Like myself Alper is his own most frequent reader of his blog. Mentions realising how much he did in a week earlier in his life. Same for me, things that now might be a big thing in a week, were Tuesday afternoon 15yrs ago. It's not just age I suspect, but also an overall attenuation that Covid brought?

states the AMP stack is losing adoption. Any numbers to find?

https://web.archive.org/web/20251229105350/https://alper.nl/blog/18730/

[[Alper Çuğun p]] moving away from WordPress to Hugo / markdown.

https://web.archive.org/web/20251229110112/https://netzpolitik.org/2025/dsgvo-reform-beim-datenschutz-ist-deutschland-inzwischen-dem-silicon-valley-naeher-als-dem-rest-der-eu/#netzpolitik-pw

Max Schrems #2025/12 interviewed by Nextpolitik about GDPR and reform, and the position of GDPR in Germany. Mentions digital omnibus and upcoming digital fitness test by EC of GDPR

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Kind Words.

Definitely true

eLife Assessment

TrASPr is an important contribution that leverages transformer models focused on regulatory regions to enhance predictions of tissue-specific splicing events. The revisions strengthen the manuscript by clarifying methodology and expanding analyses across exon and intron sizes, and the evidence supporting TrASPr's predictive performance is compelling. This work will be of interest to researchers in computational genomics and RNA biology, offering an improved model for splicing prediction and a promising approach to RNA sequence design.

Reviewer #1 (Public review):

Summary

The authors propose a transformer-based model for prediction of condition- or tissue-specific alternative splicing and demonstrate its utility in design of RNAs with desired splicing outcomes, which is a novel application. The model is compared to relevant exising approaches (Pangolin and SpliceAI) and the authors clearly demonstrate its advantage. Overall, a compelling method that is well thought out and evaluated.

Strengths:

(1) The model is well thought out: rather than modeling a cassette exon using a single generic deep learning model as has been done e.g. in SpliceAI and related work, the authors propose a modular architecture that focuses on different regions around a potential exon skipping event, which enables the model to learn representations that are specific to those regions. Because each component in the model focuses on a fixed length short sequence segment, the model can learn position-specific features. Furthermore, the architecture of the model is designed to model alternative splicing events, whereas Pangolin and SpliceAI are focused on modeling individual splice junctions, which is an easier problem.

(2) The model is evaluated in a rigorous way - it is compared to the most relevant state-of-the-art models, uses machine learning best practices, and an ablation study demonstrates the contribution of each component of the architecture.

(3) Experimental work supports the computational predictions: Regulatory elements predicted by the model were experimentally verified; novel tissue-specific cassette exons were verified by LSV-seq.

(4) The authors use their model for sequence design to optimize splicing outcome, which is a novel application.

Weaknesses:

None noted.

Reviewer #2 (Public review):

Summary:

The authors present a transformer-based model, TrASPr, for the task of tissue-specific splicing prediction (with experiments primarily focused on the case of cassette exon inclusion) as well as an optimization framework (BOS) for the task of designing RNA sequences for desired splicing outcomes.

For the first task, the main methodological contribution is to train four transformer-based models on the 400bp regions surrounding each splice site, the rationale being that this is where most splicing regulatory information is. In contrast, previous work trained one model on a long genomic region. This new design should help the model capture more easily interactions between splice sites. It should also help in cases of very long introns, which are relatively common in the human genome.

TrASPr's performance is evaluated in comparison to previous models (SpliceAI, Pangolin, and SpliceTransformer) on numerous tasks including splicing predictions on GTEx tissues, ENCODE cell lines, RBP KD data, and mutagenesis data. The scope of these evaluations is ambitious; however, significant details on most of the analyses are missing, making it difficult to evaluate the strength of evidence.

In the second task, the authors combine Latent Space Bayesian Optimization (LSBO) with a Transformer-based variational auto encoder to optimize RNA sequences for a given splicing-related objective function. This method (BOS) appears to be a novel application of LSBO, with promising results on several computational evaluations and the potential to be impactful on sequence design for both splicing-related objectives and other tasks. However, comparison of BOS against existing methods for sequence design is lacking.

Strengths:

- A novel machine learning model for an important problem in RNA biology with excellent prediction accuracy.

- Instead of being based on a generic design as in previous work, the proposed model incorporates biological domain knowledge (that regulatory information is concentrated around splice sites). This way of using inductive bias can be important to future work on other sequence-based prediction tasks.

Weaknesses:

- Most of the analyses presented in the manuscript are described in broad strokes and are often confusing. As a result, it is difficult to assess the significance of the contribution.

- As more and more models are being proposed for splicing prediction (SpliceAI, Pangolin, SpliceTransformer, TrASPr), there is a need for establishing standard benchmarks, similar to those in computer vision (ImageNet). Without such benchmarks, it is exceedingly difficult to compare models.<br /> *This point is now addressed in the revision *<br /> *Moreover, datasets have been made available by the authors on BitBucket. *

- Related to the previous point, as discussed in the manuscript, SpliceAI and Pangolin are not designed to predict PSI of cassette exons. Instead, they assign a "splice site probability" to each nucleotide. Converting this to a PSI prediction is not obvious, and the method chosen by the authors (averaging the two probabilities (?)) is likely not optimal. It would interesting to see what happens if an MLP is used on top of the four predictions (or the outputs of the top layers) from SpliceAI/Pangolin. This could also indicate where the improvement in TrASPr comes from: is it because TrASPr combines information from all four splice sites? Also consider fine-tuning Pangolin on cassette exons only (as you do for your model).<br /> *This point is still not addressed in the revision. *

- L141, "TrASPr can handle cassette exons spanning a wide range of window sizes from 181 to 329,227 bases-thanks to its multi-transformer architecture." This is reported to be one of the primary advantages compared to existing models. Additional analysis should be included on how TrASPr performs across varying exon and intron sizes, with comparison to SpliceAI, etc.

Added after revision: The authors have added additional analyses of performance based on both the length of the exon under consideration and the total length of the surrounding intronic contexts. The result that TrASPr performs well across various context sizes (i.e., the length of the sequence between the upstream and downstream exons, ranging from <1k to >10k) is highly encouraging and supports the claim that most of the sequence-based splicing logic is located proximal to the splice sites. It is also noteworthy that TrASPr performs well for exons longer than 200, suggesting that most of the "regulatory code" is present at the exon boundaries rather than in its center (which TrASPr is blind to).<br /> Additionally, Pearson correlation is used as the sole performance metric in many analyses (e.g., Fig 2 - Supp 2). The authors should consider alternative accuracy metrics, such as RMSE, which better convey the magnitude of prediction error and are more easily comparable across datasets. Pearson correlation may also be more sensitive to outliers on the smaller samples that arise when binning sequences.

- L171, "training it on cassette exons". This seems like an important point: previous models were trained mostly on constitutive exons, whereas here the model is trained specifically on cassette exons. This should be discussed in more detail.<br /> * Our initial comment was incorrect, as pointed out by the authors. *

- L214, ablations of individual features are missing.<br /> * This was addressed in the revision. *

- L230, "ENCODE cell lines", it is not clear why other tissues from GTEx were not included<br /> * This was addressed in the revision. *

- L239, it is surprising that SpliceAI performs so badly, and might suggest a mistake in the analysis. Additional analysis and possible explanations should be provided to support these claims. Similarly for the complete failure of SpliceAI and Pangolin shown in Fig 4d.<br /> * The authors should consider adding SpliceAI/Pangolin predictions for the alternative 5' and 3' splice site selection tasks (and code for related analyses) to the BitBucket repository.*

- BOS seems like a separate contribution that belongs in a separate publication. Instead, consider providing more details on TrASPr.

*Minor comment added after revision: regarding the author response that "A completely independent evaluation would have required a high-throughput experimental system to assess designs, which is beyond the scope of the current paper.":<br /> It's not clear why BOS cannot be evaluated as a separate contribution by instead using different "teacher" models instead of TrASPr. Additionally, BOS lacks evaluation against existing methods for sequence optimization. *

- The authors should consider evaluating BOS using Pangolin or SpliceTransformer as the oracle, in order to measure the contribution to the sequence generation task provided by BOS vs TrASPr.<br /> * See comment above *

Author response:

The following is the authors’ response to the original reviews

A point by point response included below. Before we turn to that we want to note one change that we decided to introduce, related to generalization on unseen tissues/cell types (Figure 3a in the original submission and related question by Reviewer #2 below). This analysis was based on adding a latent “RBP state” representation during learning of condition/tissue specific splicing. The “RBP state” per condition is captured by a dedicated encoder. Our original plan was to have a paper describing a new RBP-AE model we developed in parallel, which also served as the base to capture this “RBP State”. However, we got delayed in getting this second paper finalized (it was led by other lab members, some of whom have already left the lab). This delay affected the TrASPr manuscript as TrASPr’s code should be available and analysis reproducible upon publication. After much deliberation, we decided that in order to comply with reproducibility standards while not self scooping the RBP-AE paper, we eventually decided to take out the RBP-AE and replace it with a vanilla PCA based embedding for the “RBP-State”. The PCA approach is simpler and reproducible, based on linear transformation of the RBPs expression vector into a lower dimension. The qualitative results included in Figure 3a still hold, and we also produced the new results suggested by Reviewer #2 in other GTEX tissues with this PCA based embedding (below). 

We don’t believe the switch to PCA based embedding should have any bearing on the current manuscript evaluation but wanted to take this opportunity to explain the reasoning behind this additional change.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors propose a transformer-based model for the prediction of condition - or tissue-specific alternative splicing and demonstrate its utility in the design of RNAs with desired splicing outcomes, which is a novel application. The model is compared to relevant existing approaches (Pangolin and SpliceAI) and the authors clearly demonstrate its advantage. Overall, a compelling method that is well thought out and evaluated.

Strengths:

(1) The model is well thought out: rather than modeling a cassette exon using a single generic deep learning model as has been done e.g. in SpliceAI and related work, the authors propose a modular architecture that focuses on different regions around a potential exon skipping event, which enables the model to learn representations that are specific to those regions. Because each component in the model focuses on a fixed length short sequence segment, the model can learn position-specific features. Another difference compared to Pangolin and SpliceAI which are focused on modeling individual splice junctions is the focus on modeling a complete alternative splicing event.

(2) The model is evaluated in a rigorous way - it is compared to the most relevant state-of-the-art models, uses machine learning best practices, and an ablation study demonstrates the contribution of each component of the architecture.

(3) Experimental work supports the computational predictions.     

(4) The authors use their model for sequence design to optimize splicing outcomes, which is a novel application.

We wholeheartedly thank Reviewer #1 for these positive comments regarding the modeling approach we took to this task and the evaluations we performed. We have put a lot of work and thought into this and it is gratifying to see the results of that work acknowledged like this.

Weaknesses:

No weaknesses were identified by this reviewer, but I have the following comments:

(1) I would be curious to see evidence that the model is learning position-specific representations.

This is an excellent suggestion to further assess what the model is learning. To get a better sense of the position-specific representation we performed the following analyses:

(1) Switching the transformers relative order: All transformers are pretrained on 3’ and 5’ splice site regions before fine-tunning for the PSI and dPSI prediction task. We hypothesized that if relative position is important, switching the order of the transformers would make a large difference on prediction accuracy. Indeed if we switch the 3’ and 5’ we see as expected a severe drop in performance, with Pearson correlation on test data dropping from 0.82 to 0.11. Next, we switched the two 5’ and 3’ transformers, observing a drop to 0.65 and 0.78 respectively. When focusing only on changing events the drop was from 0.66 to 0.54 (for 3’ SS transformers), 0.48 (for 5’ SS transformers), and 0.13 (when the 3’ and 5’ transformers flanking the alternative exon were switched). 

(2) Position specific effect of RBPs: We wanted to test whether the model is able to learn position specific effects for RBPs. For this we focused on two RBPs, FOX (a family of three highly related RBPs), and QKI, both have a relatively well defined motif, known condition and position specific effect identified via RBP KD experiments combined with CLIP experiments (e.g. PMID: 23525800, PMID: 24637117, PMID: 32728246). For each, we randomly selected 40 highly and 40 lowly included cassette exons sequences. We then ran in-silico mutagenesis experiments where we replaced small windows of sequences with the RBP motifs (80 for RBFOX and 80 for QKI), then compared TrASPR’s predictions for the average predictions for 5 random sequences inserted in the same location. The results of this are now shown in Figure 4 Supp 3, where the y-axis represents the dPSI effect per position (x-axis), and the color represents the percentile of observed effects over inserting motifs in that position across all 80 sequences tested. We see that both RBPs have strong positional preferences for exerting a strong effect on the alternative exon. We also see differences between binding upstream and downstream of the alternative exon. These results, learned by the model from natural tissue-specific variations, recapitulate nicely the results derived from high-throughput experimental assays. However, we also note that effects were highly sequence specific. For example, RBFOX is generally expected to increase inclusion when binding downstream of the alternative exon and decrease inclusion when binding upstream. While we do observe such a trend we also see cases where the opposite effects are observed. These sequence specific effects have been reported in the literature but may also represent cases where the model errs in the effect’s direction. We discuss these new results in the revised text.

(3) Assessing BOS sequence edits to achieve tissue-specific splicing: Here we decided to test whether BOS edits in intronic regions (at least 8b away from the nearest splice site) are important for the tissue-specific effect. The results are now included in Figure 6 Supp 1, clearly demonstrating that most of the neuronal specific changes achieved by BOS were based on changing the introns, with a strong effect observed for both up and downstream intron edits.

(2) The transformer encoders in TrASPr model sequences with a rather limited sequence size of 200 bp; therefore, for long introns, the model will not have good coverage of the intronic sequence. This is not expected to be an issue for exons.

The reviewer is raising a good question here. On one hand, one may hypothesize that, as the reviewer seems to suggest, TrASPr may not do well on long introns as it lacks the full intronic sequence.

Conversely, one may also hypothesize that for long introns, where the flanking exons are outside the window of SpliceAI/Pangolin, TrASPr may have an advantage.

Given this good question and a related one by Reviewer #2, we divided prediction accuracy by intron length and the alternative exon length.

For short exons  (<100bp) we find TrASPr and Pangolin perform similarly, but for longer exons, especially those > 200, TrASPr results are better. When dividing samples by the total length of the upstream and downstream intron, we find TrASPr outperform all other models for introns of combined length up to 6K, but Pangolin gets better results when the combined intron length is over 10K. This latter result is interesting as it means that contrary to the second hypothesis laid out above, Pangolin’s performance did not degrade for events where the flanking exons were outside its field of view. We note that all of the above holds whether we assess all events or just cases of tissue specific changes. It is interesting to think about the mechanistic causes for this. For example, it is possible that cassette exons involving very long introns evoke a different splicing mechanism where the flanking exons are not as critical and/or there is more signal in the introns which is missed by TrASPr. We include these new results now as Figure 2 - Supp 1,2 and discuss these in the main text.

(3) In the context of sequence design, creating a desired tissue- or condition-specific effect would likely require disrupting or creating motifs for splicing regulatory proteins. In your experiments for neuronal-specific Daam1 exon 16, have you seen evidence for that? Most of the edits are close to splice junctions, but a few are further away.

That is another good question. Regarding Daam1 exon 16, in the original paper describing the mutation locations some motif similarities were noted to PTB (CU) and CUG/Mbnl-like elements (Barash et al Nature 2010). In order to explore this question beyond this specific case we assessed the importance of intronic edits by BOS to achieve a tissue specific splicing profile - see above.

(4) For sequence design, of tissue- or condition-specific effect in neuronal-specific Daam1 exon 16 the upstream exonic splice junction had the most sequence edits. Is that a general observation? How about the relative importance of the four transformer regions in TrASPr prediction performance?

This is another excellent question. Please see new experiments described above for RBP positional effect and BOS edits in intronic regions which attempt to give at least partial answers to these questions. We believe a much more systematic analysis can be done to explore these questions but such evaluation is beyond the scope of this work.

(5) The idea of lightweight transformer models is compelling, and is widely applicable. It has been used elsewhere. One paper that came to mind in the protein realm:

Singh, Rohit, et al. "Learning the language of antibody hypervariability." Proceedings of the National Academy of Sciences 122.1 (2025): e2418918121.

We definitely do not make any claim this approach of using lighter, dedicated models instead of a large ‘foundation’ model has not been taken before. We believe Rohit et al mentioned above represents a somewhat different approach, where their model (AbMAP) fine-tunes large general protein foundational models (PLM) for antibody-sequence inputs by supervising on antibody structure and binding specificity examples. We added a description of this modeling approach citing the above work and another one which specifically handles RNA splicing (intron retention, PMID: 39792954).

Reviewer #2 (Public review):

Summary:

The authors present a transformer-based model, TrASPr, for the task of tissue-specific splicing prediction (with experiments primarily focused on the case of cassette exon inclusion) as well as an optimization framework (BOS) for the task of designing RNA sequences for desired splicing outcomes.

For the first task, the main methodological contribution is to train four transformer-based models on the 400bp regions surrounding each splice site, the rationale being that this is where most splicing regulatory information is. In contrast, previous work trained one model on a long genomic region. This new design should help the model capture more easily interactions between splice sites. It should also help in cases of very long introns, which are relatively common in the human genome.

TrASPr's performance is evaluated in comparison to previous models (SpliceAI, Pangolin, and SpliceTransformer) on numerous tasks including splicing predictions on GTEx tissues, ENCODE cell lines, RBP KD data, and mutagenesis data. The scope of these evaluations is ambitious; however, significant details on most of the analyses are missing, making it difficult to evaluate the strength of the evidence. Additionally, state-of-the-art models (SpliceAI and Pangolin) are reported to perform extremely poorly in some tasks, which is surprising in light of previous reports of their overall good prediction accuracy; the reasoning for this lack of performance compared to TrASPr is not explored.

In the second task, the authors combine Latent Space Bayesian Optimization (LSBO) with a Transformer-based variational autoencoder to optimize RNA sequences for a given splicing-related objective function. This method (BOS) appears to be a novel application of LSBO, with promising results on several computational evaluations and the potential to be impactful on sequence design for both splicing-related objectives and other tasks.

We thank Reviewer #2 for this detailed summary and positive view of our work. It seems the main issue raised in this summary regards the evaluations: The reviewer finds details of the evaluations missing and the fact that SpliceAI and Pangolin perform poorly on some of the tasks to be surprising. We made a concise effort to include the required details, including code and data tables. In short, some of the concerns were addressed by adding additional evaluations, some by clarifying missing details, and some by better explaining where Pangolin and SpliceAI may excel vs. settings where these may not do as well. More details are given below. 

Strengths:

(1) A novel machine learning model for an important problem in RNA biology with excellent prediction accuracy.

(2) Instead of being based on a generic design as in previous work, the proposed model incorporates biological domain knowledge (that regulatory information is concentrated around splice sites). This way of using inductive bias can be important to future work on other sequence-based prediction tasks.

Weaknesses:

(1) Most of the analyses presented in the manuscript are described in broad strokes and are often confusing. As a result, it is difficult to assess the significance of the contribution.

We made an effort to make the tasks be specific and detailed,  including making the code and data of those available. We believe this helped improve clarity in the revised version.

(2) As more and more models are being proposed for splicing prediction (SpliceAI, Pangolin, SpliceTransformer, TrASPr), there is a need for establishing standard benchmarks, similar to those in computer vision (ImageNet). Without such benchmarks, it is exceedingly difficult to compare models. For instance, Pangolin was apparently trained on a different dataset (Cardoso-Moreira et al. 2019), and using a different processing pipeline (based on SpliSER) than the ones used in this submission. As a result, the inferior performance of Pangolin reported here could potentially be due to subtle distribution shifts. The authors should add a discussion of the differences in the training set, and whether they affect your comparisons (e.g., in Figure 2). They should also consider adding a table summarizing the various datasets used in their previous work for training and testing. Publishing their training and testing datasets in an easy-to-use format would be a fantastic contribution to the community, establishing a common benchmark to be used by others.

There are several good points to unpack here. Starting from the last one, we very much agree that a standard benchmark will be useful to include. For tissue specific splicing quantification we used the GTEx dataset from which we select six representative human tissues (heart, cerebellum, lung, liver, spleen, and EBV-transformed lymphocytes). In total, we collected 38394 cassette exon events quantified across 15 samples (here a ‘sample’ is a cassette exon quantified in two tissues) from the GTEx dataset with high-confidence quantification for their PSIs based on MAJIQ. A detailed description of how this data was derived is now included in the Methods section, and the data itself is made available via the bitbucket repository with the code.

Next, regarding the usage of different data and distribution shifts for Pangolin: The reviewer is right to note there are many differences between how Pangolin and TrASPr were trained. This makes it hard to determine whether the improvements we saw are not just a result of different training data/labels. To address this issue, we first tried to finetune the pre-trained Pangolin with MAJIQ’s PSI dataset: we use the subset of the GTEx dataset described above, focusing on the three tissues analyzed in Pangolin’s paper—heart, cerebellum, and liver—for a fair comparison. In total, we obtained 17,218 events, and we followed the same training and test split as reported in the Pangolin paper. We got Pearson: 0.78 Spearman: 0.68 which are values similar to what we got without this extra fine tuning. Next, we retrained Pangolin from scratch, with the full tissues and training set used for TrASPr, which was derived from MAJIQ’s quantifications. Since our model only trained on human data with 6 tissues at the same time, we modified Pangolin from original 4 splice site usage outputs to 6 PSI outputs. We tried to take the sequence centered with the first or the second splice site of the mid exon. This test resulted in low performance (3’ SS: pearson 0.21 5’ SS: 0.26.). 

The above tests are obviously not exhaustive but their results suggest that the differences we observe are unlikely to be driven by distribution shifts. Notably, the original Pangolin was trained on much more data (four species, four tissues each, and sliding windows across the entire genome). This training seems to be important for performance while the fact we switched from Pangolin’s splice site usage to MAJIQ’s PSI was not a major contributor. Other potential reasons for the improvements we observed include the architecture, target function, and side information (see below) but a complete delineation of those is beyond the scope of this work. 

(3) Related to the previous point, as discussed in the manuscript, SpliceAI, and Pangolin are not designed to predict PSI of cassette exons. Instead, they assign a "splice site probability" to each nucleotide. Converting this to a PSI prediction is not obvious, and the method chosen by the authors (averaging the two probabilities (?)) is likely not optimal. It would be interesting to see what happens if an MLP is used on top of the four predictions (or the outputs of the top layers) from SpliceAI/Pangolin. This could also indicate where the improvement in TrASPr comes from: is it because TrASPr combines information from all four splice sites? Also, consider fine-tuning Pangolin on cassette exons only (as you do for your model).

Please see the above response. We did not investigate more sophisticated models that adjust Pangolin’s architecture further as such modifications constitute new models which are beyond the scope of this work.

(4) L141, "TrASPr can handle cassette exons spanning a wide range of window sizes from 181 to 329,227 bases - thanks to its multi-transformer architecture." This is reported to be one of the primary advantages compared to existing models. Additional analysis should be included on how TrASPr performs across varying exon and intron sizes, with comparison to SpliceAI, etc.

This was a good suggestion, related to another comment made by Reviewer #1. Please see above our response to them with a breakdown by exon/intron length.

(5) L171, "training it on cassette exons". This seems like an important point: previous models were trained mostly on constitutive exons, whereas here the model is trained specifically on cassette exons. This should be discussed in more detail.

Previous models were not trained exclusively on constitutive exons and Pangolin specifically was trained with their version of junction usage across tissues. That said, the reviewer’s point is valid (and similar to ones made above) about a need to have a matched training/testing and potential distribution shifts. Please see response and evaluations described above. 

(6) L214, ablations of individual features are missing.

These were now added to the table which we moved to the main text (see table also below).

(7) L230, "ENCODE cell lines", it is not clear why other tissues from GTEx were not included.

Good question. The task here was to assess predictions in unseen conditions, hence we opted to test on completely different data of human cell lines rather than additional tissue samples. Following the reviewers suggestion we also evaluated predictions on two additional GTEx tissues, Cortex and Adrenal Gland. These new results, as well as the previous ones for ENCODE, were updated to use the PCA based embedding of “RBP-State” as described above. We also compared the predictions using the PCA based embedding of the “RBP-State” to training directly on data (not the test data of course) from these tissues. See updated Figure 3a,b. Figure 3 Supp 1,2.

(8) L239, it is surprising that SpliceAI performs so badly, and might suggest a mistake in the analysis. Additional analysis and possible explanations should be provided to support these claims. Similarly, the complete failure of SpliceAI and Pangolin is shown in Figure 4d.

Line 239 refers to predicting relative inclusion levels between competing 3’ and 5’ splice sites. We admit we too expected this to be better for SpliceAI and Pangolin but we were not able to find bugs in our analysis (which is all made available for readers and reviewers alike). Regarding this expectation to perform better, first we note that we are not aware of a similar assessment being done for either of those algorithms (i.e. relative inclusion for 3’ and 5’ alternative splice site events). Instead, our initial expectation, and likely the reviewer’s as well, was based on their detection of splice site strengthening/weakening due to mutations, including cryptic splice site activation. More generally though, it is worth noting in this context that given how SpliceAI, Pangolin and other algorithms have been presented in papers/media/scientific discussions, we believe there is a potential misperception regarding tasks that SpliceAI and Pangolin excel at vs other tasks where they should not necessarily be expected to excel. Both algorithms focus on cryptic splice site creation/disruption. This has been the focus of those papers and subsequent applications.  While Pangolin added tissue specificity to SpliceAI training, the authors themselves admit “...predicting differential splicing across tissues from sequence alone is possible but remains a considerable challenge and requires further investigation”. The actual performance on this task is not included in Pangolin’s main text, but we refer Reviewer #2 to supplementary figure S4 in the Pangolin manuscript to get a sense of Pangolin’s reported performance on this task. Similar to that, Figure 4d in our manuscript is for predicting ‘tissue specific’ regulators. We do not think it is surprising that SpliceAI (tissue agnostic) and Pangolin (slight improvement compared to SpliceAI in tissue specific predictions) do not perform well on this task. Similarly, we do not find the results in Figure 4C surprising either. These are for mutations that slightly alter inclusion level of an exon, not something SpliceAI was trained on - SpiceAI was trained on genomic splice sites with yes/no labels across the genome. As noted elsewhere in our response, re-training Pangolin on this mutagenesis dataset results in performance much closer to that of TrASPr. That is to be expected as well - Pangolin is constructed to capture changes in PSI (or splice site usage as defined by the authors), those changes are not even tissue specific for the CD19 data and the model has no problem/lack of capacity to generalize from the training set just like TrASPr does. In fact, if you only use combinations of known mutations seen during training a simple regression model gives correlation of ~92-95% (Cortés-López et al 2022). In summary, we believe that better understanding of what one can realistically expect from models such as SpliceAI, Pangolin, and TrASPr will go a long way to have them better understood and used effectively. We have tried to make this more clear in the revision.

(9) BOS seems like a separate contribution that belongs in a separate publication. Instead, consider providing more details on TrASPr.

We thank the reviewer for the suggestion. We agree those are two distinct contributions/algorithms and we indeed considered having them as two separate papers. However, there is strong coupling between the design algorithm (BOS) and the predictor that enables it (TrASPr). This coupling is both conceptual (TrASPr as a “teacher”) and practical in terms of evaluations. While we use experimental data (experiments done involving Daam1 exon 16, CD19 exon 2) we still rely heavily on evaluations by TrASPr itself. A completely independent evaluation would have required a high-throughput experimental system to assess designs, which is beyond the scope of the current paper. For those reasons we eventually decided to make it into what we hope is a more compelling combined story about generative models for prediction and design of RNA splicing.

(10) The authors should consider evaluating BOS using Pangolin or SpliceTransformer as the oracle, in order to measure the contribution to the sequence generation task provided by BOS vs TrASPr.

We can definitely see the logic behind trying BOS with different predictors. That said, as we note above most of BOS evaluations are based on the “teacher”. As such, it is unclear what value replacing the teacher would bring. We also note that given this limitation we focus mostly on evaluations in comparison to existing approaches (genetic algorithm or random mutations as a strawman). 

Recommendations for the authors: 

Reviewer #1 (Recommendations for the authors):

Additional comments:

(1) Is your model picking up transcription factor binding sites in addition to RBPs? TFs have been recently shown to have a role in splicing regulation:

Daoud, Ahmed, and Asa Ben-Hur. "The role of chromatin state in intron retention: A case study in leveraging large scale deep learning models." PLOS Computational Biology 21.1 (2025): e1012755.

We agree this is an interesting point to explore, especially given the series of works from the Ben-Hur’s group. We note though that these works focus on intron retention (IR) which we haven’t focused on here, and we only cover short intronic regions flanking the exons. We leave this as a future direction as we believe the scope of this paper is already quite extensive.

(2) SpliceNouveau is a recently published algorithm for the splicing design problem:

Wilkins, Oscar G., et al. "Creation of de novo cryptic splicing for ALS and FTD precision medicine." Science 386.6717 (2024): 61-69.

Thank you for pointing out Wilkins et al recent publication, we now refer to it as well. 

(3) Please discuss the relationship between your model and this deep learning model. You will also need to change the following sentence: "Since the splicing sequence design task is novel, there are no prior implementations to reference."

We revised this statement and now refer to several recent publications that propose similar design tasks.  

(4) I would suggest adding a histogram of PSI values - they appear to be mostly close to 1 or 0.

PSI values are indeed typically close to either 0 or 1. This is a known phenomenon illustrated in previous studies of splicing (e.g. Shen et al NAR 2012 ). We are not sure what is meant by the comment to add a histogram but we made sure to point this out in the main text: 

“...Still, those statistics are dominated by extreme values, such that 33.2\% are smaller than 0.15 and 56.0\% are higher than 0.85. Furthermore, most cassette exons do not change between a given tissue pair (only 14.0\% of the samples in the dataset, \ie a cassette exon measured across two tissues, exhibit ΔΨ| ≥ 0.15).”

(5) Part of the improvement of TrASPr over Pangolin could be the result of a more extensive dataset.

Please see above responses and new analysis.

(6) In the discussion of the roles of alternative splicing, protein diversity is mentioned, but I suggest you also mention the importance of alternative splicing as a regulatory mechanism:

Lewis, Benjamin P., Richard E. Green, and Steven E. Brenner. "Evidence for the widespread coupling of alternative splicing and nonsense-mediated mRNA decay in humans." Proceedings of the National Academy of Sciences 100.1 (2003): 189-192.

Thank you for the suggestion. We added that point and citation. 

(7) Line 96: You use dPSI without defining it (although quite clear that it should be Delta PSI).

Fixed.

(8) Pretrained transformers: Have you trained separate transformers on acceptor and donor sites, or a single splice junction transformer?

Single splice junction pre-training.

(9) "TrASPr measures the probability that the splice site in the center of Se is included in some tissue" - that's not my understanding of what TrASPr is designed to do.

We revised the above sentence to make it more precise: “Given a genomic sequence context S_e = (s_e,...,s_e), made of  a cassette exon e and flanking intronic/exonic regions, TrASPr predicts for tissue c the fraction of transcripts where exon e is included or skipped over, ΔΨ-_e,c,c’.”

(10) Please include the version of the human genome annotations that you used. 

We used GENCODE v40 human genome hg38- this is now included in the Data section. 

(11) I did not see a description of the RBP-AE component in the methods section. A bit more detail on the model would be useful as well.

Please see above details about replacing RBP-AE with a simpler linear PCA “RBP-State” encoding. We added details about how the PCA was performed to the Methods section.

(12) Typos, grammar:

-   Fix the following sentence: ATP13A2, a lysosomal transmembrane cation transporter, linked to an early-onset form of Parkinson's Disease (PD) when 306 loss-of-function mutations disrupt its function.

Sentence was fixed to now read: “The first example is of a brain cerebellum-specific cassette exon skipping event predicted by TrASPr in the ATP13A2 gene (aka PARK9). ATP13A2 is a lysosomal transmembrane cation transporter, for which loss of function mutation has been linked to early-onset of Parkinson’s Disease (PD)”.

-   Line 501: "was set to 4e−4"(the - is a superscript). 

Fixed

-   A couple of citations are missing in lines 580 and 581.

Thank you for catching this error. Citations in line 580, 581 were fixed.

(13) Paper title: Generative modeling for RNA splicing predictions and design - it would read better as "Generative modeling for RNA splicing prediction and design", as you are solving the problems of splicing prediction and splicing design.  

Thank you for the suggestion. We updated the title and removed the plural form.

Reviewer #2 (Recommendations for the authors):

(1) Appendices are not very common in biology journals. It is also not clear what purpose the appendix serves exactly - it seems to repeat some of the things said earlier. Consider merging it into the methods or the main text. 

We merged the appendices into the Methods section and removed redundancy.

(2) L112, "For instance, the model could be tasked with designing a new version of the cassette exon, restricted to no more than N edit locations and M total base changes." How are N and M different? Is there a difference between an edit location and a base change? 

Yes, N is the number of locations (one can think of it as a start position) of various lengths (e.g. a SNP is of length 1) and the total number of positions edited is M. The text now reads “For instance, the model could be tasked with designing a new version of the cassette exon, restricted to no more than  $N$ edit locations (\ie start position of one or more consecutive bases) and $M$ total base changes.”

(3) L122: "DEN was developed for a distinct problem". What prevents one from adapting DEN to your sequence design task? The method should be generic. I do not see what "differs substantially" means here. (Finally, wasn't DEN developed for the task you later refer to as "alternative splice site" (as opposed to "splice site selection")? Use consistent terminology. And in L236 you use "splice site variation" - is that also the same?).

Indeed, our original description was not clear/precise enough. DEN was designed and trained for two tasks: APA, and 5’ alternative splice site usage. The terms “selection”, “usage”, and “variation” were indeed used interchangeably in different locations and the reviewer was right, noting the lack of precision. We have now revised the text to make sure the term “relative usage” is used. 

Nonetheless, we hold DEN was indeed defined for different tasks. See figures from Figure 2A, 6A of Linder et al 2020 (the reference was also incorrect as we cited the preprint and not the final paper):

In both cases DEN is trying to optimize a short region for selecting an alternative PA site (left) or a 5’ splice site (right). This work focused on an MPRA dataset of short synthetic sequences inserted in the designated region for train/test. We hold this is indeed a different type of data and task then the one we focus on here. Yes, one can potentially adopt DEN for our task, but this is beyond the scope of this paper. Finally, we note that a more closely related algorithm recently proposed is Ledidi (Schreiber et al 2025) which was posted as a pre-print. Similar to BOS, Ledidi tries to optimize a given sequence and adopt it with a few edits for a given task. Regardless, we updated the main text to make the differences between DEN and the task we defined here for BOS more clear, and we also added a reference to Ledidi and other recent works in the discussion section.

(4) L203, exons with DeltaPSI very close to 0.15 are going to be nearly impossible to classify (or even impossible, considering that the DeltaPSI measurements are not perfect). Consider removing such exons to make the task more feasible.

Yes, this is how it was done. As described in more details below, we defined changing samples as ones where the change was >= 0.15 and non-changing as ones where the change in PSI was < 0.05 to avoid ambiguous cases affecting the classification task.  

(5) L230, RBP-AE is not explained in sufficient detail (and does not appear in the methods, apparently). It is not clear how exactly it is trained on each new cellular condition.

Please see response in the opening of this document and Q11 from

Reviewer 1 

(6) L230, "significantly improving": the r value actually got worse; it is therefore not clear you can claim any significant improvement. Please mention that fact in the text.

This is a fair point. We note that we view the “a” statistic as potentially more interesting/relevant here as the Pearson “r” is dominated by points being generally close to 0/1.  Regardless, revisiting this we realized one can also make a point that the term “significant” is imprecise/misplaced since there is no statistical test done here (side note: given the amount of points, a simple null of same distribution yes/no would pass significance but we don’t think this is an interesting/relevant test here). Also, we note that with the transition to PCA instead of RBP-AE we actually get improvements in both a and r values, both for the ENCODE samples shown in Figure 3a and the two new GTEX tissues we tested (see above). We now changed the text to simply state: 

“...As shown in Figure 3a, this latent space representation allows TrSAPr to generalize from the six GTEX tissues to unseen conditions, including unseen GTEX tissues (top row), and ENCODE cell lines (bottom row). It improves prediction accuracy compared to TrASPr lacking PCA (eg a=88.5% vs a=82.3% for ENCODE cell lines), though naturally training on the additional GTEX and ENCODE conditions can lead to better performance  (eg a=91.7%, for ENCODE, Figure 3a left column).”

(7) L233, "Notably, previous splicing codes focused solely on cassette exons", Rosenberg et al. focused solely on alternative splice site choice.

Right - we removed that sentence.. 

(8) L236, "trained TrASPr on datasets for 3' and 5' splice site variations". Please provide more details on this task. What is the input to TrASPr and what is the prediction target (splice site usage, PSI of alternative isoforms)? What datasets are used for this task?

The data for this data was the same GTEx tissue data processed, just for alternative 3’ and 5’ splice sites events. We revised the description of this task in the main task and added information in the Methods section. The data is also included in the repo.

(9) L243, "directly from genomic sequences", and conservation?

Yes, we changed the sentence to read “...directly from genomic sequences combined with related features” 

(10) L262, what is the threshold for significant splicing changes?

The threshold is 0.15 We updated the main text to read the following:

The total number of mutations hitting each of the 1198 genomic positions across the 6106 sequences is shown in \FIG{mut_effect}b (left), while the distribution of effects ($|\Delta \Psi|$) observed across those 6106 samples is shown in \FIG{mut_effect}b (right). To this data we applied three testing schemes. The first is a standard 5-fold CV where 20\% of combinations of point mutations were hidden in every fold while the second test involved 'unseen mutation' (UM) where we hide any sample that includes mutations in specific positions for a total of 1480 test samples. As illustrated by the CDF in \FIG{mut_effect}b, most samples (each sample may involve multiple positions mutated) do not involve significant splicing changes. Thus, we also performed a third test using only  the 883 samples were mutations cause significant changes ($|\Delta \Psi|\geq 0.15 $). 

(11) L266, Pangolin performance is only provided for one of the settings (and it is not clear which). Please provide details of its performance in all settings.

The description was indeed not clear. Pangolin’s performance was similar to SpliceAI as mentioned above but retraining it on the CD19 data yielded much closer performance to TrASPr. We include all the matching tests for Pangolin after retraining in Figure 4 Supp Figure 1. 

(12) Please specify "n=" in all relevant plots. 

Fixed.

(13) Figure 3a, "The tissues were first represented as tokens, and new cell line results were predicted based on the average over conditions during training." Please explain this procedure in more detail. What are these tokens and how are they provided to the model? Are the cell line predictions the average of the predictions for the training tissues?

Yes, we compared to simply the average over the predictions for the training tissues for that specific event as baseline to assess improvements (see related work pointing for the need to have similar baselines in DL for genomics in https://pubmed.ncbi.nlm.nih.gov/33213499/). Regarding the tokens - we encode each tissue type as a possible value and feed the two tissues as two tokens to the transformer.

(14) Figure 4b, the total count in the histogram is much greater than 6106. Please explain the dataset you're using in more detail, and what exactly is shown here.

We updated the text to read: 

“...we used 6106 sequence samples where each sample may have multiple positions mutated (\ie mutation combinations) in exon 2 of CD19 and its flanking introns and exons (Cortes et al 2022). The total number of mutations hitting each of the 1198 genomic positions across the 6106 sequences is shown in Figure 4b (left).”

(15) Figure 5a, how are the prediction thresholds (TrASPr passed, TrASPr stringent, and TrASPr very stringent) defined?

Passed: dpsi>0.1, Stringent: dpsi>0.15, Very stringent: dpsi>0.2 This is now included in the main text.

(16) L417, please include more detail on the relative size of TrASPr compared to other models (e.g. number of parameters, required compute, etc.).

SpliceAI is a general-purpose splicing predictor with 32-layer deep residual neural network to capture long-range dependencies in genomic sequences. Pangolin is a deep learning model specifically designed for predicting tissue-specific splicing with similar architecture as SpliceAI. The implementation of SpliceAI that can be found here https://huggingface.co/multimolecule/spliceai involves an ensemble of 5 such models for a total of ~3.5M parameters. TrASPr, has 4 BERT transformers (each 6 layers and 12 heads) and MLP a top of those for a total of ~189M parameters. Evo 2, a genomic ‘foundation’ model has 40B parameters, DNABERT has ~86M (a single BERT with 12 layers and 12 heads), and Borzoi has 186M parameters (as stated in https://www.biorxiv.org/content/10.1101/2025.05.26.656171v2).  We note that the difference here is not just in model size but also the amount of data used to train the model. We edited the original L417 to reflect that.

(17) L546, please provide more detail on the VAE. What is the dimension of the latent representation?

We added more details in the Methods section like the missing dimension (256) and definitions for P(Z) and P(S). 

(18) Consider citing (and possibly comparing BOS to) Ghari et al., NeurIPS 2024 ("GFlowNet Assisted Biological Sequence Editing").

Added.

(19) Appendix Figure 2, and corresponding main text: it is not clear what is shown here. What is dPSI+ and dPSI-? What pairs of tissues are you comparing? Spearman correlation is reported instead of Pearson, which is the primary metric used throughout the text.

The dPSI+ and dPSI- sets were indeed not well defined in the original submission. Moreover, we found our own code lacked consistency due to different tests executed at different times/by different people. We apologize for this lack of consistency and clarity which we worked to remedy in the revised version. To answer the reviewer’s question, given two tissues ($c,c'$), dPSI+ and dPSI- is for correctly classifying the exons that are significantly differentially included or excluded. Specifically, differential included exons are those for which  $\Delta \Psi_{e,c1,c2} = \Psi_\Psi_{e,c1} - \Psi_{e,c2}  \geq 0.15$, compared to those that are not  ($\Delta \Psi_{e,c1,c2} < 0.05). Similarly, dPSI- is for correctly classifying the exons that are significantly differentially excluded in the first tissue or included in the second tissue ($\Delta \Psi_{e,c1,c2} = \Psi_\Psi_{e,c1} - \Psi_{e,c2}  \leq -0.15$) compared to those that are not  ($\Delta \Psi_{e,c1,c2} > -0.05). This means dPSI+ and dPSI- are dependent on the order of c1, c2. In addition, we also define a direction/order agnostic test for changing vs non changing events i.e. $|\Delta \Psi_{e,c1,c2}| \geq 0.15$ vs $|\Delta \Psi_{e,c1,c2}| < 0.05$. These test definitions are consistent with previous publications (e.g. Barash et al Nature 2010, Jha et al 2017) and also answer different biological questions: For example “Exons that go up in brain” and “Exons that go up in Liver” can reflect distinct mechanisms, while changing exons capture a model’s ability to identify regulated exons even if the direction of prediction may be wrong. The updated Appendix Figure 2 is now in the main text as Figure 2d and uses Pearson, while AUPRC and AUROC refer to the changing vs no-changing classification task described above such that we avoid dPSI+ and dPSI- when summarizing in this table over 3 pairs of tissues . Finally, we note that making sure all tests comply with the above definition also resulted in an update to Figure 2b/c labels and values, where TrASPr’s improvements over Pangolin reaches up to 1.8fold in AUPRC compared to 2.4fold in the earlier version. We again apologize for having a lack of clarity and consistent evaluations in the original submission.

(20) Minor typographical comments:

-   Some plots could use more polishing (e.g., thicker stroke, bigger font size, consistent style (compare 4a to the other plots)...).

Agreed. While not critical for the science itself we worked to improve figure polishing in the revision to make those more readable and pleasant. 

-   Consider using 2-dimensional histograms instead of the current kernel density plots, which tend to over-smooth the data and hide potentially important details. 

We were not sure what the exact suggestion is here and opted to leave the plots as is.

-   L53: dPSI_{e, c, c'} is never formally defined. Is it PSI_{e, c} - PSI_{e, c'} or vice versa?  

Definition now included (see above).

-   L91: Define/explain "transformer" and provide reference. 

We added the explanation and related reference of the transformer in the introduction section and BERT in the method section.  

-   L94: exons are short. Are you referring here to the flanking introns? Please explain. 

We apologize for the lack of clarity. We are referring to a cassette exon alternative splicing event as is commonly defined by the splice junctions involved that is from the 5’ SS of the upstream exon to the 3’ SS of the downstream exon. The text now reads:

“...In contrast, 24% of the cassette exons analyzed in this study span a region between the flanking exons' upstream 3' and downstream 5' splice sites that are larger than 10 kb.”

-   L132: It's unclear whether a single, shared transformer or four different transformers (one for each splice site) are being pre-trained. One would at least expect 5' and 3' splice sites to have a different transformer. In Methods, L506, it seems that each transformer is pre-trained separately. 

We updated the text to read:

“We then center a dedicated transformer around each of the splice sites of the cassette exon and its upstream and downstream (competing) exons (four separate transformers for four splice sites in total).”

-   L471: You explain here that it is unclear what tasks 'foundation' models are good for. Also in L128, you explain that you are not using a 'foundation' model. But then in L492, you describe the BERT model you're using as a foundation model! 

Line 492 was simply a poor choice of wording as “foundation” is meant here simply as the “base component”. We changed it accordingly.

-   L169, "pre-training ... BERT", explain what exactly this means. Is it using masking? Is it self-supervised learning? How many splice sites do you provide? Also explain more about the BERT architecture and provide references. 

We added more details about the BERT architecture and training in the Methods section.

-   L186 and later, the values for a and r provided here and in the below do not correspond to what is shown in Figure 2. 

Fixed, thank you for noticing this.

-   L187,188: What exactly do you mean by "events" and "samples"? Are they the same thing? If so, are they (exon, tissue) pairs? Please use consistent terminology. Moreover, when you say "changing between two conditions": do you take all six tissues whenever there is a 0.15 spread in PSI among them? Or do you take just the smallest PSI tissue and the largest PSI tissue when there is a 0.15 spread between them? Or something else altogether?

Reviewer #2 is yet again correct that the definitions were not precise. A “sample” involves a specific exon skipping “event” measured in two tissues.  The text now reads: 

“....most cassette exons do not change between a given tissue pair (only 14.0% of the samples in the dataset, i.e., a cassette exon measured across two tissues, exhibit |∆Ψ| ≥ 0.15). Thus, when we repeat this analysis only for samples involving exons that exhibited a change in inclusion (|∆Ψ| ≥ 0.15) between at least two tissues, performance degrades for all three models, but the differences between them become more striking (Figure 2a, right column).”

-   Figure 1a, explain the colors in the figure legend. The 3D effect is not needed and is confusing (ditto in panel C).

Color explanation is now added: “exons and introns are shown as blue rectangles and black lines. The blue dashed line indicates the inclusive pattern and the red junction indicates an alternative splicing pattern.” 

These are not 3D effects but stacks to indicate multiple events/cases. We agree these are not needed in Fig1a to illustrate types of AS and removed those. However, in Fig1c and matching caption we use the stacks to  indicate HT data captures many such LSVs over which ML algorithms can be trained. 

-   Figure 1b, this cartoon seems unnecessary and gives the wrong impression that this paper explores mechanistic aspects of splicing. The only relevant fact (RBPs serving as splicing factors) can be explained in the text (and is anyway not really shown in this figure).

We removed Figure 1b cartoon.

-   Figure 1c, what is being shown by the exon label "8"? 

This was meant to convey exon ID, now removed to simplify the figure. 

-   Figure 1e, left, write "Intron Len" in one line. What features are included under "..."? Based on the text, I did not expect more features.

Also, the arrows emanating from the features do not make sense. Is "Embedding" a layer? I don't think so. Do not show it as a thin stripe. Finally, what are dPSI'+ and dPSI'-? are those separate outputs? are those logits of a classification task?

We agree this description was not good and have updated it in the revised version. 

-   Figure 1e, the right-hand side should go to a separate figure much later, when you introduce BOS.

We appreciate the suggestion. However, we feel that Figure 1e serves as a visual representation of the entire framework. Just like we opted to not turn this work into two separate papers (though we fully agree it is a valid option that would also increase our publication count), we also prefer to leave this unified visual representation as is.

-   Figure 2, does the n=2456 refer to the number of (exons, tissues) pairs? So each exon contributes potentially six times to this plot? Typo "approximately". 

The “n” refers to the number of samples which is a cassette event measured in two tissues. The same cassette event may appear in multiple samples if it was confidently quantified in more than two tissues. We updated the caption to reflect this and corrected the typo.

-   Figure 2b, typo "differentially included (dPSI+) or excluded" .

Fixed.

-   L221, "the DNABERT" => "DNABERT".

Fixed.

-   L232, missing percent sign.

-    

Fixed.

-   L246, "see Appendix Section 2 for details" seems to instead refer to the third section of the appendix.

We do not have this as an Appendix, the reference has been updated.

-   Figure 3, bottom panels, PSI should be "splice site usage"? 

PSI is correct here - we hope the revised text/definitions make it more clear now.

-   Figure 3b: typo: "when applied to alternative alternative 3'".

Fixed.

-   p252, "polypyrimidine" (no capitalization).

Fixed.

-   Strange capitalization of tissue names (e.g., "Brain-Cerebellum"). The tissue is called "cerebellum" without capitalization.

We used EBV (capital) for the abbreviation and lower case for the rest.

-   Figure 4c: "predicted usage" on the left but "predicted PSI" on the right. 

Right. We opted to leave it as is since Pangolin and SpliceAI do predict their definition of “usage” and not directly PSI, we just measure correlations to observed PSI as many works have done in the past. 

-   Figure 4 legend typo: "two three".

Fixed.

-   L351, typo: "an (unsupervised)" (and no need to capitalize Transformer).

Fixed.

-   L384, "compared to other tissues at least" => "compared to other tissues of at least".

Fixed.

-   L549, P(Z) and P(S) are not defined in the text.

Fixed.

-   L572, remove "Subsequently". Add missing citations at the end of the paragraph.

Fixed.

-   L580-581, citations missing.

Fixed.

-   L584-585, typo: "high confidince predictions"

Fixed.

-   L659-660, BW-M and B-WM are both used. Typo?

Fixed.

-   L895, "calculating the average of these two", not clear; please rewrite.

Fixed.

-   L897, "Transformer" and "BERT", do these refer to the same thing? Be consistent.  

BOS is a transformer and not a BERT but TrASPr uses the BERT architecture. BERT is a type of transformer as the reviewer is surely well aware so the sentence is correct. Still, to follow the reviewer’s recommendation for consistency/clarity we changed it here to state BERT.

-   Appendix Figure 5: The term dPSI appears to be overloaded to also represent the difference between predicted PSI and measured PSI, which is inconsistent with previous definitions. 

Indeed! We thank the reviewer again for their sharp eye and attention to details that we missed. We changed Supp Figure 5, now Figure 4 Supplementary Figure 2, to |PSI’-PSI| and defined those as the difference between TrASPr’s predictions (PSI’) and MAJIQ based PSI quantifications.

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.

You could also make the roll a part of the solution. i.e. if they'retryong to do something hard it might tilt the balance ratger than it being the focus.

One weakness is trying to fit everything into specific boxes. I woukd argue this isn't persuasion.

Manque un verbe.

Manque un verbe.

eLife Assessment

This study offers important insights into how entorhinal and hippocampal activity support human thinking in feature spaces. It replicates hexagonal symmetry in entorhinal cortex, reports a novel three-fold symmetry in both behavior and hippocampal signals, and links these findings with a computational model. The task and analyses are sophisticated, and the results appear solid and of broad interest to neuroscientists.

Reviewer #1 (Public review):

Summary:

Zhang and colleagues examine neural representations underlying abstract navigation in entorhinal cortex (EC) and hippocampus (HC) using fMRI. This paper replicates a previously identified hexagonal modulation of abstract navigation vectors in abstract space in EC in a novel task involving navigating in a conceptual Greeble space. In HC, the authors identify a three-fold signal of the navigation angle. They also use a novel analysis technique (spectral analysis) to look at spatial patterns in these two areas and identify phase coupling between HC and EC. Interestingly, the three-fold pattern identified in the hippocampus explains quirks in participants' behavior where navigation performance follows a three-fold periodicity. Finally, the authors propose a EC-HPC PhaseSync Model to understand how the EC and HC construct cognitive maps. The wide array and creativity of the techniques used is impressive but because of their unique nature, the paper would benefit from more details on how some of these techniques were implemented.

Comments on revisions:

Most of my concerns were adequately addressed, and I believe the paper is greatly improved. I have two more points. I noticed that the legend for Figure 4 still refers to some components of the previous figure version, this should be updated to reflect the current version of the figure. I also think the paper would benefit from more details regarding some of the analyses. Specifically, the phase-amplitude coupling analysis should have a section in the methods which should be sure to clarify how the BOLD signals were reconstructed.

Reviewer #2 (Public review):

The authors report results from behavioral data, fMRI recordings, and computer simulations during a conceptual navigation task. They report 3-fold symmetry in behavioral and simulated model performance, 3-fold symmetry in hippocampal activity, and 6-fold symmetry in entorhinal activity (all as a function of movement directions in conceptual space). The analyses seem thoroughly done, and the results and simulations are very interesting.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary: 

Zhang and colleagues examine neural representations underlying abstract navigation in the entorhinal cortex (EC) and hippocampus (HC) using fMRI. This paper replicates a previously identified hexagonal modulation of abstract navigation vectors in abstract space in EC in a novel task involving navigating in a conceptual Greeble space. In HC, the authors claim to identify a three-fold signal of the navigation angle. They also use a novel analysis technique (spectral analysis) to look at spatial patterns in these two areas and identify phase coupling between HC and EC. Finally, the authors propose an EC-HPC PhaseSync Model to understand how the EC and HC construct cognitive maps. While the wide array of techniques used is impressive and their creativity in analysis is admirable, overall, I found the paper a bit confusing and unconvincing. I recommend a significant rewrite of their paper to motivate their methods and clarify what they actually did and why. The claim of three-fold modulation in HC, while potentially highly interesting to the community, needs more background to motivate why they did the analysis in the first place, more interpretation as to why this would emerge in biology, and more care taken to consider alternative hypotheses seeped in existing models of HC function. I think this paper does have potential to be interesting and impactful, but I would like to see these issues improved first.

General comments:

(1) Some of the terminology used does not match the terminology used in previous relevant literature (e.g., sinusoidal analysis, 1D directional domain).

We thank the reviewer for this valuable suggestion, which helps to improve the consistency of our terminology with previous literature and to reduce potential ambiguity. Accordingly, we have replaced “sinusoidal analysis” with “sinusoidal modulation” (Doeller et al., 2010; Bao et al., 2019; Raithel et al., 2023) and “1D directional domain” with “angular domain of path directions” throughout the manuscript.

(2) Throughout the paper, novel methods and ideas are introduced without adequate explanation (e.g., the spectral analysis and three-fold periodicity of HC).

We thank the reviewer for raising this important point. In the revised manuscript, we have substantially extended the Introduction (paragraphs 2–4) to clarify our hypothesis, explicitly explaining why the three primary axes of the hexagonal grid cell code may manifest as vector fields. We have also revised the first paragraph of the “3-fold periodicity in the HPC” section in the Results to clarify the rationale for using spectral analysis. Please refer to our responses to comment 2 and 3 below for details.

Reviewer #2 (Public review):

The authors report results from behavioral data, fMRI recordings, and computer simulations during a conceptual navigation task. They report 3-fold symmetry in behavioral and simulated model performance, 3-fold symmetry in hippocampal activity, and 6-fold symmetry in entorhinal activity (all as a function of movement directions in conceptual space). The analyses are thoroughly done, and the results and simulations are very interesting.

We sincerely thank the reviewer for the positive and encouraging comments on our study.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) This paper has quite a few spelling and grammatical mistakes, making it difficult to understand at times.

We apologize for the wordings and grammatical errors. We have thoroughly re-read and carefully edited the entire manuscript to correct typographical and grammatical errors, ensuring improved clarity and readability.

(2) Introduction - It's not clear why the three primary axes of hexagonal grid cell code would manifest as vector fields.

We thank the reviewer for raising this important point. In the revised Introduction (paragraphs 2, 3, and 4), we now explicitly explain the rationale behind our hypothesis that the three primary axes of the hexagonal grid cell code manifest as vector fields.

In paragraph 2, we present empirical evidence from rodent, bat, and human studies demonstrating that mental simulation of prospective paths relies on vectorial representations in the hippocampus (Sarel et al., 2017; Ormond and O’Keefe, 2022; Muhle-Karbe et al., 2023).

In paragraphs 3 and 4, we introduce our central hypothesis: vectorial representations may originate from population-level projections of entorhinal grid cell activity, based on three key considerations:

(1) The EC serves as the major source of hippocampal input (Witter and Amaral, 1991; van Groen et al., 2003; Garcia and Buffalo, 2020).

(2) Grid codes exhibit nearly invariant spatial orientations (Hafting et al., 2005; Gardner et al., 2022), which makes it plausible that their spatially periodic activity can be detected using fMRI.

(3) A model-based inference: for example, in the simplest case, when one mentally simulates a straight pathway aligned with the grid orientation, a subpopulation of grid cells would be activated. The resulting population activity would form a near-perfect vectorial representation, with constant activation strength along the path. In contrast, if the simulated path is misaligned with the grid orientation, the population response becomes a distorted vectorial code. Consequently, simulating all possible straight paths spanning 0°–360° results in 3-fold periodicity in the activity patterns—due to the 180° rotational symmetry of the hexagonal grid, orientations separated by 180° are indistinguishable.

We therefore speculate that vectorial representations embedded in grid cell activity exhibit 3-fold periodicity across spatial orientations and serve as a periodic structure to represent spatial direction. Supporting this view, reorientation paradigms in both rodents and young children have shown that subjects search equally in two opposite directions, reflecting successful orientation encoding but a failure to integrate absolute spatial direction (Hermer and Spelke, 1994; Julian et al., 2015; Gallistel, 2017; Julian et al., 2018).

(3) It took me a few reads to understand what the spectral analysis was. After understanding, I do think this is quite clever. However, this paper needs more motivation to understand why you are performing this analysis. E.g., why not just take the average regressor at the 10º, 70º, etc. bins and compare it to the average regressor at 40º, 100º bins? What does the Fourier transform buy you?

We are sorry for the confusion. we outline the rationale for employing Fast Fourier Transform (FFT) analysis to identify neural periodicity. In the revised manuscript, we have added these clarifications into the first paragraph of the “3-fold periodicity in the HPC” subsection in the Results.

First, FFT serves as an independent approach to cross-validate the sinusoidal modulation results, providing complementary evidence for the 6-fold periodicity in EC and the 3-fold periodicity in HPC.

Second, FFT enables unbiased detection of multiple candidate periodicities (e.g., 3–7-fold) simultaneously without requiring prior assumptions about spatial phase (orientation). By contrast, directly comparing “aligned” versus “misaligned” angular bins (e.g., 10°/70° vs. 40°/100°) would implicitly assume knowledge of the phase offset, which was not known a priori.

Finally, FFT uniquely allows periodicity analysis of behavioral performance, which is not feasible with standard sinusoidal GLM approaches. This methodological consistency makes it possible to directly compare periodicities across neural and behavioral domains.

(4) A more minor point: at one point, you say it’s a spectral analysis of the BOLD signals, but the methods description makes it sound like you estimated regressors at each of the bins before performing FFT. Please clarify. 

We apologize for the confusion. In our manuscript, we use the term spectral analysis to distinguish this approach from sinusoidal modulation analysis. Conceptually, our spectral analysis involves a three-level procedure:

(1) First level: We estimated direction-dependent activity maps using a general linear model (GLM), which included 36 regressors corresponding to path directions, down-sampled in 10° increments.

(2) Second level: We applied a Fast Fourier Transform (FFT) to the direction-dependent activity maps derived from the GLM to examine the spectral magnitude of potential spatial periodicities.

(3) Third level: We conducted group-level statistical analyses across participants to assess the consistency of the observed periodicities.

We have revised the “Spectral analysis of MRI BOLD signals” subsection in the Methods to clarify this multi-level procedure.

(5) Figure 4a:

Why do the phases go all the way to 2*pi if periodicity is either three-fold or six-fold? 

When performing correlation between phases, you should perform a circular-circular correlation instead of a Pearson's correlation.

We thank the reviewer for raising this important point. In the original Figure 4a, both EC and HPC phases spanned 0–2π because their sinusoidal phase estimates were projected into a common angular space by scaling them according to their symmetry factors (i.e., multiplying the 3-fold phase by 3 and the 6-fold phase by 6), followed by taking the modulo 2π. However, this projection forced signals with distinct intrinsic periodicities (120° vs. 60° cycles) into a shared 360° space, thereby distorting their relative angular distances and disrupting the one-to-one correspondence between physical directions and phase values. Consequently, this transformation could bias the estimation of their phase relationship.

In the revised analysis and Figure 4a, we retained the original phase estimates derived from the sinusoidal modulation within their native periodic ranges (0–120° for 3-fold and 0–60° for 6-fold) by applying modulo operations directly. Following your suggestion, the relationship between EC and HPC phases was then quantified using circular–circular correlation (Jammalamadaka & Sengupta, 2001), as implemented in the CircStat MATLAB toolbox. This updated analysis avoids the rescaling artifact and provides a statistically stronger and conceptually clearer characterization of the phase correspondence between EC and HPC. The revised Figure 4 has been included.

(6) Figure 4d needs additional clarification:

Phase-locking is typically used to describe data with a high temporal precision. I understand you adopted an EEG analysis technique to this reconstructed fMRI time-series data, but it should be described differently to avoid confusion. This needs additional control analyses (especially given that 3 is a multiple of 6) to confirm that this result is specific to the periodicities found in the paper.

We thank the reviewer for this insightful comment. We have extensively revised the description of the Figure 4 to avoid confusion with EEG-based phase-locking techniques. The revised text now explicitly clarifies that our approach quantifies spatial-domain periodic coupling across path directions, rather than temporal synchronization of neural signals.

To further address the reviewer’s concern about potential effects of the integer multiple relationship between the 3-fold HPC and 6-fold EC periodicities, we additionally performed two control analyses using the 9-fold and 12-fold EC components, both of which are also integer multiples of the 3-fold HPC periodicity. Neither control analysis showed significant coupling (p > 0.05), confirming that the observed 3-fold–6-fold coupling was specific and not driven by their harmonic relationship.

The description of the revised Figure 4 has been updated in the “Phase Synchronization Between HPC and EC Activity” subsection of the Results.

(7) Figure 5a is misleading. In the text, you say you test for propagation to egocentric cortical areas, but I don’t see any analyses done that test this. This feels more like a possible extension/future direction of your work that may be better placed in the discussion.

We are sorry for the confusion. Figure 5a was intended as a hypothesis-driven illustration to motivate our analysis of behavioral periodicity based on participants’ task performance. However, we agree with the reviewer that, on its own, Figure 5a could be misleading, as it does not directly present supporting analyses.

To provide empirical support for the interpretation depicted in Figure 5a, we conducted a whole-brain analysis (Figure S8), which revealed significant 3-fold periodic signals in egocentric cortical regions, including the parietal cortex (PC), precuneus (PCU), and motor regions.

To avoid potential misinterpretation, we have revised the main text to include these results and explicitly referenced Figure S8 in connection with Figure 5a.

The updated description in the “3-fold periodicity in human behavior” subsection in the Results is as follows:

“Considering the reciprocal connectivity between the medial temporal lobe (MTL), where the EC and HPC reside, and the parietal cortex implicated in visuospatial perception and action, together with the observed 3-fold periodicity within the DMN (including the PC and PCu; Fig. S8), we hypothesized that the 3-fold periodic representations of path directions extend beyond the MTL to the egocentric cortical areas, such as the PC, thereby influencing participants' visuospatial task performance (Fig. 5a)”.

Additionally, Figure 5a has been modified to more clearly highlight the hypothesized link between activity periodicity and behavioral periodicity, rather than suggesting a direct anatomical pathway. The revised version of Figure 5 is included.

(8) PhaseSync model: I am not an expert in this type of modeling, so please put a lower weight on this comment (especially compared to some of the other reviewers). While the PhaseSync model seems interesting, it’s not clear from the discussion how this compares to current models. E.g., Does it support them by adding the three-fold HC periodicity? Does it demonstrate that some of them can't be correct because they don't include this three-fold periodicity?

We thank the reviewer for the insightful comment regarding the PhaseSync model. We agree that further clarifying its relationship to existing computational frameworks is important.

The EC–HPC PhaseSync model is not intended to replace or contradict existing grid–place cell models of navigation (e.g., Bicanski and Burgess, 2019; Whittington et al., 2020; Edvardsen et al., 2020). Instead, it offers a hierarchical extension by proposing that vectorial representations in the hippocampus emerge from the projections of periodic grid codes in the entorhinal cortex. Specifically, the model suggests that grid cell populations encode integrated path information, forming a vectorial gradient toward goal locations.

To simplify the theoretical account, our model was implemented in an idealized square layout. In more complex real-world environments, hippocampal 3-fold periodicity may interact with additional spatial variables, such as distance, movement speed, and environmental boundaries.

We have revised the final two paragraphs of the Discussion to clarify this conceptual framework and emphasize the importance of future studies in exploring how periodic activity in the EC–HPC circuit interacts with environmental features to support navigation.

Reviewer #2 (Recommendations for the authors):

(1) Please show a histogram of movement direction sampling for each participant.

We thank the reviewer for this helpful suggestion. We have added a new supplementary figure (Figure S2) showing histograms of path direction sampling for each participant (36 bins of 10°). The figure is also included. Rayleigh tests for circular uniformity revealed no significant deviations from uniformity (all ps > 0.05, Bonferroni-corrected across participants), confirming that path directions were sampled evenly across 0°–360°.

(2) Why didn’t you use participants’ original trajectories (instead of the trajectories inferred from the movement start and end points) for the hexadirectional analyses? 

In our paradigm, participants used two MRI-compatible 2-button response boxes (one for each hand) to adjust the two features of the greebles. As a result, the raw adjustment path contained only four cardinal directions (up, down, left, right). If we were to use the raw stepwise trajectories, the analysis would be restricted to these four directions, which would severely limit the angular resolution. By instead defining direction as the vector from the start to the end position in feature space, we can expand the effective range of directions to the full 0–360°. This approach follows previous literature on abstract grid-like coding in humans (e.g., Constantinescu et al., 2016), where direction was similarly defined by the relative change between two feature dimensions rather than the literal stepwise path. We have added this clarification in the “Sinusoidal modulation” subsection of the revised method.

(3) Legend of Figure 2: the statement "localizing grid cell activity" seems too strong because it is still not clear whether hexadirectional signals indeed result from grid-cell activity (e.g., Bin Khalid et al., eLife, 2024). I would suggest rephrasing this statement (here and elsewhere). 

Thank you for this helpful suggestion. We have removed the statement “localizing grid cell activity” to avoid ambiguity and revised the legend of Figure 2a to more explicitly highlight its main purpose—defining how path directions and the aligned/misaligned conditions were constructed in the 6-fold modulation. We have also modified similar expressions throughout the manuscript to ensure consistency and clarity.

(4) Legend of Figure 2: “cluster-based SVC correction for multiple comparisons” - what is the small volume you are using for the correction? Bilateral EC?

For both Figure 2 and Figure 3, the anatomical mask of the bilateral medial temporal lobe (MTL), as defined by the AAL atlas, was used as the small volume for correction. This has been clarified in the revised Statistical Analysis section of the Methods as “… with small-volume correction (SVC) applied within the bilateral MTL”.

(5) Legend of Figure 2: "ROI-based analysis" - what kind of ROI are you using? "corrected for multiple comparisons" - which comparisons are you referring to? Different symmetries and also the right/left hemisphere?

In Figure 2b, the ROI was defined as a functional mask derived from the significant activation cluster in the right entorhinal cortex (EC). Since no robust clusters were observed in the left EC, the functional ROI was restricted to the right hemisphere. We indeed included Figure 2c to illustrate this point; however, we recognize that our description in the text was not sufficiently clear.

Regarding the correction for multiple comparisons, this refers specifically to the comparisons across different rotational symmetries (3-, 4-, 5-, 6-, and 7-fold). Only the 6-fold symmetry survived correction, whereas no significant effects were detected for the other symmetries.

We have clarified these points in the “6-fold periodicity in the EC” subsection of the result as “… The ROI was defined as a functional mask of the right EC identified in the voxel-based analysis and further restricted within the anatomical EC. These analyses revealed significant periodic modulation only at 6-fold (Figure  2c; t(32) = 3.56, p = 0.006, two-tailed, corrected for multiple comparisons across rotational symmetries; Cohen’s d = 0.62) …”.

We have also revised the “3-fold periodicity in the HPC” subsection of the result as “… ROI analysis, using a functional mask of the HPC identified in the spectral analysis and further restricted within the anatomical HPC, indicated that HPC activity selectively fluctuated at 3-fold periodicity (Figure 3e; t(32) = 3.94, p = 0.002, corrected for multiple comparisons across rotational symmetries; Cohen’s d = 0.70) …”.

(6) Figure 2d: Did you rotationally align 0{degree sign} across participants? Please state explicitly whether (or not) 0{degree sign} aligns with the x-axis in Greeble space.

We thank the reviewer for this helpful question. Yes, before reconstructing the directional tuning curve in Figure 2d, path directions were rotationally aligned for each participant by subtracting the participant-specific grid orientation (ϕ) estimated from the independent dataset (odd sessions). We have now made this description explicit in the revised manuscript in the “6-fold periodicity in the EC” subsection of the Results, stating “… To account for individual difference in spatial phase, path directions were calibrated by subtracting the participant-specific grid orientation estimated from the odd sessions ...”.

(7) Clustering of grid orientations in 30 participants: What does “Bonferroni corrected” refer to? Also, the Rayleigh test is sensitive to the number of voxels - do you obtain the same results when using pair-wise phase consistency? 

“Bonferroni corrected” here refers to correction across participants. We have clarified this in the first paragraph of the “6-fold periodicity in the EC” subsection of the Result and in the legend of Supplementary Figure S5 as “Bonferroni-corrected across participants.”

To examine whether our findings were sensitive to the number of voxels, we followed the reviewer’s guidance to compute pairwise phase consistency (PPC; Vinck et al., 2010) for each participant. The PPC results replicated those obtained with the Rayleigh test. We have updated the new results into the Supplementary Figure S5 and also included the figure for your convenience. We also updated the “Statistical Analysis” subsection of the Methods to describe PPC as “For the PPC (Vinck et al., 2010), significance was tested using 5,000 permutations of uniformly distributed random phases (0–2π) to generate a null distribution for comparison with the observed PPC”.

(8) 6-fold periodicity in the EC: Do you compute an average grid orientation across all EC voxels, or do you compute voxel-specific grid orientations?

Following the protocol originally described by Doeller et al. (2010), we estimated voxel-wise grid orientations within the EC and then obtained a participant-specific orientation by averaging across voxels within a hand-drawn bilateral EC mask. The procedure is described in detail in the “Sinusoidal modulation” subsection of the Methods.

(9) Hand-drawn bilateral EC mask: What was your procedure for drawing this mask? What results do you get with a standard mask, for example, from Freesurfer or SPM? Why do you perform this analysis bilaterally, given that the earlier analysis identified 6-fold symmetry only in the right EC? What do you mean by "permutation corrected for multiple comparisons"?

We thank the reviewer for raising these important methodological points. To our knowledge, no standard volumetric atlas provides an anatomically defined entorhinal cortex (EC) mask. For example, the built-in Harvard–Oxford cortical structural atlas in FSL contains only a parahippocampal region that encompasses, but does not isolate, the EC. The AAL atlas likewise does not contain an EC region. In FreeSurfer, an EC label is available, but only in the fsaverage surface space, which is not directly compatible with MNI-based volumetric group-level analyses.

Therefore, we constructed a bilateral EC mask by manually delineating the EC according to the detailed anatomical landmarks described by Insausti et al. (1998). Masks were created using ITK-SNAP (Version 3.8, www.itksnap.org). For transparency and reproducibility, the mask has been made publicly available at the Science Data Bank (link: https://www.scidb.cn/s/NBriAn), as indicated in the revised Data and Code availability section.

Regarding the use of a bilateral EC mask despite voxel-wise effects being strongest in the right EC. First, we did not have any a priori hypothesis regarding laterality of EC involvement before performing analyses. Second, previous studies estimated grid orientation using a bilateral EC mask in their sinusoidal analyses (Doeller et al., 2010; Constantinescu et al., 2016; Bao et al., 2019; Wagner et al., 2023; Raithel et al., 2023). We therefore followed this established approach to estimate grid orientation.

By “permutation corrected for multiple comparisons” we refer to the family-wise error correction applied to the reconstructed directional tuning curves (Figure 2d for the EC, Figure 3f for the HPC). Specifically, directional labels were randomly shuffled 5,000 times, and an FFT was applied to each shuffled dataset to compute spectral power at each fold. This procedure generated null distributions of spectral power for each symmetry. For each fold, the 95th percentile of the maximal power across permutations was used as the uncorrected threshold. To correct across folds, the 95th percentile of the maximal suprathreshold power across all symmetries was taken as the family-wise error–corrected threshold. We have clarified this procedure in the revised “Statistical Analysis” subsection of the Methods.

(10) Figures 3b and 3d: Why do different hippocampal voxels show significance for the sinusoidal versus spectral analysis? Shouldn’t the analyses be redundant and, thus, identify the same significant voxels? 

We thank the reviewer for this insightful question. Although both sinusoidal modulation and spectral analysis aim to detect periodic neural activity, the two approaches are methodologically distinct and are therefore not expected to identify exactly the same significant voxels.

Sinusoidal modulation relies on a GLM with sine and cosine regressors to test for phase-aligned periodicity (e.g., 3-fold or 6-fold), calibrated according to the estimated grid orientation. This approach is highly specific but critically depends on accurate orientation estimation. In contrast, spectral analysis applies Fourier decomposition to the directional tuning profile, enabling the detection of periodic components without requiring orientation calibration.

Accordingly, the two analyses are not redundant but complementary. The FFT approach allows for an unbiased exploration of multiple candidate periodicities (e.g., 3–7-fold) without predefined assumptions, thereby providing a critical cross-validation of the sinusoidal GLM results. This strengthens the evidence for 6-fold periodicity in EC and 3-fold periodicity in HPC. Furthermore, FFT uniquely facilitates the analysis of periodicities in behavioral performance data, which is not feasible with standard sinusoidal GLM approaches. This methodological consistency enables direct comparison of periodicities across neural and behavioral domains.

Additionally, the anatomical distributions of the HPC clusters appear more similar between Figure 3b and Figure 3d after re-plotting Figure 3d using the peak voxel coordinates (x = –24, y = –18), which are closer to those used for Figure 3b (x = –24, y = –20), as shown in the revised Figure 3. The revised figure is included for your convenience.

Taken together, the two analyses serve distinct but complementary purposes.

(11) 3-fold sinusoidal analysis in hippocampus: What kind of small volume are you using to correct for multiple comparisons?

We thank the reviewer for this comment. The same small volume correction procedure was applied as described in R4. Specifically, the anatomical mask of the bilateral medial temporal lobe (MTL), as defined by the AAL atlas, was used as the small volume for correction. This procedure has been clarified in the revised Statistical Analysis section of the Methods as following: “… with small-volume correction (SVC) applied within the bilateral MTL.”

(12) Figure S5: “right HPC” – isn’t the cluster in the left hippocampus? 

We are sorry for the confusion. The brain image was present in radiological orientation (i.e., the left and right orientations are flipped). We also checked the figure and confirmed that the cluster shown in the original Figure S5 (i.e., Figure S6 in the revised manuscript) is correctly labeled as the right hippocampus, as indicated by the MNI coordinate (x = 22), where positive x values denote the right hemisphere. To avoid potential confusion, we have explicitly added the statement “Volumetric results are displayed in radiological orientation” to the figure legends of all volume-based results.

(13) Figure S5: Why are the significant voxels different from the 3-fold symmetry analysis using 10{degree sign} bins?

As shown in R10, the apparent differences largely reflect variation in MNI coordinates. After adjusting for display coordinates, the anatomical locations of the significant clusters are in fact highly similar between the 10°-binned (Figure 3d, shown above) and the 20°-binned results (Figure S6).

Although both analyses rely on sinusoidal modulation, they differ in the resolution of the input angular bins (10° vs. 20°). Combined with the inherent noise in fMRI data, this makes it unlikely that the two approaches would yield exactly the same set of significant voxels. Importantly, both analyses consistently reveal robust 3-fold periodicity in the hippocampus, indicating that the observed effect is not dependent on angular bin size.

(14) Figure 4a and corresponding text: What is the unit? Phase at which frequency? Are you using a circular-circular correlation to test for the relationship?

We thank the reviewer for raising this important point. In the revised manuscript, we have clarified that the unit of the phase values is radians, corresponding to the 6-fold periodic component in the EC and the 3-fold periodic component in the HPC. In the original Figure 4a, both EC and HPC phases—estimated from sinusoidal modulation—were analyzed using Pearson correlation. We have since realized issues with this approach, as also noted R5 to Reviewer #1.

In the revised analysis and Figure 4a (as shown above), we re-evaluated the relationship between EC and HPC phases using a circular–circular correlation (Jammalamadaka & Sengupta, 2001), implemented in the CircStat MATLAB toolbox. The “Phase synchronization between the HPC and EC activity” subsection of the Result has been accordingly updated as following:

“To examine whether the spatial phase structure in one region could predict that in another, we tested whether the orientations of the 6-fold EC and 3-fold HPC periodic activities, estimated from odd-numbered sessions using sinusoidal modulation with rotationally symmetric parameters (in radians), were correlated across participants. A cross-participant circular–circular correlation was conducted between the spatial phases of the two areas to quantify the spatial correspondence of their activity patterns (EC: purple dots; HPC: green dots) (Jammalamadaka & Sengupta, 2001). The analysis revealed a significant circular correlation (Figure 4a; r = 0.42, p < 0.001) …”.

In the “Statistical analysis” subsection of the method:

“… The relationship between EC and HPC phases was evaluated using the circular–circular correlation (Jammalamadaka & Sengupta, 2001) implemented in the CircStat MATLAB toolbox …”.

(15) Paragraph following “We further examined amplitude-phase coupling...” - please clarify what data goes into this analysis.

We thank the reviewer for this helpful comment. In this analysis, the input data consisted of hippocampal (HPC) phase and entorhinal (EC) amplitude, both extracted using the Hilbert transform from the reconstructed BOLD signals of the EC and HPC derived through sinusoidal modulation. We have substantially revised the description of the amplitude–phase coupling analysis in the third paragraph of the “Phase Synchronization Between HPC and EC Activity” subsection of the Results to clarify this procedure.

(16) Alignment between EC 6-fold phases and HC 3-fold phases: Why don't you simply test whether the preferred 6-fold orientations in EC are similar to the preferred 3-fold phases in HC? The phase-amplitude coupling analyses seem sophisticated but are complex, so it is somewhat difficult to judge to what extent they are correct. 

We thank the reviewer for this thoughtful comment. We employed two complementary analyses to examine the relationship between EC and HPC activity. In the revised Figure 4 (as shown in Figure 4 for Reviewer #1), Figure 4a provides a direct and intuitive measure of the phase relationship between the two regions using circular–circular correlation. Figure 4b–c examines whether the activity peaks of the two regions are aligned across path directions using cross-frequency amplitude–phase coupling, given our hypothesis that the spatial phase of the HPC depends on EC projections. These two analyses are complementary: a phase correlation does not necessarily imply peak-to-peak alignment, and conversely, peak alignment does not always yield a statistically significant phase correlation. We therefore combined multiple analytical approaches as a cross-validation across methods, providing convergent evidence for robust EC–HPC coupling.

(17) Figure 5: Do these results hold when you estimate performance just based on “deviation from the goal to ending locations” (without taking path length into account)? 

We thank the reviewer for this thoughtful suggestion. Following the reviewer’s advice, we re-estimated behavioral performance using the deviation between the goal and ending locations (i.e., error size) and path length independently. As shown in the new Figure S9, no significant periodicity was observed in error size (p > 0.05), whereas a robust 3-fold periodicity was found for path length (p < 0.05, corrected for multiple comparisons).

We employed two behavioral metrics,(1) path length and (2) error size, for complementary reasons. In our task, participants navigated using four discrete keys corresponding to the cardinal directions (north, south, east, and west). This design inherently induces a 4-fold bias in path directions, as described in the “Behavioral performance” subsection of the Methods. To minimize this artifact, we computed the objectively optimal path length and used it to calibrate participants’ path lengths. However, error size could not be corrected in the same manner and retained a residual 4-fold tendency (see Figure S9d).

Given that both path length and error size are behaviorally relevant and capture distinct aspects of task performance, we decided to retain both measures when quantifying behavioral periodicity. This clarification has been incorporated into the “Behavioral performance” subsection of the Methods, and the 2^nd paragraph of the “3-fold periodicity in human behavior” subsection of the Results.

(18) Phase locking between behavioral performance and hippocampal activity: What is your way of creating surrogates here?

We thank the reviewer for this helpful question. Surrogate datasets were generated by circularly shifting the signal series along the direction axis across all possible offsets (following Canolty et al., 2006). This procedure preserves the internal phase structure within each domain while disrupting consistent phase alignment, thereby removing any systematic coupling between the two signals. Each surrogate dataset underwent identical filtering and coherence computation to generate a null distribution, and the observed coherence strength was compared with this distribution using paired t-tests across participants. The statistical analysis section has been systematically revised to incorporate these methodological details.

(19) I could not follow why the authors equate 3-fold symmetry with vectorial representations. This includes statements such as “these empirical findings provide a potential explanation for the formation of vectorial representation observed in the HPC.” Please clarify.

We thank the reviewer for raising this point. Please refer to our response to R2 for Reviewer #1 and the revised Introduction (paragraphs 2–4), where we explicitly explain why the three primary axes of the hexagonal grid cell code can manifest as vector fields.

(20) It was unclear whether the sentence “The EC provides a foundation for the formation of periodic representations in the HPC” is based on the authors’ observations or on other findings. If based on the authors’ findings, this statement seems too strong, given that no other studies have reported periodic representations in the hippocampus to date (to the best of my knowledge).

We thank the reviewer for this comment. We agree that the original wording lacked sufficient rigor. We have extensively revised the 3rd paragraph of the Discussion section with more cautious language by reducing overinterpretation and emphasizing the consistency of our findings with prior empirical evidence, as follows: “The EC–HPC PhaseSync model demonstrates how a vectorial representation may emerge in the HPC from the projections of populations of periodic grid codes in the EC. The model was motivated by two observations. First, the EC intrinsically serves as the major source of hippocampal input (Witter and Amaral, 1991; van Groen et al., 2003; Garcia and Buffalo, 2020), and grid codes exhibit nearly invariant spatial orientations (Hafting et al., 2005; Gardner et al., 2022). Second, mental planning, characterized by “forward replay” (Dragoi and Tonegawa, 2011; Pfeiffer, 2020), has the capacity to activate populations of grid cells that represent sequential experiences in the absence of actual physical movement (Nyberg et al., 2022). We hypothesize that an integrated path code of sequential experiences may eventually be generated in the HPC, providing a vectorial gradient toward the goal location. The path code exhibits regular, vector-like representations when the path direction aligns with the orientations of grid axes, and becomes irregular when they misalign. This explanation is consistent with the band-like representations observed in the dorsomedial EC (Krupic et al., 2012) and the irregular activity fields of trace cells in the HPC (Poulter et al., 2021). ”

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eLife Assessment

This important work advances our understanding of the role of kisspeptin neurons in regulating the luteinizing hormone (LH) surge in females. The evidence demonstrating increased neuronal activity in anterior hypothalamic kisspeptin neurons just before the LH surge is compelling, though additional neuroanatomical evidence showing the specificity of the methods would strengthen the study. It also confirms that high circulating levels of estradiol, but also other unidentified factors, are required for the full daily activation. This research will be of interest to reproductive biologists and neuroscientists studying the female ovarian cycle.

Joint Public Review:

Summary:

This is an excellent, timely study investigating and characterizing the underlying neural activity that generates the neuroendocrine GnRH and LH surges that are responsible for triggering ovulation. Abundant evidence accumulated over the past 20 years implicated the population of kisspeptin neurons in the hypothalamic RP3V region (also referred to as the POA or AVPV/PeN kisspeptin neurons) as being involved in driving the GnRH surge in response to elevated estradiol (E2), also known as the "estrogen positive feedback". However, while former studies used Cfos coexpression as a marker of RP3V kisspeptin neuron activation at specific times and found this correlates with the timing of the LH surge, detailed examination of the live in vivo activity of these neurons before, during, and after the LH surge remained elusive due to technical challenges.

Here, Zhou and colleagues use fiber photometry to measure the long-term synchronous activity of RP3V kisspeptin neurons across different stages of the mouse estrous cycle, including on proestrus when the LH surge occurs, as well as in a well-established OVX+E2 mouse model of the LH surge.

The authors report that RP3V kisspeptin neuron activity is low on estrous and diestrus, but increases on proestrus several hours before the late afternoon LH surge, mirroring prior reports of rising GnRH neuron activity in proestrus female mice. The measured increase in RP3V kisspeptin activation is long, spanning ~13 hours in proestrus females and extending well beyond the end of the LH secretion, and is shown by the authors to be E2 dependent.

For this work, Kiss-Cre female mice received a Cre-dependent AAV injection, containing GCaMP6, to measure the neuronal activation of RP3V Kiss1 cells. Females exhibited periods of increased neuronal activation on the day of proestrus, beginning several hours prior to the LH surge and lasting for about 12 hours. Though oscillations in the pattern of GCaMP fluorescence were occasionally observed throughout the ovarian cycle, the frequency, duration, and amplitude of these oscillations were significantly higher on the day of proestrus. This increase in RP3V Kiss1 neuronal activation that precedes the increase in LH supports the hypothesis that these neurons are critical in regulating the LH surge. The authors compare this data to new data showing a similar increased activation pattern in GnRH neurons just prior to the LH surge, further supporting the hypothesis that RP3V Kiss1 cell activation causes the release of kisspeptin to stimulate GnRH neurons and produce the LH surge.

Strengths:

This study provides compelling data demonstrating that RP3V kisspeptin neuronal activity changes throughout the ovarian cycle, likely in response to changes in estradiol levels, and that neuronal activation increases on the day of the LH surge.

The observed increase in RP3V kisspeptin neuronal activation precedes the LH surge, which lends support to the hypothesis that these neurons play a role in regulating the estradiol-induced LH surge. Continuing to examine the complexities of the LH surge and the neuronal populations involved, as done in this study, is critical for developing therapeutic treatments for women's reproductive disorders.

This innovative study uses a within-subject design to examine neuronal activation in vivo across multiple hormone milieus, providing a thorough examination of the changes in activation of these neurons. The variability in neuronal activity surrounding the LH surge across ovarian cycles in the same animals is interesting and could not be achieved without this within-subjects design. The inclusion and comparison of ovary-intact females and OVX+E2 females is valuable to help test mechanisms under these two valuable LH surge conditions, and allows for further future studies to tease apart minor differences in the LH surge pattern between these 2 conditions.

This study provides an excellent experimental setup able to monitor the daily activity of preoptic kisspeptin neurons in freely moving female mice. It will be a valuable tool to assess the putative role of these kisspeptin neurons in various aspects of altered female fertility (aging, pathologies...). This approach also offers novel and useful insights into the impact of E2 and circadian cues on the electrical activity of RP3V kisspeptin neurons.

An intriguing cyclical oscillation in kisspeptin neural activity every 90 minutes exists, which may offer critical insight into how the RP3V kisspeptin system operates. Interestingly, there was also variability in the onset and duration of RP3V Kisspeptin neuron activity between and within mice in naturally cycling females. Preoptic kisspeptin neurons show an increased activity around the light/dark transition only on the day of proestrus, and this is associated with an increase in LH secretion. An original finding is the observation that the peak of kisspeptin neuron activation continues a few hours past the peak of LH, and the authors hypothesize that this prolonged activity could drive female sexual behaviors, which usually appear after the LH surge.

The authors demonstrated that ovariectomy resulted in very little neuronal activity in RP3V kisspeptin neurons. When these ovarietomized females were treated with estradiol benzoate (EB) and an LH surge was induced, there was an increase in RP3V kisspeptin neuronal activation, as was seen during proestrus. However, the magnitude of the change in activity was greater during proestrus than during the EB-induced LH surge. Interestingly, the authors noted a consistent peak in activity about 90 minutes prior to lights out on each day of the ovarian cycle and during EB treatment, but not in ovariectomized females. The functional purpose of this consistent neuronal activity at this time remains to be determined.

Though not part of this study, the comparison of neuronal activation of GnRH neurons during the LH surge to the current data was convincing, demonstrating a similar pattern of increased activation that precedes the LH surge.

In summary, the study is well-designed, uses proper controls and analyses, has robust data, and the paper is nicely organized and written. The data from these experiments is compelling, and the authors' claims and conclusions are nicely supported and justified by the data. The data support the hypothesis in the field that these RP3V neurons regulate the LH surge. Overall, these findings are important and novel, and lend valuable insight into the underlying neural mechanisms for neuroendocrine control of ovulation.

Weaknesses:

(1) LH levels were not measured in many mice or in robust temporal detail, such as every 30 or 60 min, to allow a more detailed comparison between the fine-scale timing of RP3V neuron activation with onset and timing of LH surge dynamics.

(2) The authors report that the peak LH value occurred 3.5 hours after the first RP3V kisspeptin neuron oscillation. However, it is likely, and indeed evident from the 2 example LH patterns shown in Figures 3A-B, that LH values start to increase several hours before the peak LH. This earlier rise in LH levels ("onset" of the surge) occurs much closer in time to the first RP3V kisspeptin neuron oscillatory activation, and as such, the ensuing LH secretion may not be as delayed as the authors suggest.

(3) The authors nicely show that there is some variation (~2 hours) in the peak of the first oscillation in proestrus females. Was this same variability present in OVX+E2 females, or was the variability smaller or absent in OVX+E2 versus proestrus? It is possible that the variability in proestrus mice is due to variability in the timing and magnitude of rising E2 levels, which would, in theory, be more tightly controlled and similar among mice in the OVX+E2 model. If so, the OVX+E2 mice may have less variability between mice for the onset of RP3V kisspeptin activity.

(4) One concern regarding this study is the lack of data showing the specificity of the AAV and the GCaMP6s signals. There are no data showing that GCaMP6s is limited to the RP3V and is not expressed in other Kiss1 populations in the brain. Given that 2ul of the AAV was injected, which seems like a lot considering it was close to the ventricle, it is important to show that the signal and measured activity are specific to the RP3V region. Though the authors discuss potential reasons for the low co-expression of GCaMP6 and kisspeptin immunoreactivity, it does raise some concern regarding the interpretation of these results. The low co-expression makes it difficult to confirm the Kiss1 cell-specificity of the Cre-dependent AAV injections. In addition, if GFP (GCaMP6s) and kisspeptin protein co-localization is low, it is possible that the activation of these neurons does not coincide with changes in kisspeptin or that these neurons are even expressing Kiss1 or kisspeptin at the time of activation. It is important to remember that the study measures activation of the kisspeptin neuron, and it does not reveal anything specific about the activity of the kisspeptin protein.

(5) One additional minor concern is that LH levels were not measured in the ovariectomized females during the expected time of the LH surge. The authors suggest that the lower magnitude of activation during the LH surge in these females, in comparison to proestrus females, may be the result of lower LH levels. It's hard to interpret the difference in magnitude of neuronal activation between EB-treated and proestrus females without knowing LH levels. In addition, it's possible that an LH surge did not occur in all EB-treated females, and thus, having LH levels would confirm the success of the EB treatment.

(6) This kisspeptin neuron peak activity is abolished in ovariectomized mice, and estradiol replacement restored this activity, but only partially. Circulating levels of estradiol were not measured in these different setups, but the authors hypothesize that the lack of full restoration may be due to the absence of other ovarian signals, possibly progesterone.

(7) Recordings in several mice show inter- and intra-variability in the time of peak onset. It is not shown whether this variability is associated with a similar variability in the timing of the LH surge onset in the recorded mice. The authors hypothesized that this variability indicates a poor involvement of the circadian input. However, no experiments were done to investigate the role of the (vasopressinergic-driven) circadian input on the kisspeptin neuron activation at the light/dark transition. Thus, we suggest that the authors be more tentative about this hypothesis.

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Reply to the reviewers

The authors do not wish to provide a response at this time.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Liu et al. provided evidence of the interaction between endocytosis and VAMP8-mediated endocytic recycling of clathrin-mediated endocytosis (CME) cargo through a knockdown approach combined with total internal reflection fluorescence (TIRF) microscopy, western blotting, and functional assays in a mammalian cell line system. They demonstrated that VAMP8 impairs the initial stages of CME, such as the initiation, stabilization, and invagination of clathrin-coated pits (CCPs). VAMP8 indirectly regulates CME by facilitating endocytic recycling. The depletion of VAMP8 alters endosomal recycling, as shown here by the transferrin receptor, towards lysosomal degradation, thereby inhibiting clathrin-coated vesicle (CCV) formation. Overall, I found this study to be highly engaging because of its elucidation of the unexpected role of R-Snare in influencing the levels of cargo proteins within the context of clathrin-mediated endocytosis (CME). This MS will be helpful for researchers in endocytosis and protein trafficking fields. It appears to me that VAMP8 interacts with multiple targets within the endo-lysosomal pathway, collectively influencing the clathrin-mediated endocytosis (CME). Therefore, the contribution of lysosomes in this context should be evaluated. This matter should be addressed experimentally and discussed in the MS before considering publication.

Major comments:

1. Figure 4D demonstrates that the knockdown of VAMP8 leads to an increase in lysosome numbers and lysosomal perinuclear clustering, as evidenced by LAMP1 staining (Figure 5A). Additionally, the knockdown of VAMP8 results in the downregulation of most surface receptors, as illustrated in Figure 3A, which typically follows the lysosomal degradation pathway. The observed reduction in TfR cargo could be attributable to the decreased presence of the Tfn Receptor in siVAMP8-treated cells compared to that in control cells. How do the authors explain this phenomenon? Upon reviewing these observations, I suggest that the mechanism outlined in the manuscript-specifically, "Depletion of VAMP8 skews endosomal recycling of CME cargo, exemplified here by transferrin receptor, toward lysosomal degradation, thereby inhibiting CCV formation"-may serve as a secondary rather than a primary cause. This can be ruled out by the following experiments:
   • Assessment of lysosomal biogenesis markers through RT-PCR or Western blotting following VAMP8 knockdown.
   • Assessment of transferrin receptor stability under VAMP8 knockdown conditions using cycloheximide.
   • Previous studies have indicated that perinuclear clustering of lysosomes is correlated with increased degradative activity. Therefore, assessing the lysosomal perinuclear index in the images presented in Figure 5A (LAMP1) effectively determines the presence or absence of this phenomenon.
2. Given that VAMP8 is implicated in lysosomal fusion events, I hypothesized that VAMP8 undergoes degradation via the lysosomal pathway. However, Figure 4F indicates that there was no restoration of VAMP8 following leupeptin treatment. Could you please provide an explanation for this discrepancy or is it trafficked to proteasomal degradation pathway?
3. Figure 5A and 5C demonstrate that the restoration of TfnR in siVAMP8 under leupeptin conditions was similar to the levels observed in the sicontrol without leupeptin. However, no enhancement in TfnR uptake (Figure 5F) was detected in cells treated with siVAMP8 under leupeptin treatment conditions. How can these observations be reconciled with each other?

Minor comments:

1. The manuscript does not provide details of the western blotting method and quantification criteria.
2. Fig1A &B) - The siVAMP8 #1 blot indicates a reduction exceeding 90%, whereas the bar graph depicts a reduction of 70-80%. It is advisable to elucidate the quantification criteria in the Methods section to prevent potential confusion. Were the protein levels normalized to the loading control?
3. Enhancing the readability of the graph could be achieved by labeling the Y-axis as either 'All CCP' or 'Bonafide CCP' of CME analysis graphs.
4. The legends of panels 1M and N do not correlate with the corresponding figures. Need corrections.
5. Fig 4D- Is the technique employed for electron immunogold staining utilizing a lysosome-specific antibody? How do the authors substantiate their assertion that the darkly stained structures are lysosomes and not other cellular compartments?
6. Electron micrographs of siVAMP8 cells revealed the presence of dark-stained bodies near the plasma membrane. The implications of this observation should be explained in the discussion section.
7. Fig5A- Provide the color code for the merged images.
8. Fig5G- schematic needs to be improved to demonstrate the contribution of increased lysosomal content.

Significance

VAMP8 is an R-SNARE critical for late endosome/lysosome fusion and regulates exocytosis, especially in immune and secretory cells. It pairs with Q-SNAREs to mediate vesicle fusion, and its dysfunction alters immunity, inflammation, and secretory processes. This study revealed that the SNARE protein VAMP8 influences clathrin-mediated endocytosis (CME) by managing the recycling of endocytic cargo rather than being directly recruited to clathrin-coated vesicles. This study advances our understanding of cellular trafficking mechanisms and underscores the essential role of recycling pathways in maintaining membrane dynamics. This is an excellent piece of work, and the experiments were designed meticulously; however, the mechanism is not convincing enough at this point. This MS will surely benefit the general audience, specifically the membrane and protein trafficking and cell biology community.

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Referee #2

Evidence, reproducibility and clarity

The authors investigate the role of the SNARE protein VAMP8 in endocytic recycling and clathrin-mediated endocytosis (CME). Using siRNA knockdown, live-cell imaging, and recycling assays, they report that VAMP8 depletion impairs clathrin-coated pit (CCP) initiation, stabilisation, and invagination, thereby inhibiting CME. Furthermore, they suggest that VAMP8 knockdown promotes transferrin receptor (TfR) degradation and slows its recycling. Consistent with previous studies, knockdown of CALM expression inhibits CME, whereas overexpression of wild-type or L219S/M244K mutant CALM rescues CME.

Major concerns:

1. The authors claim their work "reshape our understanding" of CME by proposing that VAMP8 regulates CME through cargo recycling rather than by direct recruitment to clathrin-coated vesicles (CCVs). However, the concept that cargo recycling influences CME efficiency is not new. Prior work has established that cargo clustering stabilises CCPs and that cargo availability strongly impacts pit dynamics. Similarly, studies of CALM, Hrb, and SNAREs have implicated recycling and SNARE interactions in CME. The observation that reduced CME cargo expression (e.g. TfnR) in VAMP8-depleted cells impairs CME is therefore consistent with earlier findings, not a new paradigm. Moreover, the manuscript raises a conceptual paradox: if VAMP8 recruitment is dispensable for CME, why is VAMP8 recruited to CCPs, and why does its depletion produce such a striking phenotype?
2. The authors note that VAMP8 knockdown reduces TfnR expression, which in turn reduces its surface levels (Figure 1N). Nevertheless, they report that VAMP8 knockdown also diminishes the endocytic efficiency of these TfRs already delivered to the plasma membrane (Figure 1M). Without rescue experiments - for example, re-expression of VAMP8 or TfnR - the specific roles of VAMP8 or cargo availability cannot be confirmed.
3. The authors argue that overexpression of WT and L219S/M244K mutant CALM rescues CME, supporting the view that abolishing VAMP8 recruitment to CCVs does not impair CME. Yet previous studies have demonstrated that CALM is essential for CME through recruitment of multiple proteins, including the R-SNAREs VAMP8, VAMP3, and VAMP2. Miller et al. have shown a conserved interaction mechanism between CALM and these SNAREs. Thus, the finding that mutant CALM rescues CME does not sufficiently demonstrate that VAMP8 recruitment is unimportant. Furthermore, Sorkin's group showed that high levels of CALM overexpression inhibit transferrin and EGF receptor endocytosis and disrupt clathrin localisation in the trans-Golgi network (PMID: 10436022). In Figure S2, the authors clearly express CALM at levels far exceeding endogenous amounts. Such overexpression may itself perturb membrane trafficking, complicating interpretation of the rescue data.
4. Most conclusions rely solely on TfR. Without examining additional receptors (e.g. EGFR, LDLR), the general claim regarding "cargo availability" remains unsubstantiated. The authors should quantify surface TfR levels following VAMP8 knockdown and/or leupeptin treatment. It also remains unclear why leupeptin treatment fails to induce TfR accumulation in lysosomes of control siRNA-treated cells.
5. The manuscript presents several kymographs, but the appearance and disappearance of CCPs are difficult to discern. While this reviewer is not an expert in quantitative imaging analysis, it appears that in both siControl and siVAMP8 cells the tracks are either unusually persistent or very short-lived, with the only obvious differences being the brightness of the spots and tracks. Although some quantitative analyses are provided, the quality and representativeness of the imaging data remain unconvincing.
6. Terms such as "productive" and "abortive" CCPs are used inconsistently and without clear definition in figure legends. In addition, the manuscript's claims of novelty, both in the Significance Statement and the main text, are overstated relative to prior literature.

Significance

General assessment: While the study shows that VAMP8 depletion negatively affects CME and TfR trafficking, the manuscript suffers from limited novelty, logical inconsistencies, and experimental shortcomings.

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Referee #1

Evidence, reproducibility and clarity

Liu and colleagues show that the knockdown of VAMP8 impairs CME by downregulating various cargo receptors, including TfnR, by rerouting theses receptors to lysosomes for degradation instead of recycling them to the plasma membrane. The results also imply that the lack of sufficient receptors (CME-cargo and associated endocytic machinery) in turn impairs the initiation/stabilization of nascent CCPs and their subsequent invagination. As shown by specific mutations in CALM, VAMP8 is apparently not directly required for CME. The emloyed cmeAnalysis DASC assay appears to be state of the art. The data are overall convincing. Nevertheless, the authors should address/clarify the following points:

Major comments:

• A rescue experiment of the VAMP8 knockdown using VAMP8 and RFP-VAMP8 should be included to exclude off-target effects and demonstrate the functionality of the RFP-VAMP8 construct.
• Please confirm that the RFP-VAMP8 expression levels in the CALM(WT) and CALM(SNARE) cells are comparable (compare first panels in Fig. 2A and 2B) and provide information about the RFP-VAMP8 expression levels compared to endogenous VAMP8. Figure 2D shows that RFP-VAMP8 is not enriched in CCPs in CALM(SNARE) cells. This raises the questions whether endocytic vesicles in the CALM(SNARE*) background indeed lack VAMP8 or still contain some residual VAMP8 levels. A complete lack of VAMP8 would imply that VAMP8 does not play a major role in determining the fate (fusion partner) of the endocytic vesicles (in the pathways analyzed by the authors). If possible, provide experimental data to solve this issue or discuss this point.

Minor comments:

• Fig. 1 N and M: The figure panels should be switched to fit to the legend, or vice versa.
• In contrast to Table S1, which show a reduction of TfnR by a factor of 1.8, the Western blot analysis (Fig. 3C) shows a 4-fold reduction. Please explain the divergence.
• It is surprising that the TfnR knockdown phenocopies the VAMP8 knockdown. Why does the knockdown of a single receptor affect endocytosis, measured by the eGFP-CLCa recruitment? Compared to other plasma membrane receptors, how abundant is TnfR? If available, please provide references demonstrating that the knockdown of other receptors has similar effects on endocytosis?
• The authors should briefly discuss to which degree the knockdown of VAMP8 may also affect receptor exocytosis, thereby contributing to a reduction of cargo receptors at the plasma membrane and impaired CME.
• VAMP8 has an established role in autophagosome - lysosome flux, favoring the fusion with the lysosomes. In the present study, VAMP8 knockdown seems to reroute receptors for lysosomal degradation in the absence of VAMP8. Please discuss.
• For clarity, the authors may consider to restructure their abstract, directly starting with their finding that "Depletion of VAMP8 skews endosomal recycling of CME cargo, exemplified by ..........

Significance

Overall, this study provides significant insights into the role of VAMP8 in the recycling of receptors to the plasma membrane. The lack of VAMP8 results in rerouting of plasma membrane receptors to lysosomes and thereby indirectly reduces endocytosis. The results will be of broad interest in the field of membrane trafficking. The reviewers field of expertise is membrane trafficking, in particular molecular mechanisms of exocytosis.

Anytype uses Swiss data centers for backup nodes, and uses AWS to get stuff there. Everything is encrypted so in that sense not problematic, but still it means Amazon holds the off-switch.

media files may not be locally available, and require a internet connection to be streamed/downloaded on demand. Generally excluded from syncing to save bandwidth. Doesn't this also mean that media files aren't backed-up, in the sense that people will treat sync as back-ups.

The free tier is tied to Anytype hosting the syncing stuff. Self-hosters do not have limitations. You do not have a name in the Anytype naming system (needed for IPFS, they have a 'private' IPFS network set-up). This is your lock-in right there. Why would you opt-in to that?

Obsidian frontmatter will be changed into properties. This also means that any other data markers, not as frontmatter, will be ignored and treated as regular text.

One can import their Obsidian folder into Anytype, but you will lose some information. Embeds don't convert, nor scripting language. I think this is externalising friction. I get that it doesn't convert as functionality, but the convertor should be able to recognise these elements and ignore or adapt them. Most people won't know how to even find all their inclusions e.g.

Anytype has paid tiers (4-20/month depending on volume of remote storage, collaborative channels Free tier has 100mb remote storage, 10 collab channels. You can use it locally fully though, w local storage.

Il n'y a, bien sûr, aucun rapport entre l'espace vital nécessaire à la démographie allemande et l'ambition de Trump de s'approprier un espace stratégique. Folie progressiste dégénérée, lamentable fantasme d'Européen débile impuissant.

ANY is a Swiss association as it provides more IP protection and signals a community affinity. All work remote, but have an office in Berlin. The staff in Berlin is employed in a German GmbH, as a subsidiary. So based in B, not CH.

Anytype is 'source available'

vc funded with all that introduces

Provides several views, as everything is an object, the graphs can make any combi/selection. Graph, table, kanban, gallery. That is however just two basic views (graph and table), unlike e.g. Tinderbox (treemap, network graph, outline, timeline, ecology, landscape)

everything in Anytype is an object, vgl Mediamatic's 'things' in Thing CMS.

You can template objects. Something you can also do in a markdown / Obsidian setting. - [ ] check of ik meer object gerichte templates wil/kan hanteren dan nu (boek, project). #pkm #30mins

Databases seem to be 'areas' in the gtd sense, and/or projects within them?

Syncing and cross device availability is through IPFS (mentioned in documentation elsewhere).

locally and on device encrypted. Means you can't access the same material through something other than Anytype? Iow it's not a viewer but a gatekeeper? Runs foul of [[3 Distributed Eigenschappen 20180703150724]] req.

Anytype is an offline first note taking / database tool for both personal and group use.

Anytype has a collaborative mode.

nice pic

hi here

hello there

陶哲轩的父母是陶象国（父亲）和梁蕙兰（母亲），他们都是香港大学毕业生，父亲是儿科医生，母亲曾是中学数学老师，两人于1972年从香港移民澳大利亚，是高知识分子家庭，对陶哲轩的成长和教育起到了关键作用。

eLife Assessment

This study aims to identify the proteins that make up the electrical synapse, which are much less understood than those of the chemical synapse. These findings represent an important step toward understanding the molecular function of chemical synapses and will have broad utility for the wider neuroscience field. The experimental evidence is convincing.

Reviewer #1 (Public review):

This study aims to identify the proteins that compose the electrical synapse, which are much less understood than those of the chemical synapse. Identifying these proteins is important to understand how synaptogenesis and conductance are regulated in these synapses.

Using a proteomics approach, the authors identified more than 50 new proteins and used immunoprecipitation and immunostaining to validate their interaction of localization. One new protein, a scaffolding protein (Sipa1l3), shows particularly strong evidence of being an integral component of the electrical synapse. The function of Sipa1l3 remains to be determined.

Another strength is the use of two different model organisms (zebrafish and mice) to determine which components are conserved across species. This approach also expands the utility of this work to benefit researchers working with both species.

The methodology is robust and there is compelling evidence supporting the findings.

Comments on revisions:

I thank the authors for responding to the comments. No further recommendations.

Reviewer #3 (Public review):

Summary:

This study by Tetenborg S et al. identifies proteins that are physically closely associated with gap junctions in retinal neurons of mice and zebrafish using BioID, a technique that labels and isolates proteins in proximal to a protein of interest. These proteins include scaffold proteins, adhesion molecules, chemical synapse proteins, components of the endocytic machinery, and cytoskeleton-associated proteins. Using a combination of genetic tools and meticulously executed immunostaining, the authors further verified the colocalizations of some of the identified proteins with connexin-positive gap junctions. The findings in this study highlight the complexity of gap junctions. Electrical synapses are abundant in the nervous system, yet their regulatory mechanisms are far less understood than those of chemical synapses. This work will provide valuable information for future studies aiming to elucidate the regulatory mechanisms essential for the function of neural circuits.

Strengths:

A key strength of this work is the identification of novel gap junction-associated proteins in AII amacrine cells and photoreceptors using BioID in combination with various genetic tools. The well-studied functions of gap junctions in these neurons will facilitate future research into the functions of the identified proteins in regulating electrical synapses.

Comments on revisions:

The authors have addressed my concerns in the revised manuscript.

Author response:

The following is the authors’ response to the previous reviews

Reviewer 1

The authors should clarify the statement regarding the expression in horizontal cells (lines 170-172). In line 170, it is stated that GFP was observed in horizontal cells. Since GFP is fused to Cx36, the observation of GFP in horizontal cells would suggest the expression of Cx36-GFP.

We believe that there appears to be a misunderstanding. GFP is observed in horizontal cells, because the test AAV construct, which consists of the HKamac promoter and a downstream GFP sequence, was used to validate the promoter specificity in wildtype animals. This was just a test to confirm that HKamac is indeed active in AII amacrine cells as previously described by Khabou et al. 2023. This construct was not used for the large scale BioID screen. For these experiments, V5-dGBP-Turbo was expressed under the control of the HKamac promoter as illustrated in Figure 2A.

Fig 7: the legend is missing the descriptions for panels A-C.

We apologize for this mistake. We have missed the label “(A-C)” and added it to the legend.

Supplemental files are not referenced in the manuscript.

We have added a reference for these files in line 221-226.

Reviewer 2

Supplementary Files 1 and 2 are presented as two replicates of the zebrafish proteomic datasets, but they appear to be identical.

This appears to be a misunderstanding. These two replicates contain slightly different hits, although the most abundant candidates are identical.

Reviewer 3

Thank you for the positive comments

eLife Assessment

This study presents a valuable finding on how the locus coeruleus modulates the involvement of medial prefrontal cortex in set shifting using calcium imaging. The evidence supporting the claims was viewed as incomplete in comparisons of extra- (EDS) and intradimensional shifts (IDS). The work is of broad interest to those studying flexible cognition.

Reviewer #1 (Public review):

Summary:

The authors note that there is a large corpus of research establishing the importance of LC-NE projections to medial prefrontal cortex (mPFC) of rats and mice in attentional set or 'rule' shifting behaviours. However, this is complex behavior and the authors were attempting to gain an understanding of how locus coeruleus modulation of the mPFC contributes to set shifting.

The authors replicated the ED-shift impairment following NE denervation of mPFC by chemogenetic inhibition of the LC. They further showed that LC inhibition changed the way neurons in mPFC responded to the cues, with a greater proportion of individual neurons responsive to 'switching', but the individual neurons also had broader tuning, responding to other aspects of the task (i.e., response choice and response history). The population dynamics was also changed by LC inhibition, with reduced separation of population vectors between early-post-switch trials, when responding was at chance, and later trials when responding was correct. This was what they set out to demonstrate and so one can conclude they achieved their aims.

The authors concluded that LC inhibition disrupted mPFC "encoding capacity for switching" and suggest that this "underlie[s] the behavioral deficits."

Strengths:

The principal strength is combining inactivation of LC with calcium imaging in mPFC. This enabled detailed consideration of the change in behavior (i.e., defining epochs of learning, with an 'early phase' when responding is at chance being compared to a 'later phase' when the behavioral switch has occurred) and how these are reflected in neuronal activity in the mPFC, with and without LC-NE input.

Comments on revised version:

In their response to reviewers, the authors say "We report p values using 2 decimal points and standard language as suggested by this reviewer". However, no changes were made in the manuscript: for example, "P = 4.2e-3" rather than "p = 0.004".

In their response to the reviewers, they wrote: "Upon closer examination of the behavioral data, we exclude several sessions where more trials were taken in IDS than in EDS." If those sessions in which EDSIDS. Most problematic is the fact that the manuscript now reads "Importantly, control mice (pooled from Fig. 1e, 1h, Supp. Fig. 1a, 1b) took more trials to complete EDS than IDS (Trials to criterion: IDS vs. EDS, 10 {plus minus} 1 trials vs. 16 {plus minus} 1 trials, P < 1e-3, Supp. Fig. 1c), further supporting the validity of attentional switching (as in Fig. 1c)" without mentioning that data has been excluded.

Reviewer #3 (Public review):

Summary:

Nigro et al examine how the locus coeruleus (LC) influences the medial prefrontal cortex (mPFC) during attentional shifts required for behavioral flexibility. Specifically, the propose that LC-mPFC inputs enable mice to shift attention effectively from texture to odor cues to optimize behavior. The LC and its noradrenergic projections to the mPFC have previously been implicated in this behavior. The authors further establish this by using chemogenetics to inhibit LC terminals in mPFC and show a selective deficit in extradimensional set shifting behavior. But the study's primary innovation is the simultaneous inhibition of LC while recording multineuron patterns of activity in mPFC. Analysis at the single neuron and population levels revealed broadened tuning properties, less distinct population dynamics, and disrupted predictive encoding when LC is inhibited. These findings add to our understanding of how neuromodulatory inputs shape attentional encoding in mPFC and are an important advance. There are some methodological limitations and/or caveats that should be considered when interpreting the findings, and these are described below.

Strengths:

The naturalistic set-shifting task in freely-moving animals is a major strength and the inclusion of localized suppression of LC-mPFC terminals is builds confidence in the specificity of their behavioral effect. Combining chemogenetic inhibition of LC while simultaneously recording neural activity in mPFC with miniscopes is state-of-the-art. The authors apply analyses to population dynamics in particular that can advance our understanding of how the LC modifies patterns of mPFC neural activity. The authors show that neural encoding at both the single cell level and the population level are disrupted when LC is inhibited. They also show that activity is less able to predict key aspects of the behavior when the influence of LC is disrupted. This is quite interesting and adds to a growing understanding of how neuromodulatory systems sharpen tuning of mPFC activity.

Weaknesses:

Weaknesses are mostly minor, but there are some caveats that should be considered. First, the authors use a DBH-Cre mouse line and provide histological confirmation of overlap between HM4Di expression and TH immunostaining. While this strongly suggests modulation of noradrenergic circuit activity, the results should be interpreted conservatively as there is no independent confirmation that norepinephrine (NE) release is suppressed and these neurons are known to release other neurotransmitters and signaling peptides. In the absence of additional control experiments, it is important to recognize that effects on mPFC activity may or may not be directly due to LC-mPFC NE.

Another caveat is that the imaging analyses are entirely from the extradimensional shift session. Without analyzing activity data from the intradimensional shift (IDS) session, one cannot be certain that the observed changes are to some feature of activity that is specific to extradimensional shifts. Future experiments should examine animals with LC suppression during the IDS as well, which would show whether the observed effects are specific to an extradimensional shift and might explain behavioral effects.

Author response:

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

Public Reviews:

We thank the reviewers and editors for this peer review. Following the editorial assessment and specific review comments, in this revision we have included new analysis to support the validity of the behavioral task (Reviewer #2). We have improved data presentation by including 1) data points from individual animals (Reviewer #1, #3), 2) updated histology showing the expression of hM4Di in LC neurons as well as LC terminals in the mPFC (Reviewer #3), and 3) more detailed descriptions of methodology and data analysis (Reviewer #1, #2, #3).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Planned t-tests should be performed in both control and experimental animals to determine if the number of trials needed to reach criterion on the ID is lower than on the ED. Based on the data analyses showing no difference among the control group, the data could be pooled to demonstrate that the task is valid. Reporting all p-values using 2 decimal points and standard language e.g., p < 0.001 would greatly improve the readability of the data. 

Thank you for this suggestion. As pointed out by this reviewer, more trials to reach performance criterion in EDS than IDS is indicative of successful acquisition and switching of the attentional sets. Upon closer examination of the behavioral data, we exclude several sessions where more trials were taken in IDS than in EDS, and our conclusions that DREADD inhibition of the LC or LC input to the mPFC impaired rule switching in EDS remain robust (e.g., new Fig. 1e, 1h). We also pool control and test data (Fig. 1e, 1h, new Supp. Fig. 1a, 1b) to demonstrate the validity of this task (new Supp. Fig. 1c, IDS vs. EDS in the control group, 10 ± 1 trials vs. 16 ± 1 trials, P < 1e-3). The validity of set shifting is also supported by the new Fig. 1c.  

We report p values using 2 decimal points and standard language as suggested by this reviewer.

Relevant to the comments from Reviewer #1 in the public review, we now show individual data points on the bar charts (new Fig. 1e, 1h).  

(2) It may also be helpful to provide the average time between CNO infusion and onset of the ED as well as information about when maximal effects are expected after these treatments.

Systemic CNO injections were administered immediately after IDS, and we waited approximately one hour before proceeding to EDS. Maximal effects of systemic CNO activation were reported to occur after 30 minutes and last for at least 4-6 hours. Both control and test groups received the CNO injections in the same manner. This is now better described in Methods.  

Reviewer #3 (Recommendations for the authors):

(1) Add better histology images showing colocalization of TH and HM4Di. Quantification of colocalization would be optimal.

We now include better histology images (new Fig. 1d) and have quantified the colocalization of TH and HM4Di in the main text (line 115-116).  

(2) If possible, images showing HM4Di expression in mPFC axon terminals would be useful. If these are colocalized with TH immunostaining, that would increase confidence in their identity. This would be much more useful than the images provided in Figure 1C.

We now include new image to show hM4Di expression (mCherry) in LC terminals in the mPFC (new Fig. 1f). However, due to technical limitations (species of the primary antibody), we did not co-stain with TH.

(3) Include behavior of mice from the miniscope experiment in Figure 2 to show they are similar to those from Figure 1.

This is now included in Supp. Fig. 1b.

(4) More details about the processing and segmentation of miniscope data would be helpful (e.g., how many neurons were identified from each animal?). 

We use standard preprocessing and segmentation pipelines in Inscopix data processing software (version 1.6), which includes modules for motion correction and signal extraction. Briefly, raw imaging videos underwent preprocessing, including a x4 spatial down sampling to reduce file size and processing time. No temporal down sampling was performed. The images were then cropped to eliminate post-registration borders and areas where cells were not visible. Prior to the calculation of the dF/F0 traces, lateral movement was corrected. For ROI identification, we used a constrained non-negative matrix factorization algorithm optimized for endoscopic data (CNMF-E) to extract fluorescence traces from ROIs. We identified 128 ± 31 neurons after manual selection, depending on recording quality and field of view. Number of neurons acquired from each animal are now included in Methods. This is now further elaborated in Methods (line 405415).  

(5) Add more methodological detail for how cell tuning was analyzed, including how z-scoring was performed (across the entire session?), and how neurons in each category were classified. 

We have expanded the Methods section to clarify how cell tuning was analyzed (line 419430). Calcium traces were z-scored on a per-neuron basis across the entire session. For each neuron, we computed trial-averaged activity aligned to specific task events (e.g., digging in one of the two ramekins available). A neuron was classified as responsive if its activity showed a significant difference (p < 0.05) between two conditions within the defined time window in the ROC analysis.

(6) For data from Figure 2F it would be very useful to plot data from individual mice in addition to this aggregated representation.

We now include data from individual mice in Supp. Table 1.

(7) I think it would be helpful to move some parts of Figure S1 to the main Figure 1, in particular the table from S1A. 

Fig. S1 is now part of the new Fig. 1.

(8) Clarify whether Figure S2 is an independent replication, as implied, or whether the same test data is shown twice in two separate figures (In Figure 1b and Supplementary Figure 2).

The test group in Fig. S2 (new Fig. S1) is the same as the test group in Fig. 1b (new Fig. 1e), but the control group is a separate cohort. This is now clarified in the figure legends.  

(9) The authors should add a limitations section to the discussion where they specifically discuss the caveats involved in relating their results specifically to NE. This should include the possible involvement of co-transmitters and off-target expression of Cre in other populations.

Thank you for this comment. Previous pharmacology and lesion studies showed that LC input or NE content in the mPFC was specifically required for EDS-type switching processes (Lapiz, M.D. et al., 2006; Tait, D.S. et al. 2007; McGaughy, J. et al. 2008), in light of which we interpret our mPFC neurophysiological effects with LC inhibition as at least partially mediated by the direct LC-NE input.  When discussing the limitations of our study, we now explicitly acknowledge the potential involvement of co-transmitters released by LC neurons (line 253-256).  

(10) The authors should provide details about the TH antibody uses for IHC

We now include more details in immunohistochemistry (line 384-388).

(11) Throughout, it would be helpful to include datapoints from individual animals - these are included in some supplementary figures, but are missing in a number of the main plots.

Reviewer #1 made a similar comment, and we now include individual data points in the figures (e.g., Fig. 1e, 1h).

eLife Assessment

This study introduces a novel method for estimating spatial spectra from irregularly sampled intracranial EEG data, revealing cortical activity across all spatial frequencies, which supports the global and integrated nature of cortical dynamics. It showcases important technical innovations and rigorous analyses, including tests to rule out potential confounds. However, further direct evaluation of the model, for example by using simulated cortical activity with a known spatial spectrum (e.g., an iEEG volume-conductor model that describes the mapping from cortical current source density to iEEG signals, and that incorporates the reference electrodes and the particular montage used), would even further strengthen the incomplete evidence.

Reviewer #1 (Public review):

Summary:

The paper uses rigorous methods to determine phase dynamics from human cortical stereotactic EEGs. It finds that the power of the phase is higher at the lowest spatial phase. The application to data illustrates the solidity of the method and their potential for discovery.

Comments on revised submission:

The authors have provided responses to the previous recommendations.

Reviewer #3 (Public review):

Summary:

The authors propose a method for estimating the spatial power spectrum of cortical activity from irregularly sampled data and apply it to iEEG data from human patients during a delayed free recall task. The main findings are that the spatial spectra of cortical activity peak at low spatial frequencies and decrease with increasing spatial frequency. This is observed over a broad range of temporal frequencies (2-100 Hz).

Strengths:

A strength of the study is the type of data that is used. As pointed out by the authors, spatial spectra of cortical activity are difficult to estimate from non-invasive measurements (EEG and MEG) and from commonly used intracranial measurements (i.e. electrocorticography or Utah arrays) due to their limited spatial extent. In contrast, iEEG measurements are easier to interpret than EEG/MEG measurements and typically have larger spatial coverage than Utah arrays. However, iEEG is irregularly sampled within the three-dimensional brain volume and this poses a methodological problem that the proposed method aims to address.

Weaknesses:

Although the proposed method is evaluated in several indirect ways, a direct evaluation is lacking. This would entail simulating cortical current source density (CSD) with known spatial spectrum and using a realistic iEEG volume-conductor model to generate iEEG signals.

Comments on revised version:

In my original review, I raised the following issue:

"The proposed method of estimating wavelength from irregularly sampled three-dimensional iEEG data involves several steps (phase-extraction, singular value-decomposition, triangle definition, dimension reduction, etc.) and it is not at all clear that the concatenation of all these steps actually yields accurate estimates. Did the authors use more realistic simulations of cortical activity (i.e. on the convoluted cortical sheet) to verify that the method indeed yields accurate estimates of phase spectra?"

And the authors' response was:

"We now included detailed surrogate testing, in which varying combinations of sEEG phase data and veridical surrogate wavelengths are added together. See our reply from the public reviewer comments. We assess that real neurophysiological data (here, sEEG plus surrogate and MEG manipulated in various ways) is a more accurate way to address these issues. In our experience, large scale TWs appear spontaneously in realistic cortical simulations, and we now cite the relevant papers in the manuscript (line 53)."

The point that I wanted to make is not that traveling waves appear in computational models of cortical activity, as the authors seem to think. My point was that the only direct way to evaluate the proposed method for estimating spatial spectra is to use simulated cortical activity with known spatial spectrum. In particular, with "realistic simulations" I refer to the iEEG volume-conductor model that describes the mapping from cortical current source density (CSD) to iEEG signals, and that incorporates the reference electrodes and the particular montage used.

Although in the revised manuscript the authors have provided indirect evidence for the soundness of the proposed estimation method, the lack of a direct evaluation using realistic simulations with ground truth as described above makes that remain sceptical about the soundness of the method.

Author response:

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

eLife Assessment

This study introduces a novel method for estimating spatial spectra from irregularly sampled intracranial EEG data, revealing cortical activity across all spatial frequencies, which supports the global and integrated nature of cortical dynamics. The study showcases important technical innovations and rigorous analyses, including tests to rule out potential confounds; however, the lack of comprehensive theoretical justification and assumptions about phase consistency across time points renders the strength of evidence incomplete. The dominance of low spatial frequencies in cortical phase dynamics continues to be of importance, and further elaboration on the interpretation and justification of the results would strengthen the link between evidence and conclusions.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The paper uses rigorous methods to determine phase dynamics from human cortical stereotactic EEGs. It finds that the power of the phase is higher at the lowest spatial phase.

Strengths:

Rigorous and advanced analysis methods.

Weaknesses:

The novelty and significance of the results are difficult to appreciate from the current version of the paper.

(1) It is very difficult to understand which experiments were analysed, and from where they were taken, reading the abstract. This is a problem both for clarity with regard to the reader and for attribution of merit to the people who collected the data.

We now explicitly state the experiments that were used, lines 715-716.

(2) The finding that the power is higher at the lowest spatial phase seems in tune with a lot of previous studies. The novelty here is unclear and it should be elaborated better.

It is not generally accepted in neuroscience that power is higher at lowest spatial frequencies, and recent research concludes that traveling waves at this scale may be the result of artefactual measurement (Orczyk et al., 2022; Hindriks et al., 2014; Zhigalov & Jensen,2023). The question we answer is therefore timely and a source of controversy to researchers analysing TWs in cortex. While, in our view, the previous literature points in the direction of our conclusions (notably the work of Freeman et. al. 2003; 2000; Barrie et al. 1996), it is not conclusive at the scale we are interested in, specifically >8cm, and certainly not convincing to the proponents of ‘artefactual measurement’.

We have added to a sentence to make this explicit in the abstract, lines 20-22. Please also note previous text at the end of the introduction, lines 140-148 and in the first paragraph of the discussion, lines 563-569.

I could not understand reading the paper the advantage I would have if I used such a technique on my data. I think that this should be clear to every reader.

We have made the core part of the code available on github (line 1154), which should simplify adoption of the technique. We have urged, in the Discussion (lines 653-663), why habitual measurement of SF spectra is desirable, since the same task measured with EEG, sEEG or ECoG does not encompass the same spatial scales, and researchers may be comparing signals with different functional properties. Until reliable methods for estimating SF are available, not dependent on the layout of the recording array, data cannot be analysed to resolve this question. Publication of our results and methods will help this process along.

(3) It seems problematic to trust in a strong conclusion that they show low spatial frequency dynamics of up to 15-20 cm given the sparsity of the arrays. The authors seem to agree with this concern in the last paragraph of page 12. 

The new surrogate testing supports our conclusions. The sEEG arrays would not normally be a first choice to estimate SF spectra, for reasons of their sparsity, which may be why such estimates have not been done before. Yet, this is the research challenge that we sought to solve, and a problem for which there was no ready method to hand. Nevertheless, it is a problem that urgently needed to be solved given the current debate on the origin of large-scale TWs. We have now included detailed surrogate testing of real data plus varying strength model waves (Figure 6A and Supplementary Figure 4). We believe this should convince the reader that we are measuring the spatial frequency spectrum with sufficient accuracy to answer the central research question.

They also say that it would be informative to repeat the analyses presented here after the selection of more participants from all available datasets. It begs the question of why this was not done. It should be done if possible.

We have now doubled the number of participants in the main analyses. Since each participant comprises a test of the central hypothesis, now the hypothesis test now has 23 replications (Supplementary Figures 2 and 3). There were four failures to reach significance due to under-powered tests, i.e., not enough contacts. This is sufficient test of the hypothesis and, in our opinion, not the primary obstacle to scientific acceptance of our results. The main obstacle is providing convincing tests that the method is accurate, and this is what we have focussed on. Publication of python code and the detailed methods described here enable any interested researcher to extend our method to other datasets.

(4) Some of the analyses seem not to exploit in full the power of the dataset. Usually, a figure starts with an example participant but then the analysis of the entire dataset is not as exhaustive. For example, in Figure 6 we have a first row with the single participants and then an average over participants. One would expect quantifications of results from each participant (i.e. from the top rows of GFg 6) extracting some relevant features of results from each participant and then showing the distribution of these features across participants. This would complement the subject average analysis.

The results are now clearly split into sections, where we first deal with all the single participant analyses, then the surrogate testing to confirm the basic results, then the participant aggregate results (Figure 7 and Supplementary Figure 7). The participant aggregate results reiterate the basic findings for the single participants. The key finding is straightforward (SF power decreases with SF) and required only one statistical analysis per subject.

(5) The function of brain phase dynamics at different frequencies and scales has been examined in previous papers at frequencies and scales relevant to what the authors treat. The authors may want to be more extensive with citing relevant studies and elaborating on the implications for them. Some examples below:

Womelsdorf T, et alScience. 2007

Besserve M et al. PloS Biology 2015

Nauhaus I et al Nat Neurosci 2009

We have added two paragraphs to the discussion, in response to the reviewer suggestion (lines 606-623). These paragraphs place our high TF findings in the context of previous research.

Reviewer #2 (Public review):

Summary:

In this paper, the authors analyze the organization of phases across different spatial scales. The authors analyze intracranial, stereo-electroencephalogram (sEEG) recordings from human clinical patients. The authors estimate the phase at each sEEG electrode at discrete temporal frequencies. They then use higher-order SVD (HOSVD) to estimate the spatial frequency spectrum of the organization of phase in a data-driven manner. Based on this analysis, the authors conclude that most of the variance explained is due to spatially extended organizations of phase, suggesting that the best description of brain activity in space and time is in fact a globally organized process. The authors' analysis is also able to rule out several important potential confounds for the analysis of spatiotemporal dynamics in EEG.

Strengths:

There are many strengths in the manuscript, including the authors' use of SVD to address the limitation of irregular sampling and their analyses ruling out potential confounds for these signals in the EEG.

Weaknesses:

Some important weaknesses are not properly acknowledged, and some conclusions are overinterpreted given the evidence presented.

The central weakness is that the analyses estimate phase from all signal time points using wavelets with a narrow frequency band (see Methods - "Numerical methods"). This step makes the assumption that phase at a particular frequency band is meaningful at all times; however, this is not necessarily the case. Take, for example, the analysis in Figure 3, which focuses on a temporal frequency of 9.2 Hz. If we compare the corresponding wavelet to the raw sEEG signal across multiple points in time, this will look like an amplitude-modulated 9.2 Hz sinusoid to which the raw sEEG signal will not correspond at all. While the authors may argue that analyzing the spatial organization of phase across many temporal frequencies will provide insight into the system, there is no guarantee that the spatial organization of phase at many individual temporal frequencies converges to the correct description of the full sEEG signal. This is a critical point for the analysis because while this analysis of the spatial organization of phase could provide some interesting results, this analysis also requires a very strong assumption about oscillations, specifically that the phase at a particular frequency (e.g. 9.2 Hz in Figure 3, or 8.0 Hz in Figure 5) is meaningful at all points in time. If this is not true, then the foundation of the analysis may not be precisely clear. This has an impact on the results presented here, specifically where the authors assert that "phase measured at a single contact in the grey matter is more strongly a function of global phase organization than local". Finally, the phase examples given in Supplementary Figure 5 are not strongly convincing to support this point.

“using wavelets with a narrow frequency band … this analysis also requires a very strong assumption about oscillations, specifically that the phase at a particular frequency (e.g. 9.2 Hz in Figure 3, or 8.0 Hz in Figure 5) is meaningful at all points in time”

Our method uses very short time-window Morlet wavelets to avoid the assumptions of oscillations, i.e., long-lasting sinusoids in the signal, in the sense of sinusoidal waveforms, or limit cycles extending in time. Cortical TWs can only last one or two cycles (Alexander et al., 2006), requiring methods that are compact in the time domain to avoid underreporting the desired phenomena. Additionally, the short time-window Morlet wavelets have low frequency resolution, so they are robust with respect to shifts in frequency between sites. We now discuss this issue explicitly in the Methods (lines 658-674). This means the phase estimation methods used in the manuscript precisely do not have the problem of assuming narrow-band oscillations in the signal. The methods are also robust to the exact shape of the waveforms; the signal needs be only approximately sinusoidal; to rise and fall. This means the Fourier variant we use does not introduce ringing artefact that can be introduced using longer timeseries methods, such as FFT.

“This step makes the assumption that phase at a particular frequency band is meaningful at all times”

This important consideration is entrenched in our choice of methods. By way of explanatory background, we point out that this step is not the final step. Aggregation methods can be used to distinguish between signal and noise. In the simple case, event-locked time-series of phase can be averaged. This would allow consistent (non-noise) phase relations to be preserved, while the inconsistent (including noise) phase relations would be washed out. This is part of the logic behind all such aggregation procedures, e.g., phase-locking, coherence. SVD has the advantage of capturing consistent relations in this sense, but without loss of information as occurs in averaging (up to the choice of number of singular vectors in the final model). Specifically, maps of the spatial covariances in phase are captured in the order of the variance explained. Noise (in the sense conveyed by the reviewer) in the phase measurements will not contribute to highest rank singular vectors. SVD is commonly used to remove noise, and that is one of its purposes here. This point can be seen by considering the very smooth singular vectors derived from MEG (Figure 3F) in this new version of the manuscript. These maps of phase gradients pull out only the non-noisy relations, even as their weighted sums reproduce any individual sample to any desired accuracy.

To summarize, the next step (of incorporating the phase measure into the SVD) neatly bypasses the issue of non-meaningful phase quantification. This is one of the reasons why we do not undertake the spatial frequency estimates on the raw matrices of estimated phase.

We now include a new sub-paragraph on this topic in the methods, lines 831-838.

In addition, we have reworded the first description of the methods with a new paragraph at the end of the introduction, which better balances the description of the steps involved. The two sentences (lines 162-166 highlight the issue of concern to the reviewer.

“there is no guarantee that the spatial organization of phase at many individual temporal frequencies converges to the correct description of the full sEEG signal.”

The correct description of the full sEEG signal is beyond the scope of the present research. Our main goal, as stated, is to show that the hypothesis that ‘extra-cranial measurements of TWs is the result of projection from localized activity’ is not supported by the evidence of spatial patterns of activity in the cortex. Since this activity can be accessed as single frequency band (especially if localized sources create the large-scale patterns), analysis of SF on a TF-by-TF basis is sufficient.

“This has an impact on the results presented here, specifically where the authors assert that "phase measured at a single contact in the grey matter is more strongly a function of global phase organization than local".

We agree with the reviewer, even though we expect that the strongest influences on local phase are due to other cortical signals in the same band. The implicit assumption of the focus on bands of the same temporal frequency is now made explicit in the abstract (lines 31-34).

A sentence addressing this issue had been added to the first paragraph of the discussion (lines 579-582).

Inclusion of cross-frequency interactions would likely require a highly regular measurement array over the scales of interest here, i.e., the noise levels inherent in the spatial organization of sEEG contacts would not support such analyses.

“Finally, the phase examples given in Supplementary Figure 5 are not strongly convincing to support this point.”

We have removed the phase examples that were previously in Supplementary Figure 5 (and Figure 5 in the previous version of the main text), since further surrogate testing and modelling (Supplementary Figure 11) shows the LSVs from irregular arrays will inevitably capture mixtures of low and high SF signals. The final section of the Methods explains this effect in some detail. Instead, the new version of the manuscript relies on new surrogate testing to validate our methods.

Another weakness is in the discussion on spatial scale. In the analyses, the authors separate contributions at (approximately) > 15 cm as macroscopic and < 15 cm as mesoscopic. The problem with the "macroscopic" here is that 15 cm is essentially on the scale of the whole brain, without accounting for the fact that organization in sub-systems may occur. For example, if a specific set of cortical regions, spanning over a 10 cm range, were to exhibit a consistent organization of phase at a particular temporal frequency (required by the analysis technique, as noted above), it is not clear why that would not be considered a "macroscopic" organization of phase, since it comprises multiple areas of the brain acting in coordination. Further, while this point could be considered as mostly semantic in nature, there is also an important technical consideration here: would spatial phase organizations occurring in varying subsets of electrodes and with somewhat variable temporal frequency reliably be detected? If this is not the case, then could it be possible that the lowest spatial frequencies are detected more often simply because it would be difficult to detect variable organizations in subsets of electrodes?

The motivation for our study was to show that large-scale TWs measured outside the cortex cannot be the result of more localized activity being ‘projected up’. In this case, the temporal frequency of the artefactual waves would be the same as the localized sources, so the criticism does not apply.

“while this point could be considered as mostly semantic in nature”

We have changed the terminology in the paper to better coincide with standard usage. Macroscopic now refers to >1cm, while we refer to >8cm as large-scale.

“15 cm is essentially on the scale of the whole brain, without accounting for the fact that organization in sub-systems may occur.”

We can assume that subtle frequency variation (e.g., within an alpha phase binding) is greatest at the largest scales of cortex, or at least not less varying than measurements within regions. This means that not considering frequency-drift effects will not inflate low spatial frequency power over high spatial frequency power. Even so, the power spectrum we estimated is approximately 1/SF, so that unmeasured cross-frequency effects in binding (causal influences on local phase) would have to overcome the strength of this relation for this criticism to apply, which seems unlikely.

“would spatial phase organizations occurring in varying subsets of electrodes and with somewhat variable temporal frequency reliably be detected?”

See our previous comments about the low temporal frequency resolution of two cycle Morlet wavelets. The answer is yes, up to the range approximated by half-power bandwidth, which is large in the case of this method (see lines 760-764).

Another weakness is disregarding the potential spike waveform artifact in the sEEG signal in the context of these analyses. Specifically, Zanos et al. (J Neurophysiol, 2011) showed that spike waveform artifacts can contaminate electrode recordings down to approximately 60 Hz. This point is important to consider in the context of the manuscript's results on spatial organization at temporal frequencies up to 100 Hz. Because the spike waveform artifact might affect signal phase at frequencies above 60 Hz, caution may be important in interpreting this point as evidence that there is significant phase organization across the cortex at these temporal frequencies.

We have now added a sentence on this issue to the discussion (lines 600-602).

However, our reading of the Zanos et al. paper is that the low temporal frequency (60-100Hz) contribution of spikes and spike patterns is negligible compared to genuine post-synaptic membrane fluctuations (see their Figure 3). These considerations come more strongly into play when correlations between LFP and spikes are calculated or spike triggered averaging is undertaken, since then a signal is being partly correlated with itself, or, partly averaged over the supposedly distinct signal with which it was detected.

A last point is that, even though the present results provide some insight into the organization of phase across the human brain, the analyses do not directly link this to spiking activity. The predictive power that these spatial organizations of phase could provide for spiking activity - even if the analyses were not affected by the distortion due to the narrow-frequency assumption - remains unknown. This is important because relating back to spiking activity is the key factor in assessing whether these specific analyses of phase can provide insight into neural circuit dynamics. This type of analysis may be possible to do with the sEEG recordings, as well, by analyzing high-gamma power (Ray and Maunsell, PLoS Biology, 2011), which can provide an index of multi-unit spiking activity around the electrodes.

“even if the analyses were not affected by the distortion due to the narrow-frequency assumption”

See our earlier comment about narrow TFs; this is not the case in the present work.

The spiking activity analysis would be an interesting avenue for future research. It appears the 1000Hz sampling frequency in the present data is not sufficient for method described in Ray & Maunsell (2011). On a related topic, we have shown that large-scale traveling waves in the MEG and 8cm waves in ECoG can both be used to predict future localized phase at a single sensor/contact, two cycles into the future (Alexander et al., 2019). This approach could be used to predict spiking activity, by combining it with the reviewer’s suggestion. However, the current manuscript is motivated by the argument that measured large-scale extra-cranial TWs are merely projections of localized cortical activity. Since spikes do not arise in this argument, we feel it is outside the scope of the present research. We have added this suggestion to the discussion as a potential line of future research (lines 686-688).

Reviewer #3 (Public review):

Summary:

The authors propose a method for estimation of the spatial spectra of cortical activity from irregularly sampled data and apply it to publicly available intracranial EEG data from human patients during a delayed free recall task. The authors' main findings are that the spatial spectra of cortical activity peak at low spatial frequencies and decrease with increasing spatial frequency. This is observed over a broad range of temporal frequencies (2-100 Hz).

Strengths:

A strength of the study is the type of data that is used. As pointed out by the authors, spatial spectra of cortical activity are difficult to estimate from non-invasive measurements (EEG and MEG) due to signal mixing and from commonly used intracranial measurements (i.e. electrocorticography or Utah arrays) due to their limited spatial extent. In contrast, iEEG measurements are easier to interpret than EEG/MEG measurements and typically have larger spatial coverage than Utah arrays. However, iEEG is irregularly sampled within the threedimensional brain volume and this poses a methodological problem that the proposed method aims to address.

Weaknesses:

The used method for estimating spatial spectra from irregularly sampled data is weak in several respects.

First, the proposed method is ad hoc, whereas there exist well-developed (Fourier-based) methods for this. The authors don't clarify why no standard methods are used, nor do they carry out a comparative evaluation.

We disagree that the method is ad hoc, though the specific combination of SVD and multiscale differencing is novel in its application to sEEG. The SVD method has been used to isolate both ~30cm TWs in MEG and EEG (Alexander et al., 2013; 2016), as well as 8cm waves in ECoG (Alexander et al., 2013; 2019). In our opening examples in the results now reiterate these previous related findings, by way of example analysis of MEG data (Figure 3). This will better inform the reader on the extent of continuity of the method from previous research.

Standard FFT has been used after interpolating between EEG electrodes to produce a uniform array (Alamia et al., 2023). There exist well-developed Fourier methods for nonuniform grids, such as simple interpolation, the butterfly algorithm, wavefield extrapolation and multi-scale vector field techniques. However, the problems for which these methods are designed require non-sparse sampling or less irregular arrays. The sEEG contacts (reduced in number to grey matter contacts) are well outside the spatial irregularity range of any Fourierrelated methods that we are aware of, particularly at the broad range of spatial scales of interest here (2cm up to 24cm). This would make direct comparison of these specialized Fourier method to our novel methods, in the sEEG, something of a straw-man comparison.

We now include a summary paragraph in the introduction, which is a brief review of Fourier methods designed to deal with non-uniform sampling (lines 159-162).

Second, the proposed method lacks a theoretical foundation and hinges on a qualitative resemblance between Fourier analysis and singular value decomposition.

We have improved our description of the theoretical relation between Fourier analysis and SVD (additional material at lines 839-861 and 910-922). In fact, there are very strong links between the two methods, and now it should be clearer that our method does not rely on a mere qualitative resemblance.

Third, the proposed method is not thoroughly tested using simulated data. Hence it remains unclear how accurate the estimated power spectra actually are.

We now include a new surrogate testing procedure, which takes as inputs the empirical data and a model signal (of known spatial frequency) in various proportions. Thus, we test both the impact of small amount of surrogate signal on the empirical signal, and the impact of ‘noise’ (in the form of a small amount of empirical signal) added to the well-defined surrogate signal.

In addition, there are a number of technical issues and limitations that need to be addressed or clarified (see recommendations to the authors).

My assessment is that the conclusions are not completely supported by the analyses. What would convince me, is if the method is tested on simulated cortical activity in a more realistic set-up. I do believe, however, that if the authors can convincingly show that the estimated spatial spectra are accurate, the study will have an impact on the field. Regarding the methodology, I don't think that it will become a standard method in the field due to its ad hoc nature and well-developed alternatives.

Simulations of cortical activity do not seem the most direct way to achieve this goal. The first author has published in this area (Liley et. al., 1999; Wright et al., 2001), and such simulations, for both bulk and neuronally based simulations, readily display traveling wave activity at low spatial frequencies (indeed, this was the origin of the present scientific journey). The manuscript outlines these results in the introduction, as well as theoretical treatments proposing the same. Several other recent studies have highlighted the appearance of largescale travelling waves using connectome-based models (https://www.biorxiv.org/content/10.1101/2025.07.05.663278v1; https://www.nature.com/articles/s41467-024-47860-x), which we do not include in the manuscript for reasons of brevity. In short, the emergence of TW phenomenon in models is partly a function of the assumptions put into them (i.e., spatial damping, boundary conditions, parameterization of connection fields) and would therefore be inconclusive in our view.

Instead, we rely on the advantages provided by the way our central research question has been posed: that the spatial frequency distribution of grey matter signal can determine whether extra-cranial TWs are artefactual. The newly introduced surrogate methods reflect this advantage by directly adding ground truth spatial frequency components to individual sample measurements. This is a less expensive option than making cortical simulations to achieve the same goal.

For the same reasons, we include testing of the methods using real cortical signals with MEG arrays (for which we could test the effects of increasing sparseness of contacts, test the effects of average referencing, and also construct surrogate time-series with alternative spectra).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Major points

Methods, Page 18: "... using notch filters to remove the 50Hz line signal and its harmonics ...": The sEEG data appear to have been recorded in North America, where the line frequency is 60 Hz. Is this perhaps a typo, or was a 50 Hz notch filter in fact applied here (which would be a mistake)?

This has now been fixed in the text to read 60Hz. This is the notch filter that was applied.

Minor points

(1) While the authors do state that they are analyzing the "spatial frequency spectrum of phase dynamics" in the abstract, this could be more clearly emphasized. Specifically, the difference between signal power at different spatial frequencies (as analyzed by a standard Fourier analysis) and the organization of phase in space (as done here) could be more clearly distinguished.

We now address this point explicitly on lines 167-172. We now include at the end of the results additional analyses where the TF power is included. This means that the effects of including signal power at different temporal frequencies can be directly compared to our main analysis of the SF spectrum of the phase dynamics.

(2) Figure 1A-C: It was not immediately clear what the lengths provided in these panels (e.g."> 40 cm cortex", "< 10 cm", "< 30 cm") were meant to indicate. This could be made clearer.

Now fixed in the caption.

(3) Figure 2A: If this is surrogate data to explain the analysis technique, it would be helpful to note explicitly at this point.

This Figure has been completely reworked, and now the status of the examples (from illustrative toy models to actual MEG data) should be clearer.

(4) Figure 4A: Why change from "% explained variance" for the example data in Figure 2C to arbitrary units at this point?

This has now been explicitly stated in the methods (lines 1033-1036).

(5) Page 15: "This means either the results were biased by a low pass filter, or had a maximum measurable...": If the authors mean that the low-pass filter is due to spatial blurring of neural activity in the EEG signal, it would be helpful to state that more directly at this point.

Now stated directly, lines 567-568.

(6) Page 23: "...where |X| is the complex magnitude of X...": The modulus operation is defined on a complex number, yet here is applied to a vector of complex numbers. If the operation is elementwise, it should be defined explicitly.

‘Elementwise’ is now stated explicitly (line 1020).

Reviewer #3 (Recommendations for the authors):

In the submitted manuscript, the authors propose a method to estimate spatial (phase) spectra from irregularly sampled oscillatory cortical activity. They apply the method to intracranial (iEEG) data and argue that cortical activity is organized into global waves up to the size of the entire cortex. If true, this finding is certainly of interest, and I can imagine that it has profound implications for how we think about the functional organization of cortical activity.

We have added a section to the discussion outlining the most radical of these implications: what does it mean to do source localization when non-local signals dominate? Lines 670-681.

The manuscript is well-written, with comprehensive introduction and discussion sections, detailed descriptions of the results, and clear figures. However, the proposed method comprised several ad hoc elements and is not well-founded mathematically, its performance is not adequately assessed, and its limitations are not sufficiently discussed. As such, the study failed to convince (me) of the correctness of the main conclusions.

We now have a direct surrogate testing of the method. We have also improved the mathematical explanation to show that the link between Fourier analysis and SVD is not ad hoc, but well understood in both literatures. We had addressed explicitly in the text all of the limitations raised by the reviewers.

Major comments

(1) The main methodological contribution of the study is summarized in the introduction section:

"The irregular sampling of cortical spatial coordinates via stereotactic EEG was partly overcome by the resampling of the phase data into triplets corresponding to the vertices of approximately equilateral triangles within the cortical sheet."

There exist well-established Fourier methods for handling irregularly sampled data so it is unclear why the authors did not resort to these and instead proposed a rather ad hoc method without theoretical justification (see next comment).

We have re-reviewed the literature on non-uniform Fourier analysis. We now briefly review the Fourier methods for handling irregularly sampled data (lines 155-162) and conclude that none of the existing methods can deal with the degree of irregularity, and especially sparsity, found for the grey-matter sEEG contacts.

(2) In the Appendix, the authors write:

"For appropriate signals, i.e., those with power that decreases monotonically with frequency, each of the first few singular vectors, v_k, is an approximate complex sinusoid with wavenumber equal to k."

I don't think this is true in general and if it is, there must be a formal argument that proves it. Furthermore, is it also true for irregularly sampled data? And in more than one spatial dimension? Moreover, it is also unclear exactly how the spatial Fourier spectrum is estimated from the SVD.

In response to these reviewer queries, we now spend considerably more time in the conceptual set-up of the manuscript, giving examples of where SVD can be used to estimate the Fourier spectrum. We have now unpacked the word ‘appropriate’ and we are now more exact in our phrasing. This is laid out in lines 843-850 of the manuscript. In addition, the methods now describe the mathematical links between Fourier analysis and SVD (lines 851861 and 910-922).

The authors write:

"The spatial frequency spectrum can therefore be estimated using SVD by summing over the singular values assigned to each set of singular vectors with unique (or by binning over a limited range of) spatial frequencies. This procedure is illustrated in Figure 1A-C."

First, the singular vectors are ordered to decreasing values of the corresponding singular values. Hence, if the singular values are used to estimate spectral power, the estimated spectrum will necessarily decrease with increasing spatial frequency (as can be seen in Figure 2C). Then how can traveling waves be detected by looking for local maxima of the estimated power spectra?

TWs are not detected by looking for local maxima in the spectra. Our work has focussed on the global wave maps derived from the SVD of phase (i.e., k=1-3), which also explain most of the variance in phase. This is now mentioned in the caption to Figure 3 (lines 291-294).

Second, how are spatial frequencies assigned to the different singular vectors? The proposed method for estimating spatial power spectra from irregularly sampled data seems rather ad hoc and it is not at all clear if, and under what conditions, it works and how accurate it is.

The new version of the manuscript uses a combination of the method previously presented (the multi-scale differencing) and the method previously outlined in the supplementary materials (doing complex-valued SVD on the spatial vectors of phase). We hope that along with the additional expository material in the methods the new version is clearer and seems less ad hoc to the reviewer. Certainly, there are deep and well-understood links between Fourier analysis and SVD, and we hope we have brought these into focus now.

(3) The authors define spatial power spectra in three-dimensional Euclidean space, whereas the actual cortical activity occurs on a two-dimensional sheet (the union of two topological 2spheres). As such, it is not at all clear how the estimated wavelengths in three-dimensional space relate to the actual wavelengths of the cortical activity.

We define spatial power spectra on the folded cortical sheet, rather than Cartesian coordinates. We use geodesic distances in all cases where a distance measurement is required. We have included two new figures (Figure 5 and Supplementary Figure1) showing the mapping of the triangles onto the cortical sheet, which should bring this point home.

(4) The authors' analysis of the iEEG data is subject to a caveat that is not mentioned in the manuscript: As a reference for the local field potentials, the average white-matter signal was used and this can lead to artifactual power at low spatial frequencies. This is because fluctuations in the reference signal are visible as standing waves in the recording array. This might also explain the observation that

"A surprising finding was that the shape of the spatial frequency spectrum did not vary much with temporal frequency."

because fluctuations in the reference signal are expected to have power at all temporal frequencies (1/f spectrum). When superposed with local activity at the recording electrodes, this leads to spurious power at low spatial frequencies. Can the authors exclude this interpretation of the results?

The new version of the manuscript deals explicitly with this potential confound (lines 454467). First, the artefactual global synchrony due to the reference signal (the DC component in our spatial frequency spectra of phase) is at a distinct frequency from the lowest SF of interest here. The lowest spatial frequency is a function of the maximum spatial range of the recording array and not overlapping in our method with the DC component, despite the loss of SF resolution due to the noise of the spatial irregularity of the recording array. This can be seen from consideration of the SF tuning (Figure 4) for the MEG wave maps shown in Figure 3, and the spectra generated for sparse MEG arrays in Supplementary Figure 5. Additionally, this question led us to a series of surrogate tests which are now included in the manuscript. We used MEG to test for the effects of average reference, since in this modality the reference free case is available. The results show that even after imposing a strong and artefactual global synchrony, the method is highly robust to inflation of the DC component, which either way does not strongly influence the SF estimates in the range of interest (4c/m to 12c/m for the case of MEG).

(5) Related to the previous comment: Contrary to the authors' claims, local field potentials are susceptible to volume conduction, particularly when average references are used (see e.g. https://www.cell.com/neuron/fulltext/S0896-6273(11)00883-X)

Methods exist to mitigate these effects (e.g. taking first- or second-order spatial differences of the signals). I think this issue deserves to be discussed.

We have reviewed this research and do not find it to be a problem. The authors cited by the reviewer were concerned with unacknowledged volume conduction up to 1 cm for LFP. The maximum spatial frequency we report here is 50c/m, or equivalent to 2cm. While the intercontact distance on the sEEG electrodes was 0.5cm, in practice the smallest equilateral triangles (i.e., between two electrodes) to be found in the grey matter was around 2cm linear size. We make no statements about SF in the 1cm range. We do now cite this paper and mention this short-range volume conduction (lines 602-605). The method of taking derivatives has the same problems as source localization methods. They remove both artefactual correlations (volume conduction) and real correlations (the low SF interactions of interest here). We mention this now at lines 667-669. In addition, our method to remove negative SF components from the LSVs ameliorates the effects of average referencing. There are now more details in the Methods about this step (lines 924-947), as well as a new supplementary figure illustrating its effects on signal with a known SF spectrum (MEG, supplementary Figure 6).

(6) Could the authors add an analysis that excludes the possibility that the observed local maxima in the spectra are a necessary consequence of the analysis method, rather than reflecting true maxima in the spectra? A (possibly) similar effect can be observed in ordinary Fourier spectra that are estimated from zero-mean signals: Because the signals have zero mean, the power spectrum at frequency zero is close to zero and this leads to an artificial local maximum at low frequencies.

We acknowledge the reviewer’s mathematical point. We do not agree that it could be an issue, though it is important to rule it out definitively. First, removing the DC component will only produce an artefactual low SF peak if the power at low SF is high. This may occur in the reviewer’s example only because temporal frequency has a ~1/f spectrum. If the true spectrum is flat, or increasing in power with f, no such artificial low SF will be produced (see Supplementary Figure 5G). Additionally,

(1) The DC component is well separated from the low SF components in our method;

(2) We now include several surrogate methods which show that our method finds the correct spectral distribution and is not just finding a maximum at low SFs due to the suggested effect (subtraction of the DC component). Analysis of separated wave maps in MEG (Figures 3 & 4) shows the expected peaks in SF, increasing in peak SF for each family of maps when wavenumber increases (roughly three k=1 maps, three k=2 etc.). A specific surrogate test for this query was also undertaken by creating a reverse SF spectrum in MEG phase data, in which the spectrum goes linearly with f over the SF range of interest, rather than the usual 1/f. Our method correctly finds the former spectrum (Supplementary Figure 5). Additionally, we tested for the effects of introducing the average reference and the effects of our method to remove the DC component of the phase SF spectrum (Supplementary Figure 6). We can definitively rule out the reviewer’s concern.

A related issue (perhaps) is the observation that the location of the maximum (i.e. the peak spatial frequency of cortical activity) depends on array size: If cortical activity indeed has a characteristic wavelength (in the sense of its spectrum having a local maximum) would one not expect it to be independent of array size?

This is only true when making estimates for relatively clean sinusoidal signals, and not from broad-band signals. Fourier analysis and our related SVD methods are very much dependent on maximum array size used to measure cortical signals. This is why the first frequency band (after the DC component) in Fourier analysis is always at a frequency equivalent to 1/array_size, even if the signal is known to contain lower frequency components. We now include a further illustration of this in Figure 3, a more detailed exposition of this point in the methods, and in Supplementary Figure 11 we provide a more detailed example of the relation between Fourier analysis and SVD when grids with two distinct scales are used.

In short, it is not possible, mathematically, to measure wavelengths greater than the array size in broad-band data. This is now stated explicitly in the manuscript (lines 143-144). A common approach in Neuroscience research is to first do narrowband filtering, then use a method that can accurately estimate ‘instantaneous’ phase change, such as the Hilbert transform. This is not possible for highly irregular sEEG arrays.

(7) The proposed method of estimating wavelength from irregularly sampled threedimensional iEEG data involves several steps (phase-extraction, singular value decomposition, triangle definition, dimension reduction, etc.) and it is not at all clear that the concatenation of all these steps actually yields accurate estimates.

Did the authors use more realistic simulations of cortical activity (i.e. on the convoluted cortical sheet) to verify that the method indeed yields accurate estimates of phase spectra?

We now included detailed surrogate testing, in which varying combinations of sEEG phase data and veridical surrogate wavelengths are added together.

See our reply from the public reviewer comments. We assess that real neurophysiological data (here, sEEG plus surrogate and MEG manipulated in various ways) is a more accurate way to address these issues. In our experience, large scale TWs appear spontaneously in realistic cortical simulations, and we now cite the relevant papers in the manuscript (line 53).

Minor comments

(1) Perhaps move the first paragraph of the results section to the Introduction (it does not describe any results).

So moved.

(2) The authors write:

"The stereotactic EEG contacts in the grey matter were re-referenced using the average of low-amplitude white matter contacts"

Does this mean that the average is taken over a subset of white-matter contacts (namely those with low amplitude)? Or do the authors refer to all white-matter contacts as "low-amplitude"? And had contacts at different needles different references? Or where the contacts from all needles pooled?

A subset of white-matter contacts was used for re-referencing, namely those 50% with lowest amplitude signals. This subset was used to construct a pooled, single, average reference. We have rephrased the sentences referring to this procedure to improve clarity (line 202 and 743745).

eLife Assessment

This study offers important insight into the pathogenic basis of intragenic frameshift deletions in the carboxy-terminal domain of MECP2, which account for some Rett syndrome cases, yet similar variants also appear in unaffected individuals. Using base editing and mouse models, the authors present convincing evidence supporting the pathogenicity of select deletion variants, with potential implications for therapeutic development. However, comments regarding the analysis of publicly available genetic databases should be addressed to strengthen the conclusions and provide greater clarity to the field.

Reviewer #1 (Public review):

Summary:

The authors scrutinized differences in C-terminal region variant profiles between Rett syndrome patients and healthy individuals and pinpointed that subtle genetic alternation can cause benign or pathogenic output, which harbors important implications in Rett syndrome diagnosis and proposes a therapeutic strategy. This work will be beneficial to clinicians and basic scientists who work on Rett syndrome, and carries the potential to be applied to other Mendelian rare diseases.

Strengths:

Well-designed genetic and molecular experiments translate genetic differences into functional and clinical changes. This is a unique study resolving subtle changes in sequences that give rise to dramatic phenotypic consequences.

Weaknesses:

There are many base-editing and protein-expression changes throughout the manuscript, and they cause confusion. It would be helpful to readers if authors could provide a simple summary diagram at the end of the paper.

Reviewer #2 (Public review):

Summary:

This study by Guy and Bird and colleagues is a natural follow-up to their 2018 Human Molecular Genetics paper, further clarifying the molecular basis of C-terminal deletions (CTDs) in MECP2 and how they contribute to Rett syndrome. The authors combine human genetic data with well-designed experiments in embryonic stem cells, differentiated neurons, and knock-in mice to explain why some CTD mutations are disease-causing while others are harmless. They show that pathogenic mutations create a specific amino acid motif at the C-terminus, where +2 frameshifts produce a PPX ending that greatly reduces MeCP2 protein levels (likely due to translational stalling) whereas +1 frameshifts generating SPRTX endings are well tolerated.

Strengths:

This is a comprehensive and rigorous study that convincingly pinpoints the molecular mechanism behind CTD pathogenicity, with strong agreement between the cell-based and animal data. The authors also provide a proof of principle that modifying the PPX termination codon can restore MeCP2-CTD protein levels and rescue symptoms in mice. In addition, they demonstrate that adenine base editing can correct this defect in cultured cells and increase MeCP2-CTD protein levels. Overall, this is a well-executed study that provides important mechanistic and translational insight into a clinically important class of MECP2 mutations.

Weaknesses:

The adenine base editing to change the termination codon is shown to be feasible in generated cell lines, but has yet to be shown in vivo in animal models.

Reviewer #3 (Public review):

Summary:

Guy et al. explored the variation in the pathogenicity of carboxy-terminal frameshift deletions in the X-linked MECP2 gene. Loss-of-function variants in MECP2 are associated with Rett syndrome, a severe neurodevelopmental disorder. Although 100's of pathogenic MECP2 variants have been found in people with Rett syndrome, 8 recurrent point mutations are found in ~65% of disease cases, and frameshift insertions/deletions (indels) variants resulting in production of carboxy-terminal truncated (CTT) MeCP2 protein account for ~10% of cases. Many of these occur in a "deletion prone region" (DPR) between c.1110-1210, with common recurrent deletions c.1157-1197del (CTD1) and c.1164_1207del (CTD2). While two major protein functional domains have been defined in MeCP2, the methyl-binding domain (MBD) and the NCoR interacting domain (NID), the functional role of the carboxy-terminal domain (CTD, beyond the NID, predicted to have a disordered protein structure) has not been identified, and previous work by this group and others demonstrated that a Mecp2 "minigene" lacking the CTD retains MeCP2 function suggesting that the CTD is dispensable. This raises an important question: If the CTD is dispensable, what is the pathogenic basis of the various CTT frameshift variants? Prior work from this group demonstrated that genetically engineered mice expressing the CTD1 variant had decreased expression of Mecp2 RNA and MeCP2 protein and decreased survival, but those expressing the CTD2 variant had normal Mecp2 RNA and protein and survival. However, they noted that differences between the mouse and human coding sequences resulted in different terminal sequences between the two common CTD, with CTD1 ending in -PPX in both mouse and human, but CTD2 ending in -PPC in human but -SPX in mouse, and in the previous paper they demonstrated in humanized mouse ES cells (edited to have the same -PPX termination) containing the CTD2 deletion resulted in decreased Mecp2 RNA and protein levels. This previous work provides the underlying hypotheses that they sought to explore, which is that the pathological basis of disease causing CTD relates to the formation of truncated proteins that end with a specific amino acid sequence (-PPX), which leads to decreased mRNA and protein levels, whereas tolerated, non-pathogenic CTD do not lead to production of truncated proteins ending in this sequence and retain normal mRNA/protein expression.

In this manuscript, they evaluate missense variants, in-frame deletions, and frame shift deletions within the DPR from the aggregated Genome Aggregated Database (gnomAD) and find that the "apparently" normal individuals within gnomAD had numerous tolerated missense variants and in-frame deletions within this region, as well as frameshift deletions (in hemizygous males) in the defined region. All of the gnomAD deletions within this region resulted in terminal amino acid sequences -SPRTX (due to +1 frameshift), whereas nearly all deletion variants in this region from people with Rett syndrome (from the Clinvar copy of the former RettBase database) had a terminal -PPX sequence, due to a +2 frameshift. They hypothesized that terminal proline codons causing ribosomal stalling and "nonsense mediated decay like" degradation of mRNA (with subsequent decreased protein expression) was the basis of the specific pathogenicity of the +2 frameshift variants, and that utilizing adenine base editors (ABE) to convert the termination codon to a tryptophan could correct this issue. They demonstrate this by engineering the change into mouse embryonic stem cell lines and mouse lines containing the CTD1 deletion and show that this change normalized Mecp2 mRNA and protein levels and mouse phenotypes. Finally, they performed an initial proof-of-concept in an inducible HEK cell line and showed the ability of targeted ABE to edit the correct adenine and cause production of the expected larger truncated Mecp2 protein from CTD1 constructs.

The findings of this manuscript provide a level of support for their hypothesis about the pathogenicity versus non-pathogenicity of some MECP2 CTT intragenic deletions and provide preliminary evidence for a novel therapeutic approach for Rett syndrome; however, limitations in their analysis do not fully support the broader conclusions presented.

Strengths:

(1) Utilization of publicly available databases containing aggregated genetic sequencing data from adult cohorts (gnomAD) and people with Rett syndrome (Clinvar copy of RettBase) to compare differences in the composition of the resulting terminal amino acid sequences resulting from deletions presumed to be pathogenic (n+2) versus presumed to be tolerated (n+1).

(2) Evaluation of a unique human pedigree containing an n+1 deletion in this region that was reported as pathogenic, with demonstration of inheritance of this from the unaffected father and presence within other unaffected family members.

(3) Development of a novel engineered mouse model of a previously assumed n+1 pathogenic variant to demonstrate lack of detrimental effect, supporting that this is likely a benign variant and not causative of Rett syndrome.

(4) Creation and evaluation of novel cell lines and mouse models to test the hypothesis that the pathogenicity of the n+2 deletion variants could be altered by a single base change in the frameshifted stop codon.

(5) Initial proof-of-concept experiments demonstrating the potential of ABE to correct the pathogenicity of these n+2 deletion variants.

Weaknesses:

(1) While the use of the large aggregated gnomAD genetic data benefits from the overall size of the data, the presence of genetic variants within this collection does not inherently mean that they are "neutral" or benign. While gnomAD does not include children, it does include aggregated data from a variety of projects targeting neuropsychiatric (and other conditions), so there is information in gnomAD from people with various medical/neuropsychiatric conditions. The authors do make some acknowledgement of this and argue that the presence of intragenic deletion variants in their region of interest in hemizygous males indicates that it is highly likely that these are tolerated, non-pathogenic variants. Broadly, it is likely true that gnomAD MECP2 variants found in hemizygous males are unlikely to cause Rett syndrome in heterozygous females, it does not necessarily mean that these variants have no potential to cause other, milder, neuropsychiatric disorders. As a clear example, within gnomAD, there is a hemizygous male with the rs28934908 C>T variant that results in p.A140V (p.A152V in e1 transcript numbering convention). This pathogenic variant has been found in a number of pedigrees with an X-linked intellectual disability pattern, in which males have a clear neurodevelopmental disorder and heterozygous females have mild intellectual disability (see PMIDs 12325019, 24328834 as representative examples of a large number of publications describing this). Thus, while their claim that hemizygous deletion variants in gnomAD are unlikely to cause Rett syndrome, that cannot make the definitive statement that they are not pathogenic and completely benign, especially when only found in a very small number of individuals in gnomAD.

(2) The authors focus exclusively on deletions within the "DPR", they define as between c.1110-1210 and say that these deletions account for 10% of Rett syndrome cases. However, the published studies that are the basis for this 10% estimate include all genetic variants (frameshift deletions, insertions, complex insertion/deletions, nonsense variants) resulting in truncations beyond the NID. For example, Bebbington 2010 (PMID: 19914908), which includes frameshift indels as early as c.905 and beyond c.1210. Further specific examples from RettBase are described below, but the important point is that their evaluation of only frameshift variants within c.1110-1210 is not truly representative of the totality of genetic variants that collectively are considered CTT and account for 10% of Rett cases.

(3) The authors say that they evaluated the putative pathogenic variants contained within RettBase (which is no longer available, but the data were transferred to Clinvar) for all cases with Classic Rett syndrome and de novo deletion variants within their defined DPR domain. Looking at the data from the Clinvar copy of RettBase, there are a number (n=143) of c-terminal truncating variants (either frameshift or nonsense) present beyond the NID, but the authors only discuss 14 deletion frameshift variants in this manuscript. A number of these variants have molecular features that do not fall into the pathogenic classification proposed by the authors and are not addressed in the manuscript and do not support the generalization of the conclusions presented in this manuscript, especially the conclusion that the determination of pathogenicity of all c-terminal truncating variants can be determined according to their proposed n+2 rule, or that all of the 10% of people with Rett syndrome and c-terminal truncating variants could be treated by using a base editor to correct the -PPX termination codon.

(4) The HEK-based system utilized is convenient for doing the initial experiments testing ABE; however, it represents an artificial system expressing cDNA without splicing. Canonical NMD is dependent on splicing, and while non-canonical "NMD-like" processes are less well understood, a concern is whether the artificial system used can adequately predict efficacy in a native setting that includes introns and splicing.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors scrutinized differences in C-terminal region variant profiles between Rett syndrome patients and healthy individuals and pinpointed that subtle genetic alternation can cause benign or pathogenic output, which harbours important implications in Rett syndrome diagnosis and proposes a therapeutic strategy. This work will be beneficial to clinicians and basic scientists who work on Rett syndrome, and carries the potential to be applied to other Mendelian rare diseases.

Strengths:

Well-designed genetic and molecular experiments translate genetic differences into functional and clinical changes. This is a unique study resolving subtle changes in sequences that give rise to dramatic phenotypic consequences.

Weaknesses:

There are many base-editing and protein-expression changes throughout the manuscript, and they cause confusion. It would be helpful to readers if authors could provide a simple summary diagram at the end of the paper.

We thank Reviewer #1 for their encouraging comments. As suggested, we will include a summary figure of the genetic changes we have made, and the resulting expression and phenotypic consequences.

Reviewer #2 (Public review):

Summary:

This study by Guy and Bird and colleagues is a natural follow-up to their 2018 Human Molecular Genetics paper, further clarifying the molecular basis of C-terminal deletions (CTDs) in MECP2 and how they contribute to Rett syndrome. The authors combine human genetic data with well-designed experiments in embryonic stem cells, differentiated neurons, and knock-in mice to explain why some CTD mutations are disease-causing while others are harmless. They show that pathogenic mutations create a specific amino acid motif at the C-terminus, where +2 frameshifts produce a PPX ending that greatly reduces MeCP2 protein levels (likely due to translational stalling) whereas +1 frameshifts generating SPRTX endings are well tolerated.

Strengths:

This is a comprehensive and rigorous study that convincingly pinpoints the molecular mechanism behind CTD pathogenicity, with strong agreement between the cell-based and animal data. The authors also provide a proof of principle that modifying the PPX termination codon can restore MeCP2-CTD protein levels and rescue symptoms in mice. In addition, they demonstrate that adenine base editing can correct this defect in cultured cells and increase MeCP2-CTD protein levels. Overall, this is a well-executed study that provides important mechanistic and translational insight into a clinically important class of MECP2 mutations.

Weaknesses:

The adenine base editing to change the termination codon is shown to be feasible in generated cell lines, but has yet to be shown in vivo in animal models.

We thank Reviewer #2 for their positive comments. We agree that an in vivo study demonstrating effective DNA base editing in our CTD-1 mouse model is the obvious next step, and this work is in progress. However, given the ever-increasing use of pre- and neonatal screening for genetic diseases, we felt it important to disseminate our findings as soon as possible. The family pedigree in Figure 3C is a clear demonstration of this need.

Reviewer #3 (Public review):

Summary:

Guy et al. explored the variation in the pathogenicity of carboxy-terminal frameshift deletions in the X-linked MECP2 gene. Loss-of-function variants in MECP2 are associated with Rett syndrome, a severe neurodevelopmental disorder. Although 100's of pathogenic MECP2 variants have been found in people with Rett syndrome, 8 recurrent point mutations are found in ~65% of disease cases, and frameshift insertions/deletions (indels) variants resulting in production of carboxy-terminal truncated (CTT) MeCP2 protein account for ~10% of cases. Many of these occur in a "deletion prone region" (DPR) between c.1110-1210, with common recurrent deletions c.1157-1197del (CTD1) and c.1164_1207del (CTD2). While two major protein functional domains have been defined in MeCP2, the methyl-binding domain (MBD) and the NCoR interacting domain (NID), the functional role of the carboxy-terminal domain (CTD, beyond the NID, predicted to have a disordered protein structure) has not been identified, and previous work by this group and others demonstrated that a Mecp2 "minigene" lacking the CTD retains MeCP2 function suggesting that the CTD is dispensable. This raises an important question: If the CTD is dispensable, what is the pathogenic basis of the various CTT frameshift variants? Prior work from this group demonstrated that genetically engineered mice expressing the CTD1 variant had decreased expression of Mecp2 RNA and MeCP2 protein and decreased survival, but those expressing the CTD2 variant had normal Mecp2 RNA and protein and survival. However, they noted that differences between the mouse and human coding sequences resulted in different terminal sequences between the two common CTD, with CTD1 ending in -PPX in both mouse and human, but CTD2 ending in -PPC in human but -SPX in mouse, and in the previous paper they demonstrated in humanized mouse ES cells (edited to have the same -PPX termination) containing the CTD2 deletion resulted in decreased Mecp2 RNA and protein levels. This previous work provides the underlying hypotheses that they sought to explore, which is that the pathological basis of disease causing CTD relates to the formation of truncated proteins that end with a specific amino acid sequence (-PPX), which leads to decreased mRNA and protein levels, whereas tolerated, non-pathogenic CTD do not lead to production of truncated proteins ending in this sequence and retain normal mRNA/protein expression.

In this manuscript, they evaluate missense variants, in-frame deletions, and frame shift deletions within the DPR from the aggregated Genome Aggregated Database (gnomAD) and find that the "apparently" normal individuals within gnomAD had numerous tolerated missense variants and in-frame deletions within this region, as well as frameshift deletions (in hemizygous males) in the defined region. All of the gnomAD deletions within this region resulted in terminal amino acid sequences -SPRTX (due to +1 frameshift), whereas nearly all deletion variants in this region from people with Rett syndrome (from the Clinvar copy of the former RettBase database) had a terminal -PPX sequence, due to a +2 frameshift. They hypothesized that terminal proline codons causing ribosomal stalling and "nonsense mediated decay like" degradation of mRNA (with subsequent decreased protein expression) was the basis of the specific pathogenicity of the +2 frameshift variants, and that utilizing adenine base editors (ABE) to convert the termination codon to a tryptophan could correct this issue. They demonstrate this by engineering the change into mouse embryonic stem cell lines and mouse lines containing the CTD1 deletion and show that this change normalized Mecp2 mRNA and protein levels and mouse phenotypes. Finally, they performed an initial proof-of-concept in an inducible HEK cell line and showed the ability of targeted ABE to edit the correct adenine and cause production of the expected larger truncated Mecp2 protein from CTD1 constructs.

The findings of this manuscript provide a level of support for their hypothesis about the pathogenicity versus non-pathogenicity of some MECP2 CTT intragenic deletions and provide preliminary evidence for a novel therapeutic approach for Rett syndrome; however, limitations in their analysis do not fully support the broader conclusions presented.

Strengths:

(1) Utilization of publicly available databases containing aggregated genetic sequencing data from adult cohorts (gnomAD) and people with Rett syndrome (Clinvar copy of RettBase) to compare differences in the composition of the resulting terminal amino acid sequences resulting from deletions presumed to be pathogenic (n+2) versus presumed to be tolerated (n+1).

(2) Evaluation of a unique human pedigree containing an n+1 deletion in this region that was reported as pathogenic, with demonstration of inheritance of this from the unaffected father and presence within other unaffected family members.

(3) Development of a novel engineered mouse model of a previously assumed n+1 pathogenic variant to demonstrate lack of detrimental effect, supporting that this is likely a benign variant and not causative of Rett syndrome.

(4) Creation and evaluation of novel cell lines and mouse models to test the hypothesis that the pathogenicity of the n+2 deletion variants could be altered by a single base change in the frameshifted stop codon.

(5) Initial proof-of-concept experiments demonstrating the potential of ABE to correct the pathogenicity of these n+2 deletion variants.

Weaknesses:

(1) While the use of the large aggregated gnomAD genetic data benefits from the overall size of the data, the presence of genetic variants within this collection does not inherently mean that they are "neutral" or benign. While gnomAD does not include children, it does include aggregated data from a variety of projects targeting neuropsychiatric (and other conditions), so there is information in gnomAD from people with various medical/neuropsychiatric conditions. The authors do make some acknowledgement of this and argue that the presence of intragenic deletion variants in their region of interest in hemizygous males indicates that it is highly likely that these are tolerated, non-pathogenic variants. Broadly, it is likely true that gnomAD MECP2 variants found in hemizygous males are unlikely to cause Rett syndrome in heterozygous females, it does not necessarily mean that these variants have no potential to cause other, milder, neuropsychiatric disorders. As a clear example, within gnomAD, there is a hemizygous male with the rs28934908 C>T variant that results in p.A140V (p.A152V in e1 transcript numbering convention). This pathogenic variant has been found in a number of pedigrees with an X-linked intellectual disability pattern, in which males have a clear neurodevelopmental disorder and heterozygous females have mild intellectual disability (see PMIDs 12325019, 24328834 as representative examples of a large number of publications describing this). Thus, while their claim that hemizygous deletion variants in gnomAD are unlikely to cause Rett syndrome, that cannot make the definitive statement that they are not pathogenic and completely benign, especially when only found in a very small number of individuals in gnomAD.

(2) The authors focus exclusively on deletions within the "DPR", they define as between c.1110-1210 and say that these deletions account for 10% of Rett syndrome cases. However, the published studies that are the basis for this 10% estimate include all genetic variants (frameshift deletions, insertions, complex insertion/deletions, nonsense variants) resulting in truncations beyond the NID. For example, Bebbington 2010 (PMID: 19914908), which includes frameshift indels as early as c.905 and beyond c.1210. Further specific examples from RettBase are described below, but the important point is that their evaluation of only frameshift variants within c.1110-1210 is not truly representative of the totality of genetic variants that collectively are considered CTT and account for 10% of Rett cases.

(3) The authors say that they evaluated the putative pathogenic variants contained within RettBase (which is no longer available, but the data were transferred to Clinvar) for all cases with Classic Rett syndrome and de novo deletion variants within their defined DPR domain. Looking at the data from the Clinvar copy of RettBase, there are a number (n=143) of c-terminal truncating variants (either frameshift or nonsense) present beyond the NID, but the authors only discuss 14 deletion frameshift variants in this manuscript. A number of these variants have molecular features that do not fall into the pathogenic classification proposed by the authors and are not addressed in the manuscript and do not support the generalization of the conclusions presented in this manuscript, especially the conclusion that the determination of pathogenicity of all c-terminal truncating variants can be determined according to their proposed n+2 rule, or that all of the 10% of people with Rett syndrome and c-terminal truncating variants could be treated by using a base editor to correct the -PPX termination codon.

(4) The HEK-based system utilized is convenient for doing the initial experiments testing ABE; however, it represents an artificial system expressing cDNA without splicing. Canonical NMD is dependent on splicing, and while non-canonical "NMD-like" processes are less well understood, a concern is whether the artificial system used can adequately predict efficacy in a native setting that includes introns and splicing.

We thank reviewer #3 for their constructive comments. A number of these relate to our analysis of databases of pathogenic (RettBASE) and non-pathogenic (gnomAD) databases. We disagree with their assertion that we are looking at only a small subset of RTT CTD mutations. We detail 14 different RTT CTDs in the manuscript, but these include the 3 most frequently occurring, which alone account for 121 RTT cases in RettBASE.

We used the original RettBASE database for our analysis, which contained significantly more information than was transferred to Clinvar. We may not have made this sufficiently clear and will remedy this during revision of the manuscript.

We stress that RettBASE contained many non-RTT causing mutations. For this reason, we employed stringent selection criteria to define a high-confidence set of RTT CTD alleles. Importantly, this set was chosen before any investigation of reading frame or C-terminal amino acid sequence. Our stringent set was selected based on three criteria: location within the C-terminal deletion prone region (CT-DPR), a diagnosis of Classical RTT and at least one case where that mutation had been shown to be absent from both parents (i.e. that it was a de novo mutation). This excluded a large number of CTD alleles which fitted the +2 frameshift/PPX ending category as well as some in other categories. There are good reasons to believe that the vast majority of genuinely pathogenic RTT CTD mutations do fall into this class.

Concerning gnomAD CTDs, we chose to restrict our detailed analysis to those which are present in the hemizygous state, to exclude individuals which mask a pathogenic mutation due to skewed X-inactivation. Data from all zygosities are shown in Fig. 3, SF1.

We will revise the manuscript to include tables of all extracted data relevant to this region, from both gnomAD and RettBASE, along with analysis of a less stringent set of RettBASE CTDs for reading frame and C-terminal amino acid sequence. We hope this will make clear the strength of the evidence for our conclusions.

We agree with Reviewer #3 that inclusions of variants in gnomAD does not exclude the possibility that they may cause medical/psychiatric conditions other than RTT. This point is already mentioned in the Discussion, but we plan to emphasise it further. The pedigree included in the paper, as well as others that we have learned of, argue that loss of the C-terminus of MeCP2 has few if any phenotypic consequences, but more cases are needed to robustly assess this conclusion.

We disagree that our HEK cell-based system is not suitable for testing efficacy of reagents for use on endogenous alleles in vivo. The editing process is not dependent on splicing, and we have shown in this manuscript that making this single base change has the same effect on an endogenous knock-in allele (CTD1 X>W) or a cDNA-based transgene (Flp-In T-REx CTD1 + base editing), namely, to increase the amount of truncated MeCP2 produced.

eLife Assessment

This study provides an important assessment of how body size influences the occurrence of macro-organisms in urban areas across the globe. Size in most plants, but only some animal families, was positively associated with urban tolerance. The data set is impressive, but the evidence for broad-scale conclusions is incomplete due to methodological issues that need to be resolved.

Reviewer #1 (Public review):

Summary:

The authors integrate multiple large databases to test whether body sizes were positively associated with which species tolerate urban areas. In general, many plant families showed a positive association between body size and urban tolerance, whereas a smaller, though still non-trivial, percentage of animal families showed the same pattern. Notably, the authors are careful in the interpretation of their findings and provide helpful context for the ways that this analysis can be generative in shaping new hypotheses and theory around how urbanization influences biodiversity at large. They are careful to discuss how body size is an important trait, but the absence of a relationship between body size and urban tolerance in many families suggests a variety of other traits undergird urban success.

Strengths:

The authors aggregated a large dataset, but they also applied robust filters to ensure they had an adequate and representative number of detections for a given species, family, geography, etc. The authors also applied their analysis at multiple taxonomic scales (family and order), which allowed for a better interpretation of the patterns in the data and at what taxonomic scale body size might be important.

Weaknesses:

My main concern is that it is not fully clear how the measure of body size might influence the result. The authors were unable to obtain consistent measures of body size (mean, median, maximum, or sex variation). This, of course, could be very consequential as means and medians can differ quite a bit, and they certainly will differ substantially from a maximum. And of course, sex differences can be marked in multiple directions or absent altogether. The authors do note that they selected the measure that was most common in a family, but it was not clear whether species in that family that did not have that measure were removed or not. This could potentially shape the variability in the dataset and obscure true patterns. This may require additional clarity from the authors and is also a real constraint in compiling large data from disparate sources.

Reviewer #2 (Public review):

I have completed a thorough review of this paper, which seeks to use the large datasets of species occurrences available through GBIF to estimate variation in how large numbers of plant and animal species are associated with urbanization throughout the world, describing what they call the "species urbanness distribution" or SUD. They explore how these SUDs differ between regions and different taxonomic levels. They then calculate a measure of urban tolerance and seek to explore whether organism size predicts variation in tolerance among species and across regions.

The study is impressive in many respects. Over the course of several papers, Callaghan and coauthors have been leaders in using "big [biodiversity] data" to create metrics of how species' occurrence data are associated with urban environments, and in describing variation in urban tolerance among taxa and regions. This work has been creative, novel, and it has pushed the boundaries of understanding how urbanization affects a wide diversity of taxa. The current paper takes this to a new level by performing analyses on over 94000 observations from >30,000 species of plants and animals, across more than 370 plant and animal taxonomic families. All of these analyses were focused on answering two main questions:

(1) What is the shape of species' urban tolerance distributions within regional communities?

(2) Does body size consistently correlate with species' urban tolerance across taxonomic groups and biogeographic contexts?

Overall, I think the questions are interesting and important, the size and scope of the data and analyses are impressive, and this paper has a potentially large contribution to make in pushing forward urban macroecology specifically and urban ecology and evolution more generally.

Despite my enthusiasm for this paper and its potential impact, there are aspects that could be improved, and I believe the paper requires major revision.

Some of these revisions ideally involve being clearer about the methodology or arguments being made. In other cases, I think their metrics of urban tolerance are flawed and need to be rethought and recalculated, and some of the conclusions are inaccurate. I hope the authors will address these comments carefully and thoroughly. I recognize that there is no obligation for authors to make revisions. However, revising the paper along the lines of the comments made below would increase the impact of the paper and its clarity to a broad readership.

Major Comments:

(1) Subrealms

Where does the concept of "subrealms" come from? No citation is given, and it could be said that this sounds like an idea straight out of Middle Earth. How do subrealms relate to known bioclimatic designations like Koppen Climate classifications, which would arguably be more appropriate? Or are subrealms more socio-ecologically oriented? From what I can tell, each subrealm lumps together climatically diverse areas. It might be better and more tractable to break things in terms of continents, as the rationale for subrealms is unclear, and it makes the analyses and results more confusing. The authors rationalized the use of subrealms to account for potential intraspecific differences in species' response to urbanization, but that is never a core part of the questions or interpretation in the paper, and averaging across subrealms also accounts for intraspecific variation. Another issue with using the subrealm approach is that the authors only included a species if it had 100 observations in a given subrealm, leading to a focus on only the most common species, which may be biased in their SUD distribution. How many more species would be included if they did their analysis at the continental or global scale, and would this change the shape of SUDs?

(2) Methods - urban score

The authors describe their "urban score" as being calculated as "the mean of the distribution of VIIRS values as a relative species specific measure of a response to urban land cover."

I don't understand how this is a "relative species-specific measure". What is it relative to? Figures S4 and S5 show the mean distribution of VIIRS for various taxa, and this mean looks to be an absolute measure. Mean VIIRS for a given species would be fine and appropriate as an "urban score", but the authors then state in the next sentence: "this urban score represents the relative ranking of that species to other species in response to urban land cover".

That doesn't follow from the description of how this is calculated. Something is missing here. Please clarify and add an explicit equation for how the urban score is calculated because the text is unclear and confusing.

(3) Methods - urban tolerance

How the authors are defining and calculating tolerance is unclear, confusing, and flawed in my opinion.

Tolerance is a common concept in ecology, evolution, and physiology, typically defined as the ability for an organism to maintain some measure of performance (e.g., fitness, growth, physiological homeostasis) in the presence versus absence of some stressor. As one example, in the herbivory literature, tolerance is often measured as the absolute or relative difference in fitness of plants that are damaged versus undamaged (e.g., https://academic.oup.com/evolut/article/62/9/2429/6853425?login=true).

On line 309, after describing the calculation of urban scores across subrealms, they write: "Therefore, a species could be represented across multiple subrealms with differing measures of urban tolerance (Fig. S4). Importantly, this continuous metric of urban tolerance is a relative measure of a species' preference, or affinity, to urban areas: it should be interpreted only within each subrealm".

This is problematic on several fronts. First, the authors never define what they mean by the term "tolerance". Second, they refer to urban tolerance throughout the paper, but don't describe the calculation until lines 315-319, where they write (text in [ ] is from the reviewer):

"Within each subrealm, we further accounted for the potential of different levels of urbanization by scaling each species' urban score by subtracting the mean VIIRS of all observations in the subrealm (this value is hereafter referred to as urban tolerance). This 'urban tolerance' (Fig. S5) value can be negative - when species under-occupy urban areas [relative to the average across all species] suggesting they actively avoid them-or positive-when species over-occupy urban areas [relative to the average across all species] suggesting they prefer them (i.e., ranging from urban avoiders to urban exploiters, respectively).<br /> They are taking a relativized urban score and then subtracting the mean VIIRS of all observations across species in a subrealm. How exactly one interprets the magnitude isn't clear and they admit this metric is "not interpretative across subrealms".

This is not a true measure of tolerance, at least not in the conventional sense of how tolerance is typically defined. The problem is that a species distribution isn't being compared to some metric of urbanness, but instead it is relative to other species' urban scores, where species may, on average, be highly urban or highly nonurban in their distribution, and this may vary from subrealm to subrealm. A measure of urban tolerance should be independent of how other species are responding, and should be interpretable across subrealms, continents, and the globe.

I propose the authors use one of two metrics of urban tolerance:

(i) Absolute Urban Tolerance = Mean VIIRS of species_i - Mean VIIRS of city centers<br /> Here, the mean VIIRS of city centers could be taken from the center of multiple cities throughout a subrealm, across a continent, or across the world. Here, the units are in the original VIIRS units where 0 would correspond to species being centered on the most extreme urban habitats, and the most extreme negative values would correspond to species that occupy the most non-urban habitats (i.e., no artificial light at night). In essence, this measure of tolerance would quantify how far a species' distribution is shifted relative to the most highly urbanized habitat available.

(ii) % Urban Tolerance = (Mean VIIRS of species_i - Mean VIIRS of city centers)/MeanVIIRS of city centers * 100%<br /> This metric provides a % change in species mean VIIRS distribution relative to the most urban habitats. This value could theoretically be negative or positive, but will typically be negative, with -100% being completely non-urban, and 0% being completely urban tolerant.

Both of these metrics can be compared across the world, as it would provide either absolute (equation 1) or relative (equation 2) metrics of urban tolerance that are comparable and easily interpretable in any region.

In summary, the definition of tolerance should be clear, the metric should be a true measure of tolerance that is comparable across regions, and an equation should be given.

(4) Figure 1: The figure does not stand alone. For example, what is the hypothesis for thermophily or the temperature-size rule? The authors should expand the legend slightly to make the hypotheses being illustrated clearer.

(5) SUDs: I don't agree with the conclusion given on line 83 ("pattern was consistent across subrealms and several taxonomic levels") or in the legend of Figure 2 ("there were consistent patterns for kingdoms, classes, and orders, as shown by generally similar density histograms shapes for each of these").

The shapes of the curves are quite different, especially for the two Kingdoms and the different classes. I agree they are relatively consistent for the different taxonomic Orders of insects.

Reviewer #3 (Public review):

Summary:

This paper reports on an association between body size and the occurrence of species in cities, which is quantified using an 'urban score' that can be visualized as a 'Species Urbanness Distribution' for particular taxa. The authors use species records from the Global Biodiversity Information Facility (GBIF) and link the occurrence data to nighttime lighting quantified using satellite data (Visible Infrared Imaging Radiometer Suite-VIIRS). They link the urban score to body size data to find 'heterogeneous relationship between body size and urban tolerance across the tree'. The results are then discussed with reference to potential mechanisms that could possibly produce the observed effects (cf. Figure 1).

Strengths:

The novelty of this study lies in the huge number of species analyzed and the comparison of results among animal taxa, rather than in a thorough analysis of what traits allow species to persist under urban conditions. Such analyses have been done using a much more thorough approach that employs presence-absence data as well as a suite of traits by other studies, for example, in (Hahs et al. 2023, Neate-Clegg et al. 2023). The dataset that the authors produced would also be very valuable if these raw data were published, both the cleaned species records as well as the body sizes.

The paper could strongly add to our understanding of what species occur in cities when the open questions are addressed.

Weaknesses:

I value the approach of the authors, but I think the paper needs to be revised.

In my view, the authors could more carefully validate their approach. Currently, any weakness or biases in the approach are quickly explained away rather than carefully explored. This concerns particularly the use of presence-only data, but also the calculation of the urban score.

The vast majority of data in GBIF is presence-only data. This produces a strong bias in the analysis presented in the paper. For some taxa, it is likely that occurrences within the city are overrepresented, and for other taxa, the opposite is true (cf. Sweet et al. 2022). I think the authors should try to address this problem.

The authors should compare their results to studies focusing on particular taxa where extensive trait-based analyses have already been performed, i.e., plants and birds. In fact, I strongly suggest that the authors should compare their results to previous studies on the relationship between traits, including body size and occurrences along a gradient of urbanisation, to draw conclusions about the validity of the approach used in the current study, which has a number of weaknesses.

They should be be more careful in coming up with post-hoc explanations of why the pattern found in this study makes sense or suggests a particular mechanism. This reviewer considers that there is no way in which the current study can disentangle the different possible mechanisms without further analyses and data, so I would suggest pointing out carefully how the mechanisms could be studied

More details should be given about the methodology. The readers should be able to understand the methods without having to read a number of other papers.

References:

Hahs, A. K., B. Fournier, M. F. Aronson, C. H. Nilon, A. Herrera-Montes, A. B. Salisbury, C. G. Threlfall, C. C. Rega-Brodsky, C. A. Lepczyk, and F. A. La Sorte. 2023. Urbanisation generates multiple trait syndromes for terrestrial animal taxa worldwide. Nature Communications 14:4751.

Neate-Clegg, M. H. C., B. A. Tonelli, C. Youngflesh, J. X. Wu, G. A. Montgomery, Ç. H. Şekercioğlu, and M. W. Tingley. 2023. Traits shaping urban tolerance in birds differ around the world. Current Biology 33:1677-1688.

Sweet, F. S. T., B. Apfelbeck, M. Hanusch, C. Garland Monteagudo, and W. W. Weisser. 2022. Data from public and governmental databases show that a large proportion of the regional animal species pool occur in cities in Germany. Journal of Urban Ecology 8:juac002.

eLife Assessment

The goal of this useful study is to examine learning-related changes in neural representations of global and local spatial reference frames in a spatial navigation task. Although the study addresses an interesting question, the evidence for neural representations in the hippocampus and retrosplenial cortex remains incomplete because of confounds in the experimental design and partial data analysis. There are further concerns about the framing of the study in the context of the relevant literature as well as the discussion.

Reviewer #1 (Public review):

Summary:

In this paper, Qiu et al. developed a novel spatial navigation task to investigate the formation of multi-scale representations in the human brain. Over multiple sessions and diverse tasks, participants learned the location of 32 objects distributed across 4 different rooms. The key task was a "judgement of relative direction" task delivered in the scanner, which was designed to assess whether object representations reflect local (within-room) or global (across-room) similarity structures. In between the two scanning sessions, participants received extensive further training. The goal of this manipulation was to test how spatial representations change with learning.

Strengths:

The authors designed a very comprehensive set of tasks in virtual reality to teach participants a novel spatial map. The spatial layout is well-designed to address the question of interest in principle. Participants were trained in a multi-day procedure, and representations were assessed twice, allowing the authors to investigate changes in the representation over multiple days.

Weaknesses:

Unfortunately, I see multiple problems with the experimental design that make it difficult to draw conclusions from the results.

(1) In the JRD task (the key task in this paper), participants were instructed to imagine standing in front of the reference object and judge whether the second object was to their left or right. The authors assume that participants solve this task by retrieving the corresponding object locations from memory, rotating their imagined viewpoint and computing the target object's relative orientation. This is a challenging task, so it is not surprising that participants do not perform particularly well after the initial training (performance between 60-70% accuracy). Notably, the authors report that after extensive training, they reached more than 90% accuracy.

However, I wonder whether participants indeed perform the task as intended by the authors, especially after the second training session. A much simpler behavioural strategy is memorising the mapping between a reference object and an associated button press, irrespective of the specific target object. This basic strategy should lead to quite high success rates, since the same direction is always correct for four of the eight objects (the two objects located at the door and the two opposite the door). For the four remaining objects, the correct button press is still the same for four of the six target objects that are not located opposite to the reference object. Simply memorising the button press associated with each reference object should therefore lead to a high overall task accuracy without the necessity to mentally simulate the spatial geometry of the object relations at all.

I also wonder whether the random effect coefficients might reflect interindividual differences in such a strategy shift - someone who learnt this relationship between objects and buttons might show larger increases in RTs compared to someone who did not.

(2) On a related note, the neural effect that appears to reflect the emergence of a global representation might be more parsimoniously explained by the formation of pairwise associations between reference and target objects. Since both objects always came from the same room, an RDM reflecting how many times an object pair acted as a reference-target pair will correlate with the categorical RDM reflecting the rooms corresponding to each object. Since the categorical RDM is highly correlated with the global RDM, this means that what the authors measure here might not reflect the formation of a global spatial map, but simply the formation of pairwise associations between objects presented jointly.

(3) In general, the authors attribute changes in neural effects to new learning. But of course, many things can change between sessions (expectancy, fatigue, change in strategy, but also physiological factors...). Baseline phsiological effects are less likely to influence patterns of activity, so the RSA analyses should be less sensitive to this problem, but especially the basic differences in activation for the contrast of post-learning > pre-learning stages in the judgment of relative direction (JRD) task could in theory just reflect baseline differences in blood oxygenation, possibly due to differences in time of day, caffeine intake, sleep, etc. To really infer that any change in activity or representation is due to learning, an active control would have been great.

(4) RSA typically compares voxel patterns associated with specific stimuli. However, the authors always presented two objects on the screen simultaneously. From what I understand, this is not considered in the analysis ("The β-maps for each reference object were averaged across trials to create an overall β-map for that object."). Furthermore, participants were asked to perform a complex mental operation on each trial ("imagine standing at A, looking at B, then perform the corresponding motor response"). Assuming that participants did this (although see points 1 and 2 above), this means that the resulting neural representation likely reflects a mixture of the two object representations, the mental transformation and the corresponding motor command, and possibly additionally the semantic and perceptual similarity between the two presented words. This means that the βs taken to reflect the reference object representation must be very noisy.

This problem is aggravated by two additional points. Firstly, not all object pairs occurred equally often, because only a fraction of all potential pairs were sampled. If the selection of the object pairs is not carefully balanced, this could easily lead to sampling biases, which RSA is highly sensitive to.

Secondly, the events in the scanner are not jittered. Instead, they are phase-locked to the TR (1.2 sec TR, 1.2 sec fixation, 4.8 sec stimulus presentation). This means that every object onset starts at the same phase of the image acquisition, making HRF sampling inefficient and hurting trial-wise estimation of betas used for the RSA. This likely significantly weakens the strength of the neural inferences that are possible using this dataset.

(5) It is not clear why the authors focus their report of the results in the main manuscript on the preselected ROIs instead of showing whole-brain results. This can be misleading, as it provides the false impression that the neural effects are highly specific to those regions.

(6) I am missing behavioural support for the authors' claims.

Overall, I am not convinced that the main conclusion that global spatial representations emerge during learning is supported by the data. Unfortunately, I think there are some fundamental problems in the experimental design that might make it difficult to address the concerns.

However, if the authors can provide convincing evidence for their claims, I think the paper will have an impact on the field. The question of how multi-scale representations are represented in the human brain is a timely and important one.

Reviewer #2 (Public review):

Summary:

Qui and colleagues studied human participants who learned about the locations of 32 different objects located across 4 different rooms in a common spatial environment. Participants were extensively trained on the object locations, and fMRI scans were done during a relative direction judgement task in a pre- and post-session. Using RSA analysis, the authors report that the hippocampus increased global relative to local representations with learning; the RSC showed a similar pattern, but also increased effects of both global and local information with time.

Strengths:

(1) The manuscript asks a generally interesting question concerning the learning of global versus local spatial information.

(2) The virtual environment task provides a rich and naturalistic spatial setting for participants, and the setup with 32 objects across 4 rooms is interesting.

(3) The within-subject design and use of verbal cues for spatial retrieval is elegant .

Weaknesses:

(1) My main concern is that the global Euclidean distances and room identity are confounded. I fear this means that all neural effects in the RSA could be alternatively explained by associations to the visual features of the rooms that build up over time.

(2) The direction judgement task is not very informative about cognitive changes, as only objects in a room are compared. The setup also discourages global learning, and leaves unclear whether participants focussed on learning the left/right relationships required by the task.

(3) With N = 23, the power is low, and the effects are weak.

(4) It appears no real multiple comparisons correction is done for the ROI based approach, and significance across ROIs is not tested directly.

Reviewer #3 (Public review):

Summary:

The manuscript by Qui et al. explores the issue of spatial learning in both local (rooms) and global (connected rooms) environments. The authors perform a pointing task, which involves either pressing the right or left button in the scanner to indicate where an object is located relative to another object. Participants are repeatedly exposed to rooms over sessions of learning, with one "pre" and one "post" learning session. The authors report that the hippocampus shifted from lower to higher RSA for the global but not the local environment after learning. RSC and OFC showed higher RSA for global object pointing. Other brain regions also showed effects, including ACC, which seemed to show a similar pattern as the hippocampus, as well as other regions shown in Figure S5. The authors attempt to tie their results in with local vs. global spatial representations.

Strengths:

Extensive testing of subjects before and after learning a spatial environment, with data suggesting that there may be fMRI codes sensitive to both global and local codes. Behavioral data suggest that subjects are performing well at the task and learning both global and local object locations, although see further comments.

Weaknesses:

(1) The authors frame the entire introduction around confirming the presence of the cognitive map either locally or globally. There are some significant issues with this framing. For one, the introduction appears to be confirmatory and not testing specific hypotheses that can be falsified. What exactly are the hypotheses being tested? I believe that this relates to the testing whether neural representations are global and/or local. However, this is not clear. Given that a previous paper (Marchette et al. 2014 Nature Neuro, which bears many similarities) showed only local coding in RSC, this paper needs to be discussed in far more depth in terms of its similarities and differences. This paper looked at both position and direction, while the current paper looks at direction. Even here, direction in the current study is somewhat impoverished: it involves either pointing right or left to an object, and much of this could be categorical or even lucky guesses. From what I could tell, all behavioral inferences are based on reaction time and not accuracy, and therefore, it is difficult to determine if the subject's behavior actually reflects knowledge gained or simply faster reaction time, either due to motor learning or a speed-accuracy trade-off. The pointing task is largely egocentric: it can be solved by remembering a facing direction and an object relative to that. It is not the JRD task as has been used in other studies (e.g., Huffman et al. 2019 Neuron), which is continuous and has an allocentric component. This "version" of the task would be largely egocentric. In this way, the pointing task used does not test the core tenets of the cognitive map during navigation, which is defined as allocentric and Euclidean (please see O'Keefe and Nadel 1978, The Hippocampus as a Cognitive Map). Since neither of these assumptions appears valid, the paper should be reframed to reflect spatial representations more broadly or even egocentric spatial representations.

(2) The fMRI data workup is insufficient. What do the authors mean by "deactivations" in Figure 3b? Does this mean the object task showed more activation than the spatial task in HSC? Given that HSC is one of these regions, this would seem to suggest that the hippocampus is more involved in object than spatial processing, although it is difficult to tell from how things are written. The RSA is more helpful, but now a concern is that the analysis focuses on small clusters that are based on analyses determined previously. This appears to be the case for the correlations shown in Figure 3e as well. The issues here are several-fold. For one, it has been shown in previous work that basing secondary analyses on related first analyses can inflate the risk of false positives (i.e., Kriegeskorte et al. 2009 Nature Neuro). The authors should perform secondary analyses in ways that are unbiased by the first analyses, preferably, selecting cluster centers (if they choose to go this route) from previous papers rather than their own analyses. Another option would be to perform analyses at the level of the entire ROI, meaning that the results would generalize more readily. The authors should also perform permutation tests to ensure that the RSA results are reliable, as these can run the risk of false positives (e.g., Nolan et al. 2018 eNeuro). If these results hold, the authors should perform post-hoc (corrected) t-tests for global vs. local before and after learning to ensure these differences are robust and not simply rely on the interaction effect. The figures were difficult to follow in this regard, and an interaction effect does not necessarily mean the differences that are critical (global higher than local after) are necessarily significant. The end part of the results was hard to follow. If ACC showed a similar effect to HC and RSC, why is it not being considered? Many other areas that seemed to show local vs. global effects were dismissed, but these should instead be discussed in terms of whether they are consistent or inconsistent with the hypotheses.

(3) Concerns about the discussion: there are areas involving reverse inference about brain areas rather than connecting the findings with hypotheses (see Poldrack et al. 2006 Trends in Cognitive Science). The authors also argue for 'transfer" of information (for example, from ACC to OFC), but did not perform any connectivity analyses, so these conclusions are not based on any results. Instead, the authors should carefully compare what can be concluded from the reaction time findings and the fMRI data. What is consistent vs. inconsistent with the hypotheses? The authors should also provide a much more detailed comparison with past work. The Marchette et al. paper comes to different conclusions regarding RSC and involves more detailed analyses than those done here, including position. What is different in the current paper that might explain the differences in results? Another previous paper that came to a different conclusion (hippocampus local, retrosplenial global) and should be carefully considered and compared, as it also involved learning of environments and comparisons at different phases (e.g., Wolbers & Buchel 2005 J Neuro). Other papers that have used the JRD task have demonstrated similar, although not identical, networks (e.g., Huffman et al. 2019 Neuron) and the results here should be more carefully compared, as the current task is largely egocentric while the Huffman et al. paper involves a continuous and allocentric version of the JRD task.

(4) The authors cite rodent papers involving single neuron recordings. These are quite different experiments, however: they involve rodents, the rodents are freely moving, and single neurons are recorded. Here, the study involves humans who are supine and an indirect vascular measure of neural activity. Citations should be to studies of spatial memory and navigation in humans using fMRI: over-reliance on rodent studies should be avoided for the reasons mentioned above.

even more important that insects (esp Nicrophorus) fill this niche

Nicrophorus must be flexible in taxa and able to accept what is available

In agrarian societies, most economic activity was concentrated in farming and manual labour, where productivity depended more on land, physical effort, and traditional knowledge than on formal education. Since only a small fraction of the population was required for non-agricultural roles, such as administration, record-keeping, or trade, a mass education system focused on universal mastery was unnecessary.

Agreed.

Good summary of opposing points.

Intentional discrepancies?

it cant be proven, only disprove because absolute proof cant be attained because exceptions exist and our understanding is continually evolving, thus, it may change overtime as new knowledge exist. also because hypothesis should be falsifiable

reply to u/rawbran30 at https://old.reddit.com/r/typewriters/comments/1py74mf/internet_hype_trendeffect_and_brand_popularity/

Olympias were imported into the US from the 50s into the 70s and were manufactured at peak typewriter engineering and manufacturing methods before machines slowly got cheaper and cheaper in terms of materials and craftsmanship through the 60s and into the early 80s before typewriters were subsumed by the word processor market.

Compared to Smith-Coronas and Remingtons of the 50s and early 60s (their peaks), Olympias are slightly better manufactured in terms of fit and finish. They're also slightly more modern looking in terms of body shapes and colors compared to other machines, which also helps to drive up price amongst collectors.

Now is an Olympia SM3 or SM9 really so much better than a Smith-Corona Silent Super that they should enjoy an almost 2x jump in price for an unserviced model? Potentially not, but if this is your issue, then buy something from a professional shop that's been cleaned, oiled, and adjusted and a lot of the price differential evaporates.

Chat with Gemini:<br /> Lee:

Here's another block of text in that same lesson. Can you help me visualize what it means?

When both vectors are normalized, the arc cosine (cos⁻¹) of their dot product reveals the angle θ between them: θ=cos⁻¹((A⋅B)/(∥A∥ ∥B∥)) or cos⁻¹(Â⋅B̂), where cos⁻¹ denotes the inverse cosine function, commonly represented as acos() in programming languages.

Gemini:<br /> This block of text is explaining how to "reverse-engineer" an angle using the dot product. In 3D graphics, you often know the coordinates of two objects (like a player and an enemy), but you don't know the angle between them. This formula is how you find it.

The Logic: Working Backwards

Think of the dot product formula we just discussed:

A⋅B = ∥A∥∥B∥cos(θ)

The text is simply rearranging that equation to solve for .

1. Isolate the Cosine: Divide both sides by the magnitudes (). A⋅B cos(θ) = ------ ∥A∥∥B∥
2. Find the Angle: To get θ by itself, you use the inverse cosine (acos). / A⋅B \ θ = arccos( ------ ) \ ∥A∥∥B∥ /

Visualizing the "Normalized" Shortcut

The text mentions: θ=cos(Â⋅B̂). (The "hat" symbol  means it is a normalized unit vector).

This is the "pro-gamer move" in graphics programming. If you normalize both vectors first (meaning you force their lengths to be 1), then ∥A∥ and ∥B∥ both become 1. The denominator in our formula disappears!

• If lengths are 1: The dot product is the cosine of the angle.
• To get the angle: You just plug that dot product into acos().

A Practical Example: "Field of View"

Imagine you are coding a stealth game. You have a Guard and a Player.

• Vector A: The direction the Guard is looking.
• Vector B: The direction from the Guard to the Player.

If you normalize both vectors and calculate (A⋅B), you get the exact angle (e.g., 30°). If the Guard's peripheral vision is only 45°, you now know the Guard can see the player!

Important "Gotcha" for Programmers

When you use acos() in languages like C#, C++, or Python, the result is usually in radians, not degrees.

• Dot Product = 1: Angle is 0 (Vectors point same way).
• Dot Product = 0: Angle is 1.57 radians (90°).
• Dot Product = -1: Angle is 3.14 radians (180°).

Lee:

You said If you normalize both vectors and calculate $acos(A⋅B), you get the exact angle (e.g., 30°). If the Guard's peripheral vision is only 45°, you now know the Guard can see the player! By "only 45°", is that from left to right of the guard's visibility? So, from straight ahead to the far right of his vision would only be 22.5°, thus the player is not visible at a 30° again from the guard? Or is that 45° from straight ahead to the far right of the guard's vision (for a total viewable angle of 90°)?

Gemini:<br /> That is a fantastic catch. In game development and 3D graphics, this distinction is a common source of bugs!

When you use the dot product to check visibility, the angle θ you calculate is the offset from the center.

1. The "Half-Angle" Concept

The dot product measures the angle between two specific lines: where the guard is looking (the "forward vector") and where the player is. It doesn't know about "left" or "right"; it only knows "how far away from my nose is this object?"

• If your calculation acos(A⋅B) returns 30°, it means the player is 30° away from the center line.
• If the guard has a 45° Field of View (FOV), usually that refers to the total horizontal arc (22.5° to the left and 22.5° to the right).

In your specific scenario:

• Total FOV: 45°
• Allowed "Half-Angle": 22.5°
• Player's Angle: 30°
• Result: Not Visible. The player is "outside the cone."

2. How it's usually coded

To avoid doing the math every single frame, programmers usually define the guard's "View Cone" as a threshold value.

If the guard can see 45° to the left and 45° to the right (a 90° total FOV), the threshold is:<br /> cos(45°) ≈ 0.707 The code then looks like this:

```csharp // If dot product is greater than 0.707, the player is within the 90-degree cone if (DotProduct(GuardForward, DirectionToPlayer) > 0.707) { // I see you! }

```

3. Why the Dot Product is "Circular"

One interesting thing to visualize: because the dot product only cares about the angle between two vectors, the "visibility" it creates is actually a cone, not a flat triangle.

If you say "anything within 30° of my forward vector is visible," that includes 30° up, 30° down, 30° left, and 30° right. It creates a circular spotlight of vision.

Summary Table: FOV vs. Dot Product

| Total FOV | Angle from Center | Dot Product Threshold (Approx) | | ------------------ | ----------------- | ------------------------------ | | 180° (Flat wall) | 90° | 0.0 | | 90° (Standard) | 45° | 0.707 | | 60° (Narrow) | 30° | 0.866 | | 2° (Sniper Scope)| 1° | 0.999 |

Chat with Gemini:<br /> Lee:

I'm taking an online course of 3D graphics. Geometry (as it pertains to 3D graphics on computers) is the current focus. The text just said:

If B is a unit vector, the operation A⋅B yields ∥A∥cos(θ), signifying the magnitude of A's projection in B's direction, with a negative sign if the direction is reversed. This is termed the scalar projection of A onto B. Can you explain this better to me? What does "magnitude of A's (a non-unit vector) projection in B's (a unit vector) direction " mean?

Gemini:<br /> This is one of the most fundamental concepts in 3D graphics, but the math jargon can sometimes obscure the simple visual reality.

To understand "the magnitude of A's projection in B's direction," the best tool is the Shadow Analogy.

1. The Shadow Analogy

Imagine Vector A is a stick floating in space. Vector B represents the ground (or a specific direction along the ground).

If you were to shine a light directly from above (perpendicular to the ground B), the stick (A) would cast a shadow onto the ground.

• The Projection: The "shadow" itself is the projection.
• The Magnitude: The length of that shadow is the "magnitude of the projection."

So, when the text says "magnitude of A's projection in B's direction," it is simply asking: "How much of Vector A is pointing in the same direction as Vector B?"

2. Why does B have to be a Unit Vector?

This is the crucial part that often trips people up.

In 3D graphics, a Unit Vector has a length of exactly 1. It is used purely to point the way; it contains direction information but no "scale" or "weight."

The formula for the dot product is:

If B is a unit vector, then . The formula simplifies to:

If B wasn't a unit vector (say, it was 5 units long), the result would be the length of the shadow multiplied by 5. That gives you a useless number if you just wanted to measure the shadow. By ensuring B is length 1, the math gives you the exact, unscaled length of the shadow of A.

3. Visualizing the Angles (The "Negative" Sign)

The text mentioned a "negative sign if the direction is reversed." This happens based on the angle () between the two vectors.

• Acute Angle (): The vectors point generally in the same direction. The shadow falls forward along B. The result is Positive.
• Right Angle (): The vectors are perpendicular. There is no shadow (it's just a dot). The result is Zero.
• Obtuse Angle (): The vectors point generally away from each other. The shadow falls backward behind the start of B. The result is Negative.

Summary Table

``` | Concept | The Visual | The Math | | ----------------- | ---------------------------------------- | ------------- | | Vector A | The object casting the shadow. | ∥A∥ | | Vector B (Unit) | The ground/direction we measure against. | ∥B∥=1 | | Dot Product (A⋅B) | The length of the shadow. | A⋅B=∥A∥cos(θ) |

```

Why do you need this in 3D Graphics?

You will use this constantly. Here are two immediate examples:

1. Lighting: If is the surface normal (pointing out of a polygon) and is the light direction, the dot product tells you how directly the light hits the surface. High projection = Bright light. Negative projection = The light is hitting the back of the polygon (it's dark).
2. Mario running up a slope: If is the direction of the slope and is Mario's velocity, the projection tells you how fast he is actually moving up the hill vs just moving forward.

Lee:

So if B was pointing directly along the +X axis (X=1, Y=0, Z=0) and A was angled up from that and longer (X=2, Y=2, Z=0), A's magnitude would be ~2.83. But A⋅B would be 2 (It's X coordinate in this specific scenario). If you made a triangle with A being one side and B specifying the direction of the adjacent side, and drew a straight line from the end of A straight down to and perpendicular to the direction B, the length of that "B" side would be A⋅B assuming ∥B∥ was 1. Does that sound correct?

Gemini:<br /> Yes, that is exactly correct. You have perfectly grasped the geometric interpretation of the dot product.

Your example scenario is spot on. Here is the breakdown of why your visualization works, mapping your description to the standard trigonometry terms.

1. The Math Check

Using your numbers:

• Vector A: (Magnitude )
• Vector B: (Unit vector along X)

The calculation is:

You correctly identified that because B is aligned perfectly with the X-axis, the "shadow" of A is simply its X-coordinate (2).

2. The Triangle Visualization

You described making a triangle. This is the exact geometric definition used in physics and graphics.

• The Hypotenuse: This is your Vector A (length ).
• The "Drop" Line: The line you drew "straight down to and perpendicular to B" is the opposite side of the triangle.
• The Adjacent Side: The side lying along the direction of B is the Scalar Projection. Its length is exactly the dot product (2).

In trigonometry terms:

3. One Crucial Detail

You added the condition: "assuming ∥B∥ was 1."

This is the most important part of your insight. If Vector B had been (2, 0, 0) (length of 2), the dot product would have been:

(2×2) + (2×0) + (0×0) = 4

The math would return 4, but the "shadow" is physically still only 2 units long. The dot product scales the result by the magnitude of B. That is why we must normalize B (make it a unit vector) before using it as a "measuring stick."

You have the concept of Scalar Projection (the length of the shadow) down cold.

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might be a bit early

seems reasonable, a dark horse that could prevent extreme drawdowns <65k

currently $20B

bullish basis yield coins?

continuation of the trend - see Hashdex

even if we don’t get CLARITY in federal law, crypto is likely to get them through guidance and rulemaking. That could provide the crypto industry with a degree of regulatory comfort over the next several years, no matter what Congress is able to accomplish

Solana’s current annual inflation rate (as of late 2025) is generally reported at roughly ~4.1 %–4.2 % per year based on its built-in emission schedule. This is down from its initial ~8 % and continues to decline year-over-year toward a long-term target of ~1.5 %.

Note Ethereum's zk integration expected by 2027 further integrating liquidity via EIL and moving towards 10,000 TPS

likely due to missing last year

Similar to coding specific rules, if parameter =x and value > y then z.

Digital

El resumen captura eficazmente el giro paradigmático hacia modelos activos, respaldado por datos cuantitativos locales (Ecuador), lo que valida su aplicabilidad regional; destaca el rol docente como facilitador, un punto clave para superar resistencias en aulas tradicionales

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you will be able to understand

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you will be able to vote / can vote

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https://app.inq.live/

https://app.livescribe.com/

I like the approach here. Particularly important because it avoids the bias from cohort heterogeneity that can affect saturation estimates in sequentially recruited cohorts.

Comparing to other genomes beyond European would strengthen the claim that these are Korean-specific CG context-associated variants.

Given that there are 1,211 methylomes and 868 transcriptomes in this cohort, these claims would benefit from directly testing whether CGV sites show differential methylation or whether nearby genes show expression differences.

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