZ+ML385 group depicted in Figures 6C and 6E compared to that in the STZ group. Although the sample sources of the two groups differ and there are slight variations in the trend, it can be observed that the overall trend of the STZ+ML385 group is comparatively lower than that of the STZ group.

Author Response

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

Reviewer #1 (Public Review):

[...] Weaknesses

Showing that A-2 and especially A-3 are outliers in the PCA analysis is useful, but it may be hiding other interesting signals in the data. The other strains are remarkably colinear on these plots, hinting that if the outliers were removed, one main component would emerge along which they are situated. It also seems possible that this additional analysis step would allow the second dimension to better differentiate them in a way that is interesting with respect to their mutator status or mutations in key metabolic or regulatory genes.

We thank the reviewer for their positive comments and their constructive feedback on the manuscript. Following reviewer’s recommendation, we performed the PCA analysis on metabolism data after removing A-2 and A-3 data. We have detailed those results below. Consistent with a similar analysis performed on RNA-seq datasets in our previous publication, we find that removing these outliers has only a modest effect on separating mutators from non-mutators. We find that, while the new PC2 separates most mutators from the non-mutators, the separation is rather weak. Moreover, we do not see a similar distinction when looking at metabolic data in the Stationary phase. In the interest of improving the readability of the manuscript, we recommend not including these analysis in the final manuscript. We have presented the data for the reviewer’s benefit in Author response image 1, 2 and 3.

Author response image 1.

Author response image 2.

Author response image 3.

There is a missed opportunity to connect some key results to what is known about LTEE mutations that reduce the activity of pykF (pyruvate kinase I). This gene is mutated in all 12 LTEE populations, and often these mutations are frameshifts or transposon insertions that should completely knock out its activity. At first glance, inactivating an enzyme for a step in glycolysis does not make sense when the nutrient source in the growth medium is glucose, even though PykF is only one of two isozymes E. coli encodes for this reaction. There has been speculation that inactivating pykF increases the concentration of phosphoenolpyruvate (PEP) in cells and that this can lead to increased rates of glucose import because PEP is used by the phosphotransferase system of E. coli to import glucose (see https://doi.org/10.1002/bies.20629). The current study has confirmed the higher PEP levels, which is consistent with this model.

We thank the reviewer for pointing out this missed opportunity. We have expanded the discussion around the role of pykF mutations and the elevated concentrations of PEP observed in our data in section 3.4.

In the introduction, the papers cited to show the importance of changes in metabolism for adaptation do not seem to fit the focus of this study very well. They stress production of toxins and secondary metabolites, which do not seem to be mechanisms that are at work in the LTEE. I can think of two areas of background that would be more relevant: (1) studies of how bacterial metabolism evolves in adaptive laboratory evolution (ALE) experiments to optimize metabolic fluxes toward biomass production (for example, https://doi.org/10.1038/nature01149), and (2) discussions of how cross-feeding, metabolic niche specialization, and metabolic interdependence evolve in microbial communities, including in other evolution experiments (for example, https://doi.org/10.1073/pnas.0708504105 and https://doi.org/10.1128/mBio.00036-12).

We thank the reviewer for pointing out missed citations in our introduction. We agree that these papers are relevant to the topic and have added their citations. Additionally, following the suggestion of another reviewer, we have reorganized the introduction so that the concept of the role of metabolism in evolution is presented first and the LTEE second.

Reviewer #2 (Public Review):

[...] Overall, this is a significant and well-executed research study. It offers new insights into the complex relationship between genetic changes and observable traits in evolving populations and utilizes metabolomics in the LTEE, a novel approach in combination with RNA-seq and mutation datasets.

However, the paper's overall clarity is lacking. It is spread too thin and covers many topics without a clear focus. I strongly recommend a substantial rewrite of the manuscript, emphasizing structure and readability. The science is well executed, but the current writing does not do it justice.

We thank the reviewer for their positive comments and their constructive feedback on the lack of clarity in writing. Following the reviewer’s suggestions, we have rewritten parts of the manuscript and reorganizd a few sections to improve readability. We hope the revised manuscript is significantly improved.

Recommendations for the authors

Reviewer #1 (Recommendations For The Authors):

1) Title and Abstract: Add the study organism to the abstract, and probably also the title. Currently, E. coli is not mentioned in either! I'm also not sure that the LTEE is a sufficiently well-known acronym to abbreviate this in the title.

We have revised the title of the manuscript and now spell out LTEE and included E. coli in the title and the abstract.

2) Abstract: I would switch the usage of metabolome to metabolism in a few more places. For example, "changes in its metabolism", "networked and convoluted nature of metabolism". The metabolome, the concentrations of all metabolites, is what is being measured, but I think of this as a phenotypic readout of how metabolism evolving.

We have changed “metabolome” to “metabolism” in cases where we refer to what is evolving and use “metabolome” when we refer to what is being measured.

3) Line 16: Technically, the 12 LTEE populations were not initially identical. The Ara- differed from the Ara+ ancestors by one intentional mutation and one unintentional mutation that was not discovered until whole genomes were sequenced. I would rephrase this to "where 12 replicate populations of E. coli are propagated" or something similar so that it can be correct without needing to describe this unnecessary detail.

The line has been rephrased as suggested.

4) General Note: The text refers to populations as Ara-3 but the figures use A-3. I'd suggest going with A-3 and similar throughout for consistency.

Instances of Ara have been changed to A+/-, and a sentence specifying as such has been added to the intro to make mention of this.

5) Lines 43-44, 97-98. My understanding is that both S and L ecotypes in A-2 can use both glucose and acetate, but that the differentiation is related to their specialization that leads to each one being better on one or the other nutrient. The descriptions make it sound like each grows at a different time. Also, by definition, cells are not growing during "stationary phase". The change from glucose utilization (and acetate secretion) to acetate utilization during one cycle of growth is better described as a diauxic shift.

We have reworded this part to remove mention of “growth” during stationary phase and changed the wording such that it no longer sounds like they grow at different times.

6) Line 54: The statement "provide the ability to test hypotheses from previous data" is vague. Either provide an example or delete.

We have removed this sentence as suggested.

7) Lines 71-72: The terms "interphase" and "intraphase" sound too much like parts of the cell cycle. I'd suggest describing the comparisons as between and within growth phases.

The use of intra and interphase have been changed as suggested.

8) Line 79: The citrate is presumably still a chelating agent, so change phrasing to "Citrate is present in the medium because it was originally added as a chelating agent" or something similar.

This sentence has been rewritten as suggested.

9) Line 83: Write out "mutation accumulations" so it is easier to understand as "the number of mutations that have accumulated".

The phrase has been changed as suggested.

10) Line 116: It's unclear whether the abundances of metabolites are "strategies of survival" in stationary phase. An equally valid explanation is that there is less selection on the metabolome to have a specific composition during stationary phase to have high fitness.

We have added a line about the possibility for alternative hypotheses.

11) Figure 1: There seems to be some information missing from the legend. What are R06 and R07 in Panels A and B? Is panel D exponential phase and panel E stationary phase?

This information was inadvertently missing from the caption and has been added.

12) Figures 2 and 3: Gene names should be in italics. To me, the gray for deleted genes is hard to tell apart from the blue/red. Perhaps you could put a little X in these boxes instead? I think that having a little triangle pointing from each gene or metabolite name its corresponding abundance panel would help the reader track which information goes with which features. In Fig. 3 the placement of L-aspartate is a bit awkward. I'd suggest moving it down so the dashed line does not have to go through the abundance panel.

These figures have been edited to include small triangles that link a gene or metabolite and its heatmap. Additionally, an X has been added where genes have suffered inactivating mutations and the placement of some elements has been moved to improve overall clarity.

13) Lines 183-185: It would be easier to see and judge the consistency of these argR related relationships if a correlation graph of some kind was shown, probably as a supplemental figure. This plot could, for example, have genes/metabolites across the x-axis and fold-change on the y-axis with lines connecting points corresponding to each of the twelve populations across these categories (like Fig S8 but with lines added). Alternatively, it could be a heat map with the populations across one axis and the genes/metabolites across the other axis (like Fig S3).

We have added a supplementary figure consisting of heatmaps showing the consistency of these changes within an evolved line. It is now figure S9.

14) Line 195: I think adding a sentence elaborating on what exactly mutation accumulation means in this context would be helpful to readers.

We have attempted to clarify the meaning of this by specifically stating that it is due to the accumulation of deleterious mutations.

15) Line 293: Is standard LTEE medium DM25? These omics experiments with the LTEE sometimes use similar media with different glucose concentrations, and this is a very important detail to precisely specify.

We reference “standard” LTEE medium in the methods section and have additionally specified the amount of sugar to make it clear that we are not supplementing the media with additional sugar.

16) Figure S8B. Is "cystine" used instead of "cysteine" on purpose here since the compound is oxidized in the metabolomics treatment?

The use of cystine is intentional, we detect the oxidized compound.

Reviewer #2 (Recommendations For The Authors):

Title:

The abbreviation "LTEE" should not be in the title. Most readers will not recognize what it means. Instead, either the full name of the experiment, "Long-Term Evolution Experiment with E. coli," should be used, or the title should be rephrased to "Linking genotypic and phenotypic changes during a long-term evolution experiment using metabolomics."

We have spelled out LTEE and included E. coli in the title.

Abstract:

Sentence 1: Consider softening the statement: "Do changes in an organism's environment, genome, or gene expression patterns often lead to changes in its metabolome?"

We have rephrased this sentence to “Changes in an organism's environment, genome, or gene expression patterns can lead to changes in its metabolism”.

Sentence 4: Use a hyphen for "Long-Term."

This addition has been made.

Sentence 4: Replace "transduce" with a more appropriate term: "...how the effects of mutations can be distributed through a cellular network to eventually affect metabolism and fitness."

We have rewritten this sentence as “to understand how mutations can eventually affect metabolism and perhaps fitness”.

Sentence 5: Clarify the use of "both" to refer to the ancestor of the LTEE and its descendant populations as two classes.

We have reworded this sentence so it’s clear that the ancestors and evolved lines are two separate classes “We used mass-spectrometry to broadly survey the metabolomes of the ancestral strains and all 12 evolved lines…”.

Sentence 6: Reverse the order for better emphasis: "Our work provides a better understanding of how mutations might affect fitness through the metabolome in the LTEE, and thus provides a major step in developing a complete genotype-phenotype map for this experimental system."

We have rearranged this sentence per the reviewers suggestion.

Introduction:

Revise the introduction for clarity, readability, and logical narrative progression. Start with the second paragraph to set up the basic scientific principles being studied and then transition to describing the LTEE as a model system to examine those principles.

The introduction has been rearranged and reworded in parts to increase clarity.

Sentence 1: Revise for clarity: "The Long-Term Evolution Experiment (LTEE) has studied 12 initially identical populations of Escherichia coli as they have evolved in a carbon-limited, minimal glucose medium under a daily serial transfer regime."

Sentence 2: Suggestion: "Begun in 1988, the LTEE populations have evolved for more than 75,000 generations, making it the longest-running experiment of its kind."

Paragraph 2, sentence 2: Italicize "Drosophila."

Paragraph 3, sentence 2: Make an important distinction: "Ara-3 is unique in that it evolved the ability to grow aerobically on citrate."

Paragraph 3, sentence 4: Introduce the IS-mediated loss of the rbs operon in the LTEE as if it has not been described elsewhere.

These suggestions have been incorporated into the manuscript.

Results:

Section 3.1: The use of samples from hours 2 and 24 to represent exponential and stationary phase may present some issues. For instance, capturing Ara-3 during its exponential growth on glucose, but not citrate, at hour 2. Furthermore, except for Ara-3, the LTEE populations reach stationary phase after approximately 4 hours, and there could be significant differences between early, mid, and late stationary phase. This possibility should be acknowledged, and future follow-up work should consider exploring these differences.

We have added sentences in the first paragraph of the results section to include these details. We have also added a short paragraph to the conclusions suggesting additional studies of stationary phase, citing work on evolution of E. coli during long term stationary phase.

Paragraph 3: While Turner et al. 2017 is an essential reference regarding resource use differences between Ara-3 and other LTEE populations, it would be more suitable to reference Blount et al. 2012 for the mutations that enabled access to citrate. Also, it is important to note that the difference lies in the ability to grow aerobically on citrate, rather than the ability to metabolize it.

This citation has been added.

Paragraph 4: As mentioned elsewhere, most LTEE populations exhibit balanced polymorphisms. Therefore, it is more appropriate to state that Ara-2 is the best-understood example of long-term diversity. It is likely that there are important metabolic differences between co-existing lineages in other LTEE populations.

We now refer to Ara-2 as being the best-understood example of long term diversity..

Paragraph 5: The first sentence of this paragraph should likely end with "levels."

The word “levels” was added to the end of this sentence.

Figure 3: It is preferable to refer to the "Superpathway of arginine and polyamine biosynthesis," citing EcoCyc as a reference, rather than a descriptor.

This has been changed to a reference.

Section 3.3, Paragraph 3: While higher intracellular amino acid abundances may facilitate higher translation rates and faster growth, the higher abundances themselves do not evaluate the hypothesis. To evaluate the hypothesis, it is necessary to demonstrate that higher abundances are associated with higher translation or growth rates. Therefore, the final sentence of this paragraph is not meaningful.

We have reworded this sentence to say that it’s not possible to tell what the additional amino acids are being used for given only this data and that additional experiments are needed to confirm this hypothesis.

Section 3.4: The first paragraph of this section misstates how evolution works. The low level of glucose in the LTEE does not drive innovation; instead, innovation occurs at random through the introduction of variation by mutation. Although the existence of the citrate resource acts as a reward that selects for variation that provides access to it, it is essential to remember that evolution is blind to such a reward. Moreover, regarding the evolution of the Cit+ trait, it is incorrect to assert that low glucose contributed to its evolution. As shown by Quandt et al. (2015), it seems probable that Cit+ evolution was potentiated by adaptation to specialization on acetate, which is produced by overflow metabolism resulting from rapid growth on glucose. This rapid growth only occurs when glucose is relatively abundant. The level of glucose seems low to us because it is low relative to traditional levels in bacteriological media, but not to the bacteria.

We agree that this is a semantical, but important distinction. We have reworded this part as to not suggest that evolution has any forward thinking properties and is indeed blind to any rewards that might occur as the result of adaptation.

In general, all instances of "utilize" and its cognates should be replaced with "use" and its cognates.

Instances of “utilize” have been changed to use and its cognates.

There is some uncertainty about the expectation of ramping up the TCA cycle in the LTEE. Overflow metabolism and acetate production appear to be prevalent in the LTEE, suggesting that many lineages only partially oxidize carbon derived from glucose, thereby bypassing the TCA cycle. While it is possible that this interpretation is incorrect, it would be helpful to see it addressed in the manuscript.

We agree that this is a plausible hypothesis, we have added a paragraph at the end of this section that discusses the implications of overflow metabolism as an alternative hypothesis.

Author Response

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

Reviewer #1 (Public Review):

Several concerns are raised from the current study.

1) Previous studies showed that iTregs generated in vitro from culturing naïve T cells with TGF-b are intrinsically unstable and prone to losing Foxp3 expression due to lack of DNA demethylation in the enhancer region of the Foxp3 locus (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). It is known that removing TGF-b from the culture media leads to rapid loss of Foxp3 expression. In the current study, TGF-b was not added to the media during iTreg restimulation, therefore, the primary cause for iTreg instability should be the lack of the positive signal provided by TGF-b. NFAT signal is secondary at best in this culturing condition.

In restimulation, void of TGFb is necessary to cause iTreg instability. Otherwise, the setup is similar to the iTreg-inducing environment (Author response image 1). On the other hand, the ultimate goal of this study is to provide a scenario that bears some resemblance of clinical treatment, where TGFb may not be available. The reviewer is correct in stating that TGFb is essential for iTreg stability, we are studying the role played by NFAT in iTreg instability in vitro, and possibly in potential clinical use of iTreg .

Author response image 1.

Restimulation with TGFb will persist iTreg inducing environment, resulting in less pronounced instability. Sorted Foxp3-GFP+ iTregs were rested for 1d, and then rested or restimulated in the presence of TGF-β for 2 d. Percentages of Foxp3+ cells were analyzed by intracellular staining of Foxp3 after 2 d.

2) It is not clear whether the NFAT pathway is unique in accelerating the loss of Foxp3 expression upon iTreg restimulation. It is also possible that enhancing T cell activation in general could promote iTreg instability. The authors could explore blocking T cell activation by inhibiting other critical pathways, such as NF-kb and c-Jun/c-Fos, to see if a similar effect could be achieved compared to CsA treatment.

We thank the reviewer for this suggestion. We performed this experiment according to see extent of the role that NFAT plays, or whether other major pathways are involved. As Author response image 2 shows, solely inhibiting NFAT effectively rescued the instability of iTreg. The inhibition of NFkB (BAY 11-7082), c-Jun (SP600125), or a c-Jun/c-Fos complex (T5224) had no discernable effect, or in one case, possibly further reduction in stability. These results may indicate that NFAT plays a crucial and special role in TCR activation, which leads to iTreg instability. Other pathways, as far as how this experiment is designed, do not appear to be significantly involved.

Author response image 2.

Comparing effects of NFAT, NF-kB and c-Jun/c-Fos inhibitors on iTreg instability. Sorted Foxp3-GFP+ iTregs were rested for 1d, then restimulated by anti-CD3 and CD28 in the presence of listed inhibitors. Percentages of Foxp3+ cells were analyzed by intracellular staining after 2d restimulation.

3) The authors linked chromatin accessibility and increased expression of T helper cell genes to the loss of Foxp3 expression and iTreg instability. However, it is not clear how the former can lead to the latter. It is also not clear whether NFAT binds directly to the Foxp3 locus in the restimulated iTregs and inhibits Foxp3 expression.

T helper gene activation is likely to cause instability in iTregs by secreting more inflammatory cytokines, as shown in Figure Q9, for example, IL-21 secretion. Further investigation is needed to understand how these genes contribute to Foxp3 gene instability exactly. With our limited insight, there may be two possibilities. 1. IL-21 directly affects Foxp3 through its impact on certain inflammation-related transcription factors (TFs). 2. There could be an indirect relationship where NFAT has a greater tendency to bind to those inflammatory TFs when iTreg instability appears, promoting the upregulation of these Th genes like in activated T cells, while being less likely to bind to SMAD and Foxp3, representing a competitive behavior. We at the moment cannot comprehend the intricacies that lead to the differential effects on T helper genes and Treg related genes.

With that said, we have previously attempted to explore the direct effect of NFAT on Foxp3 gene locus. Foxp3 transcription in iTregs primarily relies on histone modifications such as H3K4me3 (Tone et al., 2008; Lu et al., 2011) rather than DNA demethylation (Ohkura et al., 2012; Hilbrands et al., 2016). Previous studies have reported that NFAT and SMAD3 can together promote the histone acetylation of Foxp3 genes (Tone et al., 2008). In our previous set of experiments, we simultaneously obtained information of NFAT binding sites and H3K4me3. In Foxp3 locus, we observed a decreasing trend in NFAT binding to the CNS3 region of Foxp3 in restimulated iTregs compared to resting iTregs (Author response image 3). Additionally, the H3K4me3 modification in the CNS3 region of Foxp3 decreased upon iTreg restimulation, but inhibiting NFAT nuclear translocation with CsA could maintain this modification at its original level (Author response image 3).

Author response image 3.

The NFAT binding and histone modification on Foxp3 gene locus. Genome track visualization of NFAT binding profiles and H3K4me3 profiles in Foxp3 CNS3 locus in two batches of dataset.

Based on these preliminary explorations, it is concluded that NFAT can directly bind to the Foxp3 locus, and it appears that NFAT decreases upon restimulation, resulting in a decrease in H3K4me3, ultimately leading to the close association of NFAT and Foxp3 instability. However, due to limited sample replicates, these data need to be verified for more solid conclusions. We speculate that during the induction of iTregs, NFAT may recruit histone-modifying enzymes to open the Foxp3 CNS3 region, and this effect is synergistic with SMAD. When instability occurs upon restimulation, NFAT binding to Foxp3 weakens due to the absence of SMAD's assistance, subsequently reducing the recruitment of histone modifications enzyme and ultimately inhibiting Foxp3 transcription.

Reviewer #2 (Public Review):

(1) Some concerns about data processing and statistic analysis.

The authors did not provide sufficient information on statistical data analysis; e.g. lack of detailed descriptions about

-the precise numbers of technical/biological replicates of each experiment

-the method of how the authors analyze data of multiple comparisons... Student t-test alone is generally insufficient to compare multiple groups; e.g. figure 1.

These inappropriate data handlings are ruining the evidence level of the precious findings.

We thank the reviewer for pointing out this important aspect. In the figure legend, numbers of independently-performed experiment repeats are shown as N, biological replicates of each experiment as n. Student’s t test was used for comparing statistical significance between two groups. In this manuscript, all calculations of significant differences were based on comparisons between two groups. There were no multiple conditions compared simultaneously within a single group, and thus, no other calculation methods were used.

(2) Untransparent data production; e.g. the method of Motif enrichment analysis was not provided. Thus, we should wait for the author's correction to fully evaluate the significance and reliability of the present study.

Per this reviewer’s request, we have provided detailed descriptions of the data analysis for Fig 5, including both the method section and the Figure legend, as presented below:

“The peaks annotations were performed with the “annotatePeak” function in the R package ChIPseeker (Yu et al, 2015).

The plot of Cut&Tag signals over a set of genomic regions were calculated by using “computeMatrix” function in deepTools and plotted by using “plotHeatmap” and “plotProfile” functions in deepTools. The motif enrichment analysis was performed by using the "findMotifsGenome.pl" command in HOMER with default parameters.

The motif occurrences in each peak were identified by using FIMO (MEME suite v5.0.4) with the following settings: a first-order Markov background model, a P value cutoff of 10-4, and PWMs from the mouse HOCOMOCO motif database (v11).”

Additionally, we have also supplemented the method section with further details on the analysis of RNA-seq and ATAC-seq data.

(3) Lack of evidence in human cells. I wonder whether human PBMC-derived iTreg cells are similarly regulated.

This is a rather complicated issue, human T cells express FoxP3 upon TCR stimulation (PNAS, 103(17): 6659–6664), whose function is likely to protect T cells from activation induced cell death, and does not offer Treg like properties. In contrast in mice, FoxP3 can be used as an indicator of Treg. Currently, this is not a definitive marker for Treg in human, our FoxP3 based readouts do not apply. Nevertheless, we have now investigated whether inhibiting calcium signaling or NFAT could enhance the stability of human iTreg. As shown in Author response image 4, we found that the proportion of Foxp3-expressing cells did not show significant changes across the different conditions, while the MFI analysis revealed that CsA-treated iTreg exhibited higher Foxp3 expression levels compared to both restimulated iTreg and rest iTreg. However, CM4620 had no significant effect on Foxp3 stability, consistent with the observation of its limited efficacy in suppressing human iTreg long term activation. In summary, our results suggest that inhibiting NFAT signaling through CsA treatment can help maintain higher levels of Foxp3 expression in human iTreg.

Author response image 4.

Effect of inhibiting NFAT and calcium on human iTreg stability. Human naïve CD4 cells from PBMC were subjected to a two-week induction process to generate human iTreg. Subsequently, human iTreg were restimulated for 2 days with dynabeads followed by 2 days of rest in the prescence of CsA and CM-4620. Four days later, percentages of Foxp3+ cells and Foxp3 mean fluorescence intensity (MFI) were analyzed by intracellular staining.

(4) NFAT regulation did not explain all of the differences between iTregs and nTregs, as the authors mentioned as a limitation. Also, it is still an open question whether NFAT can directly modulate the chromatin configuration on the effector-type gene loci, or whether NFAT exploits pre-existing open chromatin due to the incomplete conversion of Treg-type chromatin landscape in iTreg cells. The authors did not fully demonstrate that the distinct pattern of chromatin regional accessibility found in iTreg cells is the direct cause of an effector-type gene expression.

To our surprise, the inhibition of NFkB (BAY 11-7082), c-Jun (SP600125), and the c-Jun/c-Fos complex (T5224) resulted in minimal alterations, as shown in Fig Q1. This seems to argue that NFAT may play a more special role in events leading iTreg instability.

We hypothesize that NFAT takes advantage of pre-existing open chromatin state due to the incomplete conversion of chromatin landscape in iTreg cells. Because iTreg cells, after induction, already exhibit inherent chromatin instability, with highly-open inflammatory genes. Furthermore, when iTreg cells were restimulated, the subsequent change in chromatin accessibility was relatively limited and not rescued by NFAT inhibitor treatment (Author response image 5). Therefore, in the case of iTreg cells, we propose that NFAT exploits the easy access of those inflammatory genes, leading to rapid destabilization of iTreg cells in the short term.

In contrast, tTreg cells possess a relatively stable chromatin structure in the beginning, it would be interesting to investigate whether NFAT or calcium signaling could disrupt chromatin accessibility during the activation or expansion of tTreg cells. It is possible that NFAT might cause the loss of the originally established demethylation map and open up inflammatory loci, thereby inducing a shift in gene transcriptional profiles, equally leading to instability.

Author response image 5.

Chromatin accessibility of Rest, Retimulated, CsA/ORAIinh treated restimulated iTreg. PCA visualization of chromatin accessibility profiles of different cell types. Color indicates cell type.

To establish a direct relationship between gene locus accessibility and its overexpression, a controlled experimental approach can be employed. One such method involves precise manipulation of the accessibility of a specific genomic locus using CRISPR-mediated epigenetic modifications at targeted loci. Subsequently, the impact of this manipulation on the expression level of the target gene can be precisely examined. By conducting these experiments, it will be possible to determine whether the augmented gene accessibility directly causes the observed gene overexpression.

Reviewer #1 (Recommendations For The Authors):

1) It might be helpful to add TGF-b to the iTreg restimulation culture to remove the influence of the lack of TGF-b from the equation, and measure the influence of SOCE/NFAT on iTreg instability.

Please refer to Author response image 1.

2) Alternatively, authors can also culture iTreg cells with TGF-b for 2 weeks when they undergo epigenetic changes and become more stabilized (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). At this point, the stabilized iTregs can be used to measure the influence of SOCE/NFAT on iTreg instability.

In the study conducted by Polansky, it was observed in Figure 1 that prolonged exposure to TGF-β fails to induce stable Foxp3 expression and demethylation of the Treg-specific demethylated region (TSDR). Based on this finding, we could consider exploring alternative approaches to obtain a more stabilized iTreg population. One such approach could be isolating Foxp3+helios-Nrp1- iTreg cells directly from the peripheral in vivo, which are also known as pTregs. Generally, pTreg cells generated in vivo tend to be more stable compared to iTreg cells induced in vitro, and they already exhibit partial demethylation of the Treg signature, as shown in Fig 6C (Polansky JK et al, Eur J Immunol., 2008, PMID: 18493985). Investigating the role of NFAT and calcium signaling in pTreg cells would provide further insights into the additional roles of NFAT in Treg phenotypical transitions, particularly its role in chromatin accessibility.

3) In Figure 3, NFAT binding to the inflammatory genes in iTreg cells was even stronger than in activated T conventional cells. This is possibly due to Tconv cells being stimulated only once while iTregs were restimulated. A fair comparison should be conducted with restimulated activated conventional T cells.

Figure 3 demonstrates the accessibility of inflammatory gene loci, rather than NFAT binding. Comparing restimulated Tconvs with restimulated iTreg cells is indeed a valuable suggestion, as their activation state and polarization in iTreg directions could lead to distinct chromatin accessibility. Although one is activated long term regularly and the other is activated long term under iTreg polarization, it is highly likely that the chromatin state of both activated Tconvs and iTreg cells is highly open, especially in terms of the accessibility of inflammatory genes. This may provide us with a new perspective to understand iTreg cells, but will unlikely affect our central conclusion.

4) In the in vivo experiment in Figure 6, a control condition without OVA immunization should be included as a baseline.

We have performed this experiment in the absence of OVA, as depicted in Author response image 6. In the absence of OVA immunization, both WT-ORAI and DN-ORAI iTreg exhibited substantial stability, although DN-ORAI demonstrated a slightly less stable trend. Upon activation with 40ug and 100ug of OVA, DN-ORAI iTreg demonstrated enhanced stability than WT-ORAI iTreg, maintaining a higher proportion of Foxp3 expression.

Author response image 6.

Stability of DN-ORAI iTreg in vivo with or without OVA immunization. WT-ORAI/DN-ORAI-GFP+-transfected CD45.2+ Foxp3-RFP+ OT-II iTregs were transferred i.v. into CD45.1 mice. Recipients were left or immunized with OVA323-339 in Alum adjuvant. On day 5, mLN were harvested and analyzed for Foxp3 expression by intracellular staining.

Reviewer #2 (Recommendations For The Authors):

Major

Some concerns about the data processing and statistic analysis, as mentioned in the public review. In the figure legend, what does it mean e.g. n=3, N=3? Technical triplicate experiments? Three mice? Independently-performed three experiments? The authors should define it at least in the "Statistical analysis" in the method section otherwise the readers cannot determine the reason why they mainly use SEM for the data description.

Moreover, in some cases, the number of experiments was not sure; e.g., Fig.1B, Fig. 5.

How did the authors analyze data including multiple comparisons? Student t-test alone is generally insufficient to compare multiple groups; e.g. figure 1.

We thank the reviewer for pointing out this omission. Now, in the figure legend, numbers of independently-performed experiment repeats are shown as N, biological replicates of each experiment as n. For Fig. 1B, N=2, and for Fig 5, we have acquired NFAT Cut&Tag data for 2 times, N=2. Student’s t test was used for comparing statistical significance between two groups. In this manuscript, all calculations of significant differences were based on comparisons between two groups. There were no multiple conditions compared simultaneously within a single group, and thus, no other calculation methods were involved apart from the Student's t-test.

In Figure 1A, the difference in suppressiveness seemed subtle. Data collection of multiple doses of Tconv:Treg ratio will enhance the reliability of such kind of analysis.

We have now attempted the suppression assay with varying Treg:Tconv ratios and observed that the suppressive effect of iTreg was more obvious than that of tTreg when co-cultured at a 1:1 ratio with Tconv cells. However, as the cell number of tTreg and iTreg decreased, the inhibitory effects converged.

Author response image 7.

Compare multiple dose of Tconv:Treg ratio in suppression function CFSE-labelled OT-II T cells were stimulated with OVA-pulsed DC, then different number of Foxp3-GFP+ iTregs and tTregs were added to the culture to suppress the OT-II proliferation. After 4 days, CFSE dilution were analyzed. Left, Representative histograms of CFSE in divided Tconvs. Right, graph for the percentage of divided Tconvs.

In Figure 3F, to which group did the shaded peaks belong? In this context, the authors should focus on "Activation Region" peaks (open chromatin signature in both TcAct & iTreg defined in Fig. 4D) but I did not find the peak in the focusing DNA regions in TcAct (e.g. the shaded regions in IL-4 loci). The clear attribution of the peaks to the heatmap will enhance the visibility and understanding of readers.

We have selected some typical peaks that belong to Fig 3D. These genes encompass some T-cell activation-associated transcription factors, such as Irf4, Atf3, as well as multiple members of the Tnf family including Lta, Tnfsf4, Tnfsf8, and Tnfsf14. Additionally, genes related to inflammation such as Il12rb2, Il9, and Gzmc are included. These genes show elevated accessibility upon T-cell activation, partially open in activated nTreg cells, referred to as the "Activation Region." They collectively exhibit high accessibility in iTreg cells, which may contribute to their instability.

Author response image 8.

Chromatin accessibility of some “Activation Region”. Genomic track showing chromatin accessibility of Irf4, Atf3, Lta, Tnfsf8, Tnfsf4, Tnsfsf14, Il12rb2, Il9, Gzmc in activated Tconv and iTreg.

In Figure 4A/S4A, the information on cell death will help the understanding of readers because the sustained SOCE is associated with cell survival as shown in Fig. S2. The authors can discuss the relationships between cell death and Foxp3 retention, which potentially leads to a further interesting question; e.g. the selective/resistance to activation-induced cell death as the identity of Treg cells.

As shown in Author response image 9, activated iTreg cells indeed exhibit a certain degree of cell death compared to resting iTreg cells. The inhibition of NFAT by CsA enhances the survival rate of iTreg cells, but the inhibition of ORAI by CM-4620 leads to more severe cell death. The cell death induced by CsA and CM-4620 is not consistent, indicating that there may not be a direct proportional relationship between cell death and the expression of Foxp3 and Treg identity.

Author response image 9.

Relationship of cell death and Foxp3 stability in restimulated iTregs. Sorted Foxp3-GFP+ iTregs were rested for 1d, then restimulated by anti-CD3 and CD28 in the presence of CsA or CM-4620. After 2d restimulation, live cell percentage were analyzed by staining of Live/Dead fixable Aqua, and percentages of Foxp3+ cells were analyzed by intracellular staining of Foxp3. Upper, live cell percentage of iTregs. Lower, percentages of Foxp3 in iTregs.

In Figure 5, the information for the data interpretation was insufficient.

We have provided detailed descriptions of the data analysis for Fig 5, including both the method section and the Figure legend, as presented below:

“The peaks annotations were performed with the “annotatePeak” function in the R package ChIPseeker (Yu et al, 2015). The plot of Cut&Tag signals over a set of genomic regions were calculated by using “computeMatrix” function in deepTools and plotted by using “plotHeatmap” and “plotProfile” functions in deepTools. The motif enrichment analysis was performed by using the "findMotifsGenome.pl" command in HOMER with default parameters. The motif occurrences in each peak were identified by using FIMO (MEME suite v5.0.4) with the following settings: a first-order Markov background model, a P value cutoff of 10-4, and PWMs from the mouse HOCOMOCO motif database (v11).”

Additionally, we have also supplemented the method section with further details on the analysis of RNA-seq and ATAC-seq data.

The correlation between the open chromatin status of the gene loci described in Fig.5E and the expression at mRNA level? e.g.; Do iTreg-Act cells produce a higher level of IL-21 than nTreg-act? The analysis in Fig.5F-G should be performed in parallel with nTreg cells to emphasize the distinct NFAT-chromatin regulation in iTreg cells.

We have now compared the secretion levels of IL-21 in tTreg and iTreg upon activation and treated with CsA by ELISA. As shown in Author response image 10, tTreg did not secrete IL-21 regardless of activation status (undetectable), while iTreg did not secrete IL-21 at resting state but exhibited IL-21 secretion after 48 h of activation. Moreover, the secretion of IL-21 was inhibited by CsA and CM-4620 treatment. This observation aligns with our earlier findings where we observed nuclear binding of NFAT to gene loci of these cytokines, enhancing their expression and pushing iTreg unstable under inflammatory conditions. These findings further underscore the likelihood that the inhibition of calcium and NFAT signaling might contribute to the stabilization of iTreg by suppressing the secretion of inflammatory cytokines.

Author response image 10.

IL-21 secretion in tTreg and iTreg upon activation. iTregs and tTregs were sorted and restimulated with anti-CD3 and anti-CD28 antibodies, in the presence of CsA and CM-4620. Cell culture supernatant were harvested after 2 d restimulation and IL-21 secretion was analyzed by ELISA.

Performing a parallel comparison of NFAT activity between tTreg and iTreg cells was initially part of our experimental plan. However, it proved challenging in practice, as we encountered difficulties in efficiently infecting tTreg cells with NFAT-flag. Consequently, we could not obtain a sufficient number of tTreg cells for conducting Cut&Tag experiments.

Based on our observations, we speculate that there might be substantial differences in the accessibility of genes in tTreg cells, leading to considerable variations in the repertoire of genes available for NFAT to regulate. As a result, we expect significant differences in the nuclear localization and activity of NFAT between iTreg and tTreg cells.

In Figure 6C, what does the FCM plot between Foxp3-CFSE look like?

The authors can discuss the mechanism of ORAI-DN-mediated through such analysis; e.g. the possibility that selective proliferation defect by ORAI-DN in Foxp3- cells led to an increased percentage of Foxp3, not only just unstable transcription of Foxp3.

This is an in vitro experiment to assess the suppressive effect of iTreg on Tconv proliferation. Therefore, CFSE is used to stain Tconv cells, but not iTreg cells, so we did not detect proliferation feature of iTreg.

Minor

Confusing terminology of "tTreg" at line 47, etc. "natural Treg" contains both thymic-derived Treg and periphery-derived Treg cells. (A Abbas et al. Nat Immunol. 2013)

We have now changed the designation to tTreg at line 47. tTreg refers to thymus-derived regulatory T cells, while nTreg includes both tTreg and pTreg. However, it is important to note that the Treg cells used in our study were isolated from the spleen of 2-4-month-old Foxp3-GFP or Foxp3-RFP mice. The CD4+ T cells were first enriched using the CD4 Isolation kit, and the FACSAriaII was utilized to collect CD4+ Foxp3-GFP/RFP+ Treg cells. Subsequently, Helios and Nrp-1 staining revealed that the majority of these cells were nTreg, with only approximately 6% being pTreg. Overall, we consider the cells we used as tTreg.

In all FCM analyses, the authors should clarify how to detect Foxp3 expression; Foxp3-GFP/Foxp3-RFP/Intracellular staining like Figure S5A (but not specified in the other FCM plots)

All Foxp3 expressions in the article were assessed using intracellular staining, as described in the methods section, and we have added specific descriptions to each figure legend. The reason for employing intracellular staining is that we used Foxp3-IRES-GFP mice, where GFP and Foxp3 are not fused into a single protein, existing as separate proteins after expression. Therefore, during induction, the appearance of GFP protein might potentially represent the presence of Foxp3. However, in cases of Foxp3 instability, the degradation of GFP protein may not be entirely synchronized with that of Foxp3 protein, making GFP an unreliable indicator of Foxp3 expression levels. As a result, for the purification of pure iTreg cells, we used Foxp3-GFP/RFP fluorescence, while for observing instability, we employed intranuclear staining of Foxp3.

In Figure 6B, the captions were lacking in the two graphs on the right side

The two restimulation conditions, 0.125+0.25 and 0.25+0.5, have been added into Fig 6B right side.

In Figure S2, the annotation of the x-y axis was missing.

Added.

Lack of reference at line 292.

Reference 42-46 were added.

In the method section, the authors should note the further product information of antibodies and reagents to enhance reproducibility and transparency. Making a list that clarifies the suppliers, Ab clone, product IDs, etc. is encouraged. The authors did not specify the supplier of recombinant proteins and which type of TGF-beta (TGF-beta 1, 2, or 3?).

A detailed description of the mice, antibodies, Peptide recombinant protein, commercial kit, and software has been provided and incorporated into the methods section.

In the method section, the authors should clarify which Foxp3-reporter strain. There are many strains of Foxp3-reporter mice in the world. In line 373, is the "FoxP3-IRES-GFP transgenic mice" true? Knock-in strain or BAC-transgene?

This mouse is a gift from Hai Qi Lab in Tsinghua University. They acquired this mouse strain from Jackson Laboratory, and the strain name is B6.Cg-Foxp3tm2Tch/J, Strain #:006772. An IRES-EGFP-SV40 poly A sequence was inserted immediately downstream of the endogenous Foxp3 translational stop codon, but upstream of the endogenous polyA signal, generating a bicistronic locus encoding both Foxp3 and EGFP.

The age of mice used in the experiments should be specified, and confusing words such as "young" should not be used in any method descriptions; e.g. line 405.

The detailed mouse age has been added in the methods section. “To prepare Tconv, tTreg and iTreg for experiments, spleen was isolated from 2-4-month-old Foxp3-GFP mice for Tconv and tTreg sorting, and 6-week-old mice for iTreg induction.”

The method of how the original ATAC-seq/Cut & Tag data were generated was not described in the method section.

Added in method section.

The reference section was incomplete, and the style was not unified. e.g.; ref 7, 24, 25, 26 ... I gave up checking all.

The style of ref 7, 22, 24, 26, 28, 31, 33, 35 were modified.

Changes in manuscript:

Author Name: “Huiyun Lv” to “Huiyun Lyu”.

Fig 1A was updated according to Reviwer 2’s suggestion.

Fig S3E and associated description was added according to Reviwer 2’s suggestion.

Fig S4C and associated description was added according to Reviwer 1’s suggestion.

Fig 5H and associated description was added according to Reviwer 2’s suggestion.

Fig 6D were updated according to Reviwer 1’s suggestion.

Fig 2D was corrected, the labels for gapdh and actin in the iTreg panel were inadvertently switched. The mistake has been rectified, and the original gel image will be provided.

Fig 2A and Fig 4A was updated.

The style of Fig 6B and Fig S2A was modified.

Method:

Mice: FoxP3-IRES-GFP with more description.

Flow Cytometry sorting and FACS: the detailed mouse age has been added. RNA-seq analysis, ATAC-sequencing, ATAC-seq analysis, Cut&Tag assay, Cut&Tag data analysis: more description was added.

Statistical analysis: “Numbers of independently-performed experiment repeats are shown as N, biological replicates of each experiment as n.” were added.

Reference: Ref 42-46 and 49-52 were added. The style of ref 7, 22, 24, 26, 28, 31, 33, 35 were corrected.

A detailed description of the mice, antibodies, Peptide recombinant protein, commercial kit, and software has been provided.

Author Response

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

eLife assessment

This study provides potentially important, new information about the combination of information from the two eyes in humans. The data included frequency tagging of each eye's inputs and measures reflecting both cortical (EEG) and sub-cortical processes (pupillometry). Binocular combination is of potentially general interest because it provides -in essence- a case study of how the brain combines information from different sources and through different circuits. The strength of supporting evidence appears to be solid, showing that temporal modulations are combined differently than spatial modulations, with additional differences between subcortical and cortical pathways. However, the manuscript's clarity could be improved, including by adding more convincing motivations for the approaches used.

We thank the editor and reviewers for their detailed comments and suggestions regarding our paper. We have implemented most of the suggested changes. In doing so we noticed a minor error in our analysis code that affected the functions shown in Figure 2e (previously Figure 1e), and have fixed this and rerun the modelling. Our main results and conclusions are unaffected by this change. We have also added a replication data set to the Appendix, as this bears on one of the points raised by a reviewer, and included a co-author who helped run this experiment.

Reviewer #1 (Public Review):

In this paper, the interocular/binocular combination of temporal luminance modulations is studied. Binocular combination is of broad interest because it provides a remarkable case study of how the brain combines information from different sources. In addition, the mechanisms of binocular combination are of interest to vision scientists because they provide insight into when/where/how information from two eyes is combined.

This study focuses on how luminance flicker is combined across two eyes, extending previous work that focused mainly on spatial modulations. The results appear to show that temporal modulations are combined in different ways, with additional differences between subcortical and cortical pathways.

1. Main concern: subcortical and cortical pathways are assessed in quite different ways. On the one hand, this is a strength of the study (as it relies on unique ways of interrogating each pathway). However, this is also a problem when the results from two approaches are combined - leading to a sort of attribution problem: Are the differences due to actual differences between the cortical and subcortical binocular combinations, or are they perhaps differences due to different methods. For example, the results suggest that the subcortical binocular combination is nonlinear, but it is not clear where this nonlinearity occurs. If this occurs in the final phase that controls pupillary responses, it has quite different implications.

At the very least, this work should clearly discuss the limitations of using different methods to assess subcortical and cortical pathways.

The modelling asserts that the nonlinearity is primarily interocular suppression, and that this is stronger in the subcortical pathway. Moreover the suppression impacts before binocular combination. So this is quite a specific location. We now say more about this in the Discussion, and also suggest that fMRI might avoid the limits on the conclusions we can draw from different methods.

1. Adding to the previous point, the paper needs to be a better job of justifying not only the specific methods but also other details of the study (e.g., why certain parameters were chosen). To illustrate, a semi-positive example: Only page 7 explains why 2Hz modulation was used, while the methods for 2Hz modulation are described in detail on page 3. No justifications are provided for most of the other experimental choices. The paper should be expanded to better explain this area of research to non-experts. A notable strength of this paper is that it should be of interest to those not working in this particular field, but this goal is not achieved if the paper is written for a specialist audience. In particular, the introduction should be expanded to better explain this area of research, the methods should include justifications for important empirical decisions, and the discussion should make the work more accessible again (in addition to addressing the issues raised in point 1 above). The results also need more context. For example, why EEG data have overtones but pupillometry does not?

We now explain the choice of frequency in the final paragraph of the introduction as follows:

‘We chose a primary flicker frequency of 2Hz as a compromise between the low-pass pupil response (see Barrionuevo et al., 2014; Spitschan et al., 2014), and the relatively higher-pass EEG response (Regan, 1966).’

We also mention why the pupil response is low-pass:

‘The pupil response can be modulated by periodic changes in luminance, and is temporally low-pass (Barrionuevo et al., 2014; Spitschan et al. 2014), most likely due to the mechanical limitations of the iris sphincter and dilator muscles’.

Reviewer #2 (Public Review):

Previous studies have extensively explored the rules by which patterned inputs from the two eyes are combined in the visual cortex. Here the authors explore these rules for un-patterned inputs (luminance flicker) at both the level of the cortex, using Steady-State Visual Evoked Potentials (SSVEPs) and at the sub-cortical level using pupillary responses. They find that the pattern of binocular combination differs between cortical and sub-cortical levels with the cortex showing less dichoptic masking and somewhat more binocular facilitation.

Importantly, the present results with flicker differ markedly from those with gratings (Hou et al., 2020, J Neurosci, Baker and Wade 2017 cerebral cortex, Norcia et al, 2000 Nuroreport, Brown et al., 1999, IOVS). When SSVEP responses are measured under dichoptic conditions where each eye is driven with a unique temporal frequency, in the case of grating stimuli, the magnitude of the response in the fixed contrast eye decreases as a function of contrast in the variable contrast eye. Here the response increases by varying (small) magnitudes. The authors favor a view that cortex and perception pool binocular flicker inputs approximately linearly using cells that are largely monocular. The lack of a decrease below the monocular level when modulation strength increase is taken to indicate that previously observed normalization mechanism in pattern vision does not play a substantial role in the processing of flicker. The authors present a computational model of binocular combination that captures features of the data when fit separately to each data set. Because the model has no frequency dependence and is based on scalar quantities, it cannot make joint predictions for the multiple experimental conditions which is one of its limitations.

A strength of the current work is the use of frequency-tagging of both pupil and EEG responses to measure responses for flicker stimuli at two anatomical levels of processing. Flicker responses are interesting but have been relatively neglected. The tagging approach allows one to access responses driven by each eye, even when the other eye is stimulated which is a great strength. The tagging approach can be applied at both levels of processing at the same time when stimulus frequencies are low, which is an advantage as they can be directly compared. The authors demonstrate the versatility of frequency tagging in a novel experimental design which may inspire other uses, both within the present context and others. A disadvantage of the tagging approach for studying sub-cortical dynamics via pupil responses is that it is restricted to low temporal frequencies given the temporal bandwidth of the pupil. The inclusion of a behavioral measure and a model is also a strength, but there are some limitations in the modeling (see below).

The authors suggest in the discussion that luminance flicker may preferentially drive cortical mechanisms that are largely monocular and in the results that they are approximately linear in the dichoptic cross condition (no effect of the fixed contrast stimulus in the other eye). By contrast, prior research using dichoptic dual frequency flickering stimuli has found robust intermodulation (IM) components in the VEP response spectrum (Baitch and Levi, 1988, Vision Res; Stevens et al., 1994 J Ped Ophthal Strab; France and Ver Hoeve, 1994, J Ped Ophthal Strab; Suter et al., 1996 Vis Neurosci). The presence of IM is a direct signature of binocular interaction and suggests that at least under some measurement conditions, binocular luminance combination is "essentially" non-linear, where essential implies a point-like non-linearity such as squaring of excitatory inputs. The two views are in striking contrast. It would thus be useful for the authors could show spectra for the dichoptic, two-frequency conditions to see if non-linear binocular IM components are present.

This is an excellent point, and one that we had not previously appreciated the importance of. We have generated a figure (Fig 8) showing the IM response in the cross frequency conditions. There is a clear response at 0.4Hz in the pupillometry data (2-1.6Hz), and at 3.6Hz in the EEG data (2+1.6Hz). We therefore agree that this shows the system is essentially nonlinear, despite the binocular combination appearing approximately linear. We now say in the Discussion:

‘In the steady-state literature, one hallmark of a nonlinear system is the presence of intermodulation responses at the sums and differences of fundamental flicker frequencies (Baitch & Levi, 1988; Tsai et al., 2012). In Figure 8 we plot the amplitude spectra of conditions from Experiment 1 in which the two eyes were stimulated at different frequencies (2Hz and 1.6Hz) but at the same contrast (48%; these correspond to the binocular cross and dichoptic cross conditions in Figures 2d,e and 3d,e). Consistent with the temporal properties of pupil responses and EEG, Figure 8a reveals a strong intermodulation difference response at 0.4Hz (red dashed line), and Figure 8b reveals an intermodulation sum response at 3.6Hz (red dashed line). The presence of these intermodulation terms is predicted by nonlinear gain control models of the type considered here (Baker and Wade, 2017; Tsai et al., 2012), and indicates that the processing of monocular flicker signals is not fully linear prior to the point at which they are combined across the eyes.’

If the IM components are indeed absent, then there is a question of the generality of the conclusions, given that several previous studies have found them with dichoptic flicker. The previous studies differ from the authors' in terms of larger stimuli and in their use of higher temporal frequencies (e.g. 18/20 Hz, 17/21 Hz, 6/8 Hz). Either retinal area stimulated (periphery vs central field) or stimulus frequency (high vs low) could affect the results and thus the conclusions about the nature of dichoptic flicker processing in cortex. It would be interesting to sort this out as it may point the research in new directions.

This is a great suggestion about retinal area. As chance would have it, we had already collected a replication data set where we stimulated the periphery, and we now include a summary of this data set as an Appendix. In general the results are similar, though we obtain a measurable (though still small) second harmonic response in the pupillometry data with this configuration, which is a further indication of nonlinear processing.

Whether these components are present or absent is of interest in terms of the authors' computational model of binocular combination. It appears that the present model is based on scalar magnitudes, rather than vectors as in Baker and Wade (2017), so it would be silent on this point. The final summation of the separate eye inputs is linear in the model. In the first stage of the model, each eye's input is divided by a weighted input from the other eye. If we take this input as inhibitory, then IM would not emerge from this stage either.

We have performed the modelling using scalar values here for simplicity and transparency, and to make the fitting process computationally feasible (it took several days even done this way). This type of model is quite capable of processing sine waves as inputs, and producing a complex output waveform which is Fourier transformed and then analysed in the same way as the experimental data (see e.g. Tsai, Wade & Norcia, 2012, J Neurosci; Baker & Wade, 2017, Cereb Cortex). However our primary aim here was to fit the model, and make inferences about the parameter values, rather than to use a specific set of parameter values to make predictions. We now say more about this family of models and how they can be applied in the methods section:

“Models from this family can handle both scalar contrast values and continuous waveforms (Tsai et al., 2012) or images (Meese and Summers, 2007) as inputs. For time-varying inputs, the calculations are performed at each time point, and the output waveform can then be analysed using Fourier analysis in the same way as for empirical data.This means that the model can make predictions for the entire Fourier spectrum, including harmonic and intermodulation responses that arise as a consequence of nonlinearities in the model (Baker and Wade, 2017). However for computational tractability, we performed fitting here using scalar contrast values.”

As a side point, there are quite a lot of ways to produce intermodulation terms, meaning they are not as diagnostic as one might suppose. We demonstrate this in Author response image 1, which shows the Fourier spectra produced by a toy model that multiplies its two inputs together (for an interactive python notebook that allows various nonlinearities to be explored, see here). Intermodulation terms also arise when two inputs of different frequencies are summed, followed by exponentiation. So it would be possible to have an entirely linear binocular summation process, followed by squaring, and have this generate IM terms (not that we think this is necessarily what is happening in our experiments).

Author response image 1

Related to the model: One of the more striking results is the substantial difference between the dichoptic and dichoptic-cross conditions. They differ in that the latter has two different frequencies in the two eyes while the former has the same frequency in each eye. As it stands, if fit jointly on the two conditions, the model would make the same prediction for the dichoptic and dichoptic-cross conditions. It would also make the same prediction whether the two eyes were in-phase temporally or in anti-phase temporally. There is no frequency/phase-dependence in the model to explain differences in these cases or to potentially explain different patterns at the different VEP response harmonics. The model also fits independently to each data set which weakens its generality. An interpretation outside of the model framework would thus be helpful for the specific case of differences between the dichoptic and dichoptic-cross conditions.

As mentioned above, the limitations the reviewer highlights are features of the specific implementation, rather than the model architecture in general. Furthermore, although this particular implementation of the model does not have separate channels for different phases, these can be added (see e.g. Georgeson et al., 2016, Vis Res, for an example in the spatial domain). In future work we intend to explore the phase relationship of flicker, but do not have space to do this here.

Prior work has defined several regimes of binocular summation in the VEP (Apkarian et al.,1981 EEG Journal). It would be useful for the authors to relate the use of their terms "facilitation" and "suppression" to these regimes and to justify/clarify differences in usage, when present. Experiment 1, Fig. 3 shows cases where the binocular response is more than twice the monocular response. Here the interpretation is clear: the responses are super-additive and would be classed as involving facilitation in the Apkarian et al framework. In the Apkarian et al framework, a ratio of 2 indicates independence/linearity. Ratios between 1 and 2 indicate sub-additivity and are diagnostic of the presence of binocular interaction but are noted by them to be difficult to interpret mechanistically. This should be discussed. A ratio of <1 indicates frank suppression which is not observed here with flicker.

Operationally, we use facilitation to mean an increase in response relative to a monocular baseline, and suppression to mean a decrease in response. We now state this explicitly in the Introduction. Facilitation greater than a factor of 2 indicates some form of super-additive summation. In the context of the model, we also use the term suppression to indicate divisive suppression between channels, however this feature does not always result in empirical suppression (it depends on the condition, and the inhibitory weight). We think that interpretation of results such as these is greatly aided by the use of a computational modelling framework, which is why we take this approach here. The broad applicability of the model we use in the domain of spatial contrast lends it credibility for our stimuli here.

Can the model explore the full range of binocular/monocular ratios in the Apkarian et al framework? I believe much of the data lies in the "partial summation" regime of Apkarian et al and that the model is mainly exploring this regime and is a way of quantifying varying degrees of partial summation.

Yes, in principle the model can produce the full range of behaviours. When the weight of suppression is 1, binocular and monocular responses are equal. When the weight is zero, the model produces linear summation. When the weight is greater than 1, suppression occurs. It is also possible to produce super-additive summation effects, most straightforwardly by changing the model exponents. However this was not required for our data here, and so we kept these parameters fixed. We agree that the model is a good way to unify the results across disparate experimental paradigms, and that is our main intention with Figure 7i.

Reviewer #3 (Public Review):

This manuscript describes interesting experiments on how information from the two eyes is combined in cortical areas, sub-cortical areas, and perception. The experimental techniques are strong and the results are potentially quite interesting. But the manuscript is poorly written and tries to do too much in too little space. I had a lot of difficulty understanding the various experimental conditions, the complicated results, and the interpretations of those results. I think this is an interesting and useful project so I hope the authors will put in the time to revise the manuscript so that regular readers like myself can better understand what it all means.

Now for my concerns and suggestions:

The experimental conditions are novel and complicated, so readers will not readily grasp what the various conditions are and why they were chosen. For example, in one condition different flicker frequencies were presented to the two eyes (2Hz to one and 1.6Hz to the other) with the flicker amplitude fixed in the eye presented to the lower frequency and the flicker amplitude varied in the eye presented to the higher frequency. This is just one of several conditions that the reader has to understand in order to follow the experimental design. I have a few suggestions to make it easier to follow. First, create a figure showing graphically the various conditions. Second, come up with better names for the various conditions and use those names in clear labels in the data figures and in the appropriate captions. Third, combine the specific methods and results sections for each experiment so that one will have just gone through the relevant methods before moving forward into the results. The authors can keep a general methods section separate, but only for the methods that are general to the whole set of experiments.

We have created a new figure (now Fig 1) that illustrates the conditions from Experiment 1, and is referenced throughout the paper. We have kept the names constant, as they are rooted in a substantial existing literature, and it will be confusing to readers familiar with that work if we diverge from these conventions. We did consider separating out the methods section, but feel it helps the flow of the results section to keep it as a single section.

I wondered why the authors chose the temporal frequencies they did. Barrionuevo et al (2014) showed that the human pupil response is greatest at 1Hz and is nearly a log unit lower at 2Hz (i.e., the change in diameter is nearly a log unit lower; the change in area is nearly 2 log units lower). So why did the authors choose 2Hz for their primary frequency? And why did the authors choose 1.6Hz which is quite close to 2Hz for their off frequency? The rationale behind these important decisions should be made explicit.

We now explain this in the Introduction as follows:

‘We chose a primary flicker frequency of 2Hz as a compromise between the low-pass pupil response (see Barrionuevo et al., 2014; Spitschan et al., 2014), and the relatively higher-pass EEG response (Regan, 1966).’

It is a compromise frequency that is not optimal for either modality, but generates a measurable signal for both. The choice of 1.6 Hz was for similar reasons - for a 10-second trial it is four frequency bins away from the primary frequency, so can be unambiguously isolated in the spectrum.

By the way, I wondered if we know what happens when you present the same flicker frequencies to the two eyes but in counter-phase. The average luminance seen binocularly would always be the same, so if the pupil system is linear, there should be no pupil response to this stimulus. An experiment like this has been done by Flitcroft et al (1992) on accommodation where the two eyes are presented stimuli moving oppositely in optical distance and indeed there was no accommodative response, which strongly suggests linearity.

We have not tried this yet, but it’s on our to-do list for future work. The accommodation work is very interesting, and we now cite it in the manuscript as follows:

‘Work on the accommodative response indicates that binocular combination there is approximately linear (Flitcroft et al. 1992), and can even cancel when signals are in antiphase (we did not try this configuration here).’

Figures 1 and 2 are important figures because they show the pupil and EEG results, respectively. But it's really hard to get your head around what's being shown in the lower row of each figure. The labeling for the conditions is one problem. You have to remember how "binocular" in panel c differs from "binocular cross" in panel d. And how "monocular" in panel d is different than "monocular 1.6Hz" in panel e. Additionally, the colors of the data symbols are not very distinct so it makes it hard to determine which one is which condition. These results are interesting. But they are difficult to digest.

We hope that the new Figure 1 outlining the conditions has helped with interpretation here.

The authors make a strong claim that they have found substantial differences in binocular interaction between cortical and sub-cortical circuits. But when I look at Figures 1 and 2, which are meant to convey this conclusion, I'm struck by how similar the results are. If the authors want to continue to make their claim, they need to spend more time making the case.

Indeed, it is hard to make direct comparisons across figures - this is why Figure 4 plots the ratio of binocular to monocular conditions, and shows a clear divergence between the EEG and pupillometry results at high contrasts.

Figure 5 is thankfully easy to understand and shows a very clear result. These perceptual results deviate dramatically from the essentially winner-take-all results for spatial sinewaves shown by Legge & Rubin (1981); whom they should cite by the way. Thus, very interestingly the binocular combination of temporal variation is quite different than the binocular combination of spatial variation. Can the pupil and EEG results also be plotted in the fashion of Figure 5? You'd pick a criterion pupil (or EEG) change and use it to make such plots.

We now cite Legge & Rubin. We see what you mean about plotting the EEG and pupillometry results in the same coordinates as the matching data, but we don’t think this is especially informative as we would end up only with data points along the axes and diagonal of the plot, without the points at other angles. This is a consequence of how the experiments were conducted.

My main suggestion is that the authors need to devote more space to explaining what they've done, what they've found, and how they interpret the data. I suggest therefore that they drop the computational model altogether so that they can concentrate on the experiments. The model could be presented in a future paper.

We feel that the model is central to the understanding and interpretation of our results, and have retained it in the revised version of the paper.

Reviewer #2 (Recommendations For The Authors):

I found the terms for the stimulus conditions confusing. I think a simple schematic diagram of the conditions would help the reader.

Now added (the new Fig 1).

In reporting the binocular to monocular ratio, please clarify whether the monocular data was from one eye alone (and how that eye was chosen) or from both eyes and then averaged, or something else. It would be useful to plot the results from the dichoptic condition in this form, as well.

These were averaged across both eyes. We now say in the Methods section:

‘We confirmed in additional analyses that the monocular consensual pupil response was complete, justifying our pooling of data across the eyes.’

Also, clarify whether the term facilitation is used as above throughout (facilitation being > 2 times monocular response under binocular condition) or if a different criterion is being used. If we take facilitation to mean a ratio > 2, then facilitation depends on temporal frequency in Figure 4.

We now explain our use of these terms in the final paragraph of the Introduction:

‘Relative to the response to a monocular signal, adding a signal in the other eye can either increase the response (facilitation) or reduce it (suppression).’

The magnitude of explicit facilitation attained is interesting, but not without precedent. Ratios of binocular to mean monocular > 2, have been reported previously and values of summation depend strongly on the stimulus used (see for example Apkarian et al., EEG Journal, 1981, Nicol et al., Doc Ophthal, 2011).

We now mention this in the Discussion as follows:

‘(however we note that facilitation as substantial as ours has been reported in previous EEG work by Apkarian et al. (1981))’

In Experiment 3, the authors say that the psychophysical matching results are consistent with the approximately linear summation effects observed in the EEG data of Experiment 1. In describing Fig. 3, the claim is that the EEG is non-linear, e.g. super-additive - at least at high contrasts. Please reconcile these statements.

We think that the ‘superadditive’ effects are close enough to linear that we don’t want to make too much of a big deal about them - this could be measurement error, for example. So we use terms such as near-linear, or approximately linear, when referring to them throughout.

Reviewer #3 (Recommendations For The Authors):

Let me make some more specific comments using a page/paragraph/line format to indicate where in the text they're relevant.

1/2 (middle)/3 from end. "In addition" seems out of place here.

Removed.

1/3/4. By "intensities" do you mean "contrasts"?

Fixed.

1/3/last. "... eyes'...".

Fixed.

2/5/3. By "one binocular disc", you mean into "one perceptually fused disc".

Rewritten as: ‘to help with their perceptual fusion, giving the appearance of a single binocular disc’

3/1/1. "calibrated" seems like the wrong word here. I think you're just changing the vergence angle to enable fusion, right?

Now rewritten as: ‘Before each experiment, participants adjusted the angle of the stereoscope mirrors to achieve binocular fusion’

3/1/1. "adjusting the angles...". And didn't changing the mirror angles affect the shapes of the discs in the retinal images?

Perhaps very slightly, but this is well within the tolerance of the visual system to compensate for in the fused image, especially for such high contrast edges.

3/3/5. "fixed contrast" is confusing here because it's still a flickering stimulus if I follow the text here. Reword.

Now ‘fixed temporal contrast’

3/4/1. It would be clearer to say "pupil tracker" rather than "eye tracker" because you're not really doing eye tracking.

True, but the device is a commercial eye tracker, so this is the appropriate term regardless of what we are using it for.

3/5/6. I'm getting lost here. "varying contrast levels" applies to the dichoptic stimulus, right?

Yes, now reworded as ‘In the other interval, a target disc was displayed, flickering at different contrast levels on each trial, but with a fixed interocular contrast ratio across the block.’

3/5/7. Understanding the "ratio of flicker amplitudes" is key to understanding what's going on here. More explanation would be helpful.

Addressed in the above point.

4/3/near end. Provide some explanation about why the Fourier approach is more robust to noise.

Added ‘(which can make the phase and amplitude of a fitted sine wave unstable)’

Figure 1. In panel a, explain what the numbers on the ordinate mean. What's zero, for example? Which direction is dilation? Same question for panel b. It's interesting in panel c that the response in one eye to 2Hz increases when the other eye sees 1.6Hz. Would be good to point that out in the text.

Good idea about panel (a) - we have changed the y-axis to ‘Relative amplitude’ for clarity, and now note in the figure caption that ‘Negative values indicate constriction relative to baseline, and positive values indicate dilation.’ Panel (b) is absolute amplitude, so is unsigned. Panel (c) only contains 2Hz conditions, but there is some dichoptic suppression across the two frequencies in panels (d,e) - we now cover this in the text and include statistics.

6/2/1. Make clear in the text that Figure 1c shows contrast response functions for the pupil.

Now noted in the caption.

Figure 3. I'm lost here. I feel like I should be able to construct this figure from Figures 1 and 2, but don't know how. More explanation is needed at least in the caption.

Done. The caption now reads:

‘Ratio of binocular to monocular response for three data types. These were calculated by dividing the binocular response by the monocular response at each contrast level, using the data underlying Figures 2c, 3c and 3f. Each value is the average ratio across N=30 participants, and error bars indicate bootstrapped standard errors.’

9/1/1-2. I didn't find the evidence supporting this statement compelling.

We now point the reader to Figure 4 as a reminder of the evidence for this difference.

9/1/6-9. You said this. But this kind of problem can be fixed by moving the methods sections as I suggested above.

As mentioned, we feel that the results section flows better with the current structure.

Figure 4. Make clear that this is EEG data.

Now added to caption.

Figure 5 caption. Infinite exponent in what equation?

Now clarified as: ‘models involving linear combination (dotted) or a winner-take-all rule (dashed)’

Figure 6. I hope this gets dropped. No one will understand how the model predictions were derived. And those who look at the data and model predictions will surely note (as the authors do) that they are rather different from one another.

As noted above, we feel that the model is central to the paper and have retained this figure. We have also worked out how to correct the noise parameter in the model for the number of participants included in the coherent averaging, which fixes the discrepancy at low contrasts. The correspondence between the data and model in is now very good, and we have plotted the data points and curves in the same panels, which makes the figure less busy.

12/1. Make clear in this paragraph that "visual cortex" is referring to EEG and perception results and that "subcortical" is referring to pupil. Explain clearly what "linear" would be and what the evidence for "non-linear" is.

Good suggestion, we have added qualifiers linking to both methods. Also tidied up the language to make it clearer that we are talking about binocular combination specifically in terms of linearity, and spelled out the evidence for each point.

12/2/6-9. Explain the Quaia et al results enough for the reader to know what reflexive eye movements were studied and how.

We now specify that these eye movements are also known as the ‘ocular following response’ and were measured using scleral search coils.

12/2/9-10. Same for Spitchan and Cajochen: more explanation.

Added:

“(melatonin is a hormone released by the pineal gland that regulates sleep; its production is suppressed by light exposure and can be measured from saliva assays)”

12/3/2-3. Intriguing statements about optimally combining noisy signals, but explain this more. It won't be obvious to most readers.

We have added some more explanation to this section.

13/1. This is an interesting paragraph where the authors have a chance to discuss what would be most advantageous to the organism. They make the standard argument for perception, but basically punt on having an argument for the pupil.

Indeed, we agree that this point is necessarily speculative, however we think it is interesting for the reader to consider.

13/2/1. "Pupil size affects the ..." is more accurate.

Fixed.

13/2/2 from end. Which "two pathways"? Be clear.

Changed to ‘the pupil and perceptual pathways’

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

Summary:

In this manuscript (eLife-RP-RA-2024-103904), the authors identified that NOLC1 was upregulated in gastric cancer samples, which promoted cancer progression and cisplatin resistance. They further found that NOLC1 could bind to p53 and decrease its nuclear transcriptional activity, then inhibit p53-mediated ferroptosis. There are several major concerns regarding the conclusions.

Strengths:

This study identified that NOLC1 could bind to p53 and decrease its nuclear transcriptional activity, then inhibit p53-mediated ferroptosis in gastric cancer.

Weaknesses:

The major conclusions were not sufficiently supported by the results. The experiments were not conducted in a comprehensive manner.

Major concerns

(1) The authors investigated NOLC1 expression in gastric cancer (GC) using clinical samples, which is valuable; however, the sample array includes only 3 patients. This sample size is insufficient to support conclusions for human samples. Please increase the sample size and apply a more robust statistical analysis. Additionally, specify the statistical methods used in the figure legend.

Thanks very much for the kind comments and great suggestions. As suggested, we have increased the sample size of GC patients, and the new data (six pair samples) was shown in Fig. S1A, further reflecting that NOLC1 was upregulate in gastric cancer (GC). Moreover, the statistical methods have been added in each figure legend.

(2) These data are not sufficient to support the key conclusion of this study "NOLC1 is significantly upregulated in GC tissues and Cis-resistant GC cells". There is no convincing data showing that NOLC1 upregulation is specific to cancer cells or any other cell types. Based on the following results that NOLC1 expressed in cancer cells can support cancer cell survival and drug resistance, the authors switched to investigating the role of NOLC1 in cancer cells without demonstrating cancer cells indeed highly upregulate NOLC1.

Thanks for raising this good question. As shown in Fig. 1E-F, the TCGA database have shown that NOLC1 was upregulated in GC. Moreover, we further analyzed the NOLC1 expression level in other cancer type, according to the Human Protein Atlas (https://www.proteinatlas.org/). The results indicated that NOLC1 mRNA level was much higher in almost all cancers except acute myeloid leukemia (LAML). In addition, according to the gene expression profiling interactive analysis (GEPIA, http://gepia.cancer-pku.cn/index.html), NOLC1 mRNA level was above 100 nTPM in most gastric cancer cell lines, however in most non-cancerous cell lines was below 100 nTPM, indicating that NOLC1 was up-regulated in gastric cancer.

Author response image 1.

The mRNA level of NOLC1 in different GC cells and non-cancerous cells.

(3) The authors primarily use MGC-803 cells for experiments; however, MGC-803 is known to be a HeLa-contaminated cell line. Could the authors explain this choice of using this cell line only? Did they validate key findings with additional cell lines? This is particularly important for assays such as cisplatin resistance validation, in vivo experiments, TEM imaging, and MitoPeDPP fluorescence imaging.

Thanks for raising this good question. We are not only use MGC-803 cells, the key findings in vitro was also validated in MKN-45 cells (Fig. 2), and in vivo experiment also validated in Mouse Forestomach Carcinoma cells (MFC)-tumor bearing 615 mice model (Fig 7). Furthermore, we further added some experiments in MKN-45 cells. The TEM imaging showed that NOLC1 could significantly inhibit cisplatin (Cis) induced lipid membrane damage in MKN-45 cells (Fig. S6A). Moreover, MitoPeDPP fluorescence assay analyzed by FCAs also indicating that rapid ROS was enriched in mitochondria in MKN-45 cells (Fig. 4E, Fig. S6J).

(4) In Figure 2, did the authors perform assays with NOLC1 overexpression? If so, please include these results to strengthen the conclusions.

Thanks very much for the kind comments and great suggestions. As suggested, we added new data about NOLC1 overexpression assay Cell counting kit-8 assay shows that NOLC1-overexpression group is more resistance to Cis compared to vector group (Fig. S4E, S5A).

(5) The authors show in Figures 2A-B that shNOLC1 without cisplatin treatment does not affect cell viability. However, Figures 2D-E suggest increased apoptosis in shNOLC1 cells without cisplatin treatment. Additionally, in vivo studies in Figure 3 show no significant difference between the shNC+PBS and shNOLC1+PBS groups, which appears contradictory to the apoptosis assays. Similarly, Ki67 staining shows decreased scores in the shNOLC1 group compared to shNC. Could the authors clarify this inconsistency?

Thanks for raising this good question. In Fig 2D-E, the difference in proportion of death cells between shNOLC1 and shNC treated with PBS groups were only 3% (MGC-803) and 7% (MKN-45) which is much lower than that treated with cisplatin in vitro. Moreover, in vivo analysis indicated that the average tumor volume in NOLC1+PBS group was smaller than that in NC group, but there was no statistical significance (p value = 0.3962). Moreover, tumor proliferation is a complex process regulated by many factors [1,2], thus the level of Ki67 is by no means the same as the rate of tumor proliferation, might be positively correlated.

(6) In Figure 4, NOLC1 knockdown appears to enhance cisplatin-induced ferroptosis rather than apoptosis. Given p53's role in apoptosis, did the authors compare the effects of NOLC1 on cisplatin-induced apoptosis vs. ferroptosis? If so, please clarify whether NOLC1 predominantly regulates apoptosis or ferroptosis.

Thanks for raising this good question. We do have compared the effects of NOLC1 on cisplatin-induced apoptosis vs. ferroptosis. As shown in Fig. 5A, NOLC1 knockdown obviously increased the BCL-2 protein level which is an anti-apoptotic protein and mediated by p53 via protein interaction in cytoplasm[3,4], this phenomenon may cause by the increasing level of p53 in cytoplasm (Fig. 6I). Also, the TEM imaging showed the classic ferroptotic morphological changes rather than apoptosis (Fig. 5A, S6A). Taken together, NOLC1 mainly regulates p53 mediated ferroptosis rather than apoptosis.

(7) Did the authors perform co-IP assays with p53 or HA antibodies to immunocapture NOLC1? If not, please add this experiment to support protein interactions. The mechanistic correlation between p53 and NOLC1 can be supported by adding experiments using multiple GC cell lines with various p53 alterations (such as loss-of- function or gain-of-function mutations/deletions). This is critical because the authors specifically claimed that NOLC1 can inhibit p53-mediated ferroptosis, but not other tumor suppressors.

Thanks very much for the kind comments and great suggestions. As suggested, we had performed Co-IP assay with anti-HA antibodies to immunocapture NOLC1-FLAG. As shown in Fig. 5K, p53 DNA binding domain (DBD)-HA could immunocapture with NOLC1, further indicated that NOLC1 could binding to p53 DBD. Moreover, we concur with the reviewer that adding experiments using multiple p53 alterations, however considering that different p53 mutants have completely different functional changes. Therefore, we using siRNA to knockdown p53 level in MGC-803 cells, the results shown that NOLC1 mediated resistance was disappear and the GPX4 level was increased (Fig. S10). These data have shown that NOLC1 promotes GC resistance via mediated p53 functions.

(8) In Figure S5B, the LDH release can be blocked by Fer-1?

Thanks for raising this good question. As suggested, Fer-1 (20 μmol/mL) significantly blocked the LDH release in NOLC1 knockdown group (Fig S6E). This data further confirmed that NOLC1 suppressed Cis-induced ferroptosis.

(9) How about the ubiquitination assay in MGC-803 cells?

Thanks for raising this good question. As suggested, we also analyzed the ubiquitination assay in MGC-803 cells. As the result showed that NOLC1 also could increasing level of ubiquitination of p53 (Fig. 6H).

(10) In Figure 6H, the DBD domain of NOLC1 is required for inhibiting P53 ubiquitination.

Thanks for your opinion. However, in our paper, we only mentioned that p53 DBD domain, rather than NOLC1 DBD domain. Also, we did not find any DNA binding function of NOLC1 in the Pubmed database. Therefore, we would like to ask whether the revised opinion is correct.

(11) In Figure 8B, the CD3 antibody is not specific, please change it to a new one.

Thanks very much for the kind comments and great suggestions. As suggested, we have used new CD3 antibody and the new data was added in Fig. 8B.

(12) The authors report that NOLC1 influences peripheral blood lymphocytes with cisplatin treatment, with or without PD-1. Could the authors explain why NOLC1 would affect peripheral blood lymphocytes? Additionally, did they assess immune cell infiltration in the tumor microenvironment (TME) by flow cytometry?

Thanks for raising good question. The tumor size of the knockdown group treated with Cis + PD-1 was too small (less than 100 mg) to extract enough infiltrated immune cells (less than 10000 CD45⁺ cells), thus we chose to detect immune cells in the blood of the mice. Considering that the infiltrating immune cells including CTLs were originate from peripheral blood by circulation. Under the normal conditions, serval tumor biology behavior impact the TME to limit immune responses and present barriers to cancer therapy. For example, tumor could express or secret lots of negative regulator like PD-L1. Causing immune cells cannot recognize tumor cells and infiltrate into tumor tissue. Ferroptosis, as a new from of ICD, could damage tumor cell plasm and release amount of tumor associated antigen and tumor-specific antigens causing immune cells priming and activation. Eventually, the activated immune cells in peripheral blood travel towards the tumor site, infiltrating the tumor tissue under favorable co-stimulatory conditions and guided by chemokine gradients. Once within the tumor microenvironment, these activated T cells can control tumor growth through direct tumor cell destruction and cytokine-mediated processes [5–8]

To assess immune cell infiltration in the TME, we analyzed the tumor infiltrated CD3⁺ and CD8⁺ immune cells in tumor tissue by immunofluorescence (Fig. 8B). Thus, the peripheral blood lymphocytes could reflect the infiltration of immune cells in the tumor.

Minor concerns:

(1) Please clarify the statistical methods in each figure legend.

Thanks for your opinion. We have added statistical methods in each figure legend.

(2) In Figure 2D, please provide statistical data of cleaved-caspase3 expression.

Thanks for your opinion. As is shown in Fig. S5B-C, the relative cleaved-caspase3 were provided.

(3) Please ensure that the canonical expressions used in the research paper are adhered to.

Thanks for your opinion. We have carefully modified our expressions in our paper.

(4) Please pay more attention to the grammar and formatting of texts.

Thanks for your opinion. We revised our manuscript through the American Journal Experts (AJE) service.

Reviewer #2:

Summary:

Shengsheng Zhao et al. investigated the role of nucleolar and coiled-body phosphoprotein 1 (NOLC1) in relegating gastric cancer (GC) development and cisplatin-induced drug resistance in GC. They found a significant correlation between high NOLC1 expression and the poor prognosis of GC. Meanwhile, upregulation of NOLC1 was associated with cis-resistant GC. Experimentally, the authors demonstrate that knocking down NOLC1 increased GC sensitivity to Cis possibly by regulating ferroptosis. Mechanistically, they found NOLC1 suppressed ferroptosis by blocking the translocation of p53 from the cytoplasm to the nucleus and promoting its degradation. In addition, The authors also evaluated the effect of combinational treatment of anti- PD-1 and cisplatin in NOLC1-knockdown tumor cells, revealing a potential role of NOLC1 in the targeted therapy for GC.

Strengths:

Chemoresistance is considered a major reason causing failure of tumor treatment and death of cancer patients. This paper explored the role of NOLC1 in the regulation of Cis-mediated resistance, which involves a regulated cell death named ferroptosis. These findings provide more evidence highlighting the study of regulated cell death to overcome drug resistance in cancer treatment, which could give us more potential strategies or targets for combating cancer.

Weaknesses:

More evidence supporting the regulation of ferroptosis induced by Cisplatin by NOLC1 should be added. Particularly, the role of ferroptosis in the cisplatin-resistance should be verified and whether NOLC1 regulates ferroptosis induced by additional FINs should be explored. Besides, the experiments to verify the regulation of ferroptosis sensitivity by NOLC1 are sort of superficial. The role of MDM2/p53 in ferroptosis or cisplatin resistance mediated by NOLC1 should be further studied by genetic manipulation of p53, which is the key evidence to confirm its contribution to NOLC1 regulation of GC and relative cell death.

Major points:

(1) More evidence supporting the regulation of ferroptosis induced by Cisplatin by NOLC1 should be added. Particularly, the role of ferroptosis in the cisplatin-resistance should be verified and whether NOLC1 regulates ferroptosis induced by additional FINs should be explored.

Thanks very much for the kind comments and great suggestions. As suggested, we have further analyzed the ferroptosis inhibit ability of NOLC1 in MGC-45 cells treated with Erastin, a common used ferroptosis activator. As shown in Fig. S6B, the ferroptosis activated by Erastin was also blocked by NOLC1.

(2) In Figure 1J, the CR cell line should obviously have less apoptosis-maker c-PARP expression, which means these cells are resistant to apoptosis induced by CR. Thus, it would be more rational to study the role of apoptosis regulation by NOLC1. Why did the later data shift to the study of ferroptosis?

Thanks for raising this good question. In the CR cells, the expression levels of many genes were changed, so it is uncertain whether the decreased expression level of cleaved-PARP in the resistant cells is caused by NOLC1 up-regulated. To explore the specific mechanism of NOLC1 mediated resistant, we performed the TEM imaging (Fig. 4A, S6A) and the results showed that cells exhibited classic ferroptosis morphological changes. Moreover, the BCL-2 (an anti-apoptotic protein, and regulated by p53 via protein interaction in cytoplasm) was increased after NOLC1 knockdown (Fig S5A). This phenomenon may cause by the increasing p53 levels in the cytoplasm[3,4] (Fig 5I). Taken together we shift to study of cisplatin induced ferroptosis.

(3) Besides, how about the regulation of apoptosis during cis-resistance by NOLC1 in GC?

Thanks for raising this good question. As mentioned above the Cis induced apoptosis was not as significant as ferroptosis, caused by BCL-2 (a key anti-apoptosis protein) increasing which is mediated by p53 via protein interaction in cytoplasm. NOLC1 increased plasm p53 level subsequently increased BCL-2 level.

(4) The experiments to verify the regulation of ferroptosis sensitivity by NOLC1 are sort of superficial. The role of MDM2/p53 in ferroptosis or cisplatin resistance mediated by NOLC1 should be further studied by genetic manipulation of p53, which is the key evidence to confirm its contribution to NOLC1 regulation of GC and relative cell death.

Thanks for raising this good question. As is shown in Fig S10, after knockdown p53 protein level by using siRNA, NOLC1 could not promote Cis-resistance and the GPX4 level was increased reflecting that NOLC1 promotes Cis resistance via mediate p53 function.

(5) In Figure 2, the data indicated that the knockdown of NOLC1 increased rH2Ax in the presence of Cisplatin, which indicated that NOLC1 might regulate DNA damage-related cellular function. These functions should be more relevant to cisplatin resistance, considering the fundamental effect of this chemo drug.

Thanks very much for the kind comments and great suggestions. Indeed, we found that DNA damage was more obvious in knockdown groups, but the ferroptotic changes like ROS and mitochondrial membrane damage were also significantly different in knockdown groups. Considering that as a chemo drug, cisplatin not only induces damage DNA but also acts as a stress which could activates various signal pathways including apoptosis, ferroptosis, pyroptosis, necroptosis, etc., under different drug concentrate or time [9–11]. Therefore, it is important to find out the NOLC1 predominantly blocked pathway in GC.

(6) In Figure.4, ferroptosis inhibitors like Ferr-1 or DFO should be used to verify the regulation of ferroptosis by Cisplatin and NOLC1.

Thanks very much for the kind comments and great suggestions. As suggested, we performed additional LDH release assay. The results showed that Fer-1 also could block cisplatin induced LDH release in NOLC1 knockdown groups (Fig. S6E).

(7) In Figure 4H, Cisplatin decreased FSP1 and GPX4, which could be enhanced in the NOLC1-konckdown cell line. Meanwhile, the knockdown of NOLC1 increased the ACSL4 level. These findings could be the key reason for the regulation of ferroptosis by NOLC1 rather than p53 since they all are direct regulators of ferroptosis.

Thanks very much for the kind comments and great suggestions. We rewrote the text as you suggested. Recently, it also has been reported that ACSL4-regulated ferroptosis is related to p53, but the exact mechanism is still unclear [12]. Moreover, further studies of specific relation between NOLC1 and FSP1/ACSL4 will be conducted in the further

(8) Whether p53 mediates the regulation of ferroptosis and cisplatin resistance by NOLC1 should be thoroughly studied using p53-KO cell lines.

Thanks very much for the kind comments and great suggestions. As previously mentioned, by using si-RNA to knockdown p53, the NOLC1 mediate Cis-resistance were blocked (Fig. S10). Meanwhile, the GPX4 level was also increased in p53/NOLC1 double-knockdown groups compared to the NOLC1 knockdown group. These data indicating that NOLC1 suppresses ferroptosis via mediating p53 functions.

Reviewer #3:

The authors have put forth a compelling argument that NOLC1 is indispensable for gastric cancer resistance in both in vivo and in vitro models. They have further elucidated that NOLC1 silencing augments cisplatin-induced ferroptosis in gastric cancer cells. The mechanistic underpinning of their findings suggests that NOLC1 modulates the p53 nuclear/plasma ratio by engaging with the p53 DNA Binding Domain, which in turn impedes p53-mediated transcriptional regulation of ferroptosis. Additionally, the authors have shown that NOLC1 knockdown triggers the release of ferroptosis-induced damage-associated molecular patterns (DAMPs), which activate the tumor microenvironment (TME) and enhance the efficacy of the anti-PD-1 and cisplatin combination therapy.

Strengths:

The manuscript presents a robust dataset that substantiates the authors' conclusion. They have identified NOLC1 as a potential oncogene that confers resistance to immuno-chemotherapy in gastric cancer through the mediation of ferroptosis and subsequent TME reprogramming. This discovery positions NOLC1 as a promising therapeutic target for gastric cancer treatment. The authors have delineated a novel mechanistic pathway whereby NOLC1 suppresses p53 transcriptional functions by reducing its nuclear/plasma ratio, underscoring the significance of p53 nuclear levels in tumor suppression over total protein levels.

Weaknesses:

While the overall findings are commendable, there are specific areas that could benefit from further refinement. The authors have posited that NOLC1 suppresses p53- mediated ferroptosis; however, the mRNA levels of ferroptosis genes regulated by p53 have not been quantified, which is a critical gap in the current study. In Figure 4A, transmission electron microscopy (TEM) results are reported solely for the MGC-803 cell line. It would be beneficial to include TEM data for the MKN-45 cell line to strengthen the findings. The authors have proposed a link between NOLC1-mediated reduction in the p53 nuclear/plasma ratio and gastric cancer resistance, yet the correlation between this ratio and patient prognosis remains unexplored, which is a significant limitation in the context of clinical relevance.

Thanks very much for the kind comments and great suggestions. As suggested, recently studies have reported that CDKN1A (also called p21, a p53 transcriptional mediated protein) could promotes ferroptosis[13], the mRNA levels of ferroptosis genes regulated by p53 have were quantified in Fig. S8G-H. Moreover, we further proceed TEM imaging in MKN-45 cells, the result was consistent to MGC-803 cells, reflecting that NOLC1 has a broad spectrum of promoting drug resistance in gastric cancer. Also, recently studies have reported that p53 transcriptional active and p53 transcriptional inactive types include patients with intermediate prognosis and recurrence rates, with the p53-acvtie group showing better prognosis[14]. Considering p53 transcriptional activity depends on p53 nuclear accumulation, we assume that the low level of p53 nuclear/plasma may cause poor prognosis in gastric cancer. Meanwhile we will further collect enough samples and their prognostic information to analysis NOLC1-mediated reduction in the p53 nuclear/plasma ratio and gastric cancer resistance.

References

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(2) T. Matsuoka, M. Yashiro, Molecular Mechanism for Malignant Progression of Gastric Cancer Within the Tumor Microenvironment, IJMS 25 (2024) 11735. https://doi.org/10.3390/ijms252111735.

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Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

This study aimed at replicating two previous findings that showed (1) a link between prediction tendencies and neural speech tracking, and (2) that eye movements track speech. The main findings were replicated which supports the robustness of these results. The authors also investigated interactions between prediction tendencies and ocular speech tracking, but the data did not reveal clear relationships. The authors propose a framework that integrates the findings of the study and proposes how eye movements and prediction tendencies shape perception.

Strengths:

This is a well-written paper that addresses interesting research questions, bringing together two subfields that are usually studied in separation: auditory speech and eye movements. The authors aimed at replicating findings from two of their previous studies, which was overall successful and speaks for the robustness of the findings. The overall approach is convincing, methods and analyses appear to be thorough, and results are compelling.

Weaknesses:

Linking the new to the previous studies could have been done in more detail, and the extent to which results were replicated could have been discussed more thoroughly.

Eye movement behavior could have been presented in more detail and the authors could have attempted to understand whether there is a particular component in eye movement behavior (e.g., microsaccades) that drives the observed effects.

We would like to thank you for your time and effort in reviewing our work and we appreciate the positive comments!

We extended our manuscript, now providing intermediate results on individual prediction tendency, which can be compared to our results from Schubert et al., (2023).

Furthermore, we expanded our discussion now detailing the extent to which our results (do not) replicate the previous findings (e.g. differences in horizontal vs. vertical ocular speech tracking, lack of distractor tracking, link between ocular speech tracking and behavioral outcomes).

While we agree with the reviewer that it is an important and most interesting question, to what extent individual features of gaze behavior (such as microsaccades, blinks etc.) contribute to the ocular speech tracking effect, it is beyond the scope of the current manuscript. It will be methodologically and conceptually challenging to distinguish these features from one another and to relate them to diverse cognitive processes. We believe that a separate manuscript is needed to give these difficult questions sufficient space for new methodological approaches and control analyses. The primary goal of this manuscript was to replicate the findings of Gehmacher et al. (2024) using similar methods and to relate them to prediction tendencies, attention, and neural speech tracking. 

Reviewer #2 (Public review):

Summary

Schubert et al. recorded MEG and eye-tracking activity while participants were listening to stories in single-speaker or multi-speaker speech. In a separate task, MEG was recorded while the same participants were listening to four types of pure tones in either structured (75% predictable) or random (25%) sequences. The MEG data from this task was used to quantify individual 'prediction tendency': the amount by which the neural signal is modulated by whether or not a repeated tone was (un)predictable, given the context. In a replication of earlier work, this prediction tendency was found to correlate with 'neural speech tracking' during the main task. Neural speech tracking is quantified as the multivariate relationship between MEG activity and speech amplitude envelope. Prediction tendency did not correlate with 'ocular speech tracking' during the main task. Neural speech tracking was further modulated by local semantic violations in the speech material, and by whether or not a distracting speaker was present. The authors suggest that part of the neural speech tracking is mediated by ocular speech tracking. Story comprehension was negatively related to ocular speech tracking.

Strengths

This is an ambitious study, and the authors' attempt to integrate the many reported findings related to prediction and attention in one framework is laudable. The data acquisition and analyses appear to be done with great attention to methodological detail (perhaps even with too much focus on detail-see below). Furthermore, the experimental paradigm used is more naturalistic than was previously done in similar setups (i.e. stories instead of sentences).

Weaknesses

For many of the key variables and analysis choices (e.g. neural/ocular speech tracking, prediction tendency, mediation) it is not directly clear how these relate to the theoretical entities under study, and why they were quantified in this particular way. Relatedly, while the analysis pipeline is outlined in much detail, an overarching rationale and important intermediate results are often missing, which makes it difficult to judge the strength of the evidence presented. Furthermore, some analysis choices appear rather ad-hoc and should be made uniform and/or better motivated.

We would like to thank you very much for supporting our paper and your thoughtful feedback!

To address your concerns, that our theoretical entities as well as some of our analytical choices lack transparency, we expanded our manuscript in several ways:

(1) We now provide the intermediate results of our prediction tendency analysis (see new Figure 2 of our manuscript). These results are comparable to our findings from Schubert et al. (2023), demonstrating that on a group level there is a tendency to pre-activate auditory stimuli of high probability and illustrating the distribution of this tendency value in our subject population.

(2) We expanded our methods section in order to explain our analytical choices (e.g. why this particular entropy modulation paradigm was used to measure individual prediction tendency).

(3) We now provide an operationalisation of the terms “neural speech tracking” and “ocular speech tracking” at their first mention, to make these metrics more transparent to the reader.

(4) We are summarizing important methodological information ahead of each results section, in order to provide the reader with a comprehensible background, without the necessity to read through the detailed methods section. 

(5) We expanded our discussion section, with a special emphasis on relating the key variables of the current investigation to theoretical entities.

Reviewer #3 (Public review):

Summary:

In this paper, the authors measured neural activity (using MEG) and eye gaze while individuals listened to speech from either one or two speakers, which sometimes contained semantic incongruencies.

The stated aim is to replicate two previous findings by this group: (1) that there is "ocular speech tracking" (that eye-movements track the audio of the speech), (2) that individual differences in neural response to tones that are predictable vs. not-predictable in their pitch is linked to neural response to speech. In addition, here they try to link the above two effects to each other, and to link "attention, prediction, and active sensing".

Strengths:

This is an ambitious project, that tackles an important issue and combines different sources of data (neural data, eye-movements, individual differences in another task) in order to obtain a comprehensive "model" of the involvement of eye-movements in sensory processing.

The authors use many adequate methods and sophisticated data-analysis tools (including MEG source analysis and multivariate statistical models) in order to achieve this.

Weaknesses:

Although I sympathize with the goal of the paper and agree that this is an interesting and important theoretical avenue to pursue, I am unfortunately not convinced by the results and find that many of the claims are very weakly substantiated in the actual data.

Since most of the analyses presented here are derivations of statistical models and very little actual data is presented, I found it very difficult to assess the reliability and validity of the results, as they currently stand. I would be happy to see a thoroughly revised version, where much more of the data is presented, as well as control analyses and rigorous and well-documented statistical testing (including addressing multiple comparisons).

We thank you for your thoughtful feedback. We appreciate your concerns and will address them below in greater detail.

These are the main points of concern that I have regarding the paper, in its current format.

(1) Prediction tendencies - assessed by listening to sequences of rhythmic tones, where the pitch was either "predictable" (i.e., followed a fixed pattern, with 25% repetition) or "unpredictable" (no particular order to the sounds). This is a very specific type of prediction, which is a general term that can operate along many different dimensions. Why was this specific design selected? Is there theoretical reason to believe that this type of prediction is also relevant to "semantic" predictions or other predictive aspects of speech processing?

Theoretical assumptions and limitations of our quantification of individual prediction tendency are now shortly summarized in the first paragraph of our discussion section. With this paradigm we focus on anticipatory “top-down” predictions, whilst controlling for possibly confounding “bottom-up” processes. Since this study aimed to replicated our previous work we chose the same entropy-modulation paradigm as in other studies from our group (e.g. Demarchi et al. 2019, Schubert et al. 2023;2024, Reisinger et al. 2024), which has proven to give reproducible findings of feature-specific preactivations of sounds in a context of low entropy. One advantage of this design is that it gives us the opportunity to directly compare the processing of “predictable” and “unpredictable” sounds of the same frequency in a time-resolved manner (this argument is now also included in the Methods section).

Regarding the question to what extent this type of prediction might also be relevant to “semantic” predictions we would like to refer to our previous study (Schubert et al., 2023), where we explicitly looked at the interaction between individual prediction tendency and encoding of semantic violations in the cortex. (In short, there we found a spatially dissociable interaction effect, indicating an increased encoding of semantic violations that scales with prediction tendency in the left hemisphere, as well as a disrupted encoding of semantic violations for individuals with stronger prediction tendency in the right hemisphere.) We did not aim to replicate all our findings in the current study, but instead we focused on merging the most important results from two independent phenomena in the domain of speech processing and bringing them into a common framework. However, as now stated in our discussion, we believe that “predictions are directly linked to the interpretation of sensory information. This interpretation is likely to occur at different levels along the cognitive (and anatomical) hierarchy…” and that “this type of prediction is relevant for acoustic processing such as speech and music, whose predictability unfolds over time.”

(2) On the same point - I was disappointed that the results of "prediction tendencies" were not reported in full, but only used later on to assess correlations with other metrics. Even though this is a "replication" of previous work, one would like to fully understand the results from this independent study. On that note, I would also appreciate a more detailed explanation of the method used to derive the "prediction tendency" metric (e.g, what portion of the MEG signal is used? Why use a pre-stimulus and not a post-stimulus time window? How is the response affected by the 3Hz steady-state response that it is riding on? How are signals integrated across channels? Can we get a sense of what this "tendency" looks like in the actual neural signal, rather than just a single number derived per participant (an illustration is provided in Figure 1, but it would be nice to see the actual data)? How is this measure verified statistically? What is its distribution across the sample? Ideally, we would want enough information for others to be able to replicate this finding).

We now included a new figure (similar to Schubert et al. 2023) showing the interim results of the “prediction tendency” effect as well as individual prediction tendency values of all subjects.

Furthermore we expanded the description of the “prediction tendency” metric in the Methods section, where we explain our analytical choices in more detail. In particular we used a pre-stimulus time window in order to capture “anticipatory predictions”. The temporally predictably design gives us the opportunity to capture this type of predictions. The integration across channels is handled by the multivariate pattern analysis (MVPA), which inherently integrates multidimensional data (as mentioned in the methods section we used data from 102 magnetometers) and links it to (in this case) categorical information.

(3) Semantic violations - half the nouns ending sentences were replaced to create incongruent endings. Can you provide more detail about this - e.g., how were the words selected? How were the recordings matched (e.g., could they be detected due to audio editing?)? What are the "lexically identical controls that are mentioned"? Also, is there any behavioral data to know how this affected listeners? Having so many incongruent sentences might be annoying/change the nature of listening. Were they told in advance about these?

We expanded the Methods section and included the missing information: 

“We randomly selected half of the nouns that ended a sentence (N = 79) and replaced them with the other half to induce unexpected semantic violations. The swap of nouns happened in the written script before the audio material was recorded in order to avoid any effects of audio clipping. Narrators were aware of the semantic violations and had been instructed to read out the words as normal. Consequently all target words occurred twice in the text, once in a natural context (serving as lexical controls) and once in a mismatched context (serving as semantic violations) within each trial, resulting in two sets of lexically identical words that differed greatly in their contextual probabilities (see Figure 1F for an example). Participants were unaware of these semantic violations.” Since we only replaced 79 words with semantic violations in a total of ~ 24 minutes of audio material we believe that natural listening was not impaired. In fact none of the participants mentioned to have noticed the semantic violations during debriefing (even though they had an effect on speech tracking in the brain). 

(4) TRF in multi-speaker condition: was a univariate or multivariate model used? Since the single-speaker condition only contains one speech stimulus - can we know if univariate and multivariate models are directly comparable (in terms of variance explained)? Was any comparison to permutations done for this analysis to assess noise/chance levels?

For mTRF models it depends on the direction (“encoding” vs. “decoding”) whether or not the model is comparable to a univariate model. In our case of an encoding model the TRFs are fitted to each MEG channel independently. This gives us the possibility to explore the effect over different areas (whereas a multivariate “decoding” model would result in only one speech reconstruction value).

In both conditions (single and multi speaker) a single input feature (the envelope of the attended speech stream) was used. Of course it would be possible to fit the model to use a multivariate encoding model, predicting the brain’s response to the total input of sounds. This would, however, target a slightly different question than ours as we aimed to investigate how much of the attended speech is tracked.

Regarding your suggestion of a comparison to permutations to assess noise levels we would like to point out that we chose the same methodological approach as in our previous studies, that we aimed to replicate here. Indeed in these original studies no permuted versions (with exception of the mediation analysis where comparing a model with an additional input predictor to a single predictor model would not result in a fair comparison) have been used. We conducted the mTRF approach considering the guidelines of Crosse et al. (2016) to the best of our knowledge and in accordance with similar studies in this field.

Crosse, M. J., Di Liberto, G. M., Bednar, A., & Lalor, E. C. (2016). The multivariate temporal response function (mTRF) toolbox: a MATLAB toolbox for relating neural signals to continuous stimuli. Frontiers in human neuroscience, 10, 604.

(5) TRF analysis at the word level: from my experience, 2-second segments are insufficient for deriving meaningful TRFs (see for example the recent work by Mesik & Wojtczak). Can you please give further details about how the analysis of the response to semantic violations was conducted? What was the model trained on (the full speech or just the 2-second long segments?) Is there a particular advantage to TRFs here, relative - say - to ERPs (one would expect a relatively nice N400 response, not)? In general, it would be nice to see the TRF results on their own (and not just the modulation effects).

We fully agree with the reviewers statement that 2-second segments would have been too short to derive meaningful TRFs. To investigate the effect of semantic violations, we used the same TRFs trained on the whole dataset (with 4-fold cross validation). The resulting true as well as the predicted data was segmented into single word epochs of 2 seconds. We selected semantic violations as well as their lexically identical controls and correlated true with predicted responses for every word. Thus, we conducted the same analysis as for the overall encoding effect, focusing on only part of the data. We have reformulated the Methods section accordingly to clear up this misunderstanding. Since the TRFs are identical to the standard TRFs from the overall neural speech tracking, they are not informative to the semantic violation effect. However, since the mTRF approach is the key method throughout the manuscript (and our main focus is not on the investigations of brain responses to semantic violations) we have favoured this approach over the classical ERF analysis. 

(6) Another related point that I did not quite understand - is the dependent measure used for the regression model "neural speech envelope tracking" the r-value derived just from the 2sec-long epochs? Or from the entire speech stimulus? The text mentions the "effect of neural speech tracking" - but it's not clear if this refers to the single-speaker vs. twospeaker conditions or to the prediction manipulation. Or is it different in the different analyses? Please spell out exactly what metric was used in each analysis.

As suggested we now provide a clear definition of each dependent metric for each analysis.

“Neural speech tracking” refers to the correlation coefficients between predicted and true brain responses from the aforementioned encoding model, trained and tested on the whole audio material within condition (single vs. multi-speaker).

Recommendations for the authors:

Reviewing Editor Comments:

The reviewers have provided a number of recommendations to improve the manuscript, particularly requesting that more data be reported, with an emphasis on the measurements themselves (eye movements and TRFs) rather than just the numerical outputs of mathematical models.

We appreciate all the reviewers' and editor’s comments and effort to improve our manuscript. In the revised version we provide interim findings and missing data, updated figures that include an intuitive illustration of the metrics (such as TRFs), and a thoroughly revised discussion section where we focus on the relationship between our observed quantities and theoretical entities. We now offer operationalized definitions of the relevant concepts (“prediction tendency”, “active ocular sensing” and “selective attention”) and suggest how these entities might be related in the context of speech processing, based on the current findings. We are confident that this revision has improved the quality of our paper a lot and we are grateful for all the feedback and suggestions. 

Reviewer #1 (Recommendations for the authors):

(1) Participants had to fixate throughout the tasks. How did the authors deal with large eye movements that violated the instructed fixation?

As described in the Methods section: “Participants were instructed to look at a black fixation cross at the center of a grey screen.” This instruction was not intended to enforce strict fixation but rather to provide a general reference point, encouraging participants to keep their gaze on the grey screen and avoid freely scanning the room or closing their eyes. Unlike trial-based designs, where strict fixation is feasible due to shorter trial durations, this approach did not impose rigid fixation requirements. Consequently, the threshold for "instruction violation" was inherently more flexible, and no additional preprocessing was applied to the gaze vectors.

Fixating for such an extended period of time (1.5 hours?) is hard. Did fixation behavior change over time? Could (fixation) fatigue affect the correlations between eye movements and speech tracking? For example, fatigued participants had to correct their fixation more often and this drives, in part, the negative correlation with comprehension?

Yes, participants spent approximately 2 hours in the MEG, including preparation time (~30 minutes). However, participants were given opportunities to rest their eyes between different parts and blocks of the experiment (e.g., resting state, passive listening, and audiobook blocks), which should help mitigate fatigue to some extent.

That said, we agree that it is an intriguing idea that fatigue could drive the ocular speech tracking effect, with participants potentially needing to correct their gaze more as the experiment progresses. However, our analysis suggests this is unlikely for several reasons:

(1) Cross-validation in encoding models: Ocular speech tracking effects were calculated using a 4-fold cross-validation approach (this detail has now been added to the Methods section; please see our response to public review #3). This approach reduces the influence of potential increases in gaze corrections over time, as the models are trained and validated on independent data splits.  Moreover, if there were substantial differences in underlying response magnitudes between folds - for instance, between the first and fourth fold - this would likely compromise the TRF's ability to produce valid response functions for predicting the left-out data. Such a scenario would not result in significant tracking, further supporting the robustness of the observed effects.

(2) TRF time-course stability: If fatigue were driving increased gaze corrections, we would expect this to be reflected in a general offset (capturing the mean difference between folds) in the TRF time-courses shown in Figure 4 (right panel). However, no such trend / offset is evident.

(3) Comparison of eye movement data: To directly investigate this possibility, we compared the amount of total eye movements between the first and last blocks for both the single and multi-speaker conditions. Total movement was calculated by first calculating the differences in pixel values between consecutive eye positions on both the x- and y-axes. The Euclidean distance was then computed for each difference, providing a measure of movement between successive time points. Summing these distances yielded the total movement for each block. Statistical analysis was performed separately for the single speaker (ASS) and multi-speaker (AMS) conditions. For each condition, paired comparisons were made between the first and last blocks (we resorted to non-parametric tests, if assumptions of normality were violated):

For the single speaker condition (ASS), the normality assumption was not satisfied (p≤0.05p, Kolmogorov-Smirnov test). Consequently, a Wilcoxon signedrank test was conducted, which revealed no significant difference in total movements between the first and last blocks (z=−1.330, p=0.184). For the multi-speaker condition (AMS), the data met the normality assumption (p>0.05), allowing the use of a paired t-test. The results showed no significant difference in total movements between the first and last blocks (t=−0.184, p=0.855).

The results are visualized in a bar plot (see below), where individual data points are displayed alongside the mean and standard error for each block. Statistical annotations indicate that neither condition demonstrated significant differences between the blocks. These findings suggest that total eye movements remained stable across the experimental conditions, regardless of whether participants were exposed to a single or multiple speakers.

Author response image 1.

(4) Behavioral responses: Participants’ behavioral responses did not indicate any decrease in comprehensibility for later blocks compared to earlier ones. Specifically, a comparison of comprehension scores between the first and last blocks revealed no significant difference in either the single-speaker condition (ASS; Wilcoxon signed-rank test Z=−0.5911, p=0.5545) or the multi-speaker condition (AMS; Wilcoxon signed-rank test: Z=0.5018, p=0.6158). These findings suggest that participants maintained consistent levels of comprehension throughout the experiment, regardless of the condition or block order. The results are visualized in a bar plot (see below), where individual data points are displayed alongside the mean and standard error for each block. Statistical annotations indicate that neither condition demonstrated significant differences between the blocks.

Author response image 2.

Together, these factors suggest that fatigue is unlikely to be a significant driver of the ocular speech tracking effects observed in this study.

(2) The authors should provide descriptive statistics of fixation behavior /fixational eye movements. What was the frequency and mean direction of microsaccades, do they follow the main sequence, etc., quantify drift and tremor?

Thank you for their suggestion regarding descriptive statistics. To address this, we computed the rates of microsaccades (which were extracted using the microsaccade detection algorithm as proposed in Liu, B., Nobre, A. C. & van Ede, F. Functional but not obligatory link between microsaccades and neural modulation by covert spatial attention. Nat. Commun. 13, 3503 (2022)) and fixations as these metrics are directly relevant to our study and the requests above.

Microsaccade Rates:

- Single speaker Condition: Mean = 2.306 Hz, SD = 0.363 Hz. ○ Multi speaker: Mean = 2.268 Hz, SD = 0.355 Hz.

Fixation Rates:

- Single speaker Condition: Mean = 2.858 Hz, SD = 1.617 Hz. ○ Multi speaker Condition: Mean = 2.897 Hz, SD = 1.542 Hz.

These values fall within the expected ranges reported in the literature (fixation rates: 2– 4 Hz, microsaccade rates: ~0.5–2.5 Hz) and serve as a sanity check, confirming the plausibility of our eye-tracking data. Regarding the reviewer’s request for additional metrics (e.g., microsaccade direction, main sequence analysis, drift, and tremor), extracting these features would require advanced algorithms and analyses not supported by our current preprocessing pipeline or dataset. We hope that the provided metrics, which were the main focus of this study, serve as a sufficient sanity check and highlight the robustness of our data.

Related to this, I am wondering whether microsaccades are the feature that drives speech tracking.

This is an important and pressing question that we aim to address in future publications. Currently, our understanding - and the reason microsaccades and blinks are not analysed in this manuscript - is limited by methodological constraints. Specifically, microsaccades are binary response vectors, which are not compatible with TRF analyses. Addressing this would require adapting future models to handle timecontinuous binary response data or exploring alternative approaches, such as regression-based ERFs (for example as in Heilbron et al. 2022). As the primary goal of this manuscript was to replicate the findings of Gehmacher et al. (2024) using similar methods and to integrate these findings into an initial unified framework, we did not investigate additional eye movement features here. However, we agree that microsaccades (and also blinks, see below) likely contribute, at least in part, to the observed ocular speech tracking effects, and we now suggest this in the Discussion:  

“Relatedly, it remains an open question whether microsaccades are a key feature driving ocular speech tracking. However, our current study does not analyze microsaccades due to methodological constraints: microsaccades are binary response vectors, which are incompatible with TRF analyses used here. Addressing this would require adapting models to handle time-continuous binary response data or potentially exploring alternative approaches, such as regression-based ERFs (e.g., as in Heilbron et al., 2022). While these limitations preclude microsaccade analysis in the current study, we hypothesize that they could enhance temporal precision and selectively amplify relevant sensory input, supporting auditory perception. Future studies should explore this possibility to uncover the specific contributions of microsaccades to speech tracking.”

(3) Can the authors make sure that interpolated blinks did not drive any of the effects? Can interpolated blink trials be excluded?

Using continuous audiobooks as stimuli meant that we could not exclude blink periods from the analysis without introducing substantial continuation artifacts in the TRF analysis. Importantly, the concept of covert motor routines and active sensing suggests that participants engage more strongly in motor routines - including ocular behaviors such as microsaccades and blinks - during tasks like speech tracking. These motor routines are inherently tied to individual gaze patterns, making microsaccades and blinks correlated with other ocular behaviors. This complicates efforts to disentangle their individual contributions to the observed ocular speech tracking effects.

Engagement in these motor routines, as posited by active sensing, would naturally load onto various viewing behaviors, further intertwining their roles.

Even if we were to examine correlations, such as the amount of blinks with the ocular speech tracking effect, it is unlikely to provide a clearer understanding due to these inherent overlaps. The methodological and conceptual challenge lies in distinguishing these features from one another and understanding their respective roles in driving the observed effects.

However, the aim of this manuscript was not to dissect the ocular speech tracking effect in greater detail, but rather to relate it - based on similar analytical choices as in Gehmacher et al - to prediction tendencies, attention, and neural speech tracking. While it will be crucial in future work to differentiate these patterns and their connections to diverse cognitive processes, it is beyond the scope of this study to address all these questions comprehensively.

We acknowledge that eye movements, including microsaccades and blinks (however, see challenges for this in response 2), remain underexplored in many experimental paradigms. Their interplay with cognitive processes - such as attention, prediction, and sensory integration - will undoubtedly be an important focus for future studies. 

(4) Could the authors provide more details on how time shuffling was done for the eyemovement predictor, and include a circularly shifted version (or a version that does not destroy temporal contiguity) in their model comparisons? Some types of shuffling can result in unrealistic time series, which would end up in an unfair comparison with the model that has the real eye movement traces as predictors.

We thank the reviewer for their insightful question regarding the time-shuffling procedure for the eye-movement predictor and for suggesting the inclusion of a circularly shifted version in our model comparisons. Below, we provide further details about our approach and the rationale behind it:

(1) Random Shuffling: In our analysis, the eye-movement predictor was randomly shuffled over time, meaning that individual samples were randomly replaced. This method completely disrupts the temporal structure of the signal, providing a null model that directly tests whether the temporal mediation observed is due to the specific temporal relationship between ocular movements and envelope tracking.

(2) Circular Shifting: While circular shifting maintains temporal contiguity, it introduces certain challenges in the context of TRF analysis. Specifically:

- Adaptation to Shifts: The TRF model could adapt to the introduced shift, potentially reducing the validity of the null comparison.

- Similarity due to Repetition: The broadband envelope exhibits strong repetitive patterns over time, such as rhythms inherent to speech. Circular shifting can therefore produce predictors that are very similar to the original signal. As a result, this similarity may lead to null distributions that do not adequately disrupt the temporal mediation we aim to test, making it less robust as a control.

(3) Rationale for Random Shuffling: The primary goal of our mediation analysis is to determine whether there is a temporal mediation of envelope tracking by ocular movements. By deliberately destroying the temporal structure through random shuffling, we ensure that the null model tests for the specific temporal relationship that is central to our hypothesis. Circularly shifted predictors, on the other hand, may partially preserve temporal dependencies, making them less suitable for this purpose.

In summary, while circular shifting is a valuable approach in other contexts, it is less appropriate for the specific goals of this study. We hope this explanation clarifies our methodological choices and demonstrates their alignment with the aims of our analysis.

(5) Replication: I want to point out that it is great that the previous findings were in principle replicated. However, I would like to suggest a more nuanced evaluation of the replication:

a) Instead of a (direct) replication, the present study should be called a 'conceptual replication', since modifications in design and procedure were made.

Thank you very much for this suggestion! We now use the term ‘conceptual replication’ throughout the manuscript.

b) Not all the findings from the Gehmacher et al., 2024 study were replicated to a full extent:

Did the authors find indications of a vertical vs. horizontal tracking difference in the Gehmacher 2024 data? Could they check this in the Gehmacher 2024 data?

The findings for horizontal and vertical gaze tracking in Gehmacher et al. (2024) are detailed in the supplementary material of that publication. Both single-speaker and multi-speaker target conditions showed significant speech tracking effects in both horizontal and vertical directions. However, there was a slightly stronger tracking effect for the single-speaker condition in the vertical direction. Due to the highly predictable structure of words in Gehmacher et al. effects here were probably overall boosted as compared to continuous audiobook listening, likely leading to the differentiation of horizontal and vertical gaze. See figures in Gehmacher et al. supplementary file for reference.

c) Another difference between their previous and this study is the non-existent tracking of the multi-speaker distractor in this study. The authors should point this out clearly in the discussion and potentially provide an explanation.

Thank you for highlighting this point! We now address this in the discussion:

“Importantly, in contrast to Gehmacher et al. (2024), we did not observe ocular tracking of the multi-speaker distractor in this study. This difference is likely attributable to the simplistic single-trial, 5-word task structure in Gehmacher et al., which resulted in high temporal overlap between the target and distractor speech streams and likely drove the significant distractor-tracking effects observed in that study. The absence of such an effect during continuous listening in our study suggests that ocular tracking is indeed more specific to selective attention.”

Minor:

(1) I was a little surprised to not see an indication of eyes/eye movements in Figure 6. The intention of the authors might have been to create a general schematic illustration, but I find this a bit misleading. This paper provides nice evidence for a specific ocular effect in speech tracking. There is, to my knowledge, no indication that speech would be influenced by different kinds of active sensing (if there are, please include them in the discussion). Given that the visuomotor system is quite dominant in humans, it might actually be the case that the speech tracking the authors describe is specifically ocular.

Taking into account all the reviewers' remarks on the findings and interpretations, we have updated this figure (now Fig. 7) in the manuscript to make it more specific and aligned with the revised discussion section. Throughout the manuscript, we now explicitly refer to active ocular sensing in relation to speech processing and have avoided the broader term 'active sensing' in this context. We hope these revisions address the concerns raised.

(2) I find the part in the discussion (page 2, last paragraph) on cognitive processes hard to follow. I don't agree that 'cognitive processes' are easily separable from any of the measured responses (eye and brain). Referring to the example they provide, there is evidence that eye movements are correlated with brain activity that is correlated with memory performance. How, and more importantly, why would one separate those?

Thank you for raising this important point. We have carefully considered your comments, particularly regarding the interplay between cognitive processes and measured responses (eye and brain), as well as the challenge of conceptually separating them. Additionally, we have incorporated Reviewer #2's query (13) into a unified and complementary reasoning. In response, we have rewritten the relevant paragraph in the discussion to provide a clearer and more detailed explanation of how ocular and neural responses contribute to speech processing in an interdependent manner. We hope this revision addresses your concerns and offers a more precise and coherent discussion on this topic:

“Despite the finding that eye movements mediate neural speech tracking, the behavioural relevance for semantic comprehension appears to differ between ocular and neural speech tracking. Specifically, we found a negative association between ocular speech tracking and comprehension, indicating that participants with lower comprehension performance exhibited increased ocular speech tracking. Interestingly, no significant relationship was observed between neural tracking and comprehension.

In this context, the negative association between ocular tracking and comprehension might reflect individual differences in how participants allocate cognitive resources. Participants with lower comprehension may rely more heavily on attentional mechanisms to process acoustic features, as evidenced by increased ocular tracking. This reliance could represent a compensatory strategy when higher-order processes, such as semantic integration or memory retrieval, are less effective. Importantly, our comprehension questions (see Experimental Procedure) targeted a broad range of processes, including intelligibility and memory, suggesting that this relationship reflects a trade-off in resource allocation between low-level acoustic focus and integrative cognitive tasks.

Rather than separating eye and brain responses conceptually, our analysis highlights their complementary contributions. Eye movements may enhance neural processing by increasing sensitivity to acoustic properties of speech, while neural activity builds on this foundation to integrate information and support comprehension. Together, these systems form an interdependent mechanism, with eye and brain responses working in tandem to facilitate different aspects of speech processing.

This interpretation is consistent with the absence of a difference in ocular tracking for semantic violations (e.g., words with high surprisal versus lexically matched controls), reinforcing the view that ocular tracking primarily reflects attentional engagement with acoustic features rather than direct involvement in semantic processing. This aligns with previous findings that attention modulates auditory responses to acoustic features (e.g., Forte et al., 2017), further supporting the idea that ocular tracking reflects mechanisms of selective attention rather than representations of linguistic content.

Future research should investigate how these systems interact and explore how ocular tracking mediates neural responses to linguistic features, such as lexical or semantic processing, to better understand their joint contributions to comprehension.”.  

(3) Attention vs. predictive coding. I think the authors end up with an elegant description of the observed effects, "as an "active sensing" mechanism that implements the attentional optimization of sensory precision." However, I feel the paragraph starts with the ill-posed question "whether ocular speech tracking is modulated not by predictive, but other (for example attentional) processes". If ocular tracking is the implementation of a process (optimization of sensory precision, aka attention), how could it be at the same time modulated by that process? In my opinion, adding the notion that there is a modulation by a vague cognitive concept like attention on top of what the paper shows does not improve our understanding of how speech tracking in humans works.

Thank you for raising this point. We agree that it is critical to clarify the relationship between ocular speech tracking, attention, and predictive processes, and we appreciate the opportunity to refine this discussion.  

To avoid the potential confusion that active ocular sensing represents on the one hand an implementation of selective attention on the other it seems to be modulated by it, we now use  the formulation “ocular speech tracking reflects attentional mechanisms rather than predictive processes.”

To address your concern that the conceptualization of attention seems rather vague, we have revised the whole paragraph in order to redefine the theoretical entities in question (including selective attention) and to provide a clearer and more precise picture (see also our revised version of Fig. 6, now Fig. 7). We now focus on highlighting the distinct yet interdependent roles of selective attention and individual prediction tendencies for speech tracking.:

“With this speculative framework we attempt to describe and relate three important phenomena with respect to their relevance for speech processing: 1) “Anticipatory predictions” that are created in absence of attentional demands and contain probabilistic information about stimulus features (here, inferred from frequency-specific pre-activations during passive listening to sound sequences). 2) “Selective attention” that allocates resources towards relevant (whilst suppressing distracting) information (which was manipulated by the presence or absence of a distractor speaker). And finally 3) “active ocular sensing”, which refers to gaze behavior that is temporally aligned to attended (but not unattended) acoustic speech input (inferred from the discovered phenomenon of ocular speech tracking). We propose that auditory inflow is, at a basic level, temporally modulated via active ocular sensing, which “opens the gates” in the sensory periphery at relevant timepoints. How exactly this mechanism is guided (for example where the information about crucial timepoints comes from, if not from prediction, and whether it requires habituation to a speechstream etc.) is yet unclear. Unlike predictive tendencies, active ocular sensing appears to reflect selective attention, manifesting as a mechanism that optimizes sensory precision. Individual differences with respect to anticipatory predictions on the other hand, seem to be independent from the other two entities, but nevertheless relevant for speech processing. We therefore support the notion that representational content is interpreted based on prior probabilistic assumptions. If we consider the idea that “a percept” of an (auditory) object is actually temporally and spatially distributed (across representational spacetime - see Fig. 7), the content of information depends on where and when it is probed (see for example Dennett, 1991 for similar ideas on consciousness). Having to select from multiple interpretations across space and time requires a careful balance between the weighting of internal models and the allocation of resources based on current goals. We suggest that in the case of speech processing, this challenge results in an independent adaptation of feature-based precision-weighting by predictions on the one hand and temporal precision-weighting by selective attention on the other.”

Reviewer #2 (Recommendations for the authors):

My main recommendation is outlined in the Weaknesses above: the overarching rationale for many analysis choices should be made explicit, and intermediate results should be shown where appropriate, so the reader can follow what is being quantified and what the results truly mean. Specifically, I recommend to pay attention to the following (in no particular order):

(1) Define 'neural speech tracking' early on. (e.g.: 'The amount of information in the MEG signal that can multivariately be explained by the speech amplitude envelope.' (is that correct?))

Thank you for pointing out that this important definition is missing. It is now defined at the first mention in the Introduction as follows: “Here (and in the following) “neural speech tracking” refers to a correlation coefficient between actual brain responses and responses predicted from an encoding model based solely on the speech envelope”.

(2) Same for 'ocular speech tracking'. Here even reading the Methods does not make it unambiguous how this term is used.

It is now defined at the first mention in the Introduction as follows: “Ocular speech tracking” (similarly to “neural speech tracking” refers to the correlation coefficient between actual eye movements and movements predicted from an encoding model based on the speech envelope”.

In addition also define both (neural and ocular speech tracking) metrics in the Methods Section.

(3) Related to this: for ocular speech tracking, are simply the horizontal and vertical eye traces compared to the speech envelope? If so, this appears somewhat strange: why should the eyes move more rightward/upward with a larger envelope? And the direction here depends on the (arbitrary) sign of right = positive, etc. (It would make more sense to quantify 'amount of movement' in some way, but if this is done, I missed it in Methods.)

Thank you for your insightful comments. You are correct that the horizontal and vertical traces were used for ocular speech tracking, and no additional details were included in the Methods. While we agree that the observed rightward/upward movement may seem unusual, this pattern is consistent with previous findings, including those reported in Gehmacher et al. (2024). In that study, we discussed how ocular speech tracking could reflect a broader engagement of the motor system during speech perception. For example, we observed a general right-lateralized gaze bias when participants attended to auditory speech, which we hypothesized might resemble eye movements during text reading, with a similar temporal alignment (~200 ms). We also speculated that this pattern might differ in cultures that read text from right to left.

We appreciate your suggestion to explore alternative methods for quantifying gaze patterns, such as the "amount of movement" or microsaccades. While these approaches hold promise for future studies, our primary aim here was to replicate previous findings using the same signal and analysis methods to establish a basis for further exploration.  

(4) In the Introduction, specifically blink-related ocular activity is mentioned as being related to speech tracking (for which a reference is, incidentally, missing), while here, any blink-related activity is excluded from the analysis. This should be motivated, as it appears in direct contradiction.

Thank you for pointing this out. The mention of blink-related ocular activity in the Introduction refers to findings by Jin et al. (2018), where such activity was shown to align with higher-order syntactic structures in artificial speech. We have now included the appropriate reference for clarity.

While Jin et al. focused on blink-related activity, in the present study, we focused on gaze patterns to investigate ocular speech tracking, replicating findings from

Gehmacher et al. (2024). This approach was motivated by our goal to validate previous results using the same methodology. Importantly to this point, the exclusion of blinks in our analysis was due to methodological constraints of TRF analysis, which requires a continuous response signal; blinks, being discrete and artifact-prone, are incompatible with this approach.

To address your concern, we revised the Introduction to clarify this distinction and provide explicit motivation for focusing on gaze patterns. It now reads:

“Along these lines, It has been shown that covert, mostly blink related eye activity aligns with higher-order syntactic structures of temporally predictable, artificial speech (i.e. monosyllabic words; Jin et al, 2018). In support of ideas that the motor system is actively engaged in speech perception (Galantucci et al., 2006; Liberman & Mattingly, 1985), the authors suggest a global entrainment across sensory and (oculo)motor areas which implements temporal attention. 

In another recent study from our lab (Gehmacher et al., 2024), we showed that eye movements continuously track intensity fluctuations of attended natural speech, a phenomenon we termed ocular speech tracking. In the present study, we focused on gaze patterns rather than blink-related activity, both to replicate findings from

Gehmacher et al. (2024) and because blink activity is unsuitable for TRF analysis due to its discrete and artifact-prone nature. Hence, “Ocular speech tracking” (similarly to “neural speech tracking” refers to the correlation coefficient between actual eye movements and movements predicted from an encoding model based on the speech envelope.”

Jin, P., Zou, J., Zhou, T., & Ding, N. (2018). Eye activity tracks task-relevant structures during speech and auditory sequence perception. Nature communications, 9(1), 5374.

(5) The rationale for the mediation analysis is questionable. Let speech envelope = A, brain activity = B, eye movements = C. The authors wish to claim that A -> C -> B. But it is equally possible that A -> B -> C. They reflect on this somewhat in Discussion, but throughout the rest of the paper, the mediation analysis is presented as specifically testing whether A -> B is mediated by C, which is potentially misleading.

Indeed we share your concern regarding the directionality of the relationships in the mediation analysis. Our choice of ocular movements as a mediator was motivated by the fact that the relationship between acoustic speech and neural activity is well established, as well as previous results indicating that oculomotor activity contributes to cognitive effects in auditory attention (Popov et al., 2022). 

Indeed, here we treat both interpretations (“ocular movements contribute to neural speech tracking” versus “neural activity contributes to ocular speech tracking”) as equal.  We now emphasise this point in our discussion quite thoroughly:

“It is important to note that our current findings do not allow for inference on directionality. Our choice of ocular movements as a mediator was motivated by the fact that the relationship between acoustic speech and neural activity is well established, as well as previous results indicating that oculomotor activity contributes to cognitive effects in auditory attention (Popov et al., 2022). However, an alternative model may suggest that neural activity mediates the effect of ocular speech tracking. Hence, it is possible that ocular mediation of speech tracking may reflect a) active (ocular) sensing for information driven by (top-down) selective attention or b) improved neural representations as a consequence of temporally aligned increase of sensory gain or c) (not unlikely) both. In fact, when rejecting the notion of a single bottom-up flow of information and replacing it with a model of distributed parallel and dynamic processing, it seems only reasonable to assume that the direction of communication (between our eyes and our brain) will depend on where (within the brain) as well as when we look at the effect. Thus, the regions and time-windows reported here should be taken as an illustration of oculo-neural communication during speech processing rather than an attempt to "explain" neural speech processing by ocular movements.”

(6) The mediation analysis can be improved by a proper quantification of the effect (sizes or variance explained). E.g. how much % of B is explained by A total, and how much of that can in turn be explained by C being involved? For drawing directional conclusions perhaps Granger causality could be used.

In Figure 4 (now Figure 5) of our manuscript we use standardized betas (which correspond to effect sizes) to illustrate the mediation effect. With the current mTRF approach it is however not possible (or insightful) to compare the variance explained. It is reasonable to assume that variance in neural activity will be explained better when including oculomotor behavior as a second predictor along with acoustic simulation. However this increase gives no indication to what extent this oculomotor behavior was task relevant or irrelevant (since all kinds of “arbitrary” movements will be captured with brain activity and therefore lead to an increase in variance explained). For this reason we chose to pursue the widely accepted framework of mediation (Baron & Kenny, 1986). This (correlational) approach is indeed limited in its interpretations (see prev. response), however the goal of the current study was to replicate and illustrate the triad relationship of acoustic speech input, neural activity and ocular movements with no particular hypotheses on directionality.

(7) Both prediction tendency and neural speech tracking depend on MEG data, and thus on MEG signal-to-noise ratio (SNR). It is possible some participants may have higher SNR recordings in both tasks, which may result in both higher (estimated) prediction tendency and higher (estimated) speech tracking. This would result in a positive correlation, as the authors observe. This trivial explanation should be ruled out, by quantifying the relative SNR and testing for the absence of a mediation here.

We agree that for both approaches (MVPA and mTRF models) individual MEG SNR plays an important role. This concern has been raised previously and addressed in our previous manuscript (Schubert et al., 2023). First, it should be noted that our prediction tendency value is the result of a condition contrast (rather than simple decoding accuracy) which compensates for the influence of subject specific signal-to-noise ratio (as no vacuous difference in SNR is to be expected between conditions). Second, in our previous study we also used frequency decoding accuracy as a control variable to correlate with speech tracking variables of interest and found no significant effect.

(8) Much of the analysis pipeline features temporal response functions (TRFs). These should be shown in a time-resolved manner as a key intermediate step.

We now included the Neural Speech tracking TRFs into the Figure (now Figure 3).

(9) Figure 2 shows much-condensed results from different steps in the pipeline. If I understand correctly, 2A shows raw TRF weights (averaged over some time window?), while 2B-F shows standardized mean posterior regressor weights after Bayesian stats? It would be very helpful to make much more explicit what is being shown here, in addition to showing the related TRFs.

Thank you for pointing this out! The figure description so far has been indeed not very insightful on this issue. We now adapted the caption and hope this clarifies the confusion: “ Neural speech tracking is related to prediction tendency and word surprisal, independent of selective attention. A) Envelope (x) - response (y) relationships are estimated using deconvolution (Boosting). The TRF (filter kernel, h) models how the brain processes the envelope over time. This filter is used to predict neural responses via convolution. Predicted responses are correlated with  actual neural activity to evaluate model fit and the TRF's ability to capture response dynamics. Correlation coefficients from these models are then used as dependent variables in Bayesian regression models. (Panel adapted from Gehmacher et al., 2024b). B) Temporal response functions (TRFs) depict the time-resolved neural tracking of the speech envelope for the single speaker and multi speaker target condition, shown here as absolute values averaged across channels. Solid lines represent the group average. Shaded areas represent 95% Confidence Intervals. C–H) The beta weights shown in the sensor plots are derived from Bayesian regression models in A). For Panel C, this statistical model is based on correlation coefficients computed from the TRF models (further details can be found in the Methods Section). C) In a single speaker condition, neural tracking of the speech envelope was significant for widespread areas, most pronounced over auditory processing regions. D) The condition effect indicates a decrease in neural speech tracking with increasing noise (1 distractor). E) Stronger prediction tendency was associated with increased neural speech tracking over left frontal areas. F) However, there was no interaction between prediction tendency and conditions of selective attention. G) Increased neural tracking of semantic violations was observed over left temporal areas. H) There was no interaction between word surprisal and speaker condition, suggesting a representation of surprising words independent of background noise. Marked sensors indicate ‘significant’ clusters, defined as at least two neighboring channels showing a significant result. N = 29.”

Gehmacher, Q., Schubert, J., Kaltenmaier, A., Weisz, N., & Press, C. (2024b). The "Ocular Response Function" for encoding and decoding oculomotor related neural activity. bioRxiv, 2024-11.

(10) Bayesian hypothesis testing is not done consistently. Some parts test for inclusion of 0 in 94% HDI, while some parts adopt a ROPE approach. The same approach should be taken throughout. Additionally, Bayes factors would be very helpful (I appreciate these depend on the choice of priors, but the default Bambi priors should be fine).

Our primary aim in this study was to replicate two recent findings: (1) the relationship between individual prediction tendencies and neural speech tracking, and (2) the tracking of the speech envelope by eye movements. To maintain methodological consistency with the original studies, we did not apply a ROPE approach when analyzing these replication effects. Instead, we followed the same procedures as the original work, focusing on the inclusion of 0 in the HDI for the neural effects and using the same methods for the ocular effects. Additionally, we were not specifically interested in potential null effects in these replication analyses, as our primary goal was to test whether we could reproduce the previously reported findings.

For the mediation analysis, however, we chose to extend the original approach by not only performing the analysis in a time-resolved manner but also applying a ROPE approach. This decision was motivated by our interest in gaining more comprehensive insights — beyond the replication goals — by also testing for potential null effects, which can provide valuable information about the presence or absence of mediation effects.

We appreciate your thoughtful feedback and hope this clarifies our rationale for the differing approaches in our Bayesian hypothesis testing. 

Regarding Bayes Factors, 

We understand that some researchers find Bayes Factors appealing, as they offer a seemingly simple and straightforward way to evaluate the evidence in favor of/ or against H0 in relation to H1 (e.g. BF10 > 102 =  Decisive; according to the Jeffreys Scale). However, in practice Bayes Factors are often misunderstood e.g. by interpreting Bayes Factor as posterior odds or not acknowledging the notion of relative evidence in the Bayes Factor (see Wong et al. 2022). Instead of using Bayes Factors, we prefer to rely on estimating and reporting the posterior distribution of parameters given the data, prior and model assumptions (in form of the 94% HDI). This allows for a continuous evaluation of evidence for a given hypothesis that is in our eyes easier to interpret as a Bayes Factor.

Jeffreys, Harold (1998) [1961]. The Theory of Probability (3rd ed.). Oxford, England. p. 432. ISBN 9780191589676.

Wong, T. K., Kiers, H., & Tendeiro, J. (2022). On the Potential Mismatch Between the Function of the Bayes Factor and Researchers’ Expectations. Collabra: Psychology, 8(1), 36357. https://doi.org/10.1525/collabra.36357

(11) It would be helpful if Results could be appreciated without a detailed read of Methods. I would recommend a recap of each key methodological step before introducing the relevant Result. (This may also help in making the rationale explicit.)

In addition to the short recaps of methods that were already present, and information on quantifications of neural and ocular tracking and bayes statistics (see responses 1, 2, 9), we now added the following parts below to the results sections. Please refer to them in the context of the manuscript where they should now complement a key recap of methodological steps necessary to readily understand each analysis and rational that led to the results:

Individual prediction tendency is related to neural speech tracking:

“Thus, this measure is a single value per subject, which comprises a) differences between two contextual probabilities (i.e. ordered vs. random) in b) feature-specific tone representations c) in advance of their observation (summed over a time-window of -0.3 - 0 s). Importantly, this prediction tendency was assessed in an independent entropy modulation paradigm (see Fig. 1). On a group level we found an increased tendency to pre-activate a stimulus of high probability (i.e. forward transition) in an ordered context compared to a random context (see Fig, 2A). This effect replicates results from our previous work (Schubert et al., 2023, 2024). Using the summed difference between entropy levels (ordered - random) across pre-stimulus time, one value was extracted per subject (Fig. 2B). This value was used as a proxy for “individual prediction tendency” and correlated with encoding of clear speech across different MEG sensors. [...]

Neural speech tracking, quantified as the correlation coefficients between predicted and observed MEG responses to the speech envelope, was used as the dependent variable in Bayesian regression models. These models included condition (single vs. multi-speaker) as a fixed effect, with either prediction tendency or word surprisal as an additional predictor, and random effects for participants.”

Eye movements track acoustic speech in selective attention:

“For this, we separately predicted horizontal and vertical eye movements from the acoustic speech envelope using temporal response functions (TRFs). The resulting model fit (i.e. correlation between true and predicted eye movements) is commonly referred to as “speech tracking”. Bayesian regression models were applied to evaluate tracking effects under different conditions of selective attention (single speaker, attended multi-speaker, unattended multi-speaker). Furthermore, we assessed whether individual prediction tendency or semantic word surprisal influenced ocular speech tracking.”

Neural speech tracking is mediated by eye movements:

“This model evaluates to what extent gaze behaviour functions as a mediator between acoustic speech input and brain activity.”

Neural and ocular speech tracking are differently related to comprehension: “Bayesian regression models were used to investigate relationships between neural/ocular speech tracking and comprehension or difficulty. Ocular speech tracking was analyzed separately for horizontal and vertical eye movements.”

(12) The research questions in the Introduction should be sharpened up, to make explicit when a question concerns a theoretical entity, and when it concerns something concretely measured/measurable.

We sharpened them up:

“Taking into account the aforementioned study by Schubert and colleagues (2023), the two recently uncovered predictors of neural tracking (individual prediction tendency and ocular tracking) raise several empirical questions regarding the relationship between predictive processes, selective attention, and active ocular sensing in speech processing:

(1) Are predictive processes related to active ocular sensing in the same way they are to neural speech tracking? Specifically, do individuals with a stronger tendency to anticipate predictable auditory features, as quantified through prestimulus neural representations in an independent tone paradigm, show increased or even decreased ocular speech tracking, measured as the correlation between predicted and actual eye movements? Or is there no relationship at all?

(2) To what extent does selective attention influence the relationship between prediction tendency, neural speech tracking, and ocular speech tracking? For example, does the effect of prediction tendency or ocular speech tracking on neural tracking differ between a single-speaker and multi-speaker listening condition?

(3) Are individual prediction tendency and ocular speech tracking related to behavioral outcomes, such as comprehension and perceived task difficulty? Speech comprehension is assessed through accuracy on comprehension questions, and task difficulty is measured through subjective ratings.

Although predictive processes, selective attention, and active sensing have been shown to contribute to successful listening, their potential interactions and specific roles in naturalistic speech perception remain unclear. Addressing these questions will help disentangle their contributions and establish an integrated framework for understanding how neural and ocular speech tracking support speech processing.”

(13) The negative relationship between story comprehension and ocular speech tracking appears to go against the authors' preferred interpretation, but the reflection on this in the Discussion is very brief and somewhat vague.

Thank you for pointing this out. We have taken your comments into careful consideration and also incorporated Reviewer #1's query (Minor point 2) into a unified and complementary reasoning. We have rewritten the relevant paragraph in the discussion to provide a clearer and more detailed explanation. We hope this revision offers a more precise and less vague discussion on this important point.

“Despite the finding that eye movements mediate neural speech tracking, the behavioural relevance for semantic comprehension appears to differ between ocular and neural speech tracking. Specifically, we found a negative association between ocular speech tracking and comprehension, indicating that participants with lower comprehension performance exhibited increased ocular speech tracking. Interestingly, no significant relationship was observed between neural tracking and comprehension.

In this context, the negative association between ocular tracking and comprehension might reflect individual differences in how participants allocate cognitive resources. Participants with lower comprehension may rely more heavily on attentional mechanisms to process acoustic features, as evidenced by increased ocular tracking. This reliance could represent a compensatory strategy when higher-order processes, such as semantic integration or memory retrieval, are less effective. Importantly, our comprehension questions (see Experimental Procedure) targeted a broad range of processes, including intelligibility and memory, suggesting that this relationship reflects a trade-off in resource allocation between low-level acoustic focus and integrative cognitive tasks.

Rather than separating eye and brain responses conceptually, our analysis highlights their complementary contributions. Eye movements may enhance neural processing by increasing sensitivity to acoustic properties of speech, while neural activity builds on this foundation to integrate information and support comprehension. Together, these systems form an interdependent mechanism, with eye and brain responses working in tandem to facilitate different aspects of speech processing.

This interpretation is consistent with the absence of a difference in ocular tracking for semantic violations (e.g., words with high surprisal versus lexically matched controls), reinforcing the view that ocular tracking primarily reflects attentional engagement with acoustic features rather than direct involvement in semantic processing. This aligns with previous findings that attention modulates auditory responses to acoustic features (e.g., Forte et al., 2017), further supporting the idea that ocular tracking reflects mechanisms of selective attention rather than representations of linguistic content.

Future research should investigate how these systems interact and explore how ocular tracking mediates neural responses to linguistic features, such as lexical or semantic processing, to better understand their joint contributions to comprehension.”.  

(14) Page numbers would be helpful.

We added the page numbers.

Reviewer #3 (Recommendations for the authors):

Results

(1) Figure 2 - statistical results are reported in this figure, but they are not fully explained in the text, nor are statistical values provided for any of the analyses (as far as I can tell).

Also, how were multiple comparisons dealt with (the choice of two neighboring channels seems quite arbitrary)? Perhaps for this reason, the main result - namely the effect of "prediction tendency" and "semantic violations" - is quite sparse and might not survive more a rigorous statistical criterion. I would feel more comfortable with these results if the reporting of the statistical analysis had been more thorough (ideally, including comparison to control models).

We would like to thank you again for your detailed queries, comments, and questions on our work. We first of all adapted this figure (now Figure 3 in the manuscript, please see responses 8 and 9 to Reviewer #2) to help readers understand the metrics and values within each statistical analysis. In addition, we indeed did not include the detailed statistics in the text! We now added the missing statistic reports calculated as averages over ‘clusters’:

“Replicating previous findings (Schubert et al., 2023), we found widespread encoding of clear speech (average over cluster: β = 0.035, 94%HDI = [0.024, 0.046]), predominantly over auditory processing regions (Fig. 3C), that was decreased (β = -0.018, 94%HDI = [0.029, -0.006]) in a multi-speaker condition (Fig. 3D). Furthermore, a stronger prediction tendency was associated with increased neural speech tracking (β = 0.014, 94%HDI = [0.004, 0.025]) over left frontal sensors (see Fig. 3E). We found no interaction between prediction tendency and condition (see Fig. 3F).” [...] “In a direct comparison with lexically identical controls, we found an increased neural tracking of semantic violations (β = 0.039, 94%HDI = [0.007, 0.071]) over left temporal areas (see Fig. 3G). Furthermore, we found no interaction between word surprisal and speaker condition (see Fig. 3H).”

Regarding the "prediction tendency" effect, it is important to note that this finding replicates a result from Schubert et al. (2023). The left frontal location of this effect is also consistent over studies, which convinces us of the robustness of the finding. Furthermore, testing this relationship properly requires a mixed-effects model in order to account for the variability across subjects that is not explained by fixed effects and the repeated measures design. For this reason a random Intercept had to be fitted for each subject (1|subject in the respective model formula). This statistical requirement motivated our decision to use bayesian statistics as (at least to our knowledge) there is no implementation of a cluster-based permutation mixed effects model (yet). In order to provide a more conservative criterion (as bayesian statistics don’t require a multiple comparison correction) we chose to impose in addition the requirement of a “clustered” effect.

The choice of using two neighboring channels is consistent with the default parameter settings in FieldTrip’s cluster-based permutation testing (cfg.minnbchan = 2). This parameter specifies the minimum number of neighboring channels required for a sample to be included in the clustering algorithm, ensuring spatial consistency in the identified clusters. This alignment ensures that our methodology is comparable to numerous prior studies in the field, where such thresholds are standard. While it is true that all statistical analyses involve some degree of arbitrariness in parameter selection (e.g., alpha levels or clustering thresholds), our approach reflects established conventions and ensures comparability with previous findings.

While the original study utilized source space analyses, we replicated this effect using only 102 magnetometers. This choice was made for computational simplicity, demonstrating that the effect is robust even without source-level modeling. Similarly, the "semantic violation" effect, while perceived as sparse, is based solely on magnetometer data and - in our opinion - should not be viewed as overly sparse given the methods employed. This effect aligns with the two-neighbor clustering approach, ensuring spatial consistency across magnetometers. The results reflect the robustness of the effects within the constraints of magnetometer-level analyses.

Overall, the methodological choices, including the choice of a bayesian linear mixed effects model, the use of two neighboring channels and the reliance on magnetometers, are grounded in established practices and methodological considerations. While stricter thresholds or alternative approaches might yield different results, our methods align with best practices in the field and ensure the robustness, comparability, and replicability of our findings.

(2) Figure 3 - the difference between horizontal and vertical eye-movements. This result is quite confusing and although the authors do suggest a possible interpretation for this in the discussion, I do wonder how robust this difference is or whether the ocular signal (in either direction) is simply too noisy or the effect too small to be detected consistently across conditions. Also, the ocular-TRFs themselves are not entirely convincing in suggesting reliable response/tracking of the audio - despite the small-but-significant increase in prediction accuracy.

The horizontal versus vertical comparison was conducted to explore potential differences in how these dimensions contribute to ocular tracking of auditory stimuli (please also see our response to Reviewer #1, Response 5b, that includes the vertical vs. horizontal effects of Gehmacher at al. 2024). It would indeed be interesting to develop a measure that combines the two directions into a more natural representation of 'viewing,' such as a combined vector. However, this approach would require the use of complex numbers to represent both magnitude and direction simultaneously, hence the development of novel TRF algorithms capable of modeling this multidimensional signal. While beyond the scope of the current study, this presents an exciting avenue for future research and would allow us to move closer to understanding ocular speech tracking and the robustness of these effects, above and beyond the already successful replication.

It is also important to emphasize that ocular-TRFs are derived from (viewing) behavioral data rather than neural signals, and are thus inherently subject to greater variability across participants and time. This higher variability does not necessarily indicate a small or unreliable effect but reflects the dynamic and task-dependent nature of eye movement behavior. The TRFs with shaded error margins represent this variability, highlighting how eye movements are influenced by both individual differences and moment-to-moment changes in task engagement.

Despite this inherent variability, the significant prediction accuracy improvements confirm that ocular-TRFs reliably capture meaningful relationships between eye movements and auditory stimuli. The observed differences between horizontal and vertical TRFs further support the hypothesis that these dimensions are differentially involved in the task, possibly driven by the specific roles they play in sensorimotor coupling.

(3) Figure 4 - this figure shows source distribution of 3 PCA components, derived from the results of the mediation effect of eye movements on the speech-tracking. Here too I am having difficulty in interpreting what the results actually are. For one, all three components are quite widespread and somewhat overlapping, so although they are statistically "independent" it is hard to learn much from them about the brain regions involved and whether they truly represent separable contributions. Similarly difficult to interpret are the time courses, which share some similarities with the known TRFs to speech (especially PC3). I would have expected to find a cleaner "auditory" response, and clearer separation between sensory regions and regions involved in the control of eye movements. I also wonder why the authors chose not to show the sourcelocalization of the neural and ocular speech-tracking responses alone - this could have helped us between understand what "mediation" of the neural response might look like.

We appreciate the reviewer’s interest in better understanding the source distribution and time courses of the PCA components. While we acknowledge that the widespread and overlapping nature of the components may make a more fine grained interpretation challenging, it is important to emphasize that our analysis simply reflects the data, hence we can only present and interpret what the analysis revealed.

Regarding your suggestion to show the source localization of ocular speech tracking and neural speech tracking alone, we would like to point out that ocular tracking is represented by only one channel for vertical and one channel for horizontal eye movements. Thus, in this case the estimated source of the effect are the eyes themselves. We believe that the source localization of neural speech tracking has been a thoroughly studied topic in research so far (locating it to perisylvian, auditory areas with a stronger preference for the left hemisphere) and can also be seen in Schubert et al., (2023). Nevertheless, we believe the observed PCA components still provide valuable, and most importantly novel insights into the interplay between eye movements and neural responses in speech tracking.  

Discussion/interpretation

(1) Although I appreciate the authors' attempt to propose a "unified" theoretical model linking predictions about low-level features to higher features, and the potential involvement of eye movements in 'active sensing' I honestly think that this model is overambitious, given the data presented in the current study. Moreover, there is very little discussion of past literature and existing models of active sensing and hierarchical processing of speech, that could have helped ground the discussion in a broader theoretical context. The entire discussion contains fewer than 20 citations (some of which are by these authors) and needs to be substantially enriched in order to provide context for the authors' claims.

Thank you very much for your thoughtful feedback and for appreciating our approach. We hope that the revised manuscript addresses your concerns. Specifically, we now emphasize that our proposal is a conceptual framework, with the main goal to operationale “prediction tendency”, “active ocular sensing”, and “selective attention” and to “organise these entities according to their assumed function for speech processing and to describe their relationship with each other.” We did this by thoroughly revising our discussion section with a clear emphasis on the definition of terms, for example: 

“With this speculative framework we attempt to describe and relate three important phenomena with respect to their relevance for speech processing: 1) “Anticipatory predictions” that are created in absence of attentional demands and contain probabilistic information about stimulus features (here, inferred from frequency-specific pre-activations during passive listening to sound sequences). 2) “Selective attention” that allocates resources towards relevant (whilst suppressing distracting) information (which was manipulated by the presence or absence of a distractor speaker). And finally 3) “active ocular sensing”, which refers to gaze behavior that is temporally aligned to attended (but not unattended) acoustic speech input (inferred from the discovered phenomenon of ocular speech tracking).”

Our theoretical proposals are now followed by a recap of our results that support the respective idea, for example: 

“...these predictions are formed in parallel and carry high feature-specificity but low temporal precision (as they are anticipatory in nature). This idea is supported by our finding that pure-tone anticipation is visible over a widespread prestimulus interval, instead of being locked to sound onset”

“....we suggest that active (ocular) sensing does not necessarily convey feature- or content-specific information, it is merely used to boost (and conversely filter) sensory input at specific timescales (similar to neural oscillations). This assumption is supported by our finding that semantic violations are not differentially encoded in gaze behaviour than lexical controls.”

And we put a strong focus on highlighting the boundaries of these ideas, in order to avoid theoretical confusion, misunderstandings or implicit theoretical assumption that are not grounded in data, in particular: 

“In fact, when rejecting the notion of a single bottom-up flow of information and replacing it with a model of distributed parallel and dynamic processing, it seems only reasonable to assume that the direction of communication (between our eyes and our brain) will depend on where (within the brain) as well as when we look at the effect. Thus, the regions and time-windows reported here should be taken as an illustration of oculo-neural communication during speech processing rather than an attempt to "explain" neural speech processing by ocular movements.”

“Even though the terminology [“hierarchy”] is suggestive of a fixed sequence (similar to a multi storey building) with levels that must be traversed one after each other (and even the more spurious idea of a rooftop, where the final perceptual experience is formed and stored into memory), we distance ourselves from these (possibly unwarranted) ideas. Our usage of “higher” or “lower” simply refers to the observation that the probability of a feature at a higher (as in more associative) level affects the interpretation (and thus the representation and prediction) of a feature at lower (as in more segregated) levels (Caucheteux et al., 2023).”

Additionally, we have made substantial efforts to present complementary results (see response to Reviewer #2, point 8) to further substantiate our interpretation. Importantly, we have updated the illustration of the model (see response to Reviewer #, minor point 1) and refined both our interpretations and the conceptual language in the Discussion. Furthermore, we have included additional citations where appropriate to strengthen our argument.

We would also like to briefly note that this section of the Discussion aimed to highlight existing literature that bridges the gap our model seeks to address. However, as this is a relatively underexplored area, the references available are necessarily limited.

(2) Given my many reservations about the data, as presented in the current version of the manuscript, I find much of the discussion to be an over-interpretation of the results. This might change if the authors are able to present more robust results, as per some of my earlier comments.

We sincerely hope that our comprehensive revisions have addressed your concerns and improved the manuscript to your satisfaction.

Author Response

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

Reviewer #1 (Public Review):*

The manuscript by Hariani et al. presents experiments designed to improve our understanding of the connectivity and computational role of Unipolar Brush Cells (UBCs) within the cerebellar cortex, primarily lobes IX and X. The authors develop and cross several genetic lines of mice that express distinct fluorophores in subsets of UBCs, combined with immunocytochemistry that also distinguishes subtypes of UBCs, and they use confocal microscopy and electrophysiology to characterize the electrical and synaptic properties of subsets of so-labelled cells, and their synaptic connectivity within the cerebellar cortex. The authors then generate a computer model to test the possible computational functions of such interconnected UBCs.

Using these approaches, the authors report that:

1) GRP-driven TDtomato is expressed exclusively in a subset (20%) of ON-UBCs, defined electrophysiologically (excited by mossy fiber afferent stimulation via activation of UBC AMPA and mGluR1 receptors) and immunocytochemically by their expression of mGluR1.

2) UBCs ID'd/tagged by mCitrine expression in Brainbow mouse line P079 are expressed in a similar minority subset of OFF-UBCs defined electrophysiologically (inhibited by mossy fiber afferent stimulation via activation of UBC mGluR2 receptors) and immunocytochemically by their expression of Calretinin. However, such mCitrine expression was also detected in some mGluR1 positive UBCs, which may not have shown up electrophysiologically because of the weaker fluorophore expression without antibody amplification.

This is correctly stated with the exception that the P079 mouse line itself expresses mCitrine. The Brainbow mouse line was used in the connectivity study by crossing it to the GRP-Cre or Calretinin-Cre lines.

3) Confocal analysis of crossed lines of mice (GRP X P079) stained with antibodies to mGluR1 and calretinin documented the existence of all possible permutations of interconnectivity between cells (ON-ON, ON-OFF, OFF-OFF, OFF-ON), but their overall abundance was low, and neither their absolute nor relative abundance was quantified.

They were certainly rare to observe using our approaches, but we reasoned that the densities of such connections are not possible to estimate accurately. Please see discussion below.

4) A computational model (NEURON ) indicated that the presence of an intermediary UBC (in a polysynaptic circuit from MF to UBC to UBC) could prolong bursts (MF-ON-ON), prolong pauses (MF-ON-OFF), cause a delayed burst (MF-OFF- OFF), cause a delayed pause (MF-OFF-ON) relative to solely MF to UBC synapses which would simply exhibit long bursts (MF-ON) or long pauses (MF-OFF).

The authors thus conclude that the pattern of interconnected UBCs provides an extended and more nuanced pattern of firing within the cerebellar cortex that could mediate longer-lasting sensorimotor responses.

The cerebellum's long-known role in motor skills and reflexes, and associated disorders, combined with our nascent understanding of its role in cognitive, emotional, and appetitive processing, makes understanding its circuitry and processing functions of broad interest to the neuroscience and biomedical community. The focus on UBCs, which are largely restricted to vestibular lobules of the cerebellum reduces the breadth of likely interest somewhat. The overall design of specific experiments is rigorous and the use of fluorophore expressing mouse lines is creative. The data that is presented and the writing are clear. However, the overall experimental design has issues that reduce overall interpretation (please see specific issues for details), which combined with a lack of thorough analysis of the experimental outcomes severely undermines the value of the NEURON model results and the advance in our understanding of cerebellar processing in situ (again, please see specific issues for details).

Specific issues:

1) All data gathered with inhibition blocked. All of the UBC response data (Fig. 1) was gathered in the presence of GABAAR and Glycine R blockers. While such an approach is appropriate generally for isolating glutamatergic synaptic currents, and specifically for examining and characterizing monosynaptic responses to single stimuli, it becomes problematic in the context of assaying synaptic and action potential response durations for long-lasting responses, and in particular for trains of stimuli, when feed-forward and feed-back inhibition modulates responses to afferent stimulation. That is, even for single MF stimuli, given the >500ms duration of UBC synaptic currents, there is plenty of time for feedback inhibition from Golgi cells (or feedforward, from MF to Golgi cell excitation) to interrupt AP firing driven by the direct glutamatergic synaptic excitation. This issue is compounded further for all of the experiments examining trains of MF stimuli. Beyond the impact of feedback inhibition on the AP firing of any given UBC, it would also obviously reduce/alter/interrupt that UBC's synaptic drive of downstream UBCs. This issue fundamentally undermines our ability to interpret the simulation data of Vm and AP firing of both the modeled intermediate and downstream UBC, in terms of applying it to possible cerebellar cortical processing in situ.

The goal of Figure 1 was to determine the cell types of labeled UBCs in transgenic mouse lines, which is determined entirely by their synaptic responses to glutamate (Borges-Merjane and Trussell, 2015). Thus, blocking inhibition was essential to produce clear results in the characterization of GRP and P079 UBCs. While GABAergic/glycinergic feedforward and feedback inhibition is certainly important in the intact circuit, it was not our intention, nor was it possible, to study its contribution in the present study. Leaving inhibition unblocked does not lead to a physiologically realistic stimulation pattern in acute brain slices, because electrical stimulation produces synchronous excitation and inhibition by directly exciting Golgi cells, rather than their synaptic inputs. The main inhibition that UBCs receive that are crucial to determining burst or pause durations is not via GABA/glycine, but instead through mGluR2, which lasts for 100-1000s of milliseconds. The main excitation that drives UBC firing is mGluR1 and AMPA, which both last 100-1000s of milliseconds. Thus, these large conductances are unlikely to be significantly shaped by 1-10 ms IPSCs from feedforward and feedback GABA/glycine inhibition. Recent studies that examined the duration of bursting or pausing in UBCs had inhibition blocked in their experiments, presumably for the reasons outlined above (Guo et al., 2021; Huson et al., 2023).

In Author response image 1 is an example showing the synaptic currents and firing patterns in an ON UBC before and after blocking inhibition. The GABA/glycinergic inhibition is fast, occurs soon after the stimuli and has little to no effect on the slow inward current that develops after the end of stimulation, which is what drives firing for 100s of milliseconds.

Author response image 1.

Example showing small effect of GABAergic and glycinergic inhibition on excitatory currents and burst duration. A) Excitatory postsynaptic currents in response to train of 10 presynaptic stimuli at 50 Hz before (black) and after (Grey) blocking GABA and glycine receptors. The slow inward current that occurs at the end of stimulation is little affected. B) Expanded view of the synaptic currents evoked during the train of stimuli. GABA/glycine receptors mediate the fast outward currents that occur immediately after the first couple stimuli. C) Three examples of the bursts caused by the 50 Hz stimulation in the same cell without blocking GABA and glycine receptors. D) Three examples in the same cell after blocking GABA and glycine receptors.

2) No consideration for the involvement of polysynaptic UBCs driving UBC responses to MF stimulation in electrophysiology experiments. Given the established existence (in this manuscript and Dino et al. 2000 Neurosci, Dino et al. 2000 ProgBrainRes, Nunzi and Mugnaini 2000 JCompNeurol, Nunzi et al. 2001 JCompNeurol) of polysynaptic connections from MFs to UBCs to UBCs, the MF evoked UBC responses established in this manuscript, especially responses to trains of stimuli could be mediated by direct MF inputs, or to polysynaptic UBC inputs, or possibly both (to my awareness not established either way). Thus the response durations could already include extension of duration by polysynaptic inputs, and so would overestimate the duration of monosynaptic inputs, and thus polysynaptic amplification/modulation, observed in the NEURON model.

We are confident that the synaptic responses shown are monosynaptic for several reasons. UBCs receive a single mossy fiber input on their dendritic brush, and thus if our stimulation produces a reliable, short-latency response consistent with a monosynaptic input, then there is not likely to be a disynaptic input, because the main input is accounted for by the monosynaptic response. In all cells included in our data set, the fast AMPA receptor-mediated currents always occurred with short latency (1.24 ± 0.29 ms; mean ± SD; n = 13), high reliability (no failures to produce an EPSC in any of the 13 GRP UBCs in this data set), and low jitter (SD of latency; 0.074 ± 0.046 ms; mean ± SD; n = 13). These measurements have been added to the results section. In some rare cases, we did observe disynaptic currents, which were easily distinguishable because a single electrical stimulation produced a burst of EPSCs at variable latencies. Please see example in Author response image 2. These cases of disynaptic input, which have been reported by others (Diño et al., 2000; Nunzi and Mugnaini, 2000; van Dorp and De Zeeuw, 2015) support the conclusion that UBCs receive input from other UBCs.

Author response image 2.

Example of GRP UBC with disynaptic input. Three examples of the effect of a single presynaptic stimulus (triangle) in a GRP UBC with presumed disynaptic input. Note the variable latency of the first evoked EPSC, bursts of EPSCs, and spontaneous EPSCs.

3) Lack of quantification of subtypes of UBC interconnectivity. Given that it is already established that UBCs synapse onto other UBCs (see refs above), the main potential advance of this manuscript in terms of connectivity is the establishment and quantification of ON-ON, ON-OFF, OFF-ON, and OFF-OFF subtypes of UBC interconnections. But, the authors only establish that each type exists, showing specific examples, but no quantification of the absolute or relative density was provided, and the authors' unquantified wording explicitly or implicitly states that they are not common. This lack of quantification and likely small number makes it difficult to know how important or what impact such synapses have on cerebellar processing, in the model and in situ.

As noted by the reviewer, the connections between UBCs were rare to observe. We decided against attempting to quantify the absolute or relative density of connections for several reasons. A major reason for rare observations of anatomical connections between UBCs is likely due to the sparse labeling. First, the GRP mouse line only labels 20% of ON UBCs and we are unable to test whether postsynaptic connectivity of GRP ON UBCs is the same as that of the rest of the population of ON UBCs that are not labeled in the GRP mouse line. Second, the Brainbow reporter mouse only labels a small population of Cre expressing cells for unknown reasons. Third, the Brainbow reporter expression was so low that antibody amplification was necessary, which then limited the labeled cells to those close to the surface of the brain slices, because of known antibody penetration difficulties. Therefore, we refrained from estimating the density of these connections, because each of these variables reduced the labeling to unknown degrees and we reasoned that extrapolating our rare observations to the total population would be inaccurate.

A paper that investigated UBC connectivity using organotypic slice cultures from P8 mice suggests that 2/3 of the UBC population receives UBC input, based on the observation that 2/3 of the mossy fibers did not degenerate as would be expected after 2 days in vitro if they were severed from a distant cell body (Nunzi and Mugnaini, 2000). It remains to be seen if this high proportion is due to the young age of these mice or is also the case in adult mice. Even if these connections are indeed rare, they are expected to have profound effects on the circuit, as each UBC has multiple mossy fiber terminals (Berthie and Axelrad, 1994), and mossy fiber terminals are estimated to contact 40 granule cells each (Jakab and Hamori, 1988). We have added a comment regarding this point to the discussion.

4) Lack of critical parameters in NEURON model.

A) The model uses # of molecules of glutamate released as the presumed quantal content, and this factor is constant. However, no consideration of changes in # of vesicles released from single versus trains of APs from MFs or UBCs is included. At most simple synapses, two sequential APs alters release probability, either up or down, and release probability changes dynamically with trains of APs. It is therefore reasonable to imagine UBC axon release probability is at least as complicated, and given the large surface area of contact between two UBCs, the number of vesicles released for any given AP is also likely more complex.

B) the model does not include desensitization of AMPA receptors, which in the case of UBCs can paradoxically reduce response magnitude as vesicle release and consequent glutamate concentration in the cleft increases (Linney et al. 1997 JNeurophysiol, Lu et al. 2017 Neuron, Balmer et al. 2021 eLIFE), as would occur with trains of stimuli at MF to ON-UBCs.

A) The model produces synaptic AMPA and mGluR2 currents that reproduce those we recorded in vitro. We did not find it necessary to implement changes in glutamate release during a train as the model was fit to UBC data with the assumption that the glutamate transient did not change during the train. If there is a change in neurotransmitter release during a train, it is therefore built into the model, which has the advantage of reducing its complexity. UBCs are a special case where the postsynaptic currents are mediated mostly by the total amount of transmitter released. Most of the evoked current occurs tens to hundreds of milliseconds after neurotransmitter release and is therefore much more sensitive to total release and less sensitive to how it is released during the train. Author response image 3 shows the effect of reducing the amount of glutamate released by 10% on each stimulus in the model. Despite a significant change in the pattern of neurotransmitter release, as well as a reduction in the total amount of glutamate, the slow EPSC still decays over the course of hundreds of milliseconds.

Author response image 3.

Effect of short-term depression of neurotransmitter release. A) The top trace shows the glutamate transient that drives the AMPA receptor model used in our study. No change in release is implemented, although the slow tail of each transient summates during the train. The bottom trace shows the modeled AMPA receptor mediated current. B) In this model the amount of glutamate released is reduced by 10% on each stimulus. The duration of the slow AMPA current that develops at the end of stimulation is similar, despite a profound change in the pattern of neurotransmitter exposure.

B) The detailed kinetic AMPA receptor model used here accurately reproduces desensitization, and in fact recovery from desensitization is what mediates the slow ON UBC current. This AMPA receptor is a 13-state model, including 4 open states with 1-4 glutamates bound, 4 closed states with 1-4 glutamates bound, 4 desensitized states with 1-4 glutamates bound, and 5 closed states with 0-4 glutamates bound. The forward and reverse rates between different states in the model were fit to AMPA receptor currents recorded from dissociated UBCs and they accurately reproduced the ON UBC currents evoked by synaptic stimulation in our previous work (Balmer et al., 2021).

5) Lack of quantification of various electrophysiological responses. UBCs are defined (ON or OFF) based on inward or outward synaptic response, but no information is provided about the range of the key parameter of duration across cells, which seems most critical to the current considerations. There is a similar lack of quantification across cells of AP duration in response to stimulation or current injections, or during baseline. The latter lack is particularly problematic because, in agreement with previous publications, the raw data in Fig. 1 shows ON UBCs as quiescent until MF stimulation and OFF UBCs firing spontaneously until MF stimulation, but, for example, at least one ON UBC in the NEURON model is firing spontaneously until synaptically activated by an OFF UBC (Fig. 11A), and an OFF UBC is silent until stimulated by a presynaptic OFF UBC (Fig. 11C). This may be expected/explainable theoretically, but then such cells should be observed in the raw data.

To address this reasonable concern of a general lack of quantification of electrophysiological responses we have added data characterizing the slow inward and outward currents evoked by synaptic stimulation in GRP and P079 UBCs in the results section and in new panels in Figure 1. We report the action potential pause lengths in P079 UBCs and burst lengths in ON UBCs in the results section. However, we favor the duration of the currents to the length of burst and pause, because the currents do not depend on a stable resting membrane potential, which is itself difficult to determine in intracellular recordings of these small cells. We have added peak times and decay time constants of the slow inward and outward currents in ON and OFF UBCs in the results section and have added new panels to figure 1.

In a series of recent publications that focused on UBC firing, the authors argue that cell-attached recordings are necessary to determine accurately the burst and pause lengths, as well as spontaneous firing rates (Guo et al., 2021; Huson et al., 2023). (The trade-off of these extracellular recordings is that the monosynaptic nature of the input is nearly impossible to confirm.) Spontaneous firing rates were variable within both GRP and P079 UBCs from silent to firing regularly or in bursts, as previously reported for UBCs (Kim et al., 2012; van Dorp and De Zeeuw, 2015). For clarity, we chose to model the GRP UBCs as silent unless receiving synaptic input and P079 UBCs as active unless receiving synaptic input. As the reviewer suggests, we have observed UBCs firing in the patterns similar to those shown in the model UBCs that have input from a spontaneously active presynaptic UBC. In Author response image 4 are some examples.

Author response image 4.

Examples of UBCs that receive spontaneous input. A) Three ON UBCs that had spontaneous EPSCs, suggesting the presence of an active presynaptic UBC. B) Two OFF UBCs that had spontaneous outward currents.

Reviewer #2 (Public Review):

In this paper, the authors presented a compelling rationale for investigating the role of UBCs in prolonging and diversifying signals. Based on the two types of UBCs known as ON and OFF UBC subtypes, they have highlighted the existing gaps in understanding UBCs connectivity and the need to investigate whether UBCs target UBCs of the same subtype, different subtypes, or both. The importance of this knowledge is for understanding how sensory signals are extended and diversified in the granule cell layer.

The authors designed very interesting approaches to study UBCs connectivity by utilizing transgenic mice expressing GFP and RFP in UBCs, Brainbow approach, immunohistochemical and electrophysiological analysis, and computational models to understand how the feed-forward circuits of interconnected UBCs transform their inputs.

This study provided evidence for the existence of distinct ON and OFF UBC subtypes based on their electrophysiological properties, anatomical characteristics, and expression patterns of mGluR1 and calretinin in the cerebellum. The findings support the classification of GRP UBCs as ON UBCs and P079 UBCs as OFF UBCs and suggest the presence of synaptic connections between the ON and OFF UBC subtypes. In addition, they found that GRP and P079 UBCs form parallel and convergent pathways and have different membrane capacitance and excitability. Furthermore, they showed that UBCs of the same subtype provide input to one another and modify the input to granule cells, which could provide a circuit mechanism to diversify and extend the pattern of spiking produced by mossy fiber input. Accordingly, they suggested that these transformations could provide a circuit mechanism for maintaining a sensory representation of movement for seconds.

Overall, the article is well written in a sound detailed format, very interesting with excellent discovery and suggested model, however, I have some comments/suggestions that may help to improve this manuscript:

• The discovery of UBCs innervating each other and their own subtypes, suggesting the presence of feed-forward networks in the cerebellum, is an incredibly fascinating and exciting finding followed by an intriguing model by authors. However, it is worth considering an alternative model as well. I acknowledge that visualizing such interactions using current tools and methods can be challenging ("The approaches used here were not able to determine the existence of networks of more than 2 UBCs connected one after the other. If present, 3 or more UBCs in series could extend and transform the input in even more dramatic ways. The temporal diversity that UBC circuits generate may underlie the flexibility of the cerebellum to coordinate movements over a broad range of behaviors."). Therefore, if this is the case in which more than 2 UBCs connected one after the other, then an alternative model PERHAPS resembles the basal nuclei, with its direct and indirect circuits, can be considered (maybe a type of circular model). The basal nuclei circuits are also regulated by modulators such as D1 dopamine receptors in the direct pathway, causing depolarization, and D2 dopamine receptors in the indirect pathway, resulting in hyperpolarization upon dopamine activation. This approach could involve using computational models to gain insight into potential alternatives within this pathway (may be a future direction).

Thank you for this suggestion to consider the potentially similar circuit interactions in the basal nuclei. We will certainly investigate this further as we move forward with modeling the feed-forward networks in the cerebellum.

• GRP UBCs are more densely distributed in lobes VI-IX, while P079 UBCs are more densely distributed in the dorsal leaflet of lobe X in sagittal sections. While the cerebellum is well known for its characteristic stripy pattern, are UBC distributions the same in coronal/transverse section?

UBCs of different types, based on their expression of specific proteins, have overlapping but somewhat distinct distributions in coronal sections. The densities of calretinin-expressing UBCs are higher within Zebrin II positive zones and form sagittal stripes, whereas the densities of mGluR1-expressing and PLCb4-expressing UBCs vary less but are in their highest densities at the midline (Chung et al., 2009; Sekerkova et al., 2014). The difference noted by the reviewer between the dorsal and ventral leaflets of lobe X are the most distinct that we know of in the GRP and P079 populations.

• The extension of the axons from both subtypes of UBCs show they are long enough to pass several UBCs and even projections are directed toward the white matter (e.g. Fig 9A), suggesting targeting the UBCs or granule cells in other lobules. Is it suggesting UBCs connectivity between different lobules (perhaps longitudinal connectivity)? Is there any observation or information in coronal/transverse section to visualize mediolateral connectivity?

This is certainly worth exploring in future work. UBCs have been reported to project their axons into and across the white matter (Diño et al., 2000). To our knowledge, whether UBCs project their axons out of one lobule and into another has not been examined.

• The limitation in identifying networks involving more than two sequentially connected UBCs was briefly noted. I suggest including a paragraph describing limitations and discussing the implications of the findings would enhance the overall impact of the research and broaden our understanding of cerebellar function.

• It is a pity that there is no clear conclusion to the discussion of this very interesting study. I suggest providing the key points as a conclusion.

Thank you for these suggestions. Limitations and implications are included throughout the discussion section and we feel that the summary figure and significance statement now sufficiently convey the key conclusions of the study.

• Please make the correction in Figure 2A by relabeling it as IXa, IXb, and IXc to correct the typographical error.

Fixed

• I recommend rotating Figure 7A to align its orientation with the other figures for consistency.

Fixed

Reviewer #1 (Recommendations For The Authors):

Minor comments that should be addressed for clarity:

1) In the NEURON model, why was the reversal potential for the leak conductance and Gmax for Ih different for the two types of UBCs. Relatedly, why is Erev for GABAB -95mV if Ek is -90mV?

The h-current (Ih) was estimated from a hyperpolarizing current step in both cell types and these data have been added to the result section and as a panel in Figure 1. The conductance of Ih in the model cells were adjusted accordingly, with OFF UBCs having ~3 times that of ON UBCs and approximated the measured voltage sag, as we now describe in the methods section. The reversal potential of the model mGluR2 current (which is based on a model of GABAB) has been fixed.

2) Line 69 justification for their dual genetic approach is a bit too strong: "Paired recordings not possible". It may be difficult, but it is certainly possible.

Reworded

3) Confusing wording, only one stat for two parameters? Line 93: These currents were produced by both mGluR1 and AMPA receptors, as they were blocked by their antagonists JNJ16259685 and GYKI53655, respectively (92.86% {plus minus} 3.25; paired t-test; P=0.0066; n = 9; 95 mean {plus minus} SEM) (Fig 1D-E).

Reworded

References

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Author Response

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

First and foremost, we would like to thank all the editors and reviewers for their thoughtful and thorough evaluations of our manuscript. We greatly appreciate their assessment about the novelty and strength in this study and have revised the manuscript according to their recommendations. Below are our detailed responses and revisions based on the reviewer recommendations.

Reviewer #1 (Recommendations For The Authors):

1) It is unclear the rationale for choosing the P35-42 adolescent window for stimulating the mesofrontal dopamine system.

The dopaminergic innervation in the mesofrontal circuit exhibits a protracted maturation from P21 to P56 (Kalsbeek, Voorn et al. 1988, Niwa, Kamiya et al. 2010, Naneix, Marchand et al. 2012, Hoops and Flores 2017). P35-42 is in the center of this period and captures the mid-adolescent stage in rodents (Spear 2000). We have previously shown that increasing dopamine neuron activity by wheel running or optogenetic stimulation during this period, but not adulthood, can induce formation of mesofrontal dopaminergic boutons and enhance mesofrontal circuit activity in wild-type mice (Mastwal, Ye et al. 2014). We therefore chose the P35-P42 adolescent window to stimulate the mesofrontal dopamine circuit and test the long-term effect of this intervention on the frontal circuit and memory-guided decision-making deficits in mutant mice. We have detailed this rationale in the revised manuscript when we first introduced this intervention.

2). Please provide a justification for choosing the optical recording M2 neuronal activity instead of the prelimbic prefrontal cortex, which has been known to show the highest levels of dopamine terminals.

While the prelimbic area has the highest level of dopamine terminals among frontal cortical regions, a robust presence of dopaminergic terminals and dopamine release in the M2 frontal cortex have been well documented (Berger, Gaspar et al. 1991, Mastwal, Ye et al. 2014, Aransay, Rodriguez-Lopez et al. 2015, Patriarchi, Cho et al. 2018). The M2 cortex plays an important role in action planning, generating the earliest neural signals among frontal cortical regions that are related to upcoming choice during spatial navigation (Sul, Kim et al. 2010, Sul, Jo et al. 2011). Our chemogenetic inactivation experiments (Supplementary Fig 1) has further confirmed the involvement of M2 in the memory-guided Y-maze navigation task used in this study. Technically, M2 has the advantage of being more amendable to optical recording of neuronal activity without the tissue damage caused by implanting a lens, which would be necessary for deeper areas such as the prelimbic cortex. We have provided this justification in the revised manuscript.

3). What was the rationale for using the 3-day chemogenetic stimulation paradigm?

Our previous work in wild-type adolescent mice showed that a single optogenetic stimulation session or a 2-hr wheel running session is sufficient to induce bouton formation in mesofrontal dopaminergic axons (Mastwal, Ye et al. 2014). In this study, we sought to rescue existing structural and functional deficits in the mesofrontal dopaminergic circuits due to genetic mutations. Because previous studies suggested that an optimal level of dopamine is important for normal cognitive function (Arnsten, Cai et al. 1994, Robbins 2000, Floresco 2013), we elected to do multiple stimulation sessions to boost the potential rescue effects. We tested both a 3-day and a 3-week stimulation paradigm, and found that the 3-day, but not the 3-week paradigm led to robust functional improvement (Fig. 5). These results indicate that moderate but not excessive stimulation of dopamine neurons can provide functional improvement of a deficient mesofrontal circuit. We have revised our text to clarify the rationale for these experiments.

4). A major maturational event occurring in the prefrontal cortex is the gain of local GABAergic transmission, which is crucial for sustaining proper levels of Y-maze tasks. I am wondering if the authors have any thoughts about what is really happening at the postsynaptic level following adolescent dopamine stimulation.

The developmental increases in dopaminergic innervation to the frontal cortex and local GABAergic transmission are likely synergistic processes, which both contribute to the maturation of high-order cognitive functions supported by the frontal cortex (Caballero and Tseng 2016, Larsen and Luna 2018). Previous electrophysiological studies have suggested that dopamine can act on five different receptors expressed in both excitatory and inhibitory postsynaptic neurons (Seamans and Yang 2004, Tseng and O'Donnell 2007, O'Donnell 2010). At the network level, dopaminergic signaling can increase the signal-to-noise ratio and temporal synchrony of neural activity during cognitive tasks (Rolls, Loh et al. 2008, Vander Weele, Siciliano et al. 2018, Lohani, Martig et al. 2019). As the frontal GABAergic inhibitory network undergoes major functional remodeling during adolescence (Caballero and Tseng 2016), adolescent stimulation of dopamine neurons may interact with this maturational process to promote a network configuration conducive for synchronous and high signal-to-noise neural computation (Porter, Rizzo et al. 1999, Murty, Calabro et al. 2016, Mukherjee, Carvalho et al. 2019). The microcircuit mechanisms underlying adolescent dopamine stimulation induced changes, particularly in the GABAergic inhibitory neurons, will be an exciting direction for future research. We have extended our discussion about these points in the revised manuscript.

5). A change in the density of dopamine boutons is unlikely to be limited to the M2 region in Arc-/- mice. The authors should provide some data illustrating that similar changes are widespread across the medial prefrontal cortex, and that the optical recording in the M2 region was preferred for technical limitations and to avoid damaging areas in the frontal cortex.

As discussed above, this study focused on the M2 region of the frontal cortex because it is functionally required for memory-guided Y-maze navigation, generates behavioral choice-related neural signals during spatial navigation, and is optically most accessible. The medial prefrontal regions (anterior cingulate, prelimbic and infralimbic) ventral to M2 also receive dense dopaminergic innervation and can act in concert with M2 in decision making (Sul, Kim et al. 2010, Sul, Jo et al. 2011, Barthas and Kwan 2017). As dopaminergic innervations to the frontal cortical regions progress in a ventral-to-dorsal direction during development (Kalsbeek, Voorn et al. 1988, Hoops and Flores 2017), how the changes induced by adolescent dopamine stimulation may proceed spatial-temporally across different frontal subregions requires more extensive investigation in the future. We have added this discussion into the revised manuscript.

Reviewer #2 (Public Review):

The manuscript by Mastwal and colleagues explores how transient adolescent stimulation of ventral midbrain neurons that project to the frontal cortex may help to improve performance on certain memory tasks. The manuscript provides an interesting set of observations that DREADD-based activation over only 3 days during adolescence provides a fast-acting and long-lasting improvement in performance on Y-maze spontaneous alternation as well as aspects of neuronal function as assessed using in vivo imaging methods. While interesting, there are several weaknesses. First and foremost, it is not clear that the effects the authors are observing are mediated by dopamine. It has been clearly documented that the DAT-Cre line provides a better representation of midbrain dopamine cells in the mouse, particularly near the midline of the ventral midbrain (Lammel et al., Neuron 2015). This is precisely where the cells that project to the frontal cortex are located. Therefore, the selection of TH-Cre is problematic. It is very likely that the authors are labeling a substantial number of non-dopaminergic cells.

We agree with Review 2 that the DAT-Cre line can provide specific labeling of midbrain dopamine neurons, particularly those projecting to the striatum, as discussed in the cited study (Lammel, Steinberg et al. 2015). DAT transports the extracellularly released dopamine back into presynaptic terminals, but it is not essential for dopamine synthesis and release (Sulzer, Cragg et al. 2016). Mesocortical dopamine neurons in the ventral tegmental area (VTA) express very little DAT (Sesack, Hawrylak et al. 1998, Lammel, Hetzel et al. 2008, Li, Qi et al. 2013), which limits the use of the DAT-Cre line to target these neurons (Lammel, Steinberg et al. 2015). Because mesocortical dopamine neurons have strong expression of TH, a key enzyme involved in dopamine synthesis, TH-Cre lines have been extensively used to study the mesocortical pathway (Lammel, Lim et al. 2012, Gunaydin, Grosenick et al. 2014, Ellwood, Patel et al. 2017, Vander Weele, Siciliano et al. 2018, Lohani, Martig et al. 2019). We provide more details below about our rationales for using TH-Cre rather than DAT-Cre mice in our study and the revisions we made in response to the reviewer’s specific recommendations.

Reviewer #2 (Recommendations For The Authors):

1). The authors should rigorously demonstrate that there is a reasonable midbrain DA projection to the coordinates that they are assessing and that their effects are due to DA release from these cells. It is not clear that there is a VTA dopaminergic projection to M2 - it does not appear for example in the Allen Mouse Brain Connectivity Atlas (https://connectivity.brainmap.org/projection/experiment/siv/160540751? imageId=160541123&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=17321&y=15284&z=3). Though there is a projection to the mPFC, at the coordinates the authors report, there does not appear to be any signal from DAT-Cre mice. However, there is much more signal when expression is not restricted to dopamine cells (https://connectivity.brain-map.org/projection/experiment/siv/165975096? imageId=165975158&imageType=TWO_PHOTON,SEGMENTATION&initImage=TWO_PHOTON&x=17950&y=11504&z=3). The argument that these cells may express less TH is not relevant for this particular issue. Therefore, it is possible that the vast majority of observed effects are not in fact mediated by dopamine but another neurotransmitter such as glutamate. While the experiment using SCH23390 does suggest DA receptors may be involved, this result in isolation doesn't alleviate this caveat - there can be, for example, DA release from NE cells (e.g., Takeuchi et al., Nature 2016). While this does not entirely invalidate the authors' results, as their effects of stimulation of ventral midbrain cells to the forebrain don't necessarily have to occur via dopamine - the mechanism by how this is occurring needs to be clear.

While the prelimbic area has the highest level of dopaminergic terminals among frontal cortical regions, a robust presence of midbrain dopaminergic projections and dopamine release in the M2 frontal cortex have been well established by immunostaining, viral labeling, single-cell axon-tracing, and in vivo imaging of recently developed dopamine biosensors (Berger, Gaspar et al. 1991, Mastwal, Ye et al. 2014, Aransay, Rodriguez-Lopez et al. 2015, Ye, Mastwal et al. 2017, Patriarchi, Cho et al. 2018). It has also been reported repeatedly that mesocortical dopamine neurons in the VTA express very little DAT, which is different from mesostriatal dopamine neurons (Sesack, Hawrylak et al. 1998, Lammel, Hetzel et al. 2008, Li, Qi et al. 2013). This limitation in the use of the DAT-Cre line to target mesocortical dopamine neurons has been acknowledged in previous studies (Lammel, Steinberg et al. 2015) and is consistent with the reviewer’s observation of DAT-Cre labeling in the Allen Brain Mouse Connectivity atlas. Additionally, and interestingly, recent extensive evaluation of the DAT-Cre line reported ectopic labeling of multiple non-dopaminergic neuronal populations (Soden, Miller et al. 2016, Stagkourakis, Spigolon et al. 2018, Papathanou, Dumas et al. 2019). Our own evaluation of the DAT-Cre line’s utility for cortical imaging also revealed sparse axonal labeling and sporadic ectopic labeling of cortical cell somas. We have included representative DAT-Cre images in Author response image 1 to highlight the limitations of this line in the study of the dopaminergic mesocortical circuit.

Author response image 1.

Example images from DAT-Cre/Ai14 mice. Left most panel shows little axonal labeling in Layer 5/6 of M2. The center panel shows sparse axonal label in Layer 1/2 of M2, but also ectopic labeling of cell soma. The right panel shows a lack of labeling in L1/2 of prelimbic cortex as well. Scale bars 50um.

We as well as others have confirmed that TH immunoreactivity in the frontal cortex can label dopaminergic axons originated from the VTA, and ablation of VTA dopaminergic neurons removes this labeling (Niwa, Jaaro-Peled et al. 2013, Ye, Mastwal et al. 2017). Because mesocortical dopamine neurons have much stronger TH expression than DAT expression (Sesack, Hawrylak et al. 1998, Lammel, Hetzel et al. 2008, Li, Qi et al. 2013, Lammel, Steinberg et al. 2015), TH-Cre lines have been frequently used to label these neurons and study the mesocortical pathway (Lammel, Lim et al. 2012, Gunaydin, Grosenick et al. 2014, Ellwood, Patel et al. 2017, Vander Weele, Siciliano et al. 2018, Lohani, Martig et al. 2019). While TH-Cre expression itself is not restricted to dopaminergic neurons, we targeted our viral injections to the VTA and optogenetic stimulation to the cortical dopaminergic projection target area in M2 (Patriarchi, Cho et al. 2018) to specifically modulate mesofrontal dopaminergic axons. In addition, we tested D1 antagonist’s effects in our manipulations. Although we targeted dopamine neurons in our adolescent stimulation, the final behavioral outcome likely includes contributions from co-released neurotransmitters such as glutamate and non-dopaminergic neurons via network effects (Morales and Margolis 2017, Lohani, Martig et al. 2019), which will be interesting directions for future research. We have revised our results and discussion sections to highlight our rationales for using the TH-Cre line and the open mechanistic questions for future studies.

2) SSFOs don't increase excitability like DREADDs, but rather, cause long-lasting hyperactivity through continuous passage of cations. What the actual firing properties are of these cells over a long period of time is not clear.

We did not measure the precise firing patterns of the dopaminergic neurons targeted by SSFOs but evaluated the effects of SSFO activation on the frontal cortex. Similar to our DREADD-Gq mediated activity changes in the mesofrontal circuit, we found increased frontal cortical activity post-light stimulation of frontal dopamine axons in our SSFO treated animals (Fig 6a-c, S6e). While quantitatively the firing patterns of DREADD-Gq and SSFO activated dopaminergic neurons likely differ, qualitatively both of these manipulations lead to increased mesofrontal circuit activity and improvements in cognitive behaviors. In our previous work with wild-type adolescent mice, both wheel running and a single 10-min session of phasic optogenetic stimulation of the VTA resulted in dopaminergic bouton outgrowth in the frontal cortex (Mastwal, Ye et al. 2014). Taken together, these results suggest that adolescent dopaminergic mesofrontal projections are highly responsive to neural activity changes and a variety of adolescent stimulation paradigms are sufficient to elicit lasting changes in this circuit. We have added this discussion of the limitations and implications of our study into the revised manuscript.

3) It is not clear what the increase in boutons means, given that DA release is thought to largely occur via non-synaptic release.

Although many of dopamine boutons are not associated with defined postsynaptic structures, these axonal boutons and the active zones they contain are the major release sites for dopamine (Goldman-Rakic, Leranth et al. 1989, Arbuthnott and Wickens 2007, Sulzer, Cragg et al. 2016, Liu, Goel et al. 2021). Past studies have established a consistent association between increased dopaminergic innervation in the frontal cortex and an increase in dopamine levels (Niwa, Kamiya et al. 2010, Naneix, Marchand et al. 2012). Our previous work also found that increasing dopaminergic boutons through adolescent VTA stimulation led to prolonged frontal local field potential responses with high-frequency oscillations (Mastwal, Ye et al. 2014), which is characteristic of increased dopaminergic signaling (Lewis and O'Donnell 2000, Gireesh and Plenz 2008, Wood, Kim et al. 2012, Lohani, Martig et al. 2019). Importantly, in our quantification of the structural changes in this study, we evaluated boutons which were labeled with synaptophysin, a molecular marker indicating the presence of synaptic vesicle release machinery (Li, Tasic et al. 2010, Oh, Harris et al. 2014). Thus, our study, taken in the context of the previous work, suggests the increased number of boutons signifying an increase in dopaminergic signaling within the mesofrontal circuit. We have added this discussion into the revised manuscript.

4) The use of Arc and DISC mutants as models of schizophrenia is perhaps a bit overstated - while deficits in prefrontal innervation certainly occur, there are many differences between these models and the human disease states. Language should be toned down accordingly, particularly in the introduction.

We strived to avoid overstating the extent to which the mouse lines are models for specific diseases, but we can appreciate that this may not have been clear in our original writing. We have adjusted our language to better distinguish between the utility of the animal models for the purposes of our study and their relationship to specific human disease states. Particularly in the introduction, we stated that: “Genetic disruptions of several genes involved in synaptic functions related to psychiatric disorders, such as Arc and DISC1, lead to hypoactive mesofrontal dopaminergic input in mice (Niwa, Kamiya et al. 2010, Niwa, Jaaro-Peled et al. 2013, Fromer, Pocklington et al. 2014, Purcell, Moran et al. 2014, Wen, Nguyen et al. 2014, Manago, Mereu et al. 2016). Although there are many differences between these mouse lines and specific human disease states, these mice offer opportunities to test whether genetic deficits in frontal cortex function can be reversed through circuit interventions.”

5) Some experiments are missing proper controls, e.g., Figure 3g-I where a WT mouse should be used as a positive control.

The goal of this experimental design (Fig 3g-i) was to evaluate the potential effects of chemogenetic VTA stimulation in the Arc-/- mice. We used Arc-/- mice with mCherry injections to control for the potential effects of CNO administration. While WT mice could be used to determine if adolescent VTA stimulation would lead to long-lasting enhancement of VTA-to-Cortical transmission, this wouldn’t necessarily be a positive control for our experiments, but rather a separate line of inquiry. As dopamine’s effects often display an inverted-U dose-response curve (Vijayraghavan, Wang et al. 2007, Floresco 2013), evaluating the effects adolescent VTA stimulation in the absence of underlying dopamine deficiency could be an interesting future research direction. We have added this discussion into the revised manuscript.

Reviewer #3 (Recommendations For The Authors):

1) Did the SSFO stimulation of the TH+ axons in PFC during adolescence lead to the same long-term change in DA bouton number the authors saw with DREADDs?

We did not examine the degree of bouton growth in the SSFO cohort, which is a limitation of this study. Accurate quantification of dopamine boutons requires the co-injection of another AAV vector encoding Synaptophysin-GFP to label the boutons. Because we used light to directly stimulate SSFO-labeled dopaminergic axons in the frontal cortex, we were concerned that co-injecting another AAV vector may dilute SSFO-labeling of axons and reduce the efficacy of optogenetic stimulation. Given the behavioral benefits we observed, we would expect an increase in bouton density after optogenetic stimulation. A systematic optimization of viral co-labeling and optogenetic stimulation protocols will facilitate examination of the impact of SSFO stimulation at the structural level in future studies. We have added a discussion of the limitation of this study in the revised manuscript.

2) The DISC1 section is far less detailed than the Arc section, and it was not completely clear to me that the mechanisms of dysfunction and rescue were the same in these mice compared with the Arc mice. For example, there was no mention of DA bouton density or the patterned firing of the PFC neurons at the time of decision making.

The initial motivation of this study was to test if adolescent dopamine stimulation can rescue the deficits in the mesofrontal dopaminergic circuit and cognitive function of Arc-/- mice, which were identified in our previous studies (Manago, Mereu et al. 2016). We first conducted multiple levels of analyses including viral tracing, in vivo calcium imaging, and behavioral tests to establish the coherent impacts of adolescent dopamine neuron stimulation on circuits and behaviors. We then examined a range of stimulation protocols to assess the efficacy requirements for cognitive improvement, which is our primary goal. Finally, we included DISC1 mice in our study to test if adolescent dopamine stimulation can also reverse the cognitive deficit in another genetic model for mesofrontal dopamine deficiency. By demonstrating a similar cognitive recuse effect of adolescent VTA stimulation in an independent mouse model, this study provides a foundation for future research to compare the detailed cellular mechanisms that underlie the functional rescue in different genetic models. We have added the discussion of the scope and limitation of this study to the revised manuscript.

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Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, the authors address whether the dorsal nucleus of the inferior colliculus (DCIC) in mice encodes sound source location within the front horizontal plane (i.e., azimuth). They do this using volumetric two-photon Ca2+ imaging and high-density silicon probes (Neuropixels) to collect single-unit data. Such recordings are beneficial because they allow large populations of simultaneous neural data to be collected. Their main results and the claims about those results are the following:

(1) DCIC single-unit responses have high trial-to-trial variability (i.e., neural noise);

(2) approximately 32% to 40% of DCIC single units have responses that are sensitive tosound source azimuth;

(3) single-trial population responses (i.e., the joint response across all sampled single unitsin an animal) encode sound source azimuth "effectively" (as stated in title) in that localization decoding error matches average mouse discrimination thresholds;

(4) DCIC can encode sound source azimuth in a similar format to that in the central nucleusof the inferior colliculus (as stated in Abstract);

(5) evidence of noise correlation between pairs of neurons exists;

and 6) noise correlations between responses of neurons help reduce population decoding error.

While simultaneous recordings are not necessary to demonstrate results #1, #2, and #4, they are necessary to demonstrate results #3, #5, and #6.

Strengths:

- Important research question to all researchers interested in sensory coding in the nervous system.

- State-of-the-art data collection: volumetric two-photon Ca2+ imaging and extracellularrecording using high-density probes. Large neuronal data sets.

- Confirmation of imaging results (lower temporal resolution) with more traditionalmicroelectrode results (higher temporal resolution).

- Clear and appropriate explanation of surgical and electrophysiological methods. I cannot comment on the appropriateness of the imaging methods.

Strength of evidence for claims of the study:

(1) DCIC single-unit responses have high trial-to-trial variability - The authors' data clearlyshows this.

(2) Approximately 32% to 40% of DCIC single units have responses that are sensitive tosound source azimuth - The sensitivity of each neuron's response to sound source azimuth was tested with a Kruskal-Wallis test, which is appropriate since response distributions were not normal. Using this statistical test, only 8% of neurons (median for imaging data) were found to be sensitive to azimuth, and the authors noted this was not significantly different than the false positive rate. The Kruskal-Wallis test was not performed on electrophysiological data. The authors suggested that low numbers of azimuth-sensitive units resulting from the statistical analysis may be due to the combination of high neural noise and relatively low number of trials, which would reduce statistical power of the test. This may be true, but if single-unit responses were moderately or strongly sensitive to azimuth, one would expect them to pass the test even with relatively low statistical power. At best, if their statistical test missed some azimuthsensitive units, they were likely only weakly sensitive to azimuth. The authors went on to perform a second test of azimuth sensitivity-a chi-squared test-and found 32% (imaging) and 40% (e-phys) of single units to have statistically significant sensitivity. This feels a bit like fishing for a lower p-value. The Kruskal-Wallis test should have been left as the only analysis. Moreover, the use of a chi-squared test is questionable because it is meant to be used between two categorical variables, and neural response had to be binned before applying the test.

The determination of what is a physiologically relevant “moderate or strong azimuth sensitivity” is not trivial, particularly when comparing tuning across different relays of the auditory pathway like the CNIC, auditory cortex, or in our case DCIC, where physiologically relevant azimuth sensitivities might be different. This is likely the reason why azimuth sensitivity has been defined in diverse ways across the bibliography (see Groh, Kelly & Underhill, 2003 for an early discussion of this issue). These diverse approaches include reaching a certain percentage of maximal response modulation, like used by Day et al. (2012, 2015, 2016) in CNIC, and ANOVA tests, like used by Panniello et al. (2018) and Groh, Kelly & Underhill (2003) in auditory cortex and IC respectively. Moreover, the influence of response variability and biases in response distribution estimation due to limited sampling has not been usually accounted for in the determination of azimuth sensitivity.

As Reviewer #1 points out, in our study we used an appropriate ANOVA test (KruskalWallis) as a starting point to study response sensitivity to stimulus azimuth at DCIC. Please note that the alpha = 0.05 used for this test is not based on experimental evidence about physiologically relevant azimuth sensitivity but instead is an arbitrary p-value threshold. Using this test on the electrophysiological data, we found that ~ 21% of the simultaneously recorded single units reached significance (n = 4 mice). Nevertheless these percentages, in our small sample size (n = 4) were not significantly different from our false positive detection rate (p = 0.0625, Mann-Whitney, See Author response image 1 below).  In consequence, for both our imaging (Fig. 3C) and electrophysiological data, we could not ascertain if the percentage of neurons reaching significance in these ANOVA tests were indeed meaningfully sensitive to azimuth or this was due to chance. 

Author response image 1.

Percentage of the neuropixels recorded DCIC single units across mice that showed significant median response tuning, compared to false positive detection rate (α = 0.05, chance level).

We reasoned that the observed markedly variable responses from DCIC units, which frequently failed to respond in many trials (Fig. 3D, 4A), in combination with the limited number of trial repetitions we could collect, results in under-sampled response distribution estimations. This under-sampling can bias the determination of stochastic dominance across azimuth response samples in Kruskal-Wallis tests. We would like to highlight that we decided not to implement resampling strategies to artificially increase the azimuth response sample sizes with “virtual trials”, in order to avoid “fishing for a smaller p-value”, when our collected samples might not accurately reflect the actual response population variability.

As an alternative to hypothesis testing based on ranking and determining stochastic dominance of one or more azimuth response samples (Kruskal-Wallis test), we evaluated the overall statistical dependency to stimulus azimuth of the collected responses.  To do this we implement the Chi-square test by binning neuronal responses into categories. Binning responses into categories can reduce the influence of response variability to some extent, which constitutes an advantage of the Chi-square approach, but we note the important consideration that these response categories are arbitrary.

Altogether, we acknowledge that our Chi-square approach to define azimuth sensitivity is not free of limitations and despite enabling the interrogation of azimuth sensitivity at DCIC, its interpretability might not extend to other brain regions like CNIC or auditory cortex. Nevertheless we hope the aforementioned arguments justify why the Kruskal-Wallis test simply could not “have been left as the only analysis”.

(3) Single-trial population responses encode sound source azimuth "effectively" in that localization decoding error matches average mouse discrimination thresholds - If only one neuron in a population had responses that were sensitive to azimuth, we would expect that decoding azimuth from observation of that one neuron's response would perform better than chance. By observing the responses of more than one neuron (if more than one were sensitive to azimuth), we would expect performance to increase. The authors found that decoding from the whole population response was no better than chance. They argue (reasonably) that this is because of overfitting of the decoder modeltoo few trials used to fit too many parameters-and provide evidence from decoding combined with principal components analysis which suggests that overfitting is occurring. What is troubling is the performance of the decoder when using only a handful of "topranked" neurons (in terms of azimuth sensitivity) (Fig. 4F and G). Decoder performance seems to increase when going from one to two neurons, then decreases when going from two to three neurons, and doesn't get much better for more neurons than for one neuron alone. It seems likely there is more information about azimuth in the population response, but decoder performance is not able to capture it because spike count distributions in the decoder model are not being accurately estimated due to too few stimulus trials (14, on average). In other words, it seems likely that decoder performance is underestimating the ability of the DCIC population to encode sound source azimuth.

To get a sense of how effective a neural population is at coding a particular stimulus parameter, it is useful to compare population decoder performance to psychophysical performance. Unfortunately, mouse behavioral localization data do not exist. Therefore, the authors compare decoder error to mouse left-right discrimination thresholds published previously by a different lab. However, this comparison is inappropriate because the decoder and the mice were performing different perceptual tasks. The decoder is classifying sound sources to 1 of 13 locations from left to right, whereas the mice were discriminating between left or right sources centered around zero degrees. The errors in these two tasks represent different things. The two data sets may potentially be more accurately compared by extracting information from the confusion matrices of population decoder performance. For example, when the stimulus was at -30 deg, how often did the decoder classify the stimulus to a lefthand azimuth? Likewise, when the stimulus was +30 deg, how often did the decoder classify the stimulus to a righthand azimuth?

The azimuth discrimination error reported by Lauer et al. (2011) comes from engaged and highly trained mice, which is a very different context to our experimental setting with untrained mice passively listening to stimuli from 13 random azimuths. Therefore we did not perform analyses or interpretations of our results based on the behavioral task from Lauer et al. (2011) and only made the qualitative observation that the errors match for discussion.

We believe it is further important to clarify that Lauer et al. (2011) tested the ability of mice to discriminate between a positively conditioned stimulus (reference speaker at 0º center azimuth associated to a liquid reward) and a negatively conditioned stimulus (coming from one of five comparison speakers positioned at 20º, 30º, 50º, 70 and 90º azimuth, associated to an electrified lickport) in a conditioned avoidance task. In this task, mice are not precisely “discriminating between left or right sources centered around zero degrees”, making further analyses to compare the experimental design of Lauer et al (2011) and ours even more challenging for valid interpretation.

(4) DCIC can encode sound source azimuth in a similar format to that in the central nucleusof the inferior colliculus - It is unclear what exactly the authors mean by this statement in the Abstract. There are major differences in the encoding of azimuth between the two neighboring brain areas: a large majority of neurons in the CNIC are sensitive to azimuth (and strongly so), whereas the present study shows a minority of azimuth-sensitive neurons in the DCIC. Furthermore, CNIC neurons fire reliably to sound stimuli (low neural noise), whereas the present study shows that DCIC neurons fire more erratically (high neural noise).

Since sound source azimuth is reported to be encoded by population activity patterns at CNIC (Day and Delgutte, 2013), we refer to a population activity pattern code as the “similar format” in which this information is encoded at DCIC. Please note that this is a qualitative comparison and we do not claim this is the “same format”, due to the differences the reviewer precisely describes in the encoding of azimuth at CNIC where a much larger majority of neurons show stronger azimuth sensitivity and response reliability with respect to our observations at DCIC. By this qualitative similarity of encoding format we specifically mean the similar occurrence of activity patterns from azimuth sensitive subpopulations of neurons in both CNIC and DCIC, which carry sufficient information about the stimulus azimuth for a sufficiently accurate prediction with regard to the behavioral discrimination ability.

(5) Evidence of noise correlation between pairs of neurons exists - The authors' data andanalyses seem appropriate and sufficient to justify this claim.

(6) Noise correlations between responses of neurons help reduce population decodingerror - The authors show convincing analysis that performance of their decoder increased when simultaneously measured responses were tested (which include noise correlation) than when scrambled-trial responses were tested (eliminating noise correlation). This makes it seem likely that noise correlation in the responses improved decoder performance. The authors mention that the naïve Bayesian classifier was used as their decoder for computational efficiency, presumably because it assumes no noise correlation and, therefore, assumes responses of individual neurons are independent of each other across trials to the same stimulus. The use of decoder that assumes independence seems key here in testing the hypothesis that noise correlation contains information about sound source azimuth. The logic of using this decoder could be more clearly spelled out to the reader. For example, if the null hypothesis is that noise correlations do not carry azimuth information, then a decoder that assumes independence should perform the same whether population responses are simultaneous or scrambled. The authors' analysis showing a difference in performance between these two cases provides evidence against this null hypothesis.

We sincerely thank the reviewer for this careful and detailed consideration of our analysis approach. Following the reviewer’s constructive suggestion, we justified the decoder choice in the results section at the last paragraph of page 18:

“To characterize how the observed positive noise correlations could affect the representation of stimulus azimuth by DCIC top ranked unit population responses, we compared the decoding performance obtained by classifying the single-trial response patterns from top ranked units in the modeled decorrelated datasets versus the acquired data (with noise correlations). With the intention to characterize this with a conservative approach that would be less likely to find a contribution of noise correlations as it assumes response independence, we relied on the naive Bayes classifier for decoding throughout the study. Using this classifier, we observed that the modeled decorrelated datasets produced stimulus azimuth prediction error distributions that were significantly shifted towards higher decoding errors (Fig. 5B, C) and, in our imaging datasets, were not significantly different from chance level (Fig. 5B). Altogether, these results suggest that the detected noise correlations in our simultaneously acquired datasets can help reduce the error of the IC population code for sound azimuth.”

Minor weakness:

- Most studies of neural encoding of sound source azimuth are done in a noise-free environment, but the experimental setup in the present study had substantial background noise. This complicates comparison of the azimuth tuning results in this study to those of other studies. One is left wondering if azimuth sensitivity would have been greater in the absence of background noise, particularly for the imaging data where the signal was only about 12 dB above the noise. The description of the noise level and signal + noise level in the Methods should be made clearer. Mice hear from about 2.5 - 80 kHz, so it is important to know the noise level within this band as well as specifically within the band overlapping with the signal.

We agree with the reviewer that this information is useful. In our study, the background R.M.S. SPL during imaging across the mouse hearing range (2.5-80kHz) was 44.53 dB and for neuropixels recordings 34.68 dB. We have added this information to the methods section of the revised manuscript.

Reviewer #2 (Public Review):

In the present study, Boffi et al. investigate the manner in which the dorsal cortex of the of the inferior colliculus (DCIC), an auditory midbrain area, encodes sound location azimuth in awake, passively listening mice. By employing volumetric calcium imaging (scanned temporal focusing or s-TeFo), complemented with high-density electrode electrophysiological recordings (neuropixels probes), they show that sound-evoked responses are exquisitely noisy, with only a small portion of neurons (units) exhibiting spatial sensitivity. Nevertheless, a naïve Bayesian classifier was able to predict the presented azimuth based on the responses from small populations of these spatially sensitive units. A portion of the spatial information was provided by correlated trial-to-trial response variability between individual units (noise correlations). The study presents a novel characterization of spatial auditory coding in a non-canonical structure, representing a noteworthy contribution specifically to the auditory field and generally to systems neuroscience, due to its implementation of state-of-the-art techniques in an experimentally challenging brain region. However, nuances in the calcium imaging dataset and the naïve Bayesian classifier warrant caution when interpreting some of the results.

Strengths:

The primary strength of the study lies in its methodological achievements, which allowed the authors to collect a comprehensive and novel dataset. While the DCIC is a dorsal structure, it extends up to a millimetre in depth, making it optically challenging to access in its entirety. It is also more highly myelinated and vascularised compared to e.g., the cerebral cortex, compounding the problem. The authors successfully overcame these challenges and present an impressive volumetric calcium imaging dataset. Furthermore, they corroborated this dataset with electrophysiological recordings, which produced overlapping results. This methodological combination ameliorates the natural concerns that arise from inferring neuronal activity from calcium signals alone, which are in essence an indirect measurement thereof.

Another strength of the study is its interdisciplinary relevance. For the auditory field, it represents a significant contribution to the question of how auditory space is represented in the mammalian brain. "Space" per se is not mapped onto the basilar membrane of the cochlea and must be computed entirely within the brain. For azimuth, this requires the comparison between miniscule differences between the timing and intensity of sounds arriving at each ear. It is now generally thought that azimuth is initially encoded in two, opposing hemispheric channels, but the extent to which this initial arrangement is maintained throughout the auditory system remains an open question. The authors observe only a slight contralateral bias in their data, suggesting that sound source azimuth in the DCIC is encoded in a more nuanced manner compared to earlier processing stages of the auditory hindbrain. This is interesting, because it is also known to be an auditory structure to receive more descending inputs from the cortex.

Systems neuroscience continues to strive for the perfection of imaging novel, less accessible brain regions. Volumetric calcium imaging is a promising emerging technique, allowing the simultaneous measurement of large populations of neurons in three dimensions. But this necessitates corroboration with other methods, such as electrophysiological recordings, which the authors achieve. The dataset moreover highlights the distinctive characteristics of neuronal auditory representations in the brain. Its signals can be exceptionally sparse and noisy, which provide an additional layer of complexity in the processing and analysis of such datasets. This will be undoubtedly useful for future studies of other less accessible structures with sparse responsiveness.

Weaknesses:

Although the primary finding that small populations of neurons carry enough spatial information for a naïve Bayesian classifier to reasonably decode the presented stimulus is not called into question, certain idiosyncrasies, in particular the calcium imaging dataset and model, complicate specific interpretations of the model output, and the readership is urged to interpret these aspects of the study's conclusions with caution.

I remain in favour of volumetric calcium imaging as a suitable technique for the study, but the presently constrained spatial resolution is insufficient to unequivocally identify regions of interest as cell bodies (and are instead referred to as "units" akin to those of electrophysiological recordings). It remains possible that the imaging set is inadvertently influenced by non-somatic structures (including neuropil), which could report neuronal activity differently than cell bodies. Due to the lack of a comprehensive ground-truth comparison in this regard (which to my knowledge is impossible to achieve with current technology), it is difficult to imagine how many informative such units might have been missed because their signals were influenced by spurious, non-somatic signals, which could have subsequently misled the models. The authors reference the original Nature Methods article (Prevedel et al., 2016) throughout the manuscript, presumably in order to avoid having to repeat previously published experimental metrics. But the DCIC is neither the cortex nor hippocampus (for which the method was originally developed) and may not have the same light scattering properties (not to mention neuronal noise levels). Although the corroborative electrophysiology data largely eleviates these concerns for this particular study, the readership should be cognisant of such caveats, in particular those who are interested in implementing the technique for their own research.

A related technical limitation of the calcium imaging dataset is the relatively low number of trials (14) given the inherently high level of noise (both neuronal and imaging). Volumetric calcium imaging, while offering a uniquely expansive field of view, requires relatively high average excitation laser power (in this case nearly 200 mW), a level of exposure the authors may have wanted to minimise by maintaining a low the number of repetitions, but I yield to them to explain.

We assumed that the levels of heating by excitation light measured at the neocortex in Prevedel et al. (2016), were representative for DCIC also. Nevertheless, we recognize this approximation might not be very accurate, due to the differences in tissue architecture and vascularization from these two brain areas, just to name a few factors. The limiting factor preventing us from collecting more trials in our imaging sessions was that we observed signs of discomfort or slight distress in some mice after ~30 min of imaging in our custom setup, which we established as a humane end point to prevent distress. In consequence imaging sessions were kept to 25 min in duration, limiting the number of trials collected. However we cannot rule out that with more extensive habituation prior to experiments the imaging sessions could be prolonged without these signs of discomfort or if indeed influence from our custom setup like potential heating of the brain by illumination light might be the causing factor of the observed distress. Nevertheless, we note that previous work has shown that ~200mW average power is a safe regime for imaging in the cortex by keeping brain heating minimal (Prevedel et al., 2016), without producing the lasting damages observed by immunohistochemisty against apoptosis markers above 250mW (Podgorski and Ranganathan 2016, https://doi.org/10.1152/jn.00275.2016).

Calcium imaging is also inherently slow, requiring relatively long inter-stimulus intervals (in this case 5 s). This unfortunately renders any model designed to predict a stimulus (in this case sound azimuth) from particularly noisy population neuronal data like these as highly prone to overfitting, to which the authors correctly admit after a model trained on the entire raw dataset failed to perform significantly above chance level. This prompted them to feed the model only with data from neurons with the highest spatial sensitivity. This ultimately produced reasonable performance (and was implemented throughout the rest of the study), but it remains possible that if the model was fed with more repetitions of imaging data, its performance would have been more stable across the number of units used to train it. (All models trained with imaging data eventually failed to converge.) However, I also see these limitations as an opportunity to improve the technology further, which I reiterate will be generally important for volume imaging of other sparse or noisy calcium signals in the brain.

Transitioning to the naïve Bayesian classifier itself, I first openly ask the authors to justify their choice of this specific model. There are countless types of classifiers for these data, each with their own pros and cons. Did they actually try other models (such as support vector machines), which ultimately failed? If so, these negative results (even if mentioned en passant) would be extremely valuable to the community, in my view. I ask this specifically because different methods assume correspondingly different statistical properties of the input data, and to my knowledge naïve Bayesian classifiers assume that predictors (neuronal responses) are assumed to be independent within a class (azimuth). As the authors show that noise correlations are informative in predicting azimuth, I wonder why they chose a model that doesn't take advantage of these statistical regularities. It could be because of technical considerations (they mention computing efficiency), but I am left generally uncertain about the specific logic that was used to guide the authors through their analytical journey.

One of the main reasons we chose the naïve Bayesian classifier is indeed because it assumes that the responses of the simultaneously recorded neurons are independent and therefore it does not assume a contribution of noise correlations to the estimation of the posterior probability of each azimuth. This model would represent the null hypothesis that noise correlations do not contribute to the encoding of stimulus azimuth, which would be verified by an equal decoding outcome from correlated or decorrelated datasets. Since we observed that this is not the case, the model supports the alternative hypothesis that noise correlations do indeed influence stimulus azimuth encoding. We wanted to test these hypotheses with the most conservative approach possible that would be least likely to find a contribution of noise correlations. Other relevant reasons that justify our choice of the naive Bayesian classifier are its robustness against the limited numbers of trials we could collect in comparison to other more “data hungry” classifiers like SVM, KNN, or artificial neuronal nets. We did perform preliminary tests with alternative classifiers but the obtained decoding errors were similar when decoding the whole population activity (Author response image 2A). Dimensionality reduction following the approach described in the manuscript showed a tendency towards smaller decoding errors observed with an alternative classifier like KNN, but these errors were still larger than the ones observed with the naive Bayesian classifier (median error 45º). Nevertheless, we also observe a similar tendency for slightly larger decoding errors in the absence of noise correlations (decorrelated, Author response image 2B). Sentences detailing the logic of classifier choice are now included in the results section at page 10 and at the last paragraph of page 18 (see responses to Reviewer 1).

Author response image 2.

A) Cumulative distribution plots of the absolute cross-validated single-trial prediction errors obtained using different classifiers (blue; KNN: K-nearest neighbors; SVM: support vector machine ensemble) and chance level distribution (gray) on the complete populations of imaged units. Cumulative distribution plots of the absolute cross-validated singletrial prediction errors obtained using a Bayes classifier (naive approximation for computation efficiency) to decode the single-trial response patterns from the 31 top ranked units in the simultaneously imaged datasets across mice (cyan), modeled decorrelated datasets (orange) and the chance level distribution associated with our stimulation paradigm (gray). Vertical dashed lines show the medians of cumulative distributions. K.S. w/Sidak: Kolmogorov-Smirnov with Sidak.

That aside, there remain other peculiarities in model performance that warrant further investigation. For example, what spurious features (or lack of informative features) in these additional units prevented the models of imaging data from converging?

Considering the amount of variability observed throughout the neuronal responses both in imaging and neuropixels datasets, it is easy to suspect that the information about stimulus azimuth carried in different amounts by individual DCIC neurons can be mixed up with information about other factors (Stringer et al., 2019). In an attempt to study the origin of these features that could confound stimulus azimuth decoding we explored their relation to face movement (Supplemental Figure 2), finding a correlation to snout movements, in line with previous work by Stringer et al. (2019).

In an orthogonal question, did the most spatially sensitive units share any detectable tuning features? A different model trained with electrophysiology data in contrast did not collapse in the range of top-ranked units plotted. Did this model collapse at some point after adding enough units, and how well did that correlate with the model for the imaging data?

Our electrophysiology datasets were much smaller in size (number of simultaneously recorded neurons) compared to our volumetric calcium imaging datasets, resulting in a much smaller total number of top ranked units detected per dataset. This precluded the determination of a collapse of decoder performance due to overfitting beyond the range plotted in Fig 4G.

How well did the form (and diversity) of the spatial tuning functions as recorded with electrophysiology resemble their calcium imaging counterparts? These fundamental questions could be addressed with more basic, but transparent analyses of the data (e.g., the diversity of spatial tuning functions of their recorded units across the population). Even if the model extracts features that are not obvious to the human eye in traditional visualisations, I would still find this interesting.

The diversity of the azimuth tuning curves recorded with calcium imaging (Fig. 3B) was qualitatively larger than the ones recorded with electrophysiology (Fig. 4B), potentially due to the larger sampling obtained with volumetric imaging. We did not perform a detailed comparison of the form and a more quantitative comparison of the diversity of these functions because the signals compared are quite different, as calcium indicator signal is subject to non linearities due to Ca2+ binding cooperativity and low pass filtering due to binding kinetics. We feared this could lead to misleading interpretations about the similarities or differences between the azimuth tuning functions in imaged and electrophysiology datasets. Our model uses statistical response dependency to stimulus azimuth, which does not rely on features from a descriptive statistic like mean response tuning. In this context, visualizing the trial-to-trial responses as a function of azimuth shows “features that are not obvious to the human eye in traditional visualizations” (Fig. 3D, left inset).

Finally, the readership is encouraged to interpret certain statements by the authors in the current version conservatively. How the brain ultimately extracts spatial neuronal data for perception is anyone's guess, but it is important to remember that this study only shows that a naïve Bayesian classifier could decode this information, and it remains entirely unclear whether the brain does this as well. For example, the model is able to achieve a prediction error that corresponds to the psychophysical threshold in mice performing a discrimination task (~30 {degree sign}). Although this is an interesting coincidental observation, it does not mean that the two metrics are necessarily related. The authors correctly do not explicitly claim this, but the manner in which the prose flows may lead a non-expert into drawing that conclusion.

To avoid misleading the non-expert readers, we have clarified in the manuscript that the observed correspondence between decoding error and psychophysical threshold is explicitly coincidental.

Page 13, end of middle paragraph:

“If we consider the median of the prediction error distribution as an overall measure of decoding performance, the single-trial response patterns from subsamples of at least the 7 top ranked units produced median decoding errors that coincidentally matched the reported azimuth discrimination ability of mice (Fig 4G, minimum audible angle = 31º) (Lauer et al., 2011).”

Page 14, bottom paragraph:

“Decoding analysis (Fig. 4F) of the population response patterns from azimuth dependent top ranked units simultaneously recorded with neuropixels probes showed that the 4 top ranked units are the smallest subsample necessary to produce a significant decoding performance that coincidentally matches the discrimination ability of mice (31° (Lauer et al., 2011)) (Fig. 5F, G).”

We also added to the Discussion sentences clarifying that a relationship between these two variables remains to be determined and it also remains to be determined if the DCIC indeed performs a bayesian decoding computation for sound localization.

Page 20, bottom:

“… Concretely, we show that sound location coding does indeed occur at DCIC on the single trial basis, and that this follows a comparable mechanism to the characterized population code at CNIC (Day and Delgutte, 2013). However, it remains to be determined if indeed the DCIC network is physiologically capable of Bayesian decoding computations. Interestingly, the small number of DCIC top ranked units necessary to effectively decode stimulus azimuth suggests that sound azimuth information is redundantly distributed across DCIC top ranked units, which points out that mechanisms beyond coding efficiency could be relevant for this population code.

While the decoding error observed from our DCIC datasets obtained in passively listening, untrained mice coincidentally matches the discrimination ability of highly trained, motivated mice (Lauer et al., 2011), a relationship between decoding error and psychophysical performance remains to be determined. Interestingly, a primary sensory representations should theoretically be even more precise than the behavioral performance as reported in the visual system (Stringer et al., 2021).”

Moreover, the concept of redundancy (of spatial information carried by units throughout the DCIC) is difficult for me to disentangle. One interpretation of this formulation could be that there are non-overlapping populations of neurons distributed across the DCIC that each could predict azimuth independently of each other, which is unlikely what the authors meant. If the authors meant generally that multiple neurons in the DCIC carry sufficient spatial information, then a single neuron would have been able to predict sound source azimuth, which was not the case. I have the feeling that they actually mean "complimentary", but I leave it to the authors to clarify my confusion, should they wish.

We observed that the response patterns from relatively small fractions of the azimuth sensitive DCIC units (4-7 top ranked units) are sufficient to generate an effective code for sound azimuth, while 32-40% of all simultaneously recorded DCIC units are azimuth sensitive. In light of this observation, we interpreted that the azimuth information carried by the population should be redundantly distributed across the complete subpopulation of azimuth sensitive DCIC units.

In summary, the present study represents a significant body of work that contributes substantially to the field of spatial auditory coding and systems neuroscience. However, limitations of the imaging dataset and model as applied in the study muddles concrete conclusions about how the DCIC precisely encodes sound source azimuth and even more so to sound localisation in a behaving animal. Nevertheless, it presents a novel and unique dataset, which, regardless of secondary interpretation, corroborates the general notion that auditory space is encoded in an extraordinarily complex manner in the mammalian brain.

Reviewer #3 (Public Review):

Summary:

Boffi and colleagues sought to quantify the single-trial, azimuthal information in the dorsal cortex of the inferior colliculus (DCIC), a relatively understudied subnucleus of the auditory midbrain. They used two complementary recording methods while mice passively listened to sounds at different locations: a large volume but slow sampling calcium-imaging method, and a smaller volume but temporally precise electrophysiology method. They found that neurons in the DCIC were variable in their activity, unreliably responding to sound presentation and responding during inter-sound intervals. Boffi and colleagues used a naïve Bayesian decoder to determine if the DCIC population encoded sound location on a single trial. The decoder failed to classify sound location better than chance when using the raw single-trial population response but performed significantly better than chance when using intermediate principal components of the population response. In line with this, when the most azimuth dependent neurons were used to decode azimuthal position, the decoder performed equivalently to the azimuthal localization abilities of mice. The top azimuthal units were not clustered in the DCIC, possessed a contralateral bias in response, and were correlated in their variability (e.g., positive noise correlations). Interestingly, when these noise correlations were perturbed by inter-trial shuffling decoding performance decreased. Although Boffi and colleagues display that azimuthal information can be extracted from DCIC responses, it remains unclear to what degree this information is used and what role noise correlations play in azimuthal encoding.

Strengths:

The authors should be commended for collection of this dataset. When done in isolation (which is typical), calcium imaging and linear array recordings have intrinsic weaknesses. However, those weaknesses are alleviated when done in conjunction with one another - especially when the data largely recapitulates the findings of the other recording methodology. In addition to the video of the head during the calcium imaging, this data set is extremely rich and will be of use to those interested in the information available in the DCIC, an understudied but likely important subnucleus in the auditory midbrain.

The DCIC neural responses are complex; the units unreliably respond to sound onset, and at the very least respond to some unknown input or internal state (e.g., large inter-sound interval responses). The authors do a decent job in wrangling these complex responses: using interpretable decoders to extract information available from population responses.

Weaknesses:

The authors observe that neurons with the most azimuthal sensitivity within the DCIC are positively correlated, but they use a Naïve Bayesian decoder which assume independence between units. Although this is a bit strange given their observation that some of the recorded units are correlated, it is unlikely to be a critical flaw. At one point the authors reduce the dimensionality of their data through PCA and use the loadings onto these components in their decoder. PCA incorporates the correlational structure when finding the principal components and constrains these components to be orthogonal and uncorrelated. This should alleviate some of the concern regarding the use of the naïve Bayesian decoder because the projections onto the different components are independent. Nevertheless, the decoding results are a bit strange, likely because there is not much linearly decodable azimuth information in the DCIC responses. Raw population responses failed to provide sufficient information concerning azimuth for the decoder to perform better than chance. Additionally, it only performed better than chance when certain principal components or top ranked units contributed to the decoder but not as more components or units were added. So, although there does appear to be some azimuthal information in the recoded DCIC populations - it is somewhat difficult to extract and likely not an 'effective' encoding of sound localization as their title suggests.

As described in the responses to reviewers 1 and 2, we chose the naïve Bayes classifier as a decoder to determine the influence of noise correlations through the most conservative approach possible, as this classifier would be least likely to find a contribution of correlated noise. Also, we chose this decoder due to its robustness against limited numbers of trials collected, in comparison to “data hungry” non linear classifiers like KNN or artificial neuronal nets. Lastly, we observed that small populations of noisy, unreliable (do not respond in every trial) DCIC neurons can encode stimulus azimuth in passively listening mice matching the discrimination error of trained mice. Therefore, while this encoding is definitely not efficient, it can still be considered effective.

Although this is quite a worthwhile dataset, the authors present relatively little about the characteristics of the units they've recorded. This may be due to the high variance in responses seen in their population. Nevertheless, the authors note that units do not respond on every trial but do not report what percent of trials that fail to evoke a response. Is it that neurons are noisy because they do not respond on every trial or is it also that when they do respond they have variable response distributions? It would be nice to gain some insight into the heterogeneity of the responses.

The limited number of azimuth trial repetitions that we could collect precluded us from making any quantification of the unreliability (failures to respond) and variability in the response distributions from the units we recorded, as we feared they could be misleading. In qualitative terms, “due to the high variance in responses seen” in the recordings and the limited trial sampling, it is hard to make any generalization. In consequence we referred to the observed response variance altogether as neuronal noise. Considering these points, our datasets are publicly available for exploration of the response characteristics.

Additionally, is there any clustering at all in response profiles or is each neuron they recorded in the DCIC unique?

We attempted to qualitatively visualize response clustering using dimensionality reduction, observing different degrees of clustering or lack thereof across the azimuth classes in the datasets collected from different mice. It is likely that the limited number of azimuth trials we could collect and the high response variance contribute to an inconsistent response clustering across datasets.

They also only report the noise correlations for their top ranked units, but it is possible that the noise correlations in the rest of the population are different.

For this study, since our aim was to interrogate the influence of noise correlations on stimulus azimuth encoding by DCIC populations, we focused on the noise correlations from the top ranked unit subpopulation, which likely carry the bulk of the sound location information.  Noise correlations can be defined as correlation in the trial to trial response variation of neurons. In this respect, it is hard to ascertain if the rest of the population, that is not in the top rank unit percentage, are really responding and showing response variation to evaluate this correlation, or are simply not responding at all and show unrelated activity altogether. This makes observations about noise correlations from “the rest of the population” potentially hard to interpret.

It would also be worth digging into the noise correlations more - are units positively correlated because they respond together (e.g., if unit x responds on trial 1 so does unit y) or are they also modulated around their mean rates on similar trials (e.g., unit x and y respond and both are responding more than their mean response rate). A large portion of trial with no response can occlude noise correlations. More transparency around the response properties of these populations would be welcome.

Due to the limited number of azimuth trial repetitions collected, to evaluate noise correlations we used the non parametric Kendall tau correlation coefficient which is a measure of pairwise rank correlation or ordinal association in the responses to each azimuth. Positive rank correlation would represent neurons more likely responding together. Evaluating response modulation “around their mean rates on similar trials” would require assumptions about the response distributions, which we avoided due to the potential biases associated with limited sample sizes.

It is largely unclear what the DCIC is encoding. Although the authors are interested in azimuth, sound location seems to be only a small part of DCIC responses. The authors report responses during inter-sound interval and unreliable sound-evoked responses. Although they have video of the head during recording, we only see a correlation to snout and ear movements (which are peculiar since in the example shown it seems the head movements predict the sound presentation). Additional correlates could be eye movements or pupil size. Eye movement are of particular interest due to their known interaction with IC responses - especially if the DCIC encodes sound location in relation to eye position instead of head position (though much of eye-position-IC work was done in primates and not rodent). Alternatively, much of the population may only encode sound location if an animal is engaged in a localization task. Ideally, the authors could perform more substantive analyses to determine if this population is truly noisy or if the DCIC is integrating un-analyzed signals.

We unsuccessfully attempted eye tracking and pupillometry in our videos. We suspect that the reason behind this is a generally overly dilated pupil due to the low visible light illumination conditions we used which were necessary to protect the PMT of our custom scope.

It is likely that DCIC population activity is integrating un-analyzed signals, like the signal associated with spontaneous behaviors including face movements (Stringer et al., 2019), which we observed at the level of spontaneous snout movements. However investigating if and how these signals are integrated to stimulus azimuth coding requires extensive behavioral testing and experimentation which is out of the scope of this study. For the purpose of our study, we referred to trial-to-trial response variation as neuronal noise. We note that this definition of neuronal noise can, and likely does, include an influence from un-analyzed signals like the ones from spontaneous behaviors.

Although this critique is ubiquitous among decoding papers in the absence of behavioral or causal perturbations, it is unclear what - if any - role the decoded information may play in neuronal computations. The interpretation of the decoder means that there is some extractable information concerning sound azimuth - but not if it is functional. This information may just be epiphenomenal, leaking in from inputs, and not used in computation or relayed to downstream structures. This should be kept in mind when the authors suggest their findings implicate the DCIC functionally in sound localization.

Our study builds upon previous reports by other independent groups relying on “causal and behavioral perturbations” and implicating DCIC in sound location learning induced experience dependent plasticity (Bajo et al., 2019, 2010; Bajo and King, 2012), which altogether argues in favor of DCIC functionality in sound localization.

Nevertheless, we clarified in the discussion of the revised manuscript that a relationship between the observed decoding error and the psychophysical performance, or the ability of the DCIC network to perform Bayesian decoding computations, both remain to be determined (please see responses to Reviewer #2).

It is unclear why positive noise correlations amongst similarly tuned neurons would improve decoding. A toy model exploring how positive noise correlations in conjunction with unreliable units that inconsistently respond may anchor these findings in an interpretable way. It seems plausible that inconsistent responses would benefit from strong noise correlations, simply by units responding together. This would predict that shuffling would impair performance because you would then be sampling from trials in which some units respond, and trials in which some units do not respond - and may predict a bimodal performance distribution in which some trials decode well (when the units respond) and poor performance (when the units do not respond).

In samples with more that 2 dimensions, the relationship between signal and noise correlations is more complex than in two dimensional samples (Montijn et al., 2016) which makes constructing interpretable and simple toy models of this challenging. Montijn et al. (2016) provide a detailed characterization and model describing how the accuracy of a multidimensional population code can improve when including “positive noise correlations amongst similarly tuned neurons”. Unfortunately we could not successfully test their model based on Mahalanobis distances as we could not verify that the recorded DCIC population responses followed a multivariate gaussian distribution, due to the limited azimuth trial repetitions we could sample.

Significance:

Boffi and colleagues set out to parse the azimuthal information available in the DCIC on a single trial. They largely accomplish this goal and are able to extract this information when allowing the units that contain more information about sound location to contribute to their decoding (e.g., through PCA or decoding on top unit activity specifically). The dataset will be of value to those interested in the DCIC and also to anyone interested in the role of noise correlations in population coding. Although this work is first step into parsing the information available in the DCIC, it remains difficult to interpret if/how this azimuthal information is used in localization behaviors of engaged mice.

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors):

General:

The manuscript is generally well written, but could benefit from a quick proof by a native English speaker (e.g., "the" inferior colliculus is conventionally used with its article). The flow of arguments is also generally easy to follow, but I would kindly ask the authors to consider elaborating or clarifying the following points (including those already mentioned in my public review).

(1) Choice of model:

There are countless ways one can construct a decoder or classifier that can predict a presented sensory stimulus based on a population neuronal response. Given the assumptions of independence as mentioned in my public review, I would ask the authors to explicitly justify their choice of a naïve Bayesian classifier.

A section detailing the logic of classifier choice is now included in the results section at page 10 and the last paragraph of page 18 from the revised version of the manuscript.

(2) Number of imaging repetitions:

For particularly noisy datasets, 14 repetitions is indeed quite few. I reckon this was not the choice of the authors, but rather limited by the inherent experimental conditions. Despite minimisation of required average laser power during the development of s-TeFo imaging, the authors still required almost 200 mW (which is still quite a lot of exposure). Although 14 repetitions for 13 azimuthal locations every 5 s is at face value a relatively short imaging session (~15 min.), at 191 mW, with the desire to image mice multiple times, I could imagine that this is a practical limitation the authors faced (to avoid excessive tissue heating or photodamage, which was assessed in the original Nature Methods article, but not here). Nevertheless, this logic (or whatever logic they had) should be explained for non-imaging experts in the readership.

This is now addressed in the answers to the public reviews.

(3) Redundancy:

It is honestly unclear to me what the authors mean by this. I don't speculate that they mean there are "redundant" (small) populations of neurons that sufficiently encode azimuth, but I'm actually not certain. If that were the case, I believe this would need further clarification, since redundant representations would be both inconsistent with the general (perhaps surprising) finding that large populations are not required in the DCIC, which is thought to be the case at earlier processing stages.

In the text we are referring to the azimuth information being redundantly distributed across DCIC top ranked units. We do not mention redundant “populations of neurons”.

(4) Correspondence of decoding accuracy with psychometric functions in mice: While this is an interesting coincidental observation, it should not be interpreted that the neuronal detection threshold in the DCIC somehow is somehow responsible its psychometric counterpart (which is an interesting yet exceedingly complex question). Although I do not believe the authors intended to suggest this, I would personally be cautious in the way I describe this correspondence. I mention this because the authors point it out multiple times in the manuscript (whereas I would have just mentioned it once in passing).

This is now clarified in the revised manuscript.

(5) Noisy vs. sparse:

I'm confident that the authors understand the differences between these terms, both in concept (stochastic vs. scattered) and in context (neuronal vs. experimental), but I personally would be cautious in the way I use them in the description of the study. Indeed, auditory neuronal signals are to my knowledge generally thought to be both sparse and noisy, which is in itself interesting, but the study also deals with substantial experimental (recording) noise, and I think it's important for the readership to understand when "noise" refers to the recordings (in particular the imaging data) and to neuronal activity. I mention this specifically because "noisy" appears in the title.

We have clarified this issue at the bottom of page 5 by adding the following sentences to the revised manuscript:

“In this section we used the word “noise” to refer to the sound stimuli used and recording setup background sound levels or recording noise in the acquired signals. To avoid confusion, from now on in the manuscript the word “noise” will be used in the context of neuronal noise, which is the trial-to-trial variation in neuronal responses unrelated to stimuli, unless otherwise noted.”

(6)  More details in the Methods:

The Methods section is perhaps the least-well structured part of the present manuscript in my view, and I encourage the authors to carefully go through it and add the following information (in case I somehow missed it).

a. Please also indicate the number of animals used here.

Added.

b. How many sessions were performed on each mouse?

This is already specified in the methods section in page 25:

“mice were imaged a total of 2-11 times (sessions), one to three times a week.”

We added for clarification:

“Datasets here analyzed and reported come from the imaging session in which we observed maximal calcium sensor signal (peak AAV expression) and maximum number of detected units.”

c. For the imaging experiments, was it possible to image the same units from session tosession?

This is not possible for sTeFo 2P data due to low spatial resolution which makes precisely matching neuron ROIs across sessions challenging.

d. Could the authors please add more detail to the analyses of the videos (to track facialmovements) or provide a reference?

Added citation.

e. The same goes for the selection of subcellular regions of interest that were used as"units."

Added to page 25:

“We used the CaImAn package (Giovannucci et al., 2019) for automatic ROI segmentation through constrained non negative matrix factorization and selected ROIs (Units) showing clear Ca transients consistent with neuronal activity, and IC neuron somatic shape and size (Schofield and Beebe, 2019).”

Specific: In order to maximise the efficiency of my comments and suggestions (as there are no line numbers), my numerated points are organised in sequential order.

(1) Abstract: I wouldn't personally motivate the study with the central nucleus of the IC (i.e. Idon't think this is necessary). I think the authors can motivate it simply with the knowledge gaps in spatial coding throughout the auditory system, in which such large data sets such as the ones presented here are of general value.

(2) Page 4: 15-50 kHz "white" noise is incorrect. It should be "band-passed" noise.

Changed.

(3) Supplemental figure 1, panel A: Since the authors could not identify cell bodiesunequivocally from their averaged volume timeseries data, it would be clearer to the readership if larger images are shown, so that they can evaluate (speculate) for themselves what subcellular structures were identified as units. Even better would be to include a planar image through a cross-section. As mentioned above, not everything determined for the cortex or hippocampus can be assumed to be true for the DCIC.

The raw images and segmentations are publicly available for detailed inspections.

(4) Supplemental figure 2, panel A: This panel requires further explanation, in particular thepanel on the right. I assume that to be a simple subtraction of sequential frames, but I'm thrown off by the "d(Grey)" colour bar. Also, if "grey" refers to the neutral colour, it is conventionally spelled "gray" in US-American English.

Changed.

(5) Supplemental figure 2, panel B: I'm personally curious why the animals exhibitedmovement just prior to a stimulus. Did they learn to anticipate the presentation of a sound after some habituation? Is that somehow a pre-emptive startle response? We observe that in our own experiments (but as we stochastically vary the inter-trial-intervals, the movement typically occurs directly after the stimulus). I don't suggest the authors dwell on this, but I find it an interesting observation.

It is indeed interesting, but we can’t conclude much about it without comparing it to random inter-trial-intervals.

(6) Supplemental figure 3: I personally find these data (decoding of all electrophysiologicaldata) of central relevance to the study, since it mirrors the analyses presented for its imaging data counterpart and encourage the authors to move it to the main text.

Changed.

(7) Page 12: Do the authors have any further analyses of spatial tuning functions? We allknow they can parametrically obscure (i.e., bi-lobed, non-monotonic, etc.), but having these parameters (even if just in a supplemental figure) would be informative for the spatial auditory community.

We dedicated significant effort to attempt to parametrize and classify the azimuth response dependency functions from the recorded DCIC cells in an unbiased way. Nevertheless, given the observed response noise and the “obscure” properties of spatial tuning functions mentioned by the reviewer, we could only reach the general qualitative observation of having a more frequent contralateral selectivity.

(8) Page 14 (end): Here, psychometric correspondence is referenced. Please add theLauer et al., (2011) reference, or, as I would, remove the statement entirely and save it for the discussion (where it is also mentioned and referenced).

Changed.

(9) Figure 5, Panels B and C: Why don't the authors report the Kruskal-Wallis tests (forincreasing number of units training the model), akin to e.g., Panel G of Figure 4? I think that would be interesting to see (e.g., if the number of required units to achieve statistical significance is the same).

Within class randomization produced a moderate effect on decoder performance, achieving statistical significance at similar numbers of units, as seen in figure 5 panels B and C. We did not include these plots for the sake of not cluttering the figure with dense distributions and fuzzing the visualization of the differences between the distributions shown.

(10) Figure 5, Panels B and C (histograms): I see a bit of skewedness in the distributions(even after randomisation). Where does this come from? This is just a small talking point.

We believe this is potentially due to more than one distribution of pairwise correlations combined into one histogram (like in a Gaussian mixture model).

(11) Page 21: Could the authors please specify that the Day and Delgutte (2013) study wasperformed on rabbits? Since rabbits have an entirely different spectral hearing range compared to mice, spatial coding principles could very well be different in those animals (and I'm fairly certain such a study has not yet been published for mice).

Specified.

(12) Page 22: I'd encourage the authors to remove the reference to Rayleigh's duplextheory, since mice hardly (if at all) use interaural time differences for azimuthal sound localisation, given their generally high-frequency hearing range.

That sentence is meant to discuss beyond the mouse model an exciting outlook of our findings in light of previous reports, which is a hypothetical functional relationship between the tonotopy in DCIC and the spatial distribution of azimuth sensitive DCIC neurons. We have clarified this now in the text.

(13) Page 23: I believe the conventional verb for gene delivery with viruses is still"transduce" (or "infect", but not "induce"). What was the specific "syringe" used for stereotactic injections? Also, why were mice housed separately after surgery? This question pertains to animal welfare.

Changed. The syringe was a 10ml syringe to generate positive or negative pressure, coupled to the glass needle through a silicon tubing via a luer 3-way T valve. Single housing was chosen to avoid mice compromising each other’s implantations. Therefore this can be seen as a refinement of our method to maximize the chances of successful imaging per implanted mouse.

(14) Page 25: Could the authors please indicate the refractory period violation time windowhere? I had to find it buried in the figure caption of Supplementary figure 1.

Added.

(15) Page 27: What version of MATLAB was used? This could be important for reproductionof the analyses, since The Mathworks is infamously known to add (or even more deplorably, modify) functions in particular versions (and not update older ones accordingly).

Added.

Reviewer #3 (Recommendations For The Authors):

Overall I thought this was a nice manuscript and a very interesting dataset. Here are some suggestions and minor corrections:

You may find this work of interest - 'A monotonic code for sound azimuth in primate inferior colliculus' 2003, Groh, Kelly & Underhill.

We thank the reviewer for pointing out this extremely relevant reference, which we regrettably failed to cite. It is now included in the revised version of the manuscript.

In your introduction, you state "our findings point to a functional role of DCIC in sound location coding". Though your results show that there is azimuthal information contained in a subset of DCIC units there's no evidence in the manuscript that shows a functional link between this representation and sound localization.

This is now addressed in the answers to the public reviews.

I found the variability in your DCIC population quite striking - especially during the intersound intervals. The entrainment of the population in the imaging datatset suggests some type of input activating the populations - maybe these are avenues for further probing the variability here:

(1) I'm curious if you can extract eye movements from your video. Work from Jennifer Grohshows that some cells in the primate inferior colliculus are sensitive to different eye positions (Groh et. al., 2001). With recent work showing eye movements in rodents, it may explain some of the variance in the DCIC responses.

This is now addressed in the answers to the public reviews.

(2) I was also curious if the motor that moves the speaker made noise It could be possiblesome of the 'on going' activity could be some sound-evoked response.

We were careful to set the stepper motor speed so that it produced low frequency noise, within a band mostly outside of the hearing range of mice (<4kHz). Nevertheless, we cannot fully rule out that a very quiet but perhaps very salient component of the motor noise could influence the activity during the inter trial periods. The motor was stationary and quiet for a period of at least one stimulus duration before and during stimulus presentation.  

(3) Was the sound you present frozen or randomly generated on each trial? Could therebe some type of structure in the noise you presented that sometimes led cells to respond to a particular azimuth location but not others?

The sound presented was frozen noise. This is now clarified in the methods section.

It may be useful to quantify the number of your units that had refractory period violations.

Our manual curation of sorted units was very stringent to avoid mixing differently tuned neurons. The single units analyzed had very infrequent refractory period violations, in less than ~5% of the spikes, considering a 2 ms refractory period.

Was the video recording contralateral or ipsilateral to the recording?

The side of the face ipsilateral to the imaged IC was recorded. Added to methods.

I was struck by the snout and ear movements - in the example shown in Supplementary Figure 2B it appears as they are almost predicting sound onset. Was there any difference in ear movements in the habituated and non-habituated animals? Also, does the placement of the cranial window disturb any of the muscles used in ear movement?

Mouse snout movements appear to be quite active perhaps reflecting arousal (Stringer et al., 2019). We cannot rule out that the cranial window implantation disturbed ear movement but while moving the mouse headfixed we observed what could be considered normal ear movements.

Did you correlate time-point by time-point in the average population activity and movement or did you try different temporal labs/leads in case the effect of the movements was delayed in some way?

Point by point due to 250ms time resolution of imaging.

Are the video recordings only available during the imaging? It would be nice to see the same type of correlations in the neuropixel-acquired data as well.

Only imaging. For neuropixels recordings, we were skeptical about face videography as we suspected that face movements were likely influenced by the acute nature of the preparation procedure. Our cranial window preparation in the other hand involved a recovery period of at least 4 weeks. Therefore we were inclined to perform videographical interrogation of face movements on these mice instead.

If you left out more than 1 trial do you think this would help your overfitting issue (e.g. leaving out 20% of the data).

Due to the relatively small number of trial repetitions collected, fitting the model with an even smaller training dataset is unlikely to help overfitting and will likely decrease decoder performance.

It would be nice to see a confusion matrix - even though azimuthal error and cumulative distribution of error are a fine way to present the data - a confusion matrix would tell us which actual sounds the decoder is confusing. Just looking at errors could result in some funky things where you reduce the error generally but never actually estimate the correct location.

We considered confusion matrices early on in our study but they were not easily interpretable or insightful, likely due to the relatively low discrimination ability of the mouse model with +/- 30º error after extensive training. Therefore, we reasoned that in passively listening mice (and likely trained mice too) with limited trial repetitions, an undersampled and diffuse confusion matrix is expected which is not an ideal means of visualizing and comparing decoding errors. Hence we relied on cumulative error distributions.

Do your top-ranked units have stronger projections onto your 10-40 principal components?

It would be interesting to know if the components are mostly taking into account those 30ish percent of the population that is dependent upon azimuth.

Inspection of PC loadings across units ranked based on response dependency to stimulus azimuth does not show a consistent stronger projection of top ranked units onto the first 10-40 principal components (Author response image 3).

Author response image 3.

PC loading matrices for each recorded mouse. The units recorded in each mouse are ranked in descending order of response dependency to stimulus azimuth based on  the p value of the chi square test. Units above the red dotted line display a chi square p value < 0.05, units below this line have p values >= 0.05.

How much overlap is there in the tuning of the top-ranked units?

This is quite varying from mouse to mouse and imaging vs electrophysiology, which makes it hard to make a generalization since this might depend on the unique DCIC population sampled in each mouse.

I'm not really sure I follow what the nS/N adds - it doesn't really measure tuning but it seems to be introduced to discuss/extract some measure of tuning.

nS/N is used to quantify how noisy neurons are, independent of how sensitive their responses are to the stimulus azimuth.

Is the noise correlation - observed to become more positive - for more contralateral stimuli a product of higher firing rates due to a more preferred stimulus presentation or a real effect in the data? Was there any relationship between distance and strength of observed noise correlation in the DCIC?

We observed a consistent and homogeneous trend of pairwise noise correlation distributions either shifted or tailed towards more positive values across stimulus azimuths, for imaging and electrophysiology datasets (Author response image 3). The lower firing frequency observed in neuropixels recordings in response to ipsilateral azimuths could have affected the statistical power of the comparison between the pairwise noise correlation coefficient distribution to its randomized chance level, but the overall histogram shapes qualitatively support this consistent trend across azimuths (Author response image 4).

Author response image 4.

Distribution histograms for the pairwise correlation coefficients (Kendall tau) from pairs of simultaneously recorded top ranked units across mice (blue) compared to the chance level distribution obtained through randomization of the temporal structure of each unit’s activity to break correlations (purple). Vertical lines show the medians of these distributions. Imaging data comes from n = 12 mice and neuropixels data comes from n = 4 mice.

Typos:

'a population code consisting on the simultaneous" > should on be of?

'half of the trails' > trails should be trials?

'referncing the demuxed channels' > should it be demixed?

Corrected.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Tateishi et al. report a Tn-seq-based analysis of genetic requirements for growth and fitness in 8 clinical strains of Mycobacterium intracellulare Mi), and compare the findings with a type strain ATCC13950. The study finds a core set of 131 genes that are essential in all nine strains, and therefore are reasonably argued as potential drug targets. Multiple other genes required for fitness in clinical isolates have been found to be important for hypoxic growth in the type strain.

Strengths:

The study has generated a large volume of Tn-seq datasets of multiple clinical strains of Mi from multiple growth conditions, including from mouse lungs. The dataset can serve as an important resource for future studies on Mi, which despite being clinically significant remains a relatively understudied species of mycobacteria.

Thank you for reviewing our manuscript and finding the significance of our data.

Weaknesses:

The paper lacks clarity in data presentation and organization. For example, some of the key data on cfu counts of clinical Mi strains in a mouse model can be presented along with the Tn-seq dataset in Figure 6, the visualization of which can be improved with volcano plots. etc. Improvement in data visualization is perhaps necessary throughout the paper.

Thank you for the comment on the data presentation of in vivo studies. We previously revealed the time-course data on CFUs, animal survival, and tissue pathology from the pure strains (Tateishi Y. BMC Microbiol. 2023; new Ref #22) . Based on these data, we assumed that we would be able to harvest sufficient number of colonies from mice infected with M.i.27 or M.i.198, and we performed in vivo TnSeq studies using these two strains. We have referred to our previous publication (new Ref #22) on the virulence of MAC-PD strains used in this study for mice in the revised manuscript (page12, line 212).

The data of CFU counts were shown in new Supplementary Fig. 3b. In the manuscript text, we explained as follows (page 12, lines 212-216): “The time course of the changes in the bacterial burden showed a pattern similar to those of the wild-type strains M.i.198 and M.i.27, respectively, except that it was not possible to harvest sufficient colonies (as few as 104/mouse) in the few mice infected with the M.i.27 Tn mutant strain in week 8 and week 16 (page 12, lines 212-216; new Supplementary Fig, 3b, new Supplementary Table 8)”.

Regarding the suggestion to include volcano plots, we appreciate the proposal but chose not to adopt this format, as the main aim of this study was to identify genes commonly required for in vitro and in vivo fitness across multiple M. intracellulare strains, rather than to highlight differential genetic requirements within a single strain. Volcano plots are useful for visualizing differential values and significance for a single dataset but are less suited for cross-strain comparisons of shared gene sets. Our approach is aligned with the methodology used by Cary et al. (PLoS Pathog. 2018; new Ref#8), who similarly focused on identifying conserved genetic requirements across M. tuberculosis genotypes without employing volcano plots.

[References]

Tateishi, Y. et al. Virulence of Mycobacterium intracellulare clinical strains in a mouse model of lung infection - role of neutrophilic inflammation in disease severity. BMC Microbiol 23, 94 (2023).

Carey, A.F. et al. TnSeq of Mycobacterium tuberculosis clinical isolates reveals strain-specific antibiotic liabilities. PLoS Pathog 14, e1006939 (2018).

The primary claim of the study that the clinical strains are better adapted for hypoxic growth is not well-supported by the data presented in Figure 7.

Thank you for the comments on the difference of adaptation for hypoxic growth between ATCC13950 and clinical MAC-PD strains. To clarify, growth rates shown in Figure 7 were calculated at the inflection point (midpoint) of the growth curves, which were modeled using a four-parameter logistic (4P logistic) model. As described in the Discussion, we found the pattern of hypoxic adaptation characteristics of the clinical MAC-PD strains from the growth curve forms. Taking into consideration the impact of growing bacteria on the disease progression of MAC-PD, the slow growth with early entry to log phase implicates the continuous impact on the infected hosts during logarithmic bacterial growth, which may be involved in the persistent and steadily progressive illness of MAC-PD for years in humans.

Unlike time-lapse imaging assay, the completely seamless sampling of culture for CFU assay is impossible. Nevertheless, we collected sufficient timepoints to allow reliable curve fitting with the 4P logistic model and thus consider our growth data to represent a valid approximation of continuous growth dynamics.

Regarding the suggestion of mixed culture experiments, we agree that such studies could be informative. However, co-culture conditions introduce additional variables, including inter-strain competition or synergy, which can obscure the specific contributions of hypoxic adaptation in each strain. Therefore, we believe that the current approach using monoculture growth curves under defined oxygen conditions offers a clearer interpretation of strain-specific hypoxic responses.

The title of the paper is misleading as the study doesn't provide any mechanistic aspect of hypoxic adaptation in Mi.

Thank you for the comment on the article title. We admit that this paper does not directly reveal the mechanism of hypoxic adaptation in M. intracellulare strains but provides the data on the different pattern of hypoxic adaptation between M. intracellulare strains in relation to the difference of genetic requirements. Therefore, we revised the title as ”Functional genomics reveals strain-specific genetic requirements conferring hypoxic growth in Mycobacterium intracellulare”

Reviewer #2 (Public Review):

Summary:

In the study titled "Functional genomics reveals the mechanism of hypoxic adaptation in nontuberculous mycobacteria" by Tateishi et al., the authors have used TnSeq to identify the common essential and growth-defect-associated genes that represent the genomic diversity of clinical M. intracellulare strains in comparison to the reference type strain. By estimating the frequency of Tn insertion, the authors speculate that genes involved in gluconeogenesis, the type VII secretion system, and cysteine desulfurase are relatively critical in the clinical MAC-PD strains than in the type strain, both for the extracellular survival and in a mouse lung infection model.

Based on their analysis, the authors proposed to identify the mechanism of hypoxic adaptation in nontuberculous mycobacteria (NTM) which offer promising drug targets in the strains causing clinical Mycobacterium avium-intracellulare complex pulmonary disease (MAC-PD).

Strengths:

A major strength of the manuscript is the performance of the exhaustive set of TnSeq experiments with multiple strains of M. intracellulare during in vitro growth and animal infection.

Thank you for reviewing our manuscript and acknowledging the performance of producing datasets in this study.

Weaknesses:

(1) The study suffers from the authors' preconceived bias toward a small subset of genes involved in hypoxic pellicle formation in ATCC13950.

Thank you for the comment regarding a potential bias toward a small subset of genes involved in hypoxic pellicle formation in ATCC13950. The rationale for the importance of hypoxic pellicle genes in clinical MAC-PD strains is that the profiles of genetic requirements in each bacterial strain reflect the adaptation to the environment in which each strain lives. When the strains are placed in a special environment, they can adapt to the situation by altering the profiles of genetic requirements, resulting in the remodeling of metabolic pathways.

In this study, we found that several of these pellicle-associated genes also showed increased genetic requirement in the clinical MAC-PD strains, suggesting a possible overlap in hypoxic adaptation mechanisms. We did not insist that clinical MAC-PD strains showed an increase of genetic requirements in all genes of hypoxic pellicle formation. Except for the gene sets involved in hypoxic pellicle formation in ATCC13950, almost no global information has been revealed on the pathogenesis of nontuberculous mycobacterial disease, which differs from the case of tuberculosis. Along with this finding, we investigated the effect of gene silencing on bacterial growth and preferential hypoxic adaptation observed by growth kinetics in clinical MAC-PD strains compared to ATCC13950. At first glance, to focus on the gene sets of hypoxic pellicle formation seems to be “biased”, but we proceeded this research step by step based on our achievements. We consider these data provide valuable information on the pathogenesis of MAC-PD by clinical MAC-PD strains.

We have added the description of the rationale for the importance of hypoxic pellicle genes in clinical MAC-PD strains in the revised manuscript (page 9, lines 148-155).

(2) An important set of data with the ATCC13950 reference strain is missing in the mouse infection study. In the absence of this, it is difficult to establish whether the identified genes are critical for infection/intracellular proliferation, specifically in the clinical isolates that are relatively more adapted for hypoxia.

Thank you for the comment on the necessity of setting ATCC13950 as a control strain of mouse TnSeq experiment. To set ATCC13950 as a control strain in mouse infection experiments would be ideal. However, we proved that ATCC13950 is eliminated within 4 weeks of infection (Tateishi Y. BMC Microbiol. 2023; new Ref#22). That means, it is impossible to perform in vivo TnSeq study due to the inability to harvest sufficient number of colonies.

[Reference]

Tateishi, Y. et al. Virulence of Mycobacterium intracellulare clinical strains in a mouse model of lung infection - role of neutrophilic inflammation in disease severity. BMC Microbiol 23, 94 (2023).

(3) Statistical enrichment analysis of gene sets by GSEA wrongly involves genes required for hypoxic pellicle formation in ATCC13950 together with the gene sets found essential in the clinical MAC-PD strains, to claim that a significant % of genes belong to hypoxia-adaptation pathways. It could be factually incorrect because a majority of these might overlap with those found critical for the in vitro survival of MAC-PD strains (and may not be related to hypoxia).

Thank you for the suggestion on the re-analysis of gene enrichment analysis of genes required for M.i.27 and M.i.198 in vivo infection, individually with genes involved in hypoxic pellicle formation in ATCC13950 and with those showing increased genetic requirements in clinical MAC-PD strains compared to ATCC13950.

About 50% (92 and 94 out of 181 genes through Day 1 to Week 16 and Week4 to Week16 of infection) and 40% (70 and 79 genes out of 179 through Day 1 to Week 16 and Week 4 to Week 16 of infection) of genes required for hypoxic pellicle formation in ATCC13950 were listed as enriched in genes required for mouse lung infection in M.i.27 and M.i.198, respectively. In addition, about 42% (54 and 56 out of 128 genes through Day 1 to Week 16 and thorough Week 4 to Week 16 of infection) and 40% (79 and 68 out of 179 genes through Day 1 to Week 16 and through Week 4 to Week 16 of infection) of genes showing increased requirements in clinical MAC-PD strains compared to ATCC13950 were listed as enriched in genes required for mouse lung infection in M.i.27 and M.i.198, respectively.

These data indicate that about 40-50% genes required for in vitro hypoxic pellicle formation are shared with the genes required for in vivo bacterial growth, and that about 40% strain-dependent/accessory essential genes are shared with the genes required for in vivo bacterial growth. Thus, the genes required for the growth of M.i.27 and M.i.198 in mouse lungs are enriched individually with those involved in hypoxic pellicle formation in ATCC13950, and with the gene sets found critical for in vitro growth. We have added the description of the reanalyzed data of GSEA in the manuscript (pages 16-17, lines 287-290). And the details of reanalyzed data of GSEA have been shown in Supplementary Fig. 5 and 6 as well as Supplementary Tables 15 and 16.

(4) Validation of mouse infection experiments with individual mutants is missing.

Thank you for the suggestion on the validation of the TnSeq hit genes on the in vivo survival. We acknowledge the importance of validating the TnSeq-hit genes by constructing knockout mutants. We have recently succeeded in constructing the vectors for making knockout strains of M. intracellulare (Tateishi. Microbiol Immunol. 2024). We will proceed to the infection experiment of knockout mutants by using our system for constructing them.

[Reference]

Tateishi Y. et al. Construction of knockout mutants in Mycobacterium intracellulare ATCC13950 strain using a thermosensitive plasmid containing negative selection marker rpsL. Microbiol Immunol 68, 339-347 (2024).

(5) Phenotypes with TnSeq and CRISPRi-based KD exhibit poor correlation with misleading justifications by the authors.

Thank you for the comment on the issue of inconsistent results between TnSeq and CRISPR-i based knockdown. We acknowledge that some inconsistencies were observed, particularly among strain-dependent/accessory essential or growth-defect-associated genes. By contrast, we found consistent data between TnSeq and CRISPR-i based knockdown results among universal essential genes such as glcB, inhA, gyrB and embB. Although the mechanism has not been fully proven yet, we consider that such inconsistent phenotypes with TnSeq and CRISPR- based knockdown may be related to the recently revealed bypass mechanism of gene essentiality which is characteristically observed in strain-specific/accessory essential genes (Rosconi F. Nat Micorbiol. 2022; new Ref#14). They suggested this bypass mechanism of gene essentiality in strain-dependent/accessory essential or growth-defect-associated genes from the ‘forced-evolution experiments’ of 36 clinical Streptococcus pneumoniae strains. For example, knockout mutants are successfully recovered from transformation experiments targeting strain-specific/accessory essential genes in TnSeq such as cytidine monophosphate kinase cmk, formate tetrahydrofolate ligase fhs and farnesyl-diphosphate synthase fpp. The bypassing of gene essentiality can be suggested by observing suppressor mutations and synthetic lethality in knockout strains. By contrast, universal essential genes fulfill the following three categories: i) high levels of conservation within and often across species, iii) limited genetic diversity, and iii) high and stable expression levels. Consequently, the universal essential genes are rigid, largely immutable key components to an organism’s survival. In the universal essential genes, the knockout recovery fails as shown by no colonies or only appearance of merodiploids. Taking into consideration such bypass mechanism of gene essentiality in strain-dependent/accessory essential genes, the lower effect of gene silencing of strain-dependent/accessory essential genes on bacterial growth may reflect pathway rewiring that helps the bacterial growth under suppression of the target gene expression.

We have added the description of the possible reason for inconsistency between TnSeq and CRISPR-i results in the Result and Discussion in the revised manuscript (page 21, lines 367-376; pages 28-29, lines 489-519).

[Reference]

Rosconi, F. et al. A bacterial pan-genome makes gene essentiality strain-dependent and evolvable. Nat Microbiol 7, 1580–1592 (2022).

In summary, this study is unable to provide mechanistic insights into why and how different MAC-PD mutant strains exhibit differential survival (in vitro and in animals) and adaptation to hypoxia. It remains to understand why the clinical strains show better adaptation to hypoxia and what is the impact of other stresses on their growth rates.

Thank you for the comments on the issue of being unable to prove the mechanism of MAC-PD pathogenesis and adaptation to hypoxia. We admit that the original manuscript did not provide the apparent reason and mechanism of MAC-PD pathogenesis and adaptation to hypoxia. Following the comment, we have modified the manuscript tile as “Functional genomics reveals strain-specific genetic requirements conferring hypoxic growth in Mycobacterium intracellulare”.

However, we revealed the diversity of genetic requirements among the genus M. intracellulare including the type strain ATCC13950 and clinical MAC-PD strains. We revealed the characteristics of genetic requirements in clinical MAC-PD strains as increased genetic requirements of gluconeogenesis, type VII secretion system and cysteine desulfurase, the former two of which are also required in hypoxic pellicle formation in ATCC13950. Along with this, we demonstrated the difference of growth behavior under hypoxia between clinical MAC-PD strains and ATCC13950. Overall, we consider that we could provide the basic information suggesting the involvement of difference of genetic requirements among strains in the pathogenesis of MAC-PD.

Reviewer #3 (Public Review):

Summary:

The study by Tateishi et al. utilized TnSeq in nine genetically diverse M. intracellulare strains, identifying 131 common essential and growth-defect-associated genes across those strains, which could serve as potential drug targets. The authors also provided an overview of the differences in gene essentiality required for hypoxic growth between the reference strain and the clinical strains. Furthermore, they validated the universal and accessory/strain-dependent essential genes by knocking down their expression using CRISPRi technique. Overall, this study offers a comprehensive assessment of gene requirements in different clinical strains of M. intracellular.

Thank you for reviewing our manuscript and finding the significance of our data.

(1) The rationale for using ATCC13950 versus clinical strains needs to be clarified. The reference strain ATCC13950 was obtained from the abdominal lymph node of a patient around 10 years ago and is therefore considered a clinical strain that has undergone passages in vitro. How many mutations have accumulated during these in vitro passages? Are these mutations significant enough to cause the behavior of ATCC13950 to differ from other recently sampled clinical strains? From the phylogenetic tree, ATCC13950 is located between M018 and M.i.27. Did the authors observe a similarity in gene essentiality between ATCC13950 and its neighbor strains? What is the key feature that separates ATCC13950 from these clinical strains? The authors should provide a strong rationale for how to interpret the results of this comparison in a clinical or biological context.

Thank you for the comments on the rationale for using ATCC13950 versus clinical strains and the key feature that separates ATCC13950 from clinical MAC-PD strains.

ATCC13950 was isolated in 1949, (not around 10 years ago) from 34-month-old female abdominal lymph node (Cuttino. Am J Pathol 1949; new Ref#11). Of note, the clinical background of the patient infected with ATCC13950 is quite different from the patients with MAC-pulmonary disease (MAC-PD), the incidence rate of which has been increasing worldwide without predisposing immunological disorders. ATCC13950 has been regarded as a type strain of genus M. intracellulare historically. And ATCC13950 is the first M. intracellulare strain to be sequenced in 2012 (Kim. J Bacteriol 2012; new Ref#59).

The rationale for using ATCC13950 versus clinical MAC-PD strains is to find the answer to the question whether the essential genes and genetic requirements are similar or different between clinical MAC-PD strains and historical type strain ATCC13950. So far, there are two reports on TnSeq that compare genetic requirements between clinical mycobacterial strains and the type strains, one of which is M. tuberculosis (Carey AF. PLoS Pathogens. 2018; new Ref#8) and the other is M. abscessus (Akusobi C. mBio. 2025; new Ref#9, published after submission of our manuscript). They reported the difference and diversity of genetic requirements between clinical strain and type strains such as M. tuberculosis H37Rv and M. abscessus ATCC19977. We have added the mention of these previous reports to explain the rationale for setting the type strain ATCC13950 as a referential control strain. (page 5, lines 83-87)

The genetic and functional analysis of clinical MAC-PD strains has not been conducted for a long time. In 2021, we have revealed the genomic diversity between clinical MAC-PD and ATCC13950 by comparative genomic analysis (Tateishi BMC Microbiol. 2021; new Ref#5). Except for our TnSeq study of ATCC13950 (Tateishi Sci Rep 2020; new Ref#10), no functional analysis has been conducted in clinical M. intracellulare strains. On our research stream of clinical MAC-PD strains, we expected that we could reveal the functional genomic characteristics of clinical MAC-PD strains by setting ATCC13950 as a referential control strain for analyzing TnSeq data.

It seems an interesting viewpoint to consider the relationship between accumulation of mutations by in vitro passages during prolonged periods from first isolation in ATCC13950, and the difference of phenotypes between ATCC13950 and recently sampled clinical MAC-PD strains. However, there are no time-course samples of ATCC13950 isolates available. Therefore, we can neither investigate how many mutations have accumulated in a time-course manner, nor evaluate how much the accumulated mutations influence the phenotype in ATCC13950. It can be expected that the accumulation of in vitro mutations may cause the behavior of ATCC13950 different from clinical MAC-PD strains. However, it is to be elucidated yet which kinds of factors contribute to the characteristics of ATCC13950 that differ from clinical MAC-PD strains specifically.

It seems an interesting viewpoint to investigate the similarity of gene essentiality between genetical neighbor strains. However, we focused on the overview of the profiles of gene essentiality in clinical MAC-PD strains compared to ATCC13950. Thus, it was out of scope to elucidate the details of gene essentiality in each genetic phylogeny that clinical MAC-PD strains belong. The overview of phylogenetic trees should be referred to our previous publication on the comparative genomic analysis of 55 strains (Tateishi Y. BMC Microbiol. 2021; new Ref#5, new Supplementary Fig. 1), and we have shown Fig. 1 as the extracted phylogenetic tree of subject strains. To elucidate the details of gene essentiality in each genetic clade, it would be necessary to include a considerable number of strains that we used for comparative genomic analysis in 2021 (Tateishi Y. BMC Microbiol. 2021; new Ref#5). Furthermore, it would be necessary to set a referential control strain other than ATCC13950 for comparing gene essentiality. So far, it is not the highest priority for us to elucidate the similarity of gene essentiality between phylogenetic clades in detail, and such investigation will be planned as a future study.

The key features that separate ATCC13950 and clinical MAC-PD strains have not been proved yet, in contrast to the case of M. tuberculosis such as mutations in the gene of the response regulator PhoPR in the type strain H37Rv vs most clinical strains. However, the features that separate ATCC13950 and clinical MAC-PD strains may not be explained by a single genetic factor but may be explained by complicated factors such as epigenetic and/or regulatory factors. For example, the reason for the weakened virulence of H37Ra compared to H37Rv has not been able to be explained by simple genetic differences (Brosch R. Infect Immun. 1999).

In summary, we set the historical type strain ATCC13950 which is derived from infant abdominal lymphadenitis as a referential control strain for TnSeq analysis, because we intended to reveal the characteristics of clinical MAC-PD strains in terms of the gene essentiality and genetic requirements by comparing the clinical MAC-PD strains with the non-MAC-PD reference strain. We consider that the profiles of gene essentiality and genetic requirements specific to clinical MAC-PD strains confer the pathogenesis in an increasing number of MAC-PD patients worldwide without predisposing immunological disorders.

[References]

Cuttino, J.T. & Mc, C.A. Pure granulomatous nocardiosis, a new fungus disease distinguished by intracellular parasitism; a description of a new disease in man due to a hitherto undescribed organism, Nocardia intracellularis, n. sp., including a study of the biologic and pathogenic properties of this species. Am J Pathol 25, 1-47 (1949).

Kim, B.J. et al. Complete genome sequence of Mycobacterium intracellulare clinical strain MOTT-64, belonging to the INT1 genotype. J Bacteriol 194, 3268 (2012).

Carey, A.F. et al. TnSeq of Mycobacterium tuberculosis clinical isolates reveals strain-specific antibiotic liabilities. PLoS Pathog 14, e1006939 (2018).

Akusobi. C. et al.. Transposon-sequencing across multiple Mycobacterium abscessus isolates reveals significant functional genomic diversity among strains. mBio 6, e0337624 (2025).

Tateishi, Y. et al. Comparative genomic analysis of Mycobacterium intracellulare: implications for clinical taxonomic classification in pulmonary Mycobacterium avium-intracellulare complex disease. BMC Microbiol 21, 103 (2021).

Tateishi, Y. et al. Genome-wide identification of essential genes in Mycobacterium intracellulare by transposon sequencing - Implication for metabolic remodeling. Sci Rep 10, 5449 (2020)

Brosch R. et al. Genomic analysis reveals variation between Mycobacterium tuberculosis H37Rv and the attenuated M. tuberculosis H37Ra strain. Infect Immun. 67, 5768-74 (1999).

(2) Regarding the 'nine representative strains of M. intracellulare with diverse genotypes in this study,' how were these nine strains selected? To what extent do they represent the genetic diversity of the M. intracellulare population? A phylogenetic tree illustrating the global genetic diversity of the M. intracellulare population, with these strains marked on it, would be important to demonstrate their genetic representativeness.

Thank you for the comments on the selection of 9 subject strains. We selected the 9 strains based on the phylogenetic tree we published in 2021 (BMC Microbiol 2021; new Ref#5). We have shown the global phylogenetic tree of the M. intracellulare population in new supplementary Fig. 1. We have selected 4 or 5 strains from the major two groups (typical M. intracellulare group and M. paraintracellulare-M. indicus pranii group) for this TnSeq study, respectively.

[Reference]

Tateishi, Y. et al. Comparative genomic analysis of Mycobacterium intracellulare: implications for clinical taxonomic classification in pulmonary Mycobacterium avium-intracellulare complex disease. BMC Microbiol 21, 103 (2021).

(3) The authors observed a considerable amount of differential gene requirements in clinical strains. However, the genetic underpinning underlying the differential requirement of genes in clinical strains was not investigated or discussed. Because M. intracellulare has a huge number of accessory genes, the authors should at least check whether the differential requirement could be explained by the existence of a second copy of functional analogous genes or duplications.

Thank you for the comments on the effect of gene duplication on the change of genetic requirements between strains. Following the comments, we conducted blast search for the 162 genes showing increased Tn insertion reads in each subject strain. We found that M019 has duplicate genes of OCU_RS44705 coding adenosylhomocysteinase (LOCUS_42940: ahcY_1, LOCUS_21000: ahcY_2). However, there were no duplicate genes found in the remaining 161 genes showing increased Tn insertion reads.

From these results, we consider that gene duplication has minor effects on the change of genetic requirements between strains. Rather, sequence differences and accessory genes may play a key role in determining the difference of genetic requirements.

We have added a description of the above-mentioned result in the Result section (pages11-12, lines 191-199).

(4) Growth in aerobic and hypoxic conditions: The authors concluded that clinical strains are better adapted to hypoxia, as reflected by their earlier entry into the log phase. They presented the 'Time at midpoint' and 'Growth rate at midpoint.' However, after reviewing the growth curves, I noticed that ATCC13950 had a longer lag phase compared to other strains under hypoxic conditions, and its phylogenetic neighbor M018 also had a longer lag phase. Hence, I do not believe a conclusion can be drawn that clinical strains are better adapted to hypoxia, as this behavior could be specific to a particular clade. It's also possible that the ATCC13950 strain has adapted to aerobic growth. I would suggest that the authors include growth curves in the main figures. The difference in 'Time at midpoint' could be attributed to several factors, and visualizing the growth curves would provide additional context and clarity.

Thank you for the comments on the possibility of genotypes as a determinant of growth pattern in M. intracelulare. Following the comments, we performed aerobic and hypoxic growth assay in the two strains (M005 and M016) that neighbor ATCC13950.

Author response image 1.

The phylogenetic relationship between M005, M016 and ATCC13950. The former two strains are squared in blue.

M005 reached midpoint later than ATCC13950 both in aerobic and hypoxic conditions. By contrast, M016 reached midpoint three quarters earlier than ATCC13950 under hypoxic conditions. The growth rate was not significantly different between M005, M016 or ATCC13950 under either aerobic or hypoxic conditions, although P-value of M005 vs ATCC13950 was 0.0512 under aerobic conditions on Steel’s multiple comparisons test.

From the data of growth pattern in M005 and M016, we suggest that in addition to gene essentiality, genotypes may have some impact on the bacterial growth pattern under hypoxia; however, since there was a significant difference in the timing of hypoxic adaptation among ATCC13950 and its neighbor strains, bacterial growth pattern under hypoxia is considered to be determined by multiple factors such as genetic requirements and unproven regulatory systems. Taking into consideration that there are lots of genetically diverse strains other than ATCC13950 clade, many clinical MAC-PD strains are possibly better adapted to hypoxia.

Responding to the reviewer’s recommendation, we have added the description of the above-mentioned result in the revised manuscript (page 18, lines 313-322). And we have shown the data of growth curves of the original 9 subject strains in the new Fig 7. And we have added the data of the growth curves of M005 and M016 in new Supplementary Fig 7. Additionally, we have corrected the label of y-axis in new Fig. 7a and new Supplementary Fig. 7a and added the description as “Data are represented as CFUs in 4 μl sample at each timepoint.” in the Figure legends. (page 58, lines 1027-1028 and Supplementary Fig. 7a legend)

(5) Lack of statistical statement: The authors emphasized the role of pellicle-formation-associated genes in strain-dependent essential and accessory essential genes. Additionally, the authors observed that 10% of the genes required for mouse infection are also required for hypoxic pellicle formation. However, these are merely descriptive statements. There is no enrichment analysis to justify whether pellicle-formation-associated genes are significantly enriched in these groups.

Thank you for the comments on the enrichment of pellicle-formation associated genes in strain-dependent essential and accessory essential genes. We performed GSEA and found that 9.1% (16 out of 175) genes were hit as core enrichment. Of them, 4 genes were hit commonly as genes showing increased genetic requirements analyzed by resampling plus HMM analyses including genes of phosphoenolpyruvate carboxykinase pckA (OCU_RS48660), type VII secretion-associated serine protease mycP5 (OCU_RS38275), type VII secretion protein eccC5 (OCU_RS38345) and glycine cleavage system amino-methyltransferase gcvT (OCU_RS35955).

Author response image 2.

We have added the description of GSEA result in the revised manuscript (page 8, lines 137-144; Supplementary Fig. 2; Supplementary Table 5).

Reviewer #1 (Recommendations For The Authors):

Tn-seq and hypoxia adaption in clinical isolates of M. intracellulare (Mi): The authors claim that clinical strains are better adapted to hypoxia because their genetic requirements for optimum fitness overlap with genetic requirements for fitness of the type strain under hypoxia. This is a reasonable hypothesis, but it has not been well-supported by the data presented in Figure 7. The growth rates (Figure 7b) of most of the clinical strains under hypoxia appear to be less than the type strain, although they all seem to grow better than the type strain under normoxia. Perhaps a continuous growth curve of each strain, both as pure and mixed cultures under these conditions will provide a clearer picture.

Thank you for the comments on the difference of adaptation of hypoxic growth between ATCC13950 and MAC-PD strains. To clarify, growth rates shown in Figure 7 were calculated at the inflection point (midpoint) of the growth curves, which were modeled using a four-parameter logistic (4P logistic) model. As described in the Discussion, we found the pattern of hypoxic adaptation characteristics of the clinical MAC-PD strains from the growth curve forms. Taking into consideration the impact of growing bacteria on the disease progression of MAC-PD, the slow growth with early entry to log phase implicates the continuous impact on the infected hosts during logarithmic bacterial growth, which may be involved in the persistent and steadily progressive illness of MAC-PD for years in humans.

Unlike time-lapse imaging assay, the completely seamless sampling of cultures for CFU assay is impossible. Nevertheless, we collected sufficient timepoints to allow reliable curve fitting with the 4P logistic model, and thus consider our growth data to represent a valid approximation of continuous growth dynamics.

Regarding the suggestion of mixed culture experiments, we agree that such studies could be informative. However, co-culture conditions introduce additional variables, including inter-strain competition or synergy, which can obscure the specific contributions of hypoxic adaptation in each strain. Therefore, we believe that the current approach using monoculture growth curves under defined oxygen conditions offers a clearer interpretation of strain-specific hypoxic responses.

In vivo studies: It is unclear how virulent the two clinical strains, Mi27 and Mi198 are in the mouse model. The CFU data in Figure S1b reports the bacterial burden of the Tn libraries of the two strains, of which the overall population of Mi27 library seems to be declining. Without any information on the CFU, animal survival, and tissue pathology from the pure strains, data from the library will have limited implications.

Thank you for the comments on the data presentation of in vivo studies. We previously revealed the time-course data on CFUs, animal survival, and tissue pathology from the pure strains (Tateishi Y. BMC Microbiol. 2023; new Ref#22). Based on these data, we assumed that we would be able to harvest sufficient number of colonies from mice infected with M.i.27 or M.i.198, and we performed in vivo TnSeq studies using these two strains. We have referred to our previous publication on the virulence of MAC-PD pure strains used in this study for mice in the revised manuscript (page 12, line 212; new Ref #22).

The data of CFU counts were shown in new Supplementary Figure 3b. In the manuscript text, we explained as follows (page 12, lines 212-216): “The time course of the changes in the bacterial burden showed a pattern similar to those of the wild-type strains M.i.198 and M.i.27, respectively (Tateishi Y. BMC Microbiol. 2023; new Ref#22), except that it was not possible to harvest sufficient colonies (as few as 104/mouse) in the few mice infected with the M.i.27 Tn mutant strain in week 8 and week 16 (new Supplementary Fig, 3b, new Supplementary Table 8)”. The decline of overall population of M.i.27 Tn mutant library strains in the infected lungs can be explained by the lower virulence of M.i.27 pure strain that shows intermediate virulence phenotype than M.i.198 that shows high virulence phenotype.

[References]

Tateishi, Y. et al. Virulence of Mycobacterium intracellulare clinical strains in a mouse model of lung infection - role of neutrophilic inflammation in disease severity. BMC Microbiol 23, 94 (2023).

Data presentation: The manuscript suffers from a lack of clarity in data visualization and presentation, especially the Tn-Seq datasets. Panels describe the experimental workflow with a densely-worded paragraph, making it difficult to navigate through the major findings.

Thank you for the comments on the issue of Fig. 1b. Following the suggestion, we have modified the new Fig. 1b entitled “Strategy of the procedure of TnSeq analyses”.

Language: The paper should be extensively revised for language. Often the authors have mixed-up the terms like 'core' and 'accessory' 'genes' in lines 116-119 with 'core and accessory genomes' in Figure 2c, which is not even mentioned in the paper. It is further unclear how they identified 3153 and 5824 core and accessory genes, respectively, from 55 different strains of Mi. Line 251: ..."involved by confer..." needs revision. The terms "increased gene essentiality" and 'growth-defected associated genes" are very confusing. The essentiality of a gene is either absolute or conditional but is not quantitative. Similarly, 'growth-defect associated' can be replaced with a better phrase that alludes to fitness loss in the clone. Additional typos were found throughout the paper that need to be fixed.

Thank you for the comments on the issue of scientific words including “'core and accessory genomes” and “gene essentiality” used in this study.

Based on Rosconi’s paper (Panel C of Fig. 1 in Nat Microbiol. 2022; new Ref#14), we used the phrases “accessory genome and core genome” as a meaning of a whole set of genes belonging to accessory and core genes. To avoid the confusion and keep consistency, we replaced the term “genomes” to “genes” in the revised manuscript.

In our previous comparative genomic analysis, we identified 3153 and 5824 core and accessory genes, respectively, from 55 different strains of M. intracellulare (Tateishi Y. BMC Microbiol. 2021; new Ref #5). To perform pangenomic analysis, we used the software Bacterial Pan-Genome Analysis tool (BGAP) (Narendrakumar NM. Sci Rep 2016).

We admit that gene essentiality is a qualitative but not a quantitative trait. We have corrected the term "increased gene essentiality" as "increased genetic requirements" throughout the manuscript.

We have used the term “growth-defect (GD)” based on the classification of gene essentiality calculated by the Hidden Markov Model (HMM) complied by TRANSIT software (DeJesus. PLoS Comput Biol. 2015; new Ref#12). The HMM classifies genes as essential (ES), GD, non-essential (NE), growth-advantage (GA). GD means difficulties of growth (growth deficiency) in aerobic conditions in vitro, because Tn insertions are less frequent. The suggested phrases “fitness loss” or “less fit” may include the meaning of the comparison of two different conditions such as culture conditions exposed to a single bacterial strain. Since the HMM analysis is performed in data of a single strain in a specific bacterial condition, we consider that the phrase including “fitness” is somewhat unsuitable for describing the classification of gene essentiality. Thus, it is difficult for us to rephrase GD to the word that implies fitness levels between two conditions in a single bacterial strain.

[References]

Rosconi, F. et al. A bacterial pan-genome makes gene essentiality strain-dependent and evolvable. Nat Microbiol 7, 1580–1592 (2022).

Tateishi, Y. et al. Comparative genomic analysis of Mycobacterium intracellulare: implications for clinical taxonomic classification in pulmonary Mycobacterium avium-intracellulare complex disease. BMC Microbiol 21, 103 (2021).

Narendrakumar NM et al. BPGA- an ultra-fast pan-genome analysis pipeline. Sci Rep 2016 6, 24373 (2016).

DeJesus, M.A. et al. TRANSIT--A Software Tool for Himar1 TnSeq Analysis. PLoS Comput Biol 11, e1004401 (2015).

Reviewer #2 (Recommendations For The Authors):

Major Comments:

(1) Result 1 (Page 6-7): Common essential and growth-defect-associated genes representing the genomic diversity of M. intracellulare strains.

(1a) From Table S1, it is observed that the numbers of Tn-inserted TA sites significantly vary (p >0.05) among biological replicates for each strain when compared with the reference strain ATCC13950. the authors should provide an explanation of how they overcame this variation in their analysis.

Thank you for the comment on the issue of a variable number of Tn-inserted TA sites among biological replicates for each strain of MAC-PD.

On TRANSIT software, we set the replicate option as Sum to combine read counts. And we used Beta-Geometric correction (BGC) to normalize the datasets to fit an “ideal” geometric distribution with a variable probability parameter ρ.

Following the comment, we have added the description on which option we used for handling the replicate data and normalization (page 36, lines 640-643).

(1b) Importantly, saturation in most of the strains is only ~50-60%. In such a case, there will be a high probability that Tn will not hit a nonessential region due to chance instead of selection (See DeJasus et al., mBio, 2017). It has been observed that the sequence pattern (GC)GNTANC(GC) is strongly associated with non-permissiveness. As shown earlier, the authors need to carefully look for the potential non-permissive sites before concluding the fate of a gene. Also, they should acknowledge the potential limitations of their approach due to the suboptimal level of saturation.

Thank you for the comment on the saturation of Tn mutant libraries. Our method of comparison of genetic requirements between strains are the same as a previous report that used duplicate Tn mutant libraries of clinical Mtb strains of different genotypes and triplicate Tn mutant libraries of H37Rv for identifying increased genetic requirements of clinical Mtb strains (Carey. PLoS Pathog 2018; new Ref#8). Our method is also based on the coauthor’s TnSeq study on H37Rv (Minato Y. mSystems 2019; new Ref#61). Moreover, by combining replicates, the saturation of our Tn mutant libraries became 62-79% as follows: ATCC13950: 67.6%, M001: 72.9%, M003: 63.0%, M018: 62.4%, M019: 74.5%, M.i.27: 76.6%, M.i.198: 68.0%, MOTT64: 77.6%, M021: 79.9%. That is, we calculated gene essentiality from the Tn mutant libraries with 62-79% saturation in each strain. The levels of saturation of transposon libraries in our study is similar to the very recent TnSeq anlaysis by Akusobi where 52-80% saturation libraries (so-called “high-density” transposon libraries) are used for HMM and resampling analyses (Supplemental Methods Table 1[merged saturation] in Akusobi. ｍBio. 2025; new Ref#9). The saturation of Tn insertion in individual replicates of our libraries is also comparable to that reported by DeJesus (Table S1 in mBio 2017; new Ref#57). Thus, we consider that our TnSeq method of identifying essential genes and detecting the difference of genetic requirements between clinical MAC-PD strains and ATCC13950 is acceptable.

As the Reviewer indicates, there is non-permissive sequence pattern in mariner transposon mutagenesis. Using more than 10 replicates of Tn mutant libraries is quite an accurate method for detecting essential genes in nonstructural small genes such as small regulatory RNAs. However, as DeJesus shows, the number essential genes identified by TnSeq are comparable in large genes possessing more than 10 TA sites between 2 and 14 TnSeq datasets, most of which seem to be structural genes (Supplementary Fig 2 in mBio 2017; new Ref#57). Thus, we do not consider that we made a serious mistake for the classification of essentiality in most of the structural genes that encode proteins. With respect to the coverage of non-permissive sites, our TnSeq method might need to be improved if it is intended to classify the gene essentiality quite accurately on the small genes including small regulatory RNAs.

We investigated the non-permissive TA sites in ATCC13950. There are 4136 (6.43% of total ORFs) nonpermissive TA sites in ATCC13950, which is less than in H37Rv (9% of total ORFs) (DeJesus MA. mBio 20171; new Ref#57) and in M. abscessus ATCC19977 (8.1% of total ORFs)(Rifat D. mBio. 2021; new Ref#58). As for larger ORFs (TA sites > = 10), there are nonpermissive TA sites in 89 genes (ORFs) of common “essential (ES)” or “growth-defect-associated (GD)” (4.82% of a total of 1844 larger ORFs in ATCC13950). As for small ORFs (2-9 TA sites), there are nonpermissive TA sites in 41 genes (ORFs) of common ES or GD (1.35% of a total of 3021 smaller ORFs in ATCC13950).

We appreciate the idea of concluding the fate of gene essentiality by the presence/absence of non-permissive TA sites. However, we cannot conclude the fate of gene essentiality classification only by the presence/absence of potential non-permissive sites. Because, strictly to say, it is impossible to conclude the scientific truth of gene essentiality without functional analysis using gene manipulation. In accurate, TnSeq can “predict” the gene essentiality but cannot perfectly guarantee the functional significance. However, in the current situation, most of the recent TnSeq studies have been published only by the TnSeq analysis without functional analysis that uses gene manipulation strains of all targets they identified. Taking such limitations of TnSeq including non-permissive sites into consideration, we consider that ｔhe essentiality of the detected genes should be determined in further studies, mainly including biological experiments such as functional studies using gene manipulation strains.

We have added the above-mentioned contents in the revised manuscript (pages 32-33, lines 559-580).

[References]

Carey, A.F. et al. TnSeq of Mycobacterium tuberculosis clinical isolates reveals strain-specific antibiotic liabilities. PLoS Pathog 14, e1006939 (2018).

Minato, Y., et al. Genomewide assessment of Mycobacterium tuberculosis conditionally essential metabolic pathways. mSystems. 4, e00070-192019 (2019).

Akusobi. C. et al. Transposon-sequencing across multiple Mycobacterium abscessus isolates reveals significant functional genomic diversity among strains. mBio 6, e0337624 (2025).

DeJesus, M.A. et al. Comprehensive essentiality analysis of the Mycobacterium tuberculosis genome via saturating transposon mutagenesis. mBio 8, e02133-16 (2017).

Rifat, D., Chen L., Kreiswirth, B.N. & Nuermberger, E.L.. Genome-wide essentiality analysis of Mycobacterium abscessus by saturated transposon mutagenesis and deep sequencing. mBio 12, e0104921 (2021).

(1c) Line 100: Authors report a total of 131 genes identified as essential or growth-defect-associated with the HMM analysis across all M. intracellulare strains. It should be explained in more detail how gene essentiality was determined (see above comment in (1b)). Furthermore, in Table S3 authors should mention the essential and growth defective trait of each of the 131 genes.

Thank you for the comment on how to classify the 131 genes as essential or growth-defect-associated with the HMM analysis across all M. intracellulare strains. As replied in (1b), the average saturation of Tn insertion of our libraries became 62-79% when combining duplicate or triplicate data in each strain. The levels of saturation of transposon libraries in our study is similar to the very recent TnSeq analysis by Akusobi where 52-80% saturation libraries (so-called “high-density” transposon libraries) were used for HMM and resampling analyses, and most of triplicate libraries ranges 70-79% saturation (Supplemental Methods Table 1[merged saturation] in Akusobi. ｍBio. 2025; new Ref#9). The saturation of Tn insertion in individual replicates of our libraries is also comparable to those with DeJesus (Table S1 in mBio 2017; new Ref#57). Thus, we consider that our TnSeq libraries are acceptable for identifying essential genes and growth-defect-associated genes by the HMM method.

We used the HMM method as reported by DeJesus (DeJesus. PLoS Comput Biol. 2015; new Ref#12). HMM method can categorize the gene essentiality throughout the genome including “Essential”, “Growth-defect”, “Non-essential” and “Growth-advantage”. “Essential” genes are defined as no insertions in all or most of their TA sites. “Non-essential” genes are defined as regions that have usual read counts. “Growth-defect” genes are defined as regions that have unusually low read counts. “Growth-advantage” genes are defined as regions that have unusually high low read counts.

Following the previous report (Carey AF. PLos Pathog 2018; new Ref#8), the annotation for the clinical MAC-PD strains was adapted from that of ATCC13950 by adjusting the START and END coordinates of each ORF in the clinical MAC-PD strains according to their alignment with the corresponding ORFs of ATCC13950. By using an adjusted annotation table, gene essentiality was classified by the HMM analysis.

We have added the explanation of how we identified essential and growth-defect-associated genes in the Methods (pages 35-36, lines 620-632). And following the comment, we have added the data of classification of gene essentiality in the 131 genes in the new Supplementary Table 3 in the revised manuscript.

[Reference]

DeJesus, M.A. et al. TRANSIT--A Software Tool for Himar1 TnSeq Analysis. PLoS Comput Biol 11, e1004401 (2015).

Carey, A.F. et al. TnSeq of Mycobacterium tuberculosis clinical isolates reveals strain-specific antibiotic liabilities. PLoS Pathog 14, e1006939 (2018).

Akusobi. C. et al. Transposon-sequencing across multiple Mycobacterium abscessus isolates reveals significant functional genomic diversity among strains. mBio 6, e0337624 (2025).

DeJesus, M.A. et al. Comprehensive essentiality analysis of the Mycobacterium tuberculosis genome via saturating transposon mutagenesis. mBio 8, e02133-16 (2017).

(1d) In Table S4, the authors show strain-specific putative essential genes from the core and accessory gene sets. For the sake of clarity, it is important to have the name of all the strains against each gene in which it is predicted essential or growth defective.

Thank you for the comment on the hit strains on the genes classified as strain-specific and accessory putative essential of growth-defect associated. Following the comment, we have added the data of hit strains in the new Supplementary Table 4 in the revised manuscript.

(1e) Lines 123-126: It is not clear what is the relevance of highlighting genes involved in hypoxic pellicle formation in ATCC13950. These appear to be randomly distributed across different clinical isolates and is not clear whether they correlate with differential susceptibility of the reference strain and clinical isolates to hypoxia.

Thank you for the comment on the relevance of highlighting genes involved in hypoxic pellicle formation in ATCC13950. The rationale for the importance of hypoxic pellicle genes in clinical MAC-PD strains is that the profiles of genetic requirements in each bacterial strain reflect the adaptation to the environment in which each strain lives. When the strains are placed in a special environment, they can adapt to the situation by altering the profiles of genetic requirements, resulting in the remodeling of metabolic pathways. We indeed found that the genetic requirements of several hypoxic pellicle genes were increased in clinical MAC-PD strains in vitro situations. These data suggest the hypoxic pellicle genes become more important in clinical MAC-PD strains for in vitro growth than in ATCC13950.

Moreover, hypoxia is known to be one of the characteristic conditions in vivo including clinical lesions (McKeown. Br Br J Radiol. 2014). We consider it reasonable to expect that the strains derived from MAC-PD patients without predisposing immunological disorders may adapt under hypoxic conditions for maintaining bacterial survival. Therefore, we highlighted the genes involved in hypoxic pellicle formation in ATCC13950.

We have added the description of the rationale for the importance of hypoxic pellicle genes in clinical MAC-PD strains in the revised manuscript (page 9, lines 148-155).<br /> [Reference]

McKeown, S.R., et al. Defining normoxia, physoxia and hypoxia in tumours-implications for treatment response. Br Br J Radiol 87,: 20130676 (2014).

(2) Result 2 (pages 8-10): Genes with increased gene essentiality in clinical MAC-PD strains are also required for hypoxic pellicle formation in the type strain.

(2a) As reported by authors (lines 123-126), only a small fraction of genes showing essentiality in clinical MAC-PD strains are required for hypoxic pellicle formation in the reference strain, which might be due to random distribution. Authors should avoid making such a generalised statement that reflects the association of the entire essential gene pool in clinical MAC-PD strains with hypoxic pellicle formation.

Thank you for the comment on the issue of a small fraction of genes showing increased genetic requirements in clinical MAC-PD strains that is shared with genes required for hypoxic pellicle formation in the type strain ATCC13950. We admit that the section title may mislead that the genes required for hypoxic pellicle formation confer the entire essential gene pool of clinical MAC-PD strains. Following the comment, we have revised the section title as “Partial overlap of the genes showing increased genetic requirements in clinical MAC-PD strains with those required for hypoxic pellicle formation in ATCC13950” (page 9, lines 146-147).

We consider that it cannot be explained by a mere coincidence that we obtained the data of partial overlap of genes showing essentiality in clinical MAC-PD strains with genes required for hypoxic pellicle formation in ATCC13950, because we demonstrated the supporting data such as the pattern of genetic requirements suggesting gluconeogenic metabolic shift (Fig. 5) and the different pattern of hypoxic growth curves between clinical MAC-PD strains and ATCC13950 (Fig. 7).

(2b) I fail to understand how the number of Tn insertions determines "more" or "less" essentiality of a gene particularly with 50-60% saturation. To my understanding, essentiality is a qualitative trait. Either a gene will be essential (based on no Tn insertion despite having the permissive sites), critical (poor representation of Tn insertions at the permissive sites due to growth defect of the strain in the pool), non-essential (expected frequency of insertion) or growth-advantageous (higher representation of Tn insertions at the permissive sites due to growth advantage of the strain in the pool). Hence, authors should avoid quantifying the essentiality of a gene.

Thank you for the comments on the trait of gene essentiality. We realize that essentiality is a qualitative trait, not a quantitative trait. Taking into consideration the number of Tn insertions determines "more" or "less" requirements of a gene, we have corrected the manuscript by using the phrase “genetic requirements” instead of “gene essentiality”.

As mentioned earlier, our method of comparison of genetic requirements between strains are the same as a previous report that used duplicate Tn mutant libraries of clinical Mtb strains of different genotypes and triplicate Tn mutant libraries of H37Rv for identifying increased genetic requirements of clinical Mtb strains (Carey AF. PLoS Pathog 2018; new Ref#8). Moreover, as described in rebuttal (1b), the saturation of our Tn mutant libraries by combining replicates are 62-79% as follows: ATCC13950: 67.6%, M001: 72.9%, M003: 63.0%, M018: 62.4%, M019: 74.5%, M.i.27: 76.6%, M.i.198: 68.0%, MOTT64: 77.6%, M021: 79.9%. That is, we calculated gene essentiality from the Tn mutant libraries with 62-79% saturation in each strain. The levels of saturation of transposon libraries in our study is similar to the recent TnSeq analysis by Akusobi where 52-80% saturation libraries (“high-density” transposon libraries) were used for HMM and resampling analyses (Supplemental Methods Table 1[merged saturation] in Akusobi C. ｍBio. 2025; new Ref#9).

Thus, we consider that our data of the difference of genetic requirements between clinical MAC-PD strains and ATCC13950 are acceptable.

[Reference]

Akusobi. C. et al. Transposon-sequencing across multiple Mycobacterium abscessus isolates reveals significant functional genomic diversity among strains. mBio 6, e0337624 (2025).

(2c) From Figures 3-4, it seems the authors intend to highlight the insertion frequencies of certain genes in the clinical isolates compared to those in the reference strain to conclude whether a gene has become more critical and its disruption results in the growth defective phenotype (poor representation) in the clinical isolates, or a critical/essential gene has become dispensable in these strains.

Based on these arguments, I suggest that the authors modify the title of the result such as "Tn insertion reveals differential requirement of genes for in vitro growth of clinical MAC-PD strains" or "Identification of genes differentially required for in vitro growth of clinical MAC-PD strains" as this is precisely the information we gain from this section of the study. Also, it is suggested to re-draft the rationale of this section as only 4 genes associated with hypoxic pellicle formation, were found to exhibit reduced insertion frequencies in the clinical isolates out of total of 283 genes. Hypoxia-related genes can be highlighted in the next section (see below).

Thank you for the suggestion to modify the section title and to re-draft the rationale of the section. Following the comment, we modified the section title as “Partial overlap of the genes showing increased genetic requirements in clinical MAC-PD strains with those required for hypoxic pellicle formation in ATCC13950 (page 9, lines 146-147)

Following the suggestion, we have revised the rationale of this section as follows: “The sharing of strain-dependent and accessory essential or growth-defect-associated genes with genes required for hypoxic pellicle formation in ATCC13950 prompts us to consider that the profiles of gene essentiality in clinical MAC-PD strains may be associated with the genes required for hypoxic pellicle formation in ATCC13950.” (page 9, lines 151-155)

The reviewer points out that only 4 genes associated with hypoxic pellicle formation were found to exhibit reduced insertion frequencies in the clinical isolates out of total of 283 genes. However, to discuss how much proportion of the genes were detected to be increasingly required in clinical MAC-PD strains compared to ATCC13950, we should focus on the 121 genes showing increased requirements in clinical MAC-PD strains compared to ATCC13950, excluding the 162 genes indispensable for clinical MAC-PD strains. Thus, we described that 4 genes associated with hypoxic pellicle formation, were found to exhibit reduced insertion frequencies in the clinical isolates out of the 121 genes having significantly fewer Tn insertions than ATCC13950 in the manuscript (Fig. 3).

(3) Result 3 (Page 10-14): Requirement of genes with increased gene essentiality in the clinical MAC-PD strains for mouse lung infection.

(3a) The title should be modified to "Identification of genes in the clinical MAC-PD strains required for mouse lung infection".

Following the comment, we have modified the section title as "Identification of genes in the clinical MAC-PD strains required for mouse lung infection". (page 12, lines 201-202).

(3b) Further, the rationale of this experiment needs to be modified. As mentioned above, up until now the impact of hypoxic pellicle formation genes in the growth of MAC-PD strains remains unconvincing. The rationale of mouse infection experiments could be straightforward- "to identify genes critical for animal infection of the clinical isolates".

Thank you for the comment on the rationale of the in vivo TnSeq experiment. Following the comment, we have revised the rationale as “The impact of hypoxia on mycobacteria under various ecological circumstances implies that the genes required for pathogenesis of MAC-PD may be in some degrees, overlapped with the genes with increased requirements in the clinical MAC-PD strains compared to ATCC13950, and also with the genes required for hypoxic pellicle formation in ATCC13950. To identify genes required for in vivo infection of clinical MAC-PD strains,” in the revised manuscript (page 12, lines 204-210).

(3c) The authors should avoid using the term "genes with increased essentiality" for the reasons explained above in point #2b.

Following the comment, we have corrected the term as “genes with increased requirements” in the revised manuscript (page 12, line 207).

(3d) From Tables S8 and S9, I can find 93 genes in Mi198Tn and 74 genes in Mi27Tn for which Tn insertion mutants are under-represented in TnSeq at all time points from Day 1 to Wk 16 in comparison to input. Importantly, excluding results from Day 1 when the infection has just settled, I find 172 and 121 genes in Mi198Tn and Mi27Tn, respectively, under-represented in lungs between Wk 4-16. My suggestion is that authors should focus more on such genes and identify the characteristics of these genes and what fraction belongs to those involved in hypoxic pellicle formation in the reference strain. I am perplexed why authors have categorically ignored other genes and only focused on a set of genes that correspond to ~10-12% of entire differentially abundant mutant pool.

Thank you for the suggestion on the genes that Tn insertion mutants are under-represented in TnSeq from Weeks 4-16 in the infected mouse lungs be analyzed for overlapping the genes involved in hypoxic pellicle formation in the type strain ATCC13950. We found that at all timepoints from Day1 to Week 16, 74 genes and 99 genes were under-represented in lungs infected with M.i.27Tn and M.i.198Tn, respectively. Of them, 21 (28.3%) and 12 (12.1%) genes belonged to the genes involved in the genes required for hypoxic pellicle formation in the type strain. We found that at timepoints from Week 4 to Week 16, 121 genes and 172 genes were under-represented in lungs infected with M.i.27Tn and M.i.198Tn, respectively. Of them, 21 (23.1%) and 30 (18.0%) genes belonged to genes involved in hypoxic pellicle formation in the type strain. These hypoxic pellicle-associated genes detected both in M.i.27 and M.i.198 encoded methionine synthesis, acyl-CoA dehydrogenase, isocitrate lyase, MMPL family transporter at all time points (from Day1 to Week 16). And additionally, multifunctional oxoglutarate decarboxylase/dehydrogenase, proteasome subunits, ABC transporter ATP-binding protein/permease, lipase chaperone at all time points (from Week 4 to Week 16). We have described these results in the Result section (page 14 lines 236-248) and new Supplementary Tables 12 and 13.

As for M. intracellulare, conditionally essential genes have not been revealed except for those required for hypoxic pellicle formation in ATCC13950 revealed by us (Tateishi Y. Sci Rep. 2020; new Ref#10). This study is the first to focus on the relationship between the difference of genetic requirements among strains and hypoxic adaptation. We found a certain proportion of overlapped genes required for mouse lung infection and ATCC13950’s hypoxic pellicle formation. We consider it reasonable to focus on the category of genes required for hypoxic pellicle formation to analyze the datasets of TnSeq in mice.

[Reference]

Tateishi, Y. et al. Genome-wide identification of essential genes in Mycobacterium intracellulare by transposon sequencing - Implication for metabolic remodeling. Sci Rep 10, 5449 (2020).

(3e) Page 13, lines 224-227: "Despite the differences in the profiles of the genes required for in vivo infection between strains, these data suggest that increased gene essentiality for hypoxic growth confers advantages for pathogenesis in vivo."

For the reason described above, I find it a misleading hypothesis that hypoxic growth confers advantages for pathogenesis in vivo. How come only 10-12% of the entire gene sets which include genes of varying functions, can be the sole contributors to bacterial survival in host organelles during infection?

More importantly, the mouse is not considered a good model for hypoxia as mouse infection does not lead to the formation of solid granuloma with a hypoxic core Though I am not convinced with the authors' bias toward hypoxia-related genes, however, if at all they aim to investigate the role of such genes by an unbiased enrichment of TnSeq mutant, they should have used C3HeJ mice which are known to form granulomas (Boute et al., 2017 (doi: 10.1186/s13567-017-0477-7)).

Thank you for the comments on the issue of the contribution of genes required for hypoxic growth and on the difference of hypoxic levels between mouse lineages. We did not intend to mention that a set of genes required for hypoxic growth is the sole contributor to bacterial survival in host organs during infection. As we discussed in the Discussion section, we acknowledge that the adaptation to the difference of carbon source between in vitr_o and _in vivo infection (i.e. preferential usage of lipid carbon source in vivo) is involved in the pathogenesis of mycobacterial diseases (Yang. Front Microbiol 2018; new Ref#33, Gouzy. Proc Natl Acad Sci U S A 2021; new Ref#29, Quinonez. mBio 2022; new Ref#40, Pandey. Proc Natl Acad Sci U S A 2008; new Ref#41). We consider that not only the genes required for hypoxic pellicle formation but also strain-dependent/accessory genes conferring kinds of metabolism other than hypoxic pellicle formation can be estimated to be involved in the in vivo mouse lung infection.

We have modified the sentence to clearly express our intention as follows: “These in vivo TnSeq data suggest that, despite the differences in the profiles of the genes required for in vivo infection between strains, increase of genetic requirements for hypoxic growth in part contribute to the pathogenesis in vivo.” (pages 15-16, lines 269-271)

It seems to be an interesting idea to perform TnSeq by using C3HeJ mice. The granuloma formed in C3HeJ mice becomes extremely hypoxic (less than 1%, corresponding the level of “pathological” hypoxia) which is as severe as the detection range by pimonidazole. In our model, the effect of such pathological levels of hypoxia on granuloma formation might not be detected. However, the lesion formed in C57BL/6 mice becomes a “physiological” level of hypoxia (5% O2) (McKeown SR. Br Br J Radiol. 2014) which is the same O2 level for M. intracellulare to form pellicles. In principle, oxygen levels inside human bodies are physiologically hypoxic, and many biological events are experimentally investigated in this condition. Thus, we consider that we were able to observe the effect of physiological hypoxia on M. intracellulre growth both in vitro (hypoxic pellicles) and in vivo (infected C57BL/6 mice).

[Reference]

Yang, T. et al. Pan-genomic study of Mycobacterium tuberculosis reflecting the primary/secondary genes, generality/individuality, and the interconversion through copy number variations. Front Microbiol 9, 1886 (2018).

Gouzy, A., Healy, C., Black, K.A., Rhee, K.Y. & Ehrt, S. Growth of Mycobacterium tuberculosis at acidic pH depends on lipid assimilation and is accompanied by reduced GAPDH activity. Proc Natl Acad Sci U S A 118, e2024571118 (2021).

Quinonez, C.G. et al. The role of fatty acid metabolism in drug tolerance of Mycobacterium tuberculosis. mBio 13, e0355921 (2022).

Pandey, A.K. & Sassetti, C.M. Mycobacterial persistence requires the utilization of host cholesterol. Proc Natl Acad Sci U S A 105, 4376-4380 (2008).

McKeown., S.R. et al. Defining normoxia, physoxia and hypoxia in tumours-implications for treatment response. Br Br J Radiol 87, 20130676 (2014).

(3f) An important set of data with the ATCC13950 reference strain is missing here. It is suggested that authors perform this study with the reference strain to identify whether the enrichment of genes is similar across all strains or is specific to the clinical isolates.

Thank you for the comment on the setting of ATCC13950 as a control strain in the mouse infection experiment. However, we proved that bacterial burden of ATCC13950 is reduced continuously from 4 weeks of infection, and that ATCC13950 is almost completely eliminated from 8 to 16 weeks of infection (BMC Microiol 2023; new Ref#22). Therefore, it is impossible to perform TnSeq to detect the genes required for persistent infection in mice infected with ATCC13950.

[Reference]

Tateishi, Y. et al. Virulence of Mycobacterium intracellulare clinical strains in a mouse model of lung infection - role of neutrophilic inflammation in disease severity. BMC Microbiol 23, 94 (2023).