• detecting IPFS
• get0ipfs#

https://github.com/fission-suite/get-ipfs

que es este formato? escribir bien y poner la pagina del grupo si existe

poner url en esta y en las de abajo

y entonces, que propones hacer?

por favor, definir claramente cual es el objetivo al comienzo de una sección, sin vueltas: voy a hacer [este] análisis por que me interesa ver [esto]. Si no se hace muy difícil la lectura realmente

gráficos tipo radar. Evitemos las comillas y mientras se pueda también minimicemos los términos anglos, es una tesis de una universidad argentina escrita en castellano

alguna conjetura del por que?

esto es de la tabla de arriba?. De nuevo, creo que ya lo mencione un millón de veces: TODA FIGURA Y/O TABLA DEBE ESTAR MENCIONADA EN EL TEXTO PRINCIPAL Y DISCUTIDA COMO CORRESPONDE.

la explicación de los casos quedaría mas clara y en una tabla de doble entrada

quien decide esta convención y por que?

no es mejor primero decir esto, que es lo que se hizo. Escrito como esta confunde, hay que decir primero y de forma clara y directa lo que se hizo y como, sin vueltas. Luego después si se quiere mencionar lo que no se pudo hacer

no entiendo este párrafo, esta para anunciar la sección siguiente?, no se entiende y queda descolgado, si se quiere mantenerlo explicitar más el contexto

de nuevo una figura sin mencionar ni discutir?

usar términos mas técnicos y formales

kamala debe tener discursos y declaraciones antes de esa fecha, es una politica importante. Lo que pasa es que no los estudiaste por que no eran como candidata

toda la discusión de esta carilla parece media obvia, si hay algo que no sea tan obvio o anti intuitivo estaría bueno comentarlo. O si hay diferencias en los discursos de los contrincantes en un estado estaría interesante remarcarlo y tratar de conjeturar el por que

Acá se necesita más discusión. No puede ser que se muestran dos gráficos que ocupan una carilla cada uno y la descripción sea tan exigua

y entonces? no se entiende para donde va esta discusión. explicar claramente que significan estas diferencias señaladas y cuales son las consecuencias para el análisis

hay que explicar un poco mas esto

y que significa?, explicar por que puede existir una correlación no lineal en tus datos y por que te parece necesario calcular esa métrica

fuente?

transparentar como se obtuvieron los datos. Fueron descargados en el contexto de este trabajo? contar como. Fueron descargados en otro contexto, citar fuente si existe. Los descargo otra persona? aclararlo

LaTex iss ue

What is "MEDI"? Should the y-axis be Log Illuminance?

Usar un formato estandarizado como APA asegura que las fuentes sean citadas de manera clara y profesional, facilitando la trazabilidad de la información. Este aprendizaje refuerza la importancia de la integridad académica, ya que citar correctamente no solo da crédito a los autores originales, sino que también permite a otros investigadores acceder a las fuentes para profundizar en el tema.

Este principio resalta la importancia de la reproducibilidad en la investigación científica. Detallar los recursos materiales (como software, equipos o documentos) asegura que el estudio sea transparente y verificable. Este aprendizaje refuerza que una investigación bien planificada considera no solo la ejecución, sino también la posibilidad de que otros puedan replicarla para validar los resultados.

La justificación es el "corazón" persuasivo de la investigación, ya que conecta el problema con su relevancia práctica o teórica. Al explicar por qué el estudio es necesario, el investigador no solo motiva su realización, sino que también convence a otros (como financiadores o académicos) de su valor. Este aprendizaje enfatiza la necesidad de alinear el proyecto con necesidades reales o vacíos de conocimiento.

El modelo SMART es una herramienta clave para garantizar que los objetivos sean prácticos y efectivos. Por ejemplo, un objetivo como "Demostrar los conocimientos de los estudiantes sobre Check4Covid en 2022" es específico (conocimientos), medible (a través de encuestas), alcanzable (dentro del contexto de la UVG), relevante (para la prevención de COVID-19) y temporal (en 2022). Este enfoque refuerza la importancia de diseñar objetivos que guíen la investigación sin desviarse.

Las preguntas auxiliares son esenciales para desglosar el problema en aspectos manejables. Esta pregunta específica guía la investigación hacia la evaluación de la efectividad de una herramienta, promoviendo un análisis crítico de sus fortalezas y limitaciones. Aprender a formular preguntas claras y enfocadas, como esta, ayuda a estructurar la investigación y a mantener el rumbo hacia el objetivo general.

Este punto destaca la importancia de contextualizar el problema para darle relevancia. Describir quiénes se ven afectados y las implicaciones (causas y consecuencias) permite al investigador justificar la pertinencia del estudio y conectar con las necesidades reales de una población o situación. Esto refuerza que un buen enunciado no solo describe el problema, sino que lo sitúa en un marco social, cultural o práctico significativo.

El título actúa como una "tarjeta de presentación" del proyecto, condensando la esencia de la investigación. Incluir especificidad, espacialidad y temporalidad asegura que el título sea claro y delimite el alcance del estudio. Por ejemplo, un título como "Conocimientos sobre COVID-19 en estudiantes de la UVG, 2022" define claramente qué, dónde y cuándo, ayudando a los lectores a comprender inmediatamente el enfoque y contexto del trabajo.

Este concepto subraya la importancia de la claridad en la definición del problema de investigación. Al formular el problema con precisión, el investigador establece una base sólida que facilita la identificación de objetivos, preguntas y métodos, reduciendo ambigüedades y enfocando el estudio hacia resultados concretos. Esto refuerza la necesidad de dedicar tiempo a la revisión de literatura y al análisis del contexto para garantizar que el problema sea comprensible y relevante.

Es fundamental aprender a describir un problema de investigación de manera estructurada. Entender las causas y consecuencias nos ayuda a visualizar el impacto de nuestra investigación, mientras que los indicadores permiten medir su alcance y efectividad. Esto refuerza la importancia de tener claridad sobre lo que se quiere lograr desde el inicio.

Este fragmento subraya la importancia de un título claro y conciso. Es vital que como investigadores, sepamos que el título no solo debe captar el área de investigación, sino también especificar detalles de lo que estamos investigando, dónde y cuándo. Un título bien definido sirve como guía clara para el desarrollo del proyecto.

DOI: 10.7554/eLife.33007

Resource: RRID:BDSC_28717

Curator: @scibot

SciCrunch record: RRID:BDSC_28717

What is this?

J'ai écris quelques lignes introductive pour homogénéiser avec les 2 autres texte s de cette page.

Est-ce qu'il devrait y avoir un lien ici ?

Hiện tại em thường sử dụng lời khen ngắn gọn, đơn giản như “Good job!”, “Yes!”, “OK” nhằm giúp học sinh nhận biết rằng mình đang làm đúng hoặc sai. Em cho rằng:

✅ Mục tiêu chính của lời khen là phản hồi kịp thời, giúp học sinh điều chỉnh hành vi, không nhất thiết phải cụ thể hoặc phức tạp.

🧠 Em đề cao sự tự chủ của học sinh – em mong các em học cách tự đánh giá, tự nhận ra sự tiến bộ và cảm thấy vui vì chính mình, chứ không hoàn toàn phụ thuộc vào lời khen từ giáo viên.

🤝 Em hiểu rằng việc khen ngợi cụ thể, sát sao có thể giúp học sinh thấy được sự quan tâm và xây dựng mối quan hệ tốt hơn, nhưng điều này cũng đòi hỏi thời gian, quan sát kỹ và sự đầu tư cảm xúc lớn từ giáo viên.

🎯 Em đồng ý rằng mình nên cố gắng quan tâm hơn, đặc biệt với những học sinh còn rụt rè, nhút nhát, chưa có khả năng tự đánh giá bản thân. Tuy nhiên, em mong có sự linh hoạt trong cách tiếp cận – để giáo viên có thể lựa chọn giữa khen ngợi cụ thể hay đơn giản, tùy theo hoàn cảnh và phong cách dạy học của mình.

Hiện tại em đang ở mức điểm 2 – em có sử dụng hình ảnh và đồ vật để hỗ trợ học sinh giao tiếp. Tuy nhiên, em gặp một số khó khăn để tiến xa hơn:

🔍 Kết nối sâu sắc là điều không dễ: Ngay cả với giáo viên là người Việt như em, việc thiết lập những kết nối sáng tạo và thực sự sâu sắc với học sinh là điều rất khó, vì bị giới hạn bởi cả ngôn ngữ, văn hóa lẫn bối cảnh lớp học.

🙁 Câu hỏi mở thường không có “mở”: Những dạng câu hỏi như “Do you like...?” hoặc “What do you do after school?” về lý thuyết là "câu hỏi mở", nhưng trên thực tế chỉ dẫn đến những câu trả lời ngắn, không tạo được đà tương tác.

🔤 Năng lực ngôn ngữ là rào cản đôi chiều: * Học sinh có vốn tiếng Anh còn hạn chế, nên dù có động lực chia sẻ, các em cũng khó diễn đạt. * Giáo viên cũng không thể “vượt ngôn ngữ” để dẫn dắt sâu, trừ khi có kỹ thuật hỗ trợ cực kỳ cụ thể và phù hợp với trình độ.

🧠 Khái niệm “hỗ trợ phát triển ngôn ngữ” rất mơ hồ nếu không được làm rõ: Việc kỳ vọng giáo viên "phản hồi và mở rộng trải nghiệm học sinh" cần có mô hình, ví dụ minh họa cụ thể. Nếu không, giáo viên rất dễ rơi vào tình trạng “biết nên làm gì, nhưng không biết làm sao”.

📌 Em nghĩ rằng ngay cả đội học liệu cũng sẽ gặp khó khăn trong việc clarify (làm rõ) yêu cầu này nếu không tiếp cận một cách hệ thống:

🎯 Kỳ vọng của em: Em không mong hướng dẫn hoàn hảo, nhưng rất cần những chỉ dẫn đủ cụ thể – đơn giản – hiệu quả để: * Vượt qua sự mơ hồ * Làm được điều nhỏ trước, rồi mới đến sáng tạo sâu

Hiện tại, em mới đạt được mức 2 – em có thể đặt các câu hỏi liên quan để liên hệ kiến thức nền của học sinh với bài học. Tuy nhiên, để đạt được mức 3 và 4, em nhận thấy cần đầu tư thêm thời gian cho việc chuẩn bị bài giảng (tìm kiếm video, hình ảnh, tình huống, hoạt động phù hợp...). Em hy vọng bên học liệu có thể hỗ trợ thiết kế sẵn các ý tưởng khởi động sáng tạo hoặc hoạt động liên hệ trải nghiệm để giảm tải phần chuẩn bị cho giáo viên ạ.

Em nghĩ mình hiện đang ở mức 0 hoặc mức 1. Trong giờ học, nếu học liệu có phần đóng vai hoặc hỏi – đáp, học sinh sẽ có cơ hội tương tác với nhau. Tuy nhiên, mức độ tương tác này vẫn còn đơn giản và khá hạn chế, chủ yếu do rào cản về năng lực ngôn ngữ. Học sinh cần có đủ vốn từ vựng và cấu trúc câu thì mới có thể thực sự tham gia giao tiếp hiệu quả. Với các lớp nhỏ tuổi hoặc trình độ thấp, các em thường chỉ dừng lại ở việc lặp lại mẫu câu.

Tuy vậy, trong thời gian tới, em sẽ đầu tư thêm vào việc nghiên cứu và ứng dụng các hình thức tương tác đơn giản nhưng hiệu quả, cụ thể theo hai hướng sau:

1. Tăng cường tương tác hỏi – đáp giữa học sinh thông qua các trò chơi hoặc hoạt động đóng vai ngắn + fill in the blank

2. Tổ chức linh hoạt các hoạt động cặp/nhóm từ học liệu để học sinh có cơ hội lắng nghe và phản hồi lẫn nhau nhiều hơn.

VD: 🎯 Gợi ý trò chơi: Find Someone Who...

✅ Mục tiêu: Giúp học sinh luyện mẫu câu hỏi và trả lời, đồng thời khuyến khích di chuyển và tương tác trong lớp học.

🧩 Cách triển khai phù hợp với học sinh trình độ thấp: Ví dụ: Luyện mẫu câu “Do you like...?”

Giáo viên chuẩn bị bảng câu hỏi:

Find someone who... Tên ...likes cats.<br /> ...likes apples. <br /> ...likes dancing. <br /> ...likes ice cream.

Học sinh sẽ đi hỏi bạn bè trong lớp: → “Do you like cats?” → Nếu bạn trả lời “Yes, I do.” thì ghi tên bạn đó vào ô tương ứng.

⏱ Sau 5 phút: Cả lớp ngồi lại và chia sẻ: → “I found Linh. She likes cats!”

✏️ Mẫu câu cần luyện trước khi chơi:

Hỏi: “Do you like ___?”

Trả lời: “Yes, I do.” / “No, I don’t.”

👉 Em hy vọng trong tương lai, bên học liệu cũng sẽ thiết kế thêm nhiều hoạt động tương tác như vậy để em được “nhàn hơn” mà lớp vẫn vui ạ!

DOI: 10.1152/japplphysiol.00886.2023

Resource: (Cell Signaling Technology Cat# 4912, RRID:AB_2218911)

Curator: @areedewitt04

SciCrunch record: RRID:AB_2218911

What is this?

DOI: 10.1101/2025.07.03.663021

Resource: RRID:Addgene_12260

Curator: @scibot

SciCrunch record: RRID:Addgene_12260

What is this?

Casi siempre se asocia creatividad con la producción artística, sin embargo es mucho mas importante por que se puede aplicar en varias áreas como la solución de problemas matemáticos.

COMETARIO 1

**comentario 1. **

CASO 1: CIRUGIA CORZON ABIERTO. EJE,P,OO CASOA RESOLVER.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC-2023-02191

Corresponding author: Jan Rehwinkel

1. General Statements

The authors wish to thank all three reviewers and the Review Commons team for carefully evaluating our study. We have addressed all points raised as detailed below.

We have thoroughly revised our bulk RNAseq analysis, which is now performed at the transcript level using the latest GENCODE release. We have updated Figure 3 and associated supplementary figures and tables. This change from gene to transcript level was important for accurate motif analysis as requested by reviewer 2: matching promoters to individual IFN-regulated transcripts – rather than aggregating all promoters per gene – avoids significant signal dilution. This strategy yields higher-resolution expression data and is biologically preferable. Indeed, several well characterised IFN-regulated RNAs (e.g., the ADAR1-202 transcript encoding the p150 isoform) originate from promoters located far from the constitutive promoters of their host genes. In our revised manuscript, we now provide in the new supplementary figure 13 the requested promoter motif analysis. Using two computational approaches – de novo motif search and analysis of a curated motif database – we find strong enrichment of interferon-stimulated response elements (ISREs) in promoters of type I IFN regulated transcripts. No other motifs reached similarly high levels of enrichment, and our analysis did not reveal differences between different type I IFNs. These new data show that all type I IFNs engage a common regulatory pathway, supporting our overall conclusion that different type I IFNs do not induce qualitatively different responses in PBMCs.

Regrettably, in the process of analysing the bulk RNAseq data at transcript level, we noticed that our original lncRNA analysis contained numerous false positives. Closer inspection showed that many “differentially expressed” LNCipedia models were likely not full-length transcripts and commonly shared a single IFN-induced set of exons that artificially inflated expression estimates for every overlapping model. To correct this issue, we replaced LNCipedia with the latest high-quality non-coding RNA catalogue from GENCODE, most entries of which were defined by full-length RNA sequencing [1]. We also tightened our filtering criteria and now report only transcripts that are robustly expressed in our dataset and are either classified as high-confidence by GENCODE or robustly supported at every splice junction by our RNAseq.

We hope our manuscript is sufficiently improved and suitable for publication in PLoS Biology. New or revised text is highlighted in green in our revised manuscript.

2. Point-by-point description of the revisions

Reviewer #1

Evidence, reproducibility and clarity:

The study can be directly connected to a landmark paper in the field (Mostafavi et al. , Cell 2016). By comparison with this study, the authors use improved technologies to address the question if and how responses to type I IFN differ between human peripheral blood-derived cells types. In line with Mostafavi et al. the authors conclude that only a comparably low number of interferon-stimulated genes (ISG) is induced in all cell types and that considerable differences exist between cell types in the IFN-induced transcriptome. The authors address a second relevant aspect, whether and how the many different subtypes of type I IFN differ in the way they engage IFN signals to produce transcriptome changes. The data lead the authors to conclude that any differences are of quantitative rather than qualitative nature.

The authors' conclusions are based on a mass cytometry approach to phenotype STAT activation in different cell types, bulk RNA sequencing to study ISG expression in PBMC, and single cell sequencing to study ISG responses in individual cell types. The data are solid, clear and reproducible in biological replicates (eg different blood donors).

Significance: While some of the data can be considered confirmatory, the comprehensive analysis of cell-type specificity and IFN-I subtype specificity advances the field and provides a reference for future analyses. The study is complete and there is no obvious lack of a critical experiment. The number of scientists interested in the multitude of open questions around type I IFN is large, thus the study is likely to attract a broad readership.

We thank the reviewer for her/his positive assessment of our study.

The biggest limitation is to my opinion the low sequencing depth of scRNAseq which is clearly the downside of this technology. Using 11 hematopoietic cell types and bulk RNA sequencing the total number of ISG was determined to be 975 by Mostafavi et al. and the core ISG numbered 166. This is in stark contrast to this studies' 10 core ISG. The authors limitations paragraph should discuss the fact that scRNAseq reduces the overall ISG number that can be analyzed.

Thank you for this valid comment. We amended the limitations paragraph as requested. We agree that the Mostafavi et al. 2016 Cell paper [2] is important but note that there are many differences to our study: Mostafavi et al. use mice, a seemingly very high IFN dose (10,000 Units) and microarrays (not RNAseq).

A minor point concerns the 25 supplementary figures of the study. There must be a better way to support the conclusions with the necessary data.

We agree that our supplementary materials are extensive. However, this is not unusual for studies reporting multiple large datasets. We would be delighted to organise our supplementary information differently in due course according to journal guidelines.

Reviewer #2

Evidence, reproducibility and clarity:

The manuscript entitled “Single-cell analysis of signalling and transcriptional responses to type I interferon" by Rigby et al. examines the response to type I IFN subtypes in PBMCs using an integrative proteomics and transcriptomics approach. Some of the analysis could be deepened to provide better insights into what governs the magnitude of change in gene expression as well as the cell type-specific response to expression and generate more excitement for the study.

We thank the reviewer for evaluating our study and the suggestions made.

*Major Comments: *

• Although the authors appropriately conclude that type I IFNs induce qualitatively similar, the response is not quantitatively similar. What elements in the promoters of ISGs make them more responsive to IFN subtypes? (PMID: 32847859) We thank the reviewer for the suggestion to study the promoters of genes regulated by type I IFNs. The analyses outlined below were performed by A. Fedorov, who is now a new co-author of our study. To investigate promoter features that might underlie the observed transcriptional responses across type I IFNs, we first performed a de novo*motif search using STREME [3] on our bulk RNAseq dataset (Figure 3). Specifically, we compared the promoters of transcripts that were up- or down-regulated by each IFN subtype (e.g., IFN-β-induced) either with one another or with promoters of robustly expressed RNAs that remained unresponsive to any treatment. No significant motifs emerged from these comparisons, except when we compared promoters of IFN-induced transcripts to the background set of unresponsive RNAs. This comparison consistently yielded strong enrichment of interferon-stimulated response element (ISRE)-like motifs in the promoters of up-regulated RNAs (new Figure S13a).

Next, we conducted a complementary analysis using known transcription factor (TF) motifs from the JASPAR database [4]. We screened all promoters of annotated RNAs using clustered JASPAR motifs and Z-standardised motif scores relative to all high-confidence GENCODE RNAs, including those not expressed in PBMCs. We reasoned that TFs actively mediating IFN responses would likely bind promoters with high motif scores (Z ≥ 2), while promoters with low scores (Z ≤ -1) would represent an unregulated background. This approach produced two sets of RNAs per TF cluster: putatively regulated and unregulated. We then restricted each set to RNAs expressed in our dataset and associated each transcript with its estimated fold change in response to each type I IFN, regardless of statistical significance. Next, we compared median fold changes between the likely regulated and unregulated sets across all TF clusters and IFN subtypes (Figure S13b). Among all tested TF motifs, only the ISRE-like cluster showed strong and consistent associations with transcriptional changes across all IFN subtypes. We also observed statistically significant but much weaker associations for other TFs, including a known negative regulator of innate antiviral signaling, NRF1 [5]. However, effect sizes for these motifs were dwarfed by those of ISRE-like motifs, suggesting that no JASPAR TFs other than those within the ISRE-like cluster play a major role in PBMCs under our conditions. Overall, these findings support the idea that all type I IFNs engage a common regulatory pathway, differing primarily in the magnitude rather than the nature of their transcriptional effects.

How do they relate to the activation of kinases by IFN subtypes?

We did not analyse the activation of the canonical kinases (i.e., TYK2 and JAK1) downstream of IFNAR. This would be interesting and may be possible using phospho-specific antibodies to these kinases in our CyTOF setup. However, this would require a very large investment of time and resources to identify specific antibodies, optimise a new CyTOF staining panel and to acquire and analyse new datasets. We therefore believe this should be pursued as a separate future study.

*Are there distinct features that dictate differential responses in monocytes and lymphocytes? *

Following the computational approach described above, we applied STREME to identify DNA motifs that could distinguish promoters associated with monocyte- and lymphocyte-specific ISGs. Regrettably, this analysis did not yield any significant motifs, likely due in part to the limited number of genes in each category.

• Figure 2a, d-h - Consider using the same scale for all heatmaps. This will allow for comparison of pSTATs median expression. Consider increasing the range in the color scale as some of the subtle changes in STAT phosphorylation across subtypes are not well appreciated. This also applies to Supplementary figures related to Figure 2.*

Thank you for this suggestion. We tried using the same scale for all heatmaps. However, given that the values for pSTAT1 are higher than those for other pSTATs, the resulting heatmaps did not show differences for the other pSTATs well. We therefore decided to leave these panels unchanged. Please also note that Figures 2b and S3b provide comparison between pSTATs (and other markers) using the same scale.

Minor Comments:

• The title of subsections are a bit generic (e.g "Analysis of the signalling response to type I IFNs using mass cytometry". Consider updating them to reflect some of the findings from each analysis.* Thank you for this suggestion. We have amended sub-headers accordingly.

• Figure 3 and S3 - Increase the heatmap scale to better appreciate changes in gene expression.*

The scales have been enlarged for better visibility as requested.

• Consider combining panel a and b in figure S7 for better contrasts of the response to IFNa1 or IFNb. *

Thank you for the suggestion. We combined these panels.

• Figure 4 - The authors could visualize ISGs that are unique across IFN types or cell types. *

Figure 5 and several accompanying supplementary figures already depict ISGs unique to IFN subtypes or cell types. Whilst we appreciate the suggestion, we prefer not to add additional figures to avoid redundancies.

• The gene ontology analysis should be performed with higher statistical stringency to capture the most significant IFN responsive processes. *

Thank you for this comment. We changed the presentation of the GO analysis in Fig S11 by sorting on p-value (instead of % of hits in category). We hope this shows more clearly that GO category enrichment amongst genes encoding IFN-induced transcripts had high statistical significance (log10 p-values of about -5 or lower for many categories).

Significance:* ** The authors provide an extensive compendium of cell type specific changes in response to type I IFN stimulation. They have created a public repository which extends the value of this dataset. *

Audience: *** This is a valuable resource for immunologists, virologists, and bioinformaticians.*

Thank you for these encouraging comments.

Reviewer #3

Evidence, reproducibility and clarity:

*Summary *

Rigby and collaborators analyzed the signaling responses and changes in gene expression of human PBMCs stimulated with different IFN type I subtypes, using mass cytometry, bulk and single-cell RNA sequencing. Their study represents the first single-cell atlas of human PBMCs stimulated with five type I IFN subtypes. The generated datasets are useful resources for anyone interested in innate immunity. The data and the methods are well presented. We thus recommend publication.

Thank you for your positive assessment of our work and for recommending publication.

*Major comments: *

• *

*Two of the key conclusions are not very convincing. *

• *

First, the authors claim that the magnitude of the responses varied between the 5 types of IFNs, however, as they point out in the 'limitation' paragraph, doses of the different IFNs were normalized using bioactivity. Knowing that this bioactivity is based on assays performed on A549 lung cells, this normalization likely induces a bias. How do the authors explain similar antiviral bioactivity but differing magnitudes of modulation of ISG expression? Would the authors expect the same differences of expression between the several IFNs tested in A549 cells? We thus recommend being very cautious when comparing magnitude of the response between the 5 types of IFNs.

We thank the reviewer for this important point and included the following reasoning in our discussion:

“An important technical consideration for our study was the normalisation of type I IFN doses used to treat cells (see also ‘Limitations of the study’ below). We relied on bioactivity (U/ml) that is measured by the manufacturer of recombinant type I IFNs using a cytopathic effect (CPE) inhibition assay. In brief, the lung cancer cell line A549 is treated with type I IFN and is infected with the cytopathic encephalomyocarditis virus (EMCV). Control cells not treated with IFN are killed by EMCV, whereas cells treated with sufficient IFN survive. How, then, is it possible that different type I IFNs induce differing magnitudes of STAT phosphorylation and ISG expression despite being used at the same bioactivity? Cell survival in the CPE inhibition assay may be due to one or a few ISGs. Indeed, single ISGs can mediate powerful antiviral defence. For example, MX1 is crucial for host defence against influenza A virus [6]. Thus, similar bioactivity of different IFNs in A549 cells against EMCV-triggered cell death may not reflect the breadth of effects on many ISGs. Moreover, IFN-induced survival of A549 cells following EMCV infection is a binary readout. Induction of the relevant ISG(s) mediating protection beyond a threshold required for cell survival is unlikely to register in this assay. Thus, similar antiviral bioactivity (in the CPE inhibition assay) and differing magnitudes of modulation of ISG expression (at transcriptome level) are compatible.”

We believe inclusion of this paragraph demonstrates an appropriate level of caution in our data interpretation. Further, we would expect to make similar observations if we were to apply transcriptomic analysis to A549 cells treated with different type I IFNs. However, given our focus in this study on primary, normal cells, we decided not to pursue work with the transformed and lab adapted A549 cell line.

Second, the qualitatively different responses to type I IFN subtypes claimed by the authors were not apparent. This seems true at the level of the bulk population (Fig. S10) but not at cell-type level (Fig. S15/S16).

We believe there may be a misunderstanding here. In relation to Figure S10, we do not claim “qualitatively different responses to type I IFN subtypes”. Instead, we conclude that “differences in expression between the different type I IFNs were quantitative” (page 8; lines 229-230, now: 238-239). Moreover, Figures S15/S16 (now: S16/S17) do not refer to analyses of responses to different type I IFN subtypes.

The authors state (line 311-312) that 'Consistent with our bulk RNAseq data, differences were again quantitative rather than qualitative' at the cell-type level. The response between cell types seems very different to us since a core set of only 10 ISGs are shared by all cell types and all 5 type I IFNs. Knowing that the expression of hundreds, sometimes thousands of genes, are induced by IFN, this seems like a rather small overlap (and thus qualitatively different responses). Fig S15 and S16 nicely illustrate that the responses are qualitatively different between cell-type. Please modify this conclusion accordingly.

Thank you for highlighting this. The statement in lines 311-312 does not refer to differences between cell types but to differences between type I IFN subtypes. We are sorry this was not clear and changed this sentence (now lines 357-358). Furthermore, we have made it clearer in the revised text that qualitative differences were observed between cell types (e.g. lines 329 and 350-352).

*No additional experiments are needed to support the claims. However, we believe that two additional analyses could provide useful information. *

• *

The levels of IFNAR1 and IFNAR2 expressed at the plasma membrane probably vary between cell types and may thus influence the magnitude of the IFN response. While it would be difficult to measure these levels by flow cytometric analysis on the different cell types, could the authors extract information from their scRNAseq analysis on the expression level of IFNAR1/2 in all cell types? This would give a hint about potential differences in expression (and thus in magnitude).

We analysed IFNAR1/2 transcript levels in our scRNAseq dataset (Figure R1 below). Unfortunately, for many cells, IFNAR1 and IFNAR2 transcripts were not detected (see width of violin plots at zero), probably due to low sequencing depth inherent to scRNAseq analysis. We therefore prefer not to draw conclusions from these data.

Could the authors investigate further the expression of lncRNAs at the single-cell levels? It would be useful to also define a core set of lncRNAs that are shared between cell types and IFN subtypes. If such a core set does not exist (since lncRNAs are less conserved than coding genes), it would be nice to mention it.

Thank you for this suggestion. The expression of lncRNAs is generally lower than protein-coding genes, resulting in high drop-out rates in 10X datasets. Indeed, Zhao et al. comment that “current development of single-cell technologies may not yet be optimized for lncRNA detection and quantification” [7]. We only detected a small number of lncRNAs in our scRNAseq analysis, and only four lncRNAs were significantly differentially expressed between cell types. We thus could not perform a meaningful analysis of lncRNAs in our scRNAseq dataset. This is now mentioned in the limitations paragraph at the end of the manuscript.

Minor comments:

There is a typo in line 355 Fig.4C =>6C.

Thank you for spotting this.

***Referees cross-commenting** *

We agree with Reviewer 1 that the low sequencing depth of scRNAseq restricts the analysis and must be discussed in the 'limitation' paragraph. This would explain why the authors identified only 10 ISGs that are common to all cell types and all 5 IFN subtypes. Of note, as a comparison, Shaw et al (10.1371/journal.pbio.2004086) identified a core set of 90 ISGs that are upregulated upon IFN treatment in cells isolated mainly from kidney and skin of nine mammalian species ("core mammalian ISGs"). It is thus expected that stimulated blood cells isolated from a single mammalian species share more than 10 ISGs.

We amended the limitations section as requested. Shaw et al. [8] used a single type I IFN (universal or IFNα, depending on species) at a very high dose (1000 U/ml). Taken together with the use of bulk RNAseq in this study, it is unsurprising that our work identified fewer core ISGs. We believe our small list of core ISGs is nonetheless both a high confidence and a high utility set of ISGs: these genes are induced by multiple type I IFNs, in all major cell types in blood and their regulation can be measured even when sequencing depth is low.

Significance (Required)

*Multiple single-cell RNAseq analysis of PBMCs, stimulated or not, have been previously performed in multiple contexts (for instance with PBMCs isolated from the blood of patients infected with influenza virus or SARS-CoV-2). The technical advance is thus limited. *

• *

*However, the work represents a conceptual advance for the field since it provides the first single-cell atlas of PBMCs stimulated with five type-I IFN subtypes. The generated datasets represent a great resource for anyone interested in innate immunity (virologists, immunologists and cancerologists). *

• *

Of note, we are studying innate immunity in the context of RNA virus infection but we have no expertise on scRNA sequencing. We may thus have missed a flaw in the analyses.

We thank the reviewer for their positive assessment of the advances of our study and the value of our IFN resource.

A

B

C

D

Figure R1. IFNAR1/2 expression in scRNAseq data.

Violin plots showing expression of IFNAR1 (A,C) or IFNAR2 (B,D) in different cell types. In (A,B), data were pooled across conditions. In (C,D), data are shown separately for unstimulated control cells and cells stimulated with different type I IFNs.

References

Kaur G, Perteghella T, Carbonell-Sala S, Gonzalez-Martinez J, Hunt T, Madry T, et al. GENCODE: massively expanding the lncRNA catalog through capture long-read RNA sequencing. bioRxiv. 2024. Epub 20241031. doi: 10.1101/2024.10.29.620654. PubMed PMID: 39554180; PubMed Central PMCID: PMCPMC11565817. Mostafavi S, Yoshida H, Moodley D, LeBoite H, Rothamel K, Raj T, et al. Parsing the Interferon Transcriptional Network and Its Disease Associations. Cell. 2016;164(3):564-78. Epub 2016/01/30. doi: 10.1016/j.cell.2015.12.032. PubMed PMID: 26824662; PubMed Central PMCID: PMCPMC4743492. Bailey TL. STREME: accurate and versatile sequence motif discovery. Bioinformatics. 2021;37(18):2834-40. doi: 10.1093/bioinformatics/btab203. PubMed PMID: 33760053; PubMed Central PMCID: PMCPMC8479671. Rauluseviciute I, Riudavets-Puig R, Blanc-Mathieu R, Castro-Mondragon JA, Ferenc K, Kumar V, et al. JASPAR 2024: 20th anniversary of the open-access database of transcription factor binding profiles. Nucleic acids research. 2024;52(D1):D174-D82. doi: 10.1093/nar/gkad1059. PubMed PMID: 37962376; PubMed Central PMCID: PMCPMC10767809. Zhao T, Zhang J, Lei H, Meng Y, Cheng H, Zhao Y, et al. NRF1-mediated mitochondrial biogenesis antagonizes innate antiviral immunity. The EMBO journal. 2023;42(16):e113258. Epub 20230706. doi: 10.15252/embj.2022113258. PubMed PMID: 37409632; PubMed Central PMCID: PMCPMC10425878. Grimm D, Staeheli P, Hufbauer M, Koerner I, Martinez-Sobrido L, Solorzano A, et al. Replication fitness determines high virulence of influenza A virus in mice carrying functional Mx1 resistance gene. Proceedings of the National Academy of Sciences of the United States of America. 2007;104(16):6806-11. Epub 20070410. doi: 10.1073/pnas.0701849104. PubMed PMID: 17426143; PubMed Central PMCID: PMCPMC1871866. Zhao X, Lan Y, Chen D. Exploring long non-coding RNA networks from single cell omics data. Comput Struct Biotechnol J. 2022;20:4381-9. Epub 20220804. doi: 10.1016/j.csbj.2022.08.003. PubMed PMID: 36051880; PubMed Central PMCID: PMCPMC9403499. Shaw AE, Hughes J, Gu Q, Behdenna A, Singer JB, Dennis T, et al. Fundamental properties of the mammalian innate immune system revealed by multispecies comparison of type I interferon responses. PLoS Biol. 2017;15(12):e2004086. Epub 2017/12/19. doi: 10.1371/journal.pbio.2004086. PubMed PMID: 29253856.

Author response:

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

Reviewer #1 (Public Review):

Summary:

This manuscript provides an initial characterization of three new missense variants of the PLCG1 gene associated with diverse disease phenotypes, utilizing a Drosophila model to investigate their molecular effects in vivo. Through the meticulous creation of genetic tools, the study assesses the small wing (sl) phenotype - the fly's ortholog of PLCG1 - across an array of phenotypes from longevity to behavior in both sl null mutants and variants. The findings indicate that the Drosophila PLCG1 ortholog displays aberrant functions. Notably, it is demonstrated that overexpression of both human and Drosophila PLCG1 variants in fly tissue leads to toxicity, underscoring their pathogenic potential in vivo.

Strengths:

The research effectively highlights the physiological significance of sl in Drosophila. In addition, the study establishes the in vivo toxicity of disease-associated variants of both human PLCG1 and Drosophila sl.

Weaknesses:

The study's limitations include the human PLCG1 transgene's inability to compensate for the Drosophila sl null mutant phenotype, suggesting potential functional divergence between the species. This discrepancy signals the need for additional exploration into the mechanistic nuances of PLCG1 variant pathogenesis, especially regarding their gain-of-function effects in vivo.

Overall:

The study offers compelling evidence for the pathogenicity of newly discovered disease-related PLCG1 variants, manifesting as toxicity in a Drosophila in vivo model, which substantiates the main claim by the authors. Nevertheless, a deeper inquiry into the specific in vivo mechanisms driving the toxicity caused by these variants in Drosophila could significantly enhance the study's impact.

Reviewer #2 (Public Review):

The manuscript by Ma et al. reports the identification of three unrelated people who are heterozygous for de novo missense variants in PLCG1, which encodes phospholipase C-gamma 1, a key signaling protein. These individuals present with partially overlapping phenotypes including hearing loss, ocular pathology, cardiac defects, abnormal brain imaging results, and immune defects. None of the patients present with all of the above phenotypes. PLCG1 has also been implicated as a possible driver for cell proliferation in cancer.

The three missense variants found in the patients result in the following amino acid substitutions: His380Arg, Asp1019Gly, and Asp1165Gly. PLCG1 (and the closely related PLCG2) have a single Drosophila ortholog called small wing (sl). sl-null flies are viable but have small wings with ectopic wing veins and supernumerary photoreceptors in the eye. As all three amino acids affected in the patients are conserved in the fly protein, in this work Ma et al. tested whether they are pathogenic by expressing either reference or patient variant fly or human genes in Drosophila and determining the phenotypes produced by doing so.

Expression in Drosophila of the variant forms of PLCG1 found in these three patients is toxic; highly so for Asp1019Gly and Asp1165Gly, much more modestly for His380Arg. Another variant, Asp1165His which was identified in lymphoma samples and shown by others to be hyperactive, was also found to be toxic in the Drosophila assays. However, a final variant, Ser1021Phe, identified by others in an individual with severe immune dysregulation, produced no phenotype upon expression in flies.

Based on these results, the authors conclude that the PLCG1 variants found in patients are pathogenic, producing gain-of-function phenotypes through hyperactivity. In my view, the data supporting this conclusion are robust, despite the lack of a detectable phenotype with Ser1021Phe, and I have no concerns about the core experiments that comprise the paper.

Figure 6, the last in the paper, provides information about PLCG1 structure and how the different variants would affect it. It shows that the His380, Asp1019, and Asp1165 all lie within catalytic domains or intramolecular interfaces and that variants in the latter two affect residues essential for autoinhibition. It also shows that Ser1021 falls outside the key interface occupied by Asp1019, but more could have been said about the potential effects of Ser1021Phe.

Overall, I believe the authors fully achieved the aims of their study. The work will have a substantial impact because it reports the identification of novel disease-linked genes, and because it further demonstrates the high value of the Drosophila model for finding and understanding gene-disease linkages.

Reviewer #3 (Public Review):

Summary:

The paper attempts to model the functional significance of variants of PLCG2 in a set of patients with variable clinical manifestations.

Strengths:

A study attempting to use the Drosophila system to test the function of variants reported from human patients.

Weaknesses:

Additional experiments are needed to shore up the claims in the paper. These are listed below.

Major Comments:

(1) Does the pLI/ missense constraint Z score prediction algorithm take into consideration whether the gene exhibits monoallelic or biallelic expression?

To our knowledge, pLI and missense Z don't consider monoallelic or biallelic expression. Instead, they reflect sequence constraint and are calculated based on the observed versus expected variant frequencies in population databases.

(2) Figure 1B: Include human PLCG2 in the alignment that displays the species-wide conserved variant residues.

We have updated Figure 1B and incorporated the alignment of PLCG2.

(3) Figure 4A:

Given that

(i) sl is predicted to be the fly ortholog for both mammalian PLCγ isozymes: PLCG1 and PLCG2 [Line 62]

(ii) they are shown to have non-redundant roles in mammals [Line 71]

(iii) reconstituting PLCG1 is highly toxic in flies, leading to increased lethality.

This raises questions about whether sl mutant phenotypes are specifically caused by the absence of PLCG1 or PLCG2 functions in flies. Can hPLCG2 reconstitution in sl mutants be used as a negative control to rule out the possibility of the same?

The studies about the non-redundant roles of PLCG1 and PLCG2 mainly concern the immune system.

We have assessed the phenotypes in the sl^T2A/Y; UAS-hPLCG2 flies. Expression of human PLCG2 in flies is also toxic and leads to severely reduced eclosion rate.

We have updated the manuscript with these results, and included the eclosion rate of sl^T2A/Y; UAS-hPLCG2 flies in the new Figure 4B.

(4) Do slT2A/Y; UAS-PLCG1Reference flies survive when grown at 22{degree sign}C? Since transgenic fly expressing PLCG1 cDNA when driven under ubiquitous gal4s, Tubulin and Da, can result in viable progeny at 22{degree sign}C, the survival of slT2A/Y; UAS-PLCG1Reference should be possible.

The eclosion rate of sl^T2A/Y >PLCG1^Reference flies at 22°C is slightly higher than at 25°C, but remains severely reduced compared to the UAS-Empty control. We have presented these results in the updated Figure S3.

and similarly

Does slT2A flies exhibit the phenotypes of (i) reduced eclosion rate (ii) reduced wing size and ectopic wing veins and (iii) extra R7 photoreceptor in the fly eye at 22{degree sign}C?

The mutant phenotypes are still observed at 22 °C.

If so, will it be possible to get a complete rescue of the slT2A mutant phenotypes with the hPLCG1 cDNA at 22{degree sign}C? This dataset is essential to establish Drosophila as an ideal model to study the PLCG1 de novo variants.

Thank you for the suggestion. It is difficult to directly assess the rescue ability of the PLCG1 cDNAs due to the toxicity. However, our ectopic expression assays show that the variants are more toxic than the reference with variable severities, suggesting that the variants are deleterious.

The ectopic expression strategy has been used to evaluate the consequence of genetic variants and has significantly contributed to the interpretation of their pathogenicity in many cases (reviewed in Her et al., Genome, 2024, PMID: 38412472).

(5) Localisation and western blot assays to check if the introduction of the de novo mutations can have an impact on the sub-cellular targeting of the protein or protein stability respectively.

Thank you for the suggestion.

We expressed PLCG1 cDNAs in the larval salivary glands and performed antibody staining (rabbit anti-Human PLCG1; 1:100, Cell Signaling Technology, #5690). The larval salivary gland are composed of large columnar epithelia cells that are ideal for analyzing subcellular localization of proteins. The PLCG1 proteins are cytoplasmic and localize near the cell surface, with some enrichment in the plasma membrane region. The variant proteins are detected, and did not show significant difference in expression level or subcellular distribution compared to the reference. We did not include this data.

(6) Analysing the nature of the reported gain of function (experimental proof for the same is missing in the manuscript) variants:

Instead of directly showing the effect of introducing the de novo variant transgenes in the Drosophila model especially when the full-length PLCG1 is not able to completely rescue the slT2A phenotype;

(i) Show that the gain-of-function variants can have an impact on the protein function or signalling via one of the three signalling outputs in the mammalian cell culture system: (i) inositol-1,4,5-trisphosphate production, (ii) intracellular Ca2+ release or (iii) increased phosphorylation of extracellular signal-related kinase, p65, and p38.

We appreciate the reviewer’s suggestion. We utilized the CaLexA (calcium-dependent nuclear import of LexA) system (Masuyama et al., J Neurogenet, 2012, PMID: 22236090) to assess the intracellular Ca²⁺ change associated with the expression of PLCG1 cDNAs in fly wing discs. The results show that, compared to the reference, expression of the D1019G or D1165G variants leads to elevated intracellular Ca²⁺ levels, similar to the hyperactive S1021F and D1165H variants. However, the H380R or L597F variants did not show a detectable phenotype in this assay. These results suggest that D1019G and D1165G are hyperactive variants, whereas H380R and L597F variant are not, or their effect is too mild to be detected in this assay. We have updated the related sections in the manuscript and Figures 5A and S5.

OR

(ii) Run a molecular simulation to demonstrate how the protein's auto-inhibited state can be disrupted and basal lipase activity increased by introducing D1019G and D1165G, which destabilise the association between the C2 and cSH2 domains. The H380R variant may also exhibit characteristics similar to the previously documented H335A mutation which leaves the protein catalytically inactive as the residue is important to coordinate the incoming water molecule required for PIP2 hydrolysis.

We utilized the DDMut platform, which predicts changes in the Gibbs Free Energy (ΔΔG) upon single and multiple point mutations (Zhou et al., Nucleic Acid Res, 2023, PMID: 37283042), to gain insight into the molecular dynamics changes of variants. The results are now presented in Figure S7.

Additionally, we performed Molecular dynamics (MD) simulations. The results show that, similar to the hyperactive D1165H variant, the D1019G and D11656G variants exhibit increased disorganization, with a higher root mean square deviations (RMSD) compared to the reference PLCG1.The data are also presented in the updated Figure S7.

(7) Clarify the reason for carrying out the wing-specific and eye-specific experiments using nub-gal4 and eyless-gal4 at 29˚C despite the high gal4 toxicity at this temperature.

We used high temperature and high expression level to see if the mild H380R and L597F variants could show phenotypes in this condition.

The toxicity of the two strong variants (D1019G and D1165G) has been consistently confirmed in multiple assays at different temperatures.

(8) For the sake of completeness the authors should also report other variants identified in the genomes of these patients that could also contribute to the clinical features.

Thank you!

The additional variants and their potential contributions to the clinical features are listed and discussed in Table 1 and its legend.

Reviewer #1 (Recommendations For The Authors):

The manuscript's significant contribution is tempered by a lack of comprehensive analysis using the generated genetic reagents in Drosophila. To enhance our understanding of the PLCG1 orthologs, I suggest the following:

(1) A more detailed molecular analysis to distinguish the actions of sl variants from the wild-type could be very informative. For example, utilizing the HA-epitope tag within the current UAS-transgenes could reveal more about the cellular dynamics and abundance of these variants, potentially elucidating mechanisms beyond gain-of-function.

We appreciate the reviewer’s suggestion. The UAS-sl cDNA constructs contain stop codon and do not express an HA-epitope tag. Alternatively, we utilized commercially available antibodies against human PLCG1 antibodies to assess the subcellular localization and protein stability by expressing the reference and variant PLCG1 cDNAs in Drosophila larval salivary glands. The reference proteins are cytoplasmic with some enrichment along the plasma membrane. However, we did not observe significant differences between the reference and variant proteins in this assay. We did not include this data.

(2) I suggest further investigating the relative contributions of developmental processes and acute (Adult) effects on the sl-variant phenotypes observed. For example, employing systems that allow for precise temporal control of gene expression, such as the temperature-sensitive Gal80, could differentiate between these effects, shedding light on the mechanisms that affect longevity and locomotion. This knowledge would be vital for a deeper understanding of the corresponding human disorders and for developing therapeutic interventions.

We appreciate the reviewer’s suggestion. We utilized Tub-GAL4, Tub-GAL80^ts to drive the expression of sl wild-type or variant cDNAs, and performed temperature shifts after eclosion to induce expression of the cDNAs only in adult flies. The sl^D1184G variant (corresponding to PLCG1^D1165G) caused severely reduced lifespan and the flies mostly die within 10 days. The sl^D1041G variant (corresponding to PLCG1^D1019G) led to reduced longevity and locomotion. The sl^H384R variant (corresponding to PLCG1^H380R) showed only a mild effect on longevity and no significant effect on climbing ability. These results suggest that the two strong variants (sl<sup>D1041G<sup> and sl^D1184G) contribute to both developmental and acute effects while the H384R variant mainly contributes to developmental stages.

I also suggest a more refined analysis of overexpression toxicity. Rather than solely focusing on ubiquitous transgene expression, overexpressing transgene in endogenous pattern using sl-t2a-Gal4 may yield a more nuanced understanding of the pathogenic mechanisms of gain-of-function mutations, particularly in the pathogenesis associated with these variants exclusively located in the coding regions.

We appreciate the reviewer’s suggestion. We therefore performed the experiments using sl^T2A to drive overexpression ofPLCG1cDNAs in heterozygous female progeny with one copy of wild-type sl+ (sl^T2A/ yw > UAS-cDNAs). In this context, expression of PLCG1<sup>Reference<sup>, PLCG1^H380RorPLCG1^L597F is viable whereas expression of PLCG1^D1019G or PLCG1^D1165G is lethal, suggesting that the PLCG1^D1019G and PLCG1^D1165G variants exert a strong dominant toxic effect while the PLCG1^H380Rand PLCG1<sup>L597F<sup> are comparatively milder. Similar patterns have been consistently observed in other ectopic expression assays with varying degrees of severity. These results are updated in the manuscript and figures.

Reviewer #2 (Recommendations For The Authors):

The work in the paper could be usefully extended by determining the effects of expressing His380Phe and His380Ala in flies. These variants suppress PLCG1 activity, so their phenotype, if any, would be predicted not to be the same as His380Arg. Determining this would add further strength to the conclusions of the paper.

We thank the reviewer for the constructive suggestions! We have tested the enzymatic-dead H380A variant, which still exhibits toxicity when expressed in sl^T2A/Y hemizygous flies, but it is not toxic in heterozygous females suggesting that the reduced eclosion rate is likely not directly associated with enzymatic activity. We have updated the manuscript and figures accordingly.

Author response:

Reviewer #1 (Public review):

Summary:

Chao et al. produced an updated version of the SpliceAI package using modern deep learning frameworks. This includes data preprocessing, model training, direct prediction, and variant effect prediction scripts. They also added functionality for model fine-tuning and model calibration. They convincingly evaluate their newly trained models against those from the original SpliceAI package and investigate how to extend SpliceAI to make predictions in new species. While their comparisons to the original SpliceAI models are convincing on the grounds of model performance, their evaluation of how well the new models match the original's understanding of non-local mutation effects is incomplete. Further, their evaluation of the new calibration functionality would benefit from a more nuanced discussion of what set of splice sites their calibration is expected to hold for, and tests in a context for which calibration is needed.

Strengths:

(1) They provide convincing evidence that their new implementation of SpliceAI matches the performance of the original model on a similar dataset while benefiting from improved computational efficiencies. This will enable faster prediction and retraining of splicing models for new species as well as easier integration with other modern deep learning tools.

(2) They produce models with strong performance on non-human model species and a simple, well-documented pipeline for producing models tuned for any species of interest. This will be a boon for researchers working on splicing in these species and make it easy for researchers working on new species to generate their own models.

(3) Their documentation is clear and abundant. This will greatly aid the ability of others to work with their code base.

We thank the reviewer for these positive comments.  

Weaknesses:

(1) The authors' assessment of how much their model retains SpliceAI's understanding of "nonlocal effects of genomic mutations on splice site location and strength" (Figure 6) is not sufficiently supported. Demonstrating this would require showing that for a large number of (non-local) mutations, their model shows the same change in predictions as SpliceAI or that attribution maps for their model and SpliceAI are concordant even at distances from the splice site. Figure 6A comes close to demonstrating this, but only provides anecdotal evidence as it is limited to 2 loci. This could be overcome by summarizing the concordance between ISM maps for the two models and then comparing across many loci. Figure 6B also comes close, but falls short because instead of comparing splicing prediction differences between the models as a function of variants, it compares the average prediction difference as a function of the distance from the splice site. This limits it to only detecting differences in the model's understanding of the local splice site motif sequences. This could be overcome by looking at comparisons between differences in predictions with mutants directly and considering non-local mutants that cause differences in splicing predictions.

We agree that two loci are insufficient to demonstrate preservation of non-local effects. To address this, we have extended our analysis to a larger set of sites: we randomly sampled 100 donor and 100 acceptor sites, applied our ISM procedure over a 5,001 nt window centered at each site for both models, and computed the ISM map as before. We then calculated the Pearson correlation between the collection of OSAI_MANE and SpliceAI ISM importance scores. We also created 10 additional ISM maps similar to those in Figure 6A, which are now provided in Figure S23.

Follow is the revised paragraph in the manuscript’s Results section:

First, we recreated the experiment from Jaganathan et al. in which they mutated every base in a window around exon 9 of the U2SURP gene and calculated its impact on the predicted probability of the acceptor site. We repeated this experiment on exon 2 of the DST gene, again using both SpliceAI and OSAI_MANE . In both cases, we found a strong similarity between the resultant patterns between SpliceAI and OSAI_MANE , as shown in Figure 6A. To evaluate concordance more broadly, we randomly selected 100 donor and 100 acceptor sites and performed the same ISM experiment on each site. The Pearson correlation between SpliceAI and OSAI_MANE yielded an overall median correlation of 0.857 (see Methods; additional DNA logos in Figure S23). 

To characterize the local sequence features that both models focus on, we computed the average decrease in predicted splice-site probability resulting from each of the three possible singlenucleotide substitutions at every position within 80bp for 100 donor and 100 acceptor sites randomly sampled from the test set (Chromosomes 1, 3, 5, 7, and 9). Figure 6B shows the average decrease in splice site strength for each mutation in the format of a DNA logo, for both tools.

We added the following text to the Methods section:

Concordance evaluation of ISM importance scores between OSAI_MANE and SpliceAI

To assess agreement between OSAI_MANE and SpliceAI across a broad set of splice sites, we applied our ISM procedure to 100 randomly chosen donor sites and 100 randomly chosen acceptor sites. For each site, we extracted a 5,001 nt window centered on the annotated splice junction and, at every coordinate within that window, substituted the reference base with each of the three alternative nucleotides. We recorded the change in predicted splice-site probability for each mutation and then averaged these Δ-scores at each position to produce a 5,001-score ISM importance profile per site.

Next, for each splice site we computed the Pearson correlation coefficient between the paired importance profiles from ensembled OSAI_MANE and ensembled SpliceAI. The median correlation was 0.857 for all splice sites. Ten additional zoom-in representative splice site DNA logo comparisons are provided in Supplementary Figure S23.

(2) The utility of the calibration method described is unclear. When thinking about a calibrated model for splicing, the expectation would be that the models' predicted splicing probabilities would match the true probabilities that positions with that level of prediction confidence are splice sites. However, the actual calibration that they perform only considers positions as splice sites if they are splice sites in the longest isoform of the gene included in the MANE annotation. In other words, they calibrate the model such that the model's predicted splicing probabilities match the probability that a position with that level of confidence is a splice site in one particular isoform for each gene, not the probability that it is a splice site more broadly. Their level of calibration on this set of splice sites may very well not hold to broader sets of splice sites, such as sites from all annotated isoforms, sites that are commonly used in cryptic splicing, or poised sites that can be activated by a variant. This is a particularly important point as much of the utility of SpliceAI comes from its ability to issue variant effect predictions, and they have not demonstrated that this calibration holds in the context of variants. This section could be improved by expanding and clarifying the discussion of what set of splice sites they have demonstrated calibration on, what it means to calibrate against this set of splice sites, and how this calibration is expected to hold or not for other interesting sets of splice sites. Alternatively, or in addition, they could demonstrate how well their calibration holds on different sets of splice sites or show the effect of calibrating their models against different potentially interesting sets of splice sites and discuss how the results do or do not differ.

We thank the reviewer for highlighting the need to clarify our calibration procedure. Both SpliceAI and OpenSpliceAI are trained on a single “canonical” transcript per gene: SpliceAI on the hg 19 Ensembl/Gencode canonical set and OpenSpliceAI on the MANE transcript set. To calibrate each model, we applied post-hoc temperature scaling, i.e. a single learnable parameter that rescales the logits before the softmax. This adjustment does not alter the model’s ranking or discrimination (AUC/precision–recall) but simply aligns the predicted probabilities for donor, acceptor, and non-splice classes with their observed frequencies. As shown in our reliability diagrams (Fig. S16-S22), temperature scaling yields negligible changes in performance, confirming that both SpliceAI and OpenSpliceAI were already well-calibrated. However, we acknowledge that we didn’t measure how calibration might affect predictions on non-canonical splice sites or on cryptic splicing. It is possible that calibration might have a detrimental effect on those, but because this is not a key claim of our paper, we decided not to do further experiments. We have updated the manuscript to acknowledge this potential shortcoming; please see the revised paragraph in our next response.

(3) It is difficult to assess how well their calibration method works in general because their original models are already well calibrated, so their calibration method finds temperatures very close to 1 and only produces very small and hard to assess changes in calibration metrics. This makes it very hard to distinguish if the calibration method works, as it doesn't really produce any changes. It would be helpful to demonstrate the calibration method on a model that requires calibration or on a dataset for which the current model is not well calibrated, so that the impact of the calibration method could be observed.

It’s true that the models we calibrated didn’t need many changes. It is possible that the calibration methods we used (which were not ours, but which were described in earlier publications) can’t improve the models much. We toned down our comments about this procedure, as follows.

Original:

“Collectively, these results demonstrate that OSAIs were already well-calibrated, and this consistency across species underscores the robustness of OpenSpliceAI’s training approach in diverse genomic contexts.” Revised:

“We observed very small changes after calibration across phylogenetically diverse species, suggesting that OpenSpliceAI’s training regimen yielded well‐calibrated models, although it is possible that a different calibration algorithm might produce further improvements in performance.”

Reviewer #2 (Public review):

Summary:

The paper by Chao et al offers a reimplementation of the SpliceAI algorithm in PyTorch so that the model can more easily/efficiently be retrained. They apply their new implementation of the SpliceAI algorithm, which they call OpenSpliceAI, to several species and compare it against the original model, showing that the results are very similar and that in some small species, pretraining on other species helps improve performance.

Strengths:

On the upside, the code runs fine, and it is well documented.

Weaknesses:

The paper itself does not offer much beyond reimplementing SpliceAI. There is no new algorithm, new analysis, new data, or new insights into RNA splicing. There is no comparison to many of the alternative methods that have since been published to surpass SpliceAI. Given that some of the authors are well-known with a long history of important contributions, our expectations were admittedly different. Still, we hope some readers will find the new implementation useful.

We thank the reviewer for the feedback. We have clarified that OpenSpliceAI is an open-source PyTorch reimplementation optimized for efficient retraining and transfer learning, designed to analyze cross-species performance gains, and supported by a thorough benchmark and the release of several pretrained models to clearly position our contribution.

Reviewer #3 (Public review):

Summary:

The authors present OpenSpliceAI, a PyTorch-based reimplementation of the well-known SpliceAI deep learning model for splicing prediction. The core architecture remains unchanged, but the reimplementation demonstrates convincing improvements in usability, runtime performance, and potential for cross-species application.

Strengths:

The improvements are well-supported by comparative benchmarks, and the work is valuable given its strong potential to broaden the adoption of splicing prediction tools across computational and experimental biology communities.

Major comments:

Can fine-tuning also be used to improve prediction for human splicing? Specifically, are models trained on other species and then fine-tuned with human data able to perform better on human splicing prediction? This would enhance the model's utility for more users, and ideally, such fine-tuned models should be made available.

We evaluated transfer learning by fine-tuning models pretrained on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), Arabidopsis (OSAI_Arabidopsis), and zebrafish (OSAI_Zebrafish) on human data. While transfer learning accelerated convergence compared to training from scratch, the final human splicing prediction accuracy was comparable between fine-tuned and scratch-trained models, suggesting that performance on our current human dataset is nearing saturation under this architecture.

We added the following paragraph to the Discussion section:

We also evaluated pretraining on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), zebrafish (OSAI_Zebrafish), and Arabidopsis (OSAI_Arabidopsis) followed by fine-tuning on the human MANE dataset. While cross-species pretraining substantially accelerated convergence during fine-tuning, the final human splicing-prediction accuracy was comparable to that of a model trained from scratch on human data. This result indicates that our architecture seems to capture all relevant splicing features from human training data alone, and thus gains little or no benefit from crossspecies transfer learning in this context (see Figure S24).

Reviewer #1 (Recommendations for the authors):

We thank the editor for summarizing the points raised by each reviewer. Below is our point-bypoint response to each comment:

(1) In Figure 3 (and generally in the other figures) OpenSpliceAI should be replaced with OSAI_{Training dataset} because otherwise it is hard to tell which precise model is being compared. And in Figure 3 it is especially important to emphasize that you are comparing a SpliceAI model trained on Human data to an OSAI model trained and evaluated on a different species.

We have updated the labels in Figures 3, replacing “OpenSpliceAI” with “OSAI_{training dataset}” to more clearly specify which model is being compared.

(2) Are genes paralogous to training set genes removed from the validation set as well as the test set? If you are worried about data leakage in the test set, it makes sense to also consider validation set leakage.

Thank you for this helpful suggestion. We fully agree, and to avoid any data leakage we implemented the identical filtering pipeline for both validation and test sets: we excluded all sequences paralogous or homologous to sequences in the training set, and further removed any sequence sharing > 80 % length overlap and > 80 % sequence identity with training sequences. The effect of this filtering on the validation set is summarized in Supplementary Figure S7C.

Figure S7. (C) Scatter plots of DNA sequence alignments between validation and training sets for Human-MANE, mouse, honeybee, zebrafish, and Arabidopsis. Each dot represents an alignment, with the x-axis showing alignment identity and the y-axis showing alignment coverage. Alignments exceeding 80% for both identity and coverage are highlighted in the redshaded region and were excluded from the test sets.

Reviewer #3 (Recommendations for the authors):

(1) The legend in Figure 3 is somewhat confusing. The labels like "SpliceAI-Keras (species name)" may imply that the model was retrained using data from that species, but that's not the case, correct?

Yes, “SpliceAI-Keras (species name)” was not retrained; it refers to the released SpliceAI model evaluated on the specified species dataset. We have revised the Figure 3 legends, changing “SpliceAI-Keras (species name)” to “SpliceAI-Keras” to clarify this.

(2) Please address the minor issues with the code, including ensuring the conda install works across various systems.

We have addressed the issues you mentioned. OpenSpliceAI is now available on Conda and can be installed with:  conda install openspliceai. 

The conda package homepage is at: https://anaconda.org/khchao/openspliceai We’ve also corrected all broken links in the documentation.

(3) Utility:

I followed all the steps in the Quick Start Guide, and aside from the issues mentioned below, everything worked as expected.

I attempted installation using conda as described in the instructions, but it was unsuccessful. I assume this method is not yet supported.

In Quick Start Guide: predict, the link labeled "GitHub (models/spliceai-mane/10000nt/)" appears to be incorrect. The correct path is likely "GitHub (models/openspliceaimane/10000nt/)".

In Quick Start Guide: variant (https://ccb.jhu.edu/openspliceai/content/quick_start_guide/quickstart_variant.html#quick-startvariant), some of the download links for input files were broken. While I was able to find some files in the GitHub repository, I think the -A option should point to data/grch37.txt, not examples/data/input.vcf, and the -I option should be examples/data/input.vcf, not data/vcf/input.vcf.

Thank you for catching these issues. We’ve now addressed all issues concerning Conda installation and file links. We thank the editor for thoroughly testing our code and reviewing the documentation.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This fundamental work employed multidisciplinary approaches and conducted rigorous experiments to study how a specific subset of neurons in the dorsal striatum (i.e., "patchy" striatal neurons) modulates locomotion speed depending on the valence of the naturalistic context.

Strengths:

The scientific findings are novel and original and significantly advance our understanding of how the striatal circuit regulates spontaneous movement in various contexts.

We appreciate the reviewer’s positive evaluation.

Weaknesses:

This is extensive research involving various circuit manipulation approaches. Some of these circuit manipulations are not physiological. A balanced discussion of the technical strengths and limitations of the present work would be helpful and beneficial to the field. Minor issues in data presentation were also noted.

We have incorporated the recommended discussion of technical limitations and addressed the physiological plausibility of our manipulations on Page 33 of the revised Discussion section. Specifically, we wrote:

“Judicious interpretation of the present data must consider the technical limitations of the various methods and circuit-level manipulations applied. Patchy neurons are distributed unevenly across the extensive structure of the striatum, and their targeted manipulation is constrained by viral spread in the dorsal striatum. Somatic calcium imaging using single-photon microscopy captures activity from only a subset of patchy neurons within a narrow focal plane beneath each implanted GRIN lens. Similarly, limitations in light diffusion from optical fibers may reduce the effective population of targeted fibers in both photometry and optogenetic experiments. For example, the more modest locomotor slowing observed with optogenetic activation of striatonigral fibers in the SNr compared to the stronger effects seen with Gq-DREADD activation across the dorsal striatum could reflect limited fiber optic coverage in the SNr. Alternatively, it may suggest that non-striatonigral mechanisms also contribute to generalized slowing. Our photometry data does not support a role for striatopallidal projections from patchy neurons in movement suppression. The potential contribution of intrastriatal mechanisms, discussed earlier, remains to be empirically tested. Although the behavioral assays used were naturalistic, many of the circuit-level interventions were not. Broad ablation or widespread activation of patchy neurons and their efferent projections represent non-physiological manipulations. Nonetheless, these perturbation results are interpreted alongside more naturalistic observations, such as in vivo imaging of patchy neuron somata and axon terminals, to form a coherent understanding of their functional role”.

Reviewer #2 (Public review):

Hawes et al. investigated the role of striatal neurons in the patch compartment of the dorsal striatum. Using Sepw1-Cre line, the authors combined a modified version of the light/dark transition box test that allows them to examine locomotor activity in different environmental valence with a variety of approaches, including cell-type-specific ablation, miniscope calcium imaging, fiber photometry, and opto-/chemogenetics. First, they found ablation of patchy striatal neurons resulted in an increase in movement vigor when mice stayed in a safe area or when they moved back from more anxiogenic to safe environments. The following miniscope imaging experiment revealed that a larger fraction of striatal patchy neurons was negatively correlated with movement speed, particularly in an anxiogenic area. Next, the authors investigated differential activity patterns of patchy neurons' axon terminals, focusing on those in GPe, GPi, and SNr, showing that the patchy axons in SNr reflect movement speed/vigor. Chemogenetic and optogenetic activation of these patchy striatal neurons suppressed the locomotor vigor, thus demonstrating their causal role in the modulation of locomotor vigor when exposed to valence differentials. Unlike the activation of striatal patches, such a suppressive effect on locomotion was absent when optogenetically activating matrix neurons by using the Calb1-Cre line, indicating distinctive roles in the control of locomotor vigor by striatal patch and matrix neurons. Together, they have concluded that nigrostriatal neurons within striatal patches negatively regulate movement vigor, dependent on behavioral contexts where motivational valence differs.

We are grateful for the reviewer’s thorough summary of our main findings.

In my view, this study will add to the important literature by demonstrating how patch (striosomal) neurons in the striatum control movement vigor. This study has applied multiple approaches to investigate their functionality in locomotor behavior, and the obtained data largely support their conclusions. Nevertheless, I have some suggestions for improvements in the manuscript and figures regarding their data interpretation, accuracy, and efficacy of data presentation.

We appreciate the reviewer’s overall positive assessment and have made substantial improvements to the revised manuscript in response to reviewers’ constructive suggestions. 

(1) The authors found that the activation of the striatonigral pathway in the patch compartment suppresses locomotor speed, which contradicts with canonical roles of the direct pathway. It would be great if the authors could provide mechanistic explanations in the Discussion section. One possibility is that striatal D1R patch neurons directly inhibit dopaminergic cells that regulate movement vigor (Nadal et al., Sci. Rep., 2021; Okunomiya et al., J Neurosci., 2025). Providing plausible explanations will help readers infer possible physiological processes and give them ideas for future follow-up studies.

We have added the recommended data interpretation and future perspectives on Page 30 of the revised Discussion section. Specifically, we wrote:

“Potential mechanisms by which striatal patchy neurons reduce locomotion involve the suppression of dopamine availability within the striatum. Dopamine, primarily supplied by neurons in the SNc and VTA, broadly facilitates locomotion (Gerfen and Surmeier 2011, Dudman and Krakauer 2016). Recent studies have shown that direct activation of patchy neurons leads to a reduction in striatal dopamine levels, accompanied by decreased walking speed (Nadel, Pawelko et al. 2021, Dong, Wang et al. 2025, Okunomiya, Watanabe et al. 2025). Patchy neuron projections terminate in structures known as “dendron bouquets”, which enwrap SNc dendrites within the SNr and can pause tonic dopamine neuron firing (Crittenden, Tillberg et al. 2016, Evans, Twedell et al. 2020). The present work highlights a role for patchy striatonigral inputs within the SN in decelerating movement, potentially through GABAergic dendron bouquets that limit dopamine release back to the striatum (Dong, Wang et al. 2025). Additionally, intrastriatal collaterals of patch spiny projection neurons (SPNs) have been shown to suppress dopamine release and associated synaptic plasticity via dynorphin-mediated activation of kappa opioid receptors on dopamine terminals (Hawes, Salinas et al. 2017). This intrastriatal mechanism may further contribute to the reduction in striatal dopamine levels and the observed decrease in locomotor speed, representing a compelling avenue for future investigation.”

(2) On page 14, Line 301, the authors stated that "Cre-dependent mCheery signals were colocalized with the patch marker (MOR1) in the dorsal striatum (Fig. 1B)". But I could not find any mCherry on that panel, so please modify it.

We have included representative images of mCherry and MOR1 staining in Supplementary Fig. S1 of the revised manuscript.

(3) From data shown in Figure 1, I've got the impression that mice ablated with striatal patch neurons were generally hyperactive, but this is probably not the case, as two separate experiments using LLbox and DDbox showed no difference in locomotor vigor between control and ablated mice. For the sake of better interpretation, it may be good to add a statement in Lines 365-366 that these experiments suggest the absence of hyperactive locomotion in general by ablating these specific neurons.

As suggested by the reviewer, we have added the following statement on Page 17 of the revised manuscript: “These data also indicate that PA elevates valence-specific speed without inducing general hyperactivity”.

(4) In Line 536, where Figure 5A was cited, the author mentioned that they used inhibitory DREADDs (AAV-DIO-hM4Di-mCherrry), but I could not find associated data on Figure 5. Please cite Figure S3, accordingly.

We have added the citation for the now Fig. S4 on Page 25 of the revised manuscript.

(5) Personally, the Figure panel labels of "Hi" and "ii" were confusing at first glance. It would be better to have alternatives.

As suggested by the reviewer, we have now labeled each figure panel with a distinct single alphabetical letter.

(6) There is a typo on Figure 4A: tdTomata → tdTomato

We have made the correction on the figure.

Reviewer #3 (Public review):

Hawes et al. combined behavioral, optical imaging, and activity manipulation techniques to investigate the role of striatal patch SPNs in locomotion regulation. Using Sepw1-Cre transgenic mice, they found that patch SPNs encode locomotion deceleration in a light-dark box procedure through optical imaging techniques. Moreover, genetic ablation of patch SPNs increased locomotion speed, while chemogenetic activation of these neurons decreased it. The authors concluded that a subtype of patch striatonigral neurons modulates locomotion speed based on external environmental cues. Below are some major concerns:

The study concludes that patch striatonigral neurons regulate locomotion speed. However, unless I missed something, very little evidence is presented to support the idea that it is specifically striatonigral neurons, rather than striatopallidal neurons, that mediate these effects. In fact, the optogenetic experiments shown in Fig. 6 suggest otherwise. What about the behavioral effects of optogenetic stimulation of striatonigral versus striatopallidal neuron somas in Sepw1-Cre mice?

Our photometry data implicate striatonigral neurons in locomotor slowing, as evidenced by a negative cross-correlation with acceleration and a negative lag, indicating that their activity reliably precedes—and may therefore contribute to—deceleration. In contrast, photometry results from striatopallidal neurons showed no clear correlation with speed or acceleration.

Figure 6 demonstrates that optogenetic manipulation within the SNr of Sepw1-Cre⁺ striatonigral axons recapitulated context-dependent locomotor changes seen with Gq-DREADD activation of both striatonigral and striatopallidal Sepw1-Cre⁺ cells in the dorsal striatum but failed to produce the broader locomotor speed change observed when targeting all Sepw1-Cre⁺ cells in the dorsal striatum using either ablation or Gq-DREADD activation. The more subtle speed-restrictive phenotype resulting from ChR activation in the SNr could, as the reviewer suggests, implicate striatopallidal neurons in broad locomotor speed regulation. However, our photometry data indicate that this scenario is unlikely, as activity of striatopallidal Sepw1-Cre⁺ fibers is not correlated with locomotor speed. Another plausible explanation is that the optogenetic approach may have affected fewer striatonigral fibers, potentially due to the limited spatial spread of light from the optical fiber within the SNr. Broad locomotor speed change in LDbox might require the recruitment of a larger number of striatonigral fibers than we were able to manipulate with optogenetics. We have added discussion of these technical limitations to the revised manuscript. Additionally, we now discuss the possibility that intrastriatal collaterals may contribute to reduced local dopamine levels by releasing dynorphin, which acts on kappa opioid receptors located on dopamine fibers (Hawes, Salinas et al. 2017), thereby suppressing dopamine release.

The reviewer also suggests an interesting experiment involving optogenetic stimulation of striatonigral versus striatopallidal somata in Sepw1-Cre mice. While we agree that this approach would yield valuable insights, we have thus far been unable to achieve reliable results using retroviral vectors. Moreover, selectively targeting striatopallidal terminals optogenetically remains technically challenging, as striatonigral fibers also traverse the pallidum, and the broad anatomical distribution of the pallidum complicates precise targeting. This proposed work will need to be pursued in a future study, either with improved retrograde viral tools or the development of additional mouse lines that offer more selective access to these neuronal populations as we documented recently (Dong, Wang et al. 2025).

In the abstract, the authors state that patch SPNs control speed without affecting valence. This claim seems to lack sufficient data to support it. Additionally, speed, velocity, and acceleration are very distinct qualities. It is necessary to clarify precisely what patch neurons encode and control in the current study.

We believe the reviewer’s interpretation pertains to a statement in the Introduction rather than the Abstract: “Our findings reveal that patchy SPNs control the speed at which mice navigate the valence differential between high- and low-anxiety zones, without affecting valence perception itself.” Throughout our study, mice consistently preferred the dark zone in the Light/Dark box, indicating intact perception of the valence differential between illuminated areas. While our manipulations altered locomotor speed, they did not affect time spent in the dark zone, supporting the conclusion that valence perception remained unaltered. We appreciate the reviewer’s insight and agree it is an intriguing possibility that locomotor responses could, over time, influence internal states such as anxiety. We addressed this in the Discussion, noting that while dark preference was robust to our manipulations, future studies are warranted to explore the relationship between anxious locomotor vigor and anxiety itself.

We report changes in scalar measures of animal speed across Light/Dark box conditions and under various experimental manipulations. Separately, we show that activity in both patchy neuron somata and striatonigral fibers is negatively correlated with acceleration—indicating a positive correlation with deceleration. Notably, the direction of the cross-correlational lag between striatonigral fiber activity and acceleration suggests that this activity precedes and may causally contribute to mouse deceleration, thereby influencing reductions in speed. To clarify this, we revised a sentence in the Results section: “Moreover, patchy neuron efferent activity at the SNr may causally contribute to deceleration, as indicated by the negative cross-correlational lag, thereby reducing animal speed.”. We also updated the Discussion to read: “Together, these data specifically implicate patchy striatonigral neurons in slowing locomotion by acting within the SNr to drive deceleration.”

One of the major results relies on chemogenetic manipulation (Figure 5). It would be helpful to demonstrate through slice electrophysiology that hM3Dq and hM4Di indeed cause changes in the activity of dorsal striatal SPNs, as intended by the DREADD system. This would support both the positive (Gq) and negative (Gi) findings, where no effects on behavior were observed.

We were unable to perform this experiment; however, hM3Dq has previously been shown to be effective in striatal neurons (Alcacer, Andreoli et al. 2017). The lack of effect observed in Gi-DREADD mice serves as an unintended but valuable control, helping to rule out off-target effects of the DREADD agonist JHU37160 and thereby reinforcing the specificity of hM3Dq-mediated activation in our study. We have now included an important caveat regarding the Gi-DREADD results, acknowledging the possibility that they may not have worked effectively in our target cells: “Potential explanations for the negative results in Gi-DREADD mice include inherently low basal activity among patchy neurons or insufficient expression of GIRK channels in striatal neurons, which may limit the effectiveness of Gi-coupling in suppressing neuronal activity (Shan, Fang et al. 2022).

Finally, could the behavioral effects observed in the current study, resulting from various manipulations of patch SPNs, be due to alterations in nigrostriatal dopamine release within the dorsal striatum?

We agree that this is an important potential implication of our work, especially given that we and others have shown that patchy striatonigral neurons provide strong inhibitory input to dopaminergic neurons involved in locomotor control (Nadel, Pawelko et al. 2021, Lazaridis, Crittenden et al. 2024, Dong, Wang et al. 2025, Okunomiya, Watanabe et al. 2025). Accordingly, we have expanded the discussion section to include potential mechanistic explanations that support and contextualize our main findings.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Here are some minor issues for the authors' reference:

(1) This work supports the motor-suppressing effect of patchy SPNs, and >80% of them are direct pathway SPNs. This conclusion is not expected from the traditional basal ganglia direct/indirect pathway model. Most experiments were performed using nonphysiological approaches to suppress (i.e., ablation) or activate (i.e., continuous chemo-optogenetic stimulation). It remains uncertain if the reported observations are relevant to the normal biological function of patchy SPNs under physiological conditions. Particularly, under what circumstances an imbalanced patch/matrix activity may be induced, as proposed in the sections related to the data presented in Figure 6. A thorough discussion and clarification remain needed. Or it should be discussed as a limitation of the present work.

We have added discussion and clarification of physiological limitations in response to reviewer feedback. Additionally, we revised the opening sentence of an original paragraph in the discussion section to emphasize that it interprets our findings in the context of more physiological studies reporting natural shifts in patchy SPN activity due to cognitive conflict, stress, or training. The revised opening sentence now reads: “Together with previous studies of naturally occurring shifts in patchy neuron activation, these data illustrate ethologically relevant roles for a subgroup of genetically defined patchy neurons in behavior.”

(2) Lines 499-500: How striato-nigral cells encode speed and deceleration deserves a thorough discussion and clarification. These striatonigral cells can target both SNr GABAergic neurons and dendrites of the dopaminergic neurons. A discussion of microcircuits formed by the patchy SPNs axons in the SNr GABAergic and SNC DAergic neurons should be presented.

We have added this point at lines 499–500, including a reference to a relevant review of microcircuitry. Additionally, we expanded the discussion section to address microcircuit mechanisms that may underlie our main findings.

(3) Line 70: "BNST" should be spelled out at the first time it is mentioned.

This has been done.

(4) Line 133: only GCaMP6 was listed in the method, but GCaMP8 was also used (Figure 4). Clarification or details are needed.

Thank you for your careful attention to detail. We have corrected the typographical errors in the Methods section. Specifically, in the Stereotaxic Injections section, we corrected “GCaMP83” to “GCaMP8s.” In the Fiber Implant section, we removed the incorrect reference to “GCaMP6s” and clarified that GCaMP8s was used for photometry, and hChR2 was used for optogenetics.

(5) Line 183: Can the authors describe more precisely what "a moment" means in terms of seconds or minutes?

This has been done.

(6) Line 288: typo: missing / in ΔF.

Thank you this has been fixed.

(7) Line 301-302: the statement of "mCherry and MOR1 colocalization" does not match the images in Figure 1B.

This has been corrected by proving a new Supplementary Figure S1.

(8) Related to the statement between Lines 303-304: Figure 1c data may reflect changes in MOR1 protein or cell loss. Quantification of NeuN+ neurons within the MOR1 area would strengthen the conclusion of 60% of patchy cell loss in Figure 1C.

Since the efficacy of AAV-FLEX-taCasp3 in cell ablation has been well established in our previous publications and those of others (Yang, Chiang et al. 2013, Wu, Kung et al. 2019), we do not believe the observed loss of MOR1 staining in Fig. 1C merely reflects reduced MOR1 expression. Moreover, a general neuronal marker such as NeuN may not reliably detect the specific loss of patchy neurons in our ablation model, given the technical limitations of conventional cell-counting methods like MBF’s StereoInvestigator, which typically exhibit a variability margin of 15–20%.

(9) Lines 313-314: "Similarly, PA mice demonstrated greater stay-time in the dark zone (Figure 1E)." Revision is needed to better reflect what is shown in Figure 1E and avoid misunderstandings.

Thank you this has been addressed.

(10) The color code in Figure 2Gi seems inconsistent with the others? Clarifications are needed.

Color coding in Figure 2Gi differs from that in 2Eii out of necessity. For example, the "Light" cells depicted in light blue in 2Eii are represented by both light gray and light red dots in 2Gi. Importantly, Figure 2G does not encode specific speed relationships; instead, any association with speed is indicated by a red hue.

(11) Lines 538-539: the statement of "Over half of the patch was covered" was not supported by Figure 5C. Clarification is needed.

Thank you. For clarity, we updated the x-axis labels in Figures 1C and 5C from “% area covered” to “% DS area covered,” and defined “DS” as “dorsal striatal” in the corresponding figure legends. Additionally, we revised the sentence in question to read: “As with ablation, histological examination indicated that a substantial fraction of dorsal patch territories, identified through MOR1 staining, were impacted (Fig. 5C).”

(12) Figure 3: statistical significance in Figure 3 should be labeled in various panels.

We believe the reviewer's concern pertains to the scatter plot in panel F—specifically, whether the data points are significantly different from zero. In panel 3F, the 95% confidence interval clearly overlaps with zero, indicating that the results are not statistically significant.

(13) Figures 6D-E: no difference in the speed of control mice and ChR2 mice under continuous optical stimulation was not expected. It was different from Gq-DRADDS study in Figure 5E-F. Clarifications are needed.

For mice undergoing constant ChR2 activation of Sepw1-Cre⁺ SNr efferents, overall locomotor speed does not differ from controls. However, the BIL (bright-to-illuminated) effect on zone transitions is disrupted: activating Sepw1-Cre⁺ fibers in the SNr blunts the typical increase in speed observed when mice flee from the light zone toward the dark zone. This impaired BIL-related speed increase upon exiting the light was similarly observed in the Gq-DREADD cohort. The reviewer is correct that this optogenetic manipulation within the SNr did not produce the more generalized speed reductions seen with broader Gq-DREADD activation of all Sepw1-Cre⁺ cells in the dorsal striatum. A likely explanation is the difference in targeting—ChR2 specifically activates SNr-bound terminals, whereas Gq-DREADD broadly activates entire Sepw1-Cre⁺ cells. Notably, many of the generalized speed profile changes observed with chemogenetic activation are opposite to those resulting from broad ablation of Sepw1-Cre⁺ cells.

The more subtle speed-restrictive phenotype observed with ChR2 activation targeted to the SNr may suggest that fewer striatonigral fibers were affected by this technique, possibly due to the limited spread of light from the fiber optic. Broad locomotor speed change in LDbox might require the recruitment of a larger number of striatonigral fibers than we were able to manipulate with an optogenetic approach. Alternatively, it could indicate that non-striatonigral Sepw1-Cre+ projections—such as striatopallidal or intrastriatal pathways—play a role in more generalized slowing. If striatopallidal fibers contributed to locomotor slowing, we would expect to see non-zero cross-correlations between neural activity and speed or acceleration, along with negative lag indicating that neural activity precedes the behavioral change. However, our fiber photometry data do not support such a role for Sepw1-Cre+ striatopallidal fibers.

We have also referenced the possibility that intrastriatal collaterals could suppress striatal dopamine levels, potentially explaining the stronger slowing phenotype observed when the entire striatal population is affected, as opposed to selectively targeting striatonigral terminals.

These technical considerations and interpretive nuances have been incorporated and clarified in the revised discussion section.

(14) Lines 632: "compliment": a typo?

Yes, it should be “complement”.

(15) Figure 4 legend: descriptions of panels A and B were swapped.

Thank you. This has been corrected.

6) Friedman (2020) was listed twice in the bibliography (Lines 920-929).

Thank you. This has been corrected.

Reviewer #3 (Recommendations for the authors):

It will be helpful to label and add figure legends below each figure.

Thank you for the suggestion.

Editor's note:

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

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

We have included detailed statistical information in the revised manuscript. Both male and female mice were used in all experiments in approximately equal numbers. Since no sex-related differences were observed, we did not report the number of animals by sex.

References

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Crittenden, J. R., P. W. Tillberg, M. H. Riad, Y. Shima, C. R. Gerfen, J. Curry, D. E. Housman, S. B. Nelson, E. S. Boyden and A. M. Graybiel (2016). "Striosome-dendron bouquets highlight a unique striatonigral circuit targeting dopamine-containing neurons." Proc Natl Acad Sci U S A 113(40): 11318-11323.

Dong, J., L. Wang, B. T. Sullivan, L. Sun, V. M. Martinez Smith, L. Chang, J. Ding, W. Le, C. R. Gerfen and H. Cai (2025). "Molecularly distinct striatonigral neuron subtypes differentially regulate locomotion." Nat Commun 16(1): 2710.

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Yang, C. F., M. C. Chiang, D. C. Gray, M. Prabhakaran, M. Alvarado, S. A. Juntti, E. K. Unger, J. A. Wells and N. M. Shah (2013). "Sexually dimorphic neurons in the ventromedial hypothalamus govern mating in both sexes and aggression in males." Cell 153(4): 896-909.

DOI: 10.1126/sciadv.adu6354

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What is this?

Procrastinación es el acto de postergar ciertas actividades o tareas por tareas que nos parecen más agradable o miedo a afrontar así como por el simple hecho de tener flojera o pereza a realizarlas

The student's fellow classmate reported the threat to a teaching assistant which led to the staff searching the student's locked and finding the knives.

When dinosaurs were alive, the days were 23.5 hours long, but because of the tidal friction against the earth, the earth has been slowly losing energy, resulting in longer days

There are several possibilities that can explain this but one of the could be atmospheric factors, or wind effects.

This shortening of day happens consistently every year, and the shortest day we’ve had this year was 1.5 milliseconds shorter than the regular 24-hour day.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The objective of this research is to understand how the expression of key selector transcription factors, Tal1, Gata2, Gata3, involved in GABAergic vs glutamatergic neuron fate from a single anterior hindbrain progenitor domain is transcriptionally controlled. With suitable scRNAseq, scATAC-seq, CUT&TAG, and footprinting datasets, the authors use an extensive set of computational approaches to identify putative regulatory elements and upstream transcription factors that may control selector TF expression. This data-rich study will be a valuable resource for future hypothesis testing, through perturbation approaches, of the many putative regulators identified in the study. The data are displayed in some of the main and supplemental figures in a way that makes it difficult to appreciate and understand the authors' presentation and interpretation of the data in the Results narrative. Primary images used for studying the timing and coexpression of putative upstream regulators, Insm1, E2f1, Ebf1, and Tead2 with Tal1 are difficult to interpret and do not convincingly support the authors' conclusions. There appears to be little overlap in the fluorescent labeling, and it is not clear whether the signals are located in the cell soma nucleus.

Strengths:

The main strength is that it is a data-rich compilation of putative upstream regulators of selector TFs that control GABAergic vs glutamatergic neuron fates in the brainstem. This resource now enables future perturbation-based hypothesis testing of the gene regulatory networks that help to build brain circuitry.

We thank Reviewer #1 for the thoughtful assessment and recognition of the extensive datasets and computational approaches employed in our study. We appreciate the acknowledgment that our efforts in compiling data-rich resources for identifying putative regulators of key selector transcription factors (TFs)—Tal1, Gata2, and Gata3—are valuable for future hypothesis-driven research.

Weaknesses:

Some of the findings could be better displayed and discussed.

We acknowledge the concerns raised regarding the clarity and interpretability of certain figures, particularly those related to expression analyses of candidate upstream regulators such as Insm1, E2f1, Ebf1, and Tead2 in relation to Tal1. We agree that clearer visualization and improved annotation of fluorescence signals are crucial to accurately support our conclusions. In our revised manuscript, we will enhance image clarity and clearly indicate sites of co-expression for Tal1 and its putative regulators, ensuring the results are more readily interpretable. Additionally, we will expand explanatory narratives within the figure legends to better align the figures with the results section.

Reviewer #2 (Public review):

Summary:

In the manuscript, the authors seek to discover putative gene regulatory interactions underlying the lineage bifurcation process of neural progenitor cells in the embryonic mouse anterior brainstem into GABAergic and glutamatergic neuronal subtypes. The authors analyze single-cell RNA-seq and single-cell ATAC-seq datasets derived from the ventral rhombomere 1 of embryonic mouse brainstems to annotate cell types and make predictions or where TFs bind upstream and downstream of the effector TFs using computational methods. They add data on the genomic distributions of some of the key transcription factors and layer these onto the single-cell data to get a sense of the transcriptional dynamics.

Strengths:

The authors use a well-defined fate decision point from brainstem progenitors that can make two very different kinds of neurons. They already know the key TFs for selecting the neuronal type from genetic studies, so they focus their gene regulatory analysis squarely on the mechanisms that are immediately upstream and downstream of these key factors. The authors use a combination of single-cell and bulk sequencing data, prediction and validation, and computation.

We also appreciate the thoughtful comments from Reviewer #2, highlighting the strengths of our approach in elucidating gene regulatory interactions that govern neuronal fate decisions in the embryonic mouse brainstem. We are pleased that our focus on a critical cell-fate decision point and the integration of diverse data modalities, combined with computational analyses, has been recognized as a key strength.

Weaknesses:

The study generates a lot of data about transcription factor binding sites, both predicted and validated, but the data are substantially descriptive. It remains challenging to understand how the integration of all these different TFs works together to switch terminal programs on and off.

Reviewer #2 correctly points out that while our study provides extensive data on predicted and validated transcription factor binding sites, clearly illustrating how these factors collectively interact to regulate terminal neuronal differentiation programs remains challenging. We acknowledge the inherently descriptive nature of the current interpretation of our combined datasets.

In our revision, we will clarify how the different data types support and corroborate one another, highlighting what we consider the most reliable observations of TF activity. Additionally, we will revise the discussion to address the challenges associated with interpreting the highly complex networks of interactions within the gene regulatory landscape.

We sincerely thank both reviewers for their constructive feedback, which we believe will significantly enhance the quality and accessibility of our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The results in Figure 3 and several associated supplements are mainly a description/inventory of putative CREs some of which are backed to some extent by previous transgenic studies. But given the way the authors chose to display the transgenic data in the Supplements, it is difficult to fully appreciate how well the transgenic data provide functional support. Take, for example, the Tal +40kb feature that maps to a midbrain enhancer: where exactly does +40kb map to the enhancer region? Is Tal +40kb really about 1kb long? The legend in Supplemental Figure 6 makes it difficult to interpret the bar charts; what is the meaning of: features not linked to gene -Enh? Some of the authors' claims are not readily evident or are inscrutable. For example, Tal locus features accessible in all cell groups are not evident (Fig 2A,B). Other cCREs are said to closely correlate with selector expression for example, Tal +.7kb and +40kb. However, inspection of the data seems to indicate that the two cCREs have very different dynamics and only +40kb seems to correlate with the expression track above it. Some features are described redundantly such as the Gata2 +22 kb, +25.3 kb, and +32.8 kb cCREs above and below the Gata3 cCRE. What is meant by: The feature is accessible at 3' position early, and gains accessibility at 5' positions ... Detailed feature analysis later indicated the binding of Nkx6-1 and Ascl1 that are expressed in the rV2 neuronal progenitors, at 3' positions, and binding of Insm1 and Tal1 TFs that are activated in early precursors, at 5' positions (Figure 3C).

To allow easier assessment of the overlap of the features described in this study in reference to the transgenic studies, we have added further information about the scATAC features, cCREs and previously published enhancers, as well as visual schematics of the feature-enhancer overlaps in the Supplementary table 4. The Supplementary Table 4 column contents are also now explained in detail in the table legend (under the table). We hope those changes make the feature descriptions clearer. To answer the reviewer's question about the Tal1+40kb enhancer, the length of the published enhancer element is 685 bp and the overlapping scATAC feature length is 2067 bp (Supplementary Table 3, sheet Tal1, row 103).

The legend and the chart labelling in the Supplementary Figure 5 (formerly Supplementary figure 6) have been elaborated, and the shown categories explained more clearly.

Regarding the features at the Tal1 locus, the text has been revised and the references to the features accessible in all cell groups were removed. These features showed differences in the intensity of signal but were accessible in all cell groups. As the accessibility of these features does not correlate with Tal1 expression, they are of less interest in the context of this paper.

The gain in accessibility of the +0.7kb and +40 kb features correlates with the onset of Tal1 RNA expression. This is now more clearly stated in the text, as " For example, the gain in the accessibility of Tal1 cCREs at +0.7 and +40 kb correlated temporally with the expression of Tal1 mRNA (Figure 2B), strongly increasing in the earliest GABAergic precursors (GA1) and maintained at a lower level in the more mature GABAergic precursor groups (GA2-GA6), " (Results, page 4). The reviewer is right that the later dynamics of the +0.7 and +40 cCREs differ and this is now stated more clearly in the text (Results, page 5, last chapter).

The repetition in the description of the Gata2 +22 kb, +25.3 kb, and +32.8 kb cCREs has been removed.

The Tal1 +23 kb cCRE showed within-feature differences in accessibility signal. This is explained in the text on page 5, referring to the relevant figure 2A, showing the accessibility or scATAC signal in cell groups and the features labelled below, and 3C, showing the location of the Nkx6-1 and Ascl1 binding sites in this feature: "The Tal1 +23 kb cCRE contained two scATAC-seq peaks, having temporally different patterns of accessibility. The feature is accessible at 3' position early, and gains accessibility at 5' positions concomitant with GABAergic differentiation (Figure 2A, accessibility). Detailed feature analysis later indicated that the 3' end of this feature contains binding sites of Nkx6-1 and Ascl1 that are expressed in the rV2 neuronal progenitors, while the 5' end contains TF binding sites of Insm1 and Tal1 TFs that are activated in early precursors (described below, see Figure 3C)."

(2) Supplementary Figure 3 is not presented in the Results.

Essential parts of previous Supplementary Figure 3 have been incorporated into the Figure 4 and the previous Supplementary Figure omitted.

(3) The significance of Figure 3 and the many related supplements is difficult to understand. A large number of footprints with wide-ranging scores, many very weak or unbound, are displayed in the various temporal cell groups in different epigenomic regions of Tal1 and Vsx2. The footprints for GA1 and Ga2 are combined despite Tal1 showing stronger expression in GA1 and stronger accessibility (Figure 2). Many possibilities are outlined in the Results for how the many different kinds of motifs in the cCREs might bind particular TFs to control downstream TF expression, but no experiments are performed to test any of the possibilities. How well do the TOBIAS footprints align with C&T peaks? How was C&T used to validate footprints? Are Gata2, 3, and Vsx2 known to control Tal1 expression from perturbation experiments?

Figure 3 and related supplements present examples of the primary data and summarise the results of comprehensive analysis. The methods of identifying the selector TF regulatory features and the regulators are described in the Methods (Materials and Methods page 16). Briefly, the correlation between feature accessibility and selector TF RNA expression (assessed by the LinkPeaks score and p-value) were used to select features shown in the Figure 3.

We are aware of differences in Tal1 expression and accessibility between GA1 and GA2. However, number of cells in GA2 was not high enough for reliable footprint calculations and therefore we opted for combining related groups throughout the rV2 lineage for footprinting.

As suggested, CUT&Tag could be used to validate the footprinting results with some restrictions. In the revised manuscript, we included analysis of CUT&Tag peak location and footprints similarly to an earlier study (Eastman et al. 2025). In summary, we analysed whether CUT&Tag peaks overlap locations in which footprinting was also recognized and vice versa. Per each TF with CUT&Tag data we calculated a) Total number of CUT&Tag consensus peaks b) Total number of bound TFBS (footprints) c) Percentage of CUT&Tag overlapping bound TFBS d) Percentage of bound TFBS overlapping CUT&Tag. These results are shown in Supplementary Table 6 and in Supplementary figure 11 with analysis described in Methods (Materials and Methods, page 19). There is considerable overlap between CUT&Tag peaks and bound footprints, comparable to one shown in Eastman et al. 2025. However, these two methods are not assumed to be completely matching for several reasons: binding by related/redundant TFs, antigen masking in the TF complex, chromatin association without DNA binding, etc. In addition, some CUT&Tag peaks with unbound footprints could arise from non-rV2 cells that were part of the bulk CUT&Tag analysis but not of the scATAC footprint analysis.

The evidence for cross-regulation of selector genes and the regulation of Tal1 by Gata2, Gata3 and Vsx2 is now discussed (Discussion, chapter Selector TFs directly autoregulate themselves and cross-regulate each other, page 12-13). The regulation of Tal1 expression by Vsx2 has, to our knowledge, not been earlier studied.

(4) Figure 4 findings are problematic as the primary images seem uninterpretable and unconvincing in supporting the authors' claims. There is a lack of clear evidence in support of TF coexpression and that their expression precedes Tal1.

Figure 4 has been entirely redrawn with higher resolution images and a more logical layout. In the revised Figure 4, only the most relevant ISH images are shown and arrowheads are added showing the colocalization of the mRNA in the cell cytoplasm. Next to the plots of RNA expression along the apical-basal axis of r1, an explanatory image of the quantification process is added (Figure 4D).

(5) What was gained from also performing ChromVAR other than finding more potential regulators and do the results of the two kinds of analyses corroborate one another? What is a dual GATA:TAL BS?

Our motivation for ChromVAR analysis is now more clearly stated in the text (Results, page 9): “In addition to the regulatory elements of GABAergic fate selectors, we wanted to understand the genome-wide TF activity during rV2 neuron differentiation. To this aim we applied ChromVAR (Schep et al., 2017)" Also, further explanation about the Tal1and Gata binding sites has been added in this chapter (Results, page 9).

The dual GATA:Tal BS (TAL1.H12CORE.0.P.B) is a 19-bp motif that consists of an E-box and GATA sequence, and is likely bound by heteromeric Gata2-Tal1 TF complex, but may also be bound by Gata2, Gata3 or Tal1 TFs separately. The other TFBSs of Tal1 contain a strong E-box motif and showed either a lower activity (TAL1.H12CORE.1.P.B) or an earlier peak of activity in common precursors with a decline after differentiation (TAL1.H12CORE.2.P.B) (Results, page 9).

(6) The way the data are displayed it is difficult to see how the C&T confirmed the binding of Ebf1 and Insm1, Tal1, Gata2, and Gata3 (Supplementary Figures 9-11). Are there strong footprints (scores) centered at these peaks? One can't assess this with the way the displays are organized in Figure 3. What is the importance of the H3K4me3 C&T? Replicate consistency, while very strong for some TFs, seems low for other TFs, e.g. Vsx2 C&T on Tal1 and Gata2. The overlaps do not appear very strong in Supplementary Figure 10. Panels are not letter labeled.

We have added an analysis of footprint locations within the CUT&Tag peaks (Supplementary Figure 11). The Figure shows that the footprints are enriched at the middle regions of the CUT&Tag peaks, which is expected if TF binding at the footprinted TFBS site was causative for the CUT&Tag peaks.

The aim of the Supplementary Figures 9-11 (Supplementary Figures 8-10 in the revised manuscript) was to show the quality and replicability of the CUT&Tag.

The anti-H3K4me3 antibody, as well as the anti-IgG antibody, was used in CUT&Tag as part of experiment technical controls. A strong CUT&Tag signal was detected in all our CUT&Tag experiments with H3K4me3. The H3K4me3 signal was not used in downstream analyses.

We have now labelled the H3K4me3 data more clearly as "positive controls" in the Supplementary Figure 8. The control samples are shown only on Supplementary Figure 8 and not in the revised Supplementary Figure 10, to avoid repetition. The corresponding figure legends have been modified accordingly.

To show replicate consistency, the genome view showing the Vsx2 CUT&Tag signal at Gata2 gene has been replaced by a more representative region (Supplementary Figure 8, Vsx2). The Vsx2 CUT&Tag signal at the Gata2 locus is weak, explaining why the replicability may have seemed low based on that example.

Panel labelling is added on Supplementary Figures S8, S9, S10.  

(7) It would be illuminating to present 1-2 detailed examples of specific target genes fulfilling the multiple criteria outlined in Methods and Figure 6A.

We now present examples of the supporting evidence used in the definition of selector gene target features and target genes. The new Supplementary Figure 12 shows an example gene Lmo1 that was identified as a target gene of Tal1, Gata2 and Gata3.

Reviewer #2 (Recommendations for the authors):

(1) The authors perform CUT&Tag to ask whether Tal1 and other TFs indeed bind putative CREs computed. However, it is unclear whether some of the antibodies (such as Gata3, Vsx2, Insm1, Tead2, Ebf1) used are knock-out validated for CUT&Tag or a similar type of assay such as ChIP-seq and therefore whether the peaks called are specific. The authors should either provide specificity data for these or a reference that has these data. The Vsx2 signal in Figure S9 looks particularly unconvincing.

Information about the target specificity of the antibodies can be found in previous studies or in the product information. The references to the studies have been now added in the Methods (Materials and Methods, CUT&Tag, pages 18-19). Some of the antibodies are indeed not yet validated for ChIP-seq, Cut-and-run or CUT&Tag. This is now clearly stated in the Materials and Methods (page 19): "The anti-Ebf1, anti-Tal1, anti-IgG and anti-H3K4me3 antibodies were tested on Cut-and-Run or ChIP-seq previously (Boller et al., 2016b; Courtial et al., 2012) and Cell Signalling product information). The anti-Gata2 and anti-Gata3 antibodies are ChIP-validated ((Ahluwalia et al., 2020a) and Abcam product information). There are no previous results on ChIP, ChIP-seq or CUT&Tag with the anti-Insm1, anti-Tead2 and anti-Vsx2 antibodies used here. The specificity and nuclear localization have been demonstrated in immunohistochemistry with anti-Vsx2 (Ahluwalia et al., 2020b) and anti-Tead2 (Biorbyt product information). We observed good correlation between replicates with anti-Insm1, similar to all antibodies used here, but its specificity to target was not specifically tested". We admit that specificity testing with knockout samples would increase confidence in our data. However, we have observed robust signals and good replicability in the CUT&Tag for the antibodies shown here.

Vsx2 CUT&Tag signal at the loci previously shown in Supplementary Figure S9 (now Supplementary Figure 8) is weak, explaining why the replicability may seem low based on those examples. The genome view showing the Vsx2 CUT&Tag signal at Gata2 gene locus in Supplementary Figure 8 (previously Supplementary figure 9) has now been replaced by a view of Vsx2 locus that is more representative of the signal.

(2) It is unclear why the authors chose to focus on the transcription factor genes described in line 626 as opposed to the many other putative TFs described in Figure 3/Supplementary Figure 8. This is the major challenge of the paper - the authors are trying to tell a very targeted story but they show a lot of different names of TFs and it is hard to follow which are most important.

We agree with the reviewer that the process of selection of the genes of interest is not always transparent. We are aware that interpretations of a paper are based on the known functions of the putative regulatory TFs, however additional aspects of regulation could be revealed even if the biological functions of all the TFs were known. This is now stated in the Discussion “Caveats of the study” chapter. It would be relevant to study all identified candidate genes, but as often is the case, our possibilities were limited by the availability of materials (probes, antibodies), time, and financial resources. In the revised manuscript, we now briefly describe the biological processes related to the selected candidate regulatory TFs of the Tal1 gene (Results, page 8, "Pattern of expression of the putative regulators of Tal1 in the r1"). We hope this justifies the focus on them in our RNA co-expression analysis. The TFs analysed by RNAscope ISH are examples, which demonstrate alignment of the tissue expression patterns with the scRNA-seq data, suggesting that the dynamics of gene expression detected by scRNA-seq generally reflects the pattern of expression in the developing brainstem.

(3) How is the RNA expression level in Figure 5B and 4D-L computed? These are the clusters defined by scATAC-seq. Is this an inferred RNA expression? This should be made more clear in the text.

The charts in Figures 5B and 4G,H,I show inferred RNA expression. The Y-axis labels have now been corrected and include the term inferred’. RNA expression in the scATAC-seq cell clusters is inferred from the scRNA-seq cells after the integration of the datasets.

(4) The convergence of the GABA TFs on a common set of target genes reminds me of a nice study from the Rubenstein lab PMID: 34921112 that looked at a set of TFs in cortical progenitors. This might be a good comparison study for the authors to use as a model to discuss the convergence data.

We thank the reviewer for bringing this article to our attention. The article is now discussed in the manuscript (Discussion, page 11).

(5) The data in Figure 4, the in-situ figure, needs significant work. First, the images especially B, F, and J appear to be of quite low resolution, so they are hard to see. It is unclear exactly what is being graphed in C, G, and K and it does not seem to match the text of the results section. Perhaps better labeling of the figure and a more thorough description will make it clear. It is not clear how D, H, and L were supposed to relate to the images - presumably, this is a case where cell type is spatially organized, but this was unclear in the text if this is known and it needs to be more clearly described. Overall, as currently presented this figure does not support the descriptions and conclusions in the text.

Figure 4 has been entirely redrawn with higher resolution images and more logical layout. In the revised Figure 4, the ISH data and the quantification plots are better presented; arrows showing the colocalization of the mRNA in the cell cytoplasm were added; and an explanatory image of the quantification process is added on (D).

Minor points

(1) Helpful if the authors include scATAC-seq coverage plots for neuronal subtype markers in Figure 1/S1.

We are unfortunately uncertain what is meant with this request. Subtype markers in Figure 1/S1 scATAC-seq based clusters are shown from inferred RNA expression, and therefore these marker expression plots do not have any coverage information available.

(2) The authors in line 429 mention the testing of features within TADs. They should make it clear in the main text (although tadmap is mentioned in the methods) that this is a prediction made by aggregating HiC datasets.

Good point and that this detail has been added to both page 3 and 16.

(3) The authors should include a table with the phastcons output described between lines 511 and 521 in the main or supplementary figures.

We have now clarified int the text that we did not recalculate any phastcons results, we merely used already published and available conservation score per nucleotide as provided by the original authors (Siepel et al. 2005). (Results, page 5: revised text is " To that aim, we used nucleotide conservation scores from UCSC (Siepel et al., 2005). We overlaid conservation information and scATAC-seq features to both validate feature definition as well as to provide corroborating evidence to recognize cCRE elements.")

(4) It is very difficult to read the names of the transcription factor genes described in Figure 3B-D and Supplementary Figure 8 - it would be helpful to resize the text.

The Figures 3B-D and Supplementary Figure 7 (former Supplementary figure 8) have been modified, removing unnecessary elements and increasing the size of text.

(5) It is unclear what strain of mouse is used in the study - this should be mentioned in the methods.

Outbred NMRI mouse strain was used in this study. Information about the mouse strain is added in Materials and Methods: scRNA-seq samples (page 14), scATAC-seq samples (page 15), RNAscope in situ hybridization (page 17) and CUT&Tag (page 18).

(6) Text size in Figure 6 should be larger. R-T could be moved to a Supplementary Figure.

The Figure 6 has been revised, making the charts clearer and the labels of charts larger. The Figure 6R-S have been replaced by Supplementary table 8 and the Figure 6T is now shown as a new Figure (Figure 7).

Additional corrections in figures

Figure 6 D,I,N had wrong y-axis scale. It has been corrected, though it does not have an effect on the interpretation of the data as Pos.link and Neg.link counts were compared to each other’s (ratio).

On Figure 2B, the heatmap labels were shifted making it difficult to identify the feature name per row. This is now corrected.

Author response:

The following is the authors’ response to the original reviews

Public reviews:

Reviewer 1 (Public Review):

Many thanks for the positive and constructive feedback on the manuscript.

This study reveals a great deal about how certain neural representations are altered by expectation and learning on shorter and longer timescales, so I am loath to describe certain limitations as 'weaknesses'. But one limitation inherent in this experimental design is that, by focusing on implicit, task-irrelevant predictions, there is not much opportunity to connect the predictive influences seen at the neural level to the perceptual performance itself (e.g., how participants make perceptual decisions about expected or unexpected events, or how these events are detected or appear).

Thank you for the interesting comment. We now discuss the limitation of task-irrelevant prediction . In brief, some studies which showed sharpening found that task demands were relevant, while some studies which showed dampening were based on task-irrelevant predictions, but it is unlikely that task relevance - which was not manipulated in the current study - would explain the switch between sharpening and dampening that we observe within and across trials.

The behavioural data that is displayed (from a post-recording behavioural session) shows that these predictions do influence perceptual choice - leading to faster reaction times when expectations are valid. In broad strokes, we may think that such a result is broadly consistent with a 'sharpening' view of perceptual prediction, and the fact that sharpening effects are found in the study to be larger at the end of the task than at the beginning. But it strikes me that the strongest test of the relevance of these (very interesting) EEG findings would be some evidence that the neural effects relate to behavioural influences (e.g., are participants actually more behaviourally sensitive to invalid signals in earlier phases of the experiment, given that this is where the neural effects show the most 'dampening' a.k.a., prediction error advantage?)

Thank you for the suggestion. We calculated Pearson’s correlation coefficients for behavioural responses (difference in mean reaction times), neural responses during the sharpening effect (difference in decoding accuracy), and neural responses during the dampening effect for each participant, which resulted in null findings.

Reviewer 2 (Public Review):

Thank you for your helpful and constructive comments on the manuscript.

The strength in controlling for repetition effects by introducing a neutral (50% expectation) condition also adds a weakness to the current version of the manuscript, as this neutral condition is not integrated into the behavioral (reaction times) and EEG (ERP and decoding) analyses. This procedure remained unclear to me. The reported results would be strengthened by showing differences between the neutral and expected (valid) conditions on the behavioral and neural levels. This would also provide a more rigorous check that participants had implicitly learned the associations between the picture category pairings.

Following the reviewer's suggestion, we have included the neutral condition in the behavioural analysis and performed a repeated measures ANOVA on all three conditions.

It is not entirely clear to me what is actually decoded in the prediction condition and why the authors did not perform decoding over trial bins in prediction decoding as potential differences across time could be hidden by averaging the data. The manuscript would generally benefit from a more detailed description of the analysis rationale and methods.

In the original version of the manuscript, prediction decoding aimed at testing if the upcoming stimulus category can be decoded from the response to the preceding ( leading) stimulus. However, in response to the other Reviewers’ comments we have decided to remove the prediction decoding analysis from the revised manuscript as it is now apparent that prediction decoding cannot be separated from category decoding based on pixel information.

Finally, the scope of this study should be limited to expectation suppression in visual perception, as the generalization of these results to other sensory modalities or to the action domain remains open for future research.

We have clarified the scope of the study in the revised manuscipt .

Reviewer 3 (Public Review):

Thank you for the thought-provoking and interesting comments and suggestions.

(1) The results in Figure 2C seem to show that the leading image itself can only be decoded with ~33% accuracy (25% chance; i.e. ~8% above chance decoding). In contrast, Figure 2E suggests the prediction (surprisingly, valid or invalid) during the leading image presentation can be decoded with ~62% accuracy (50% chance; i.e. ~12% above chance decoding). Unless I am misinterpreting the analyses, it seems implausible to me that a prediction, but not actually shown image, can be better decoded using EEG than an image that is presented on-screen.

Following this and the remaining comments by the Reviewer (see below), we have decided to remove the prediction analysis from the manuscript. Specifically, we have focused on the Reviewer’s concern that it is implausible that image prediction would be better decoded that an image that is presented on-screen. This led us to perform a control analysis, in which we tried to decode the leading image category based on pixel values alone (rather than on EEG responses). Since this decoding was above chance, we could not rule out the possibility that EEG responses to leading images reflect physical differences between image categories. This issue does not extend to trailing images, as the results of the decoding analysis based on trailing images are based on accuracy comparisons between valid and invalid trials, and thus image features are counterbalanced. We would like to thank the Reviewer for raising this issue

(2) The "prediction decoding" analysis is described by the authors as "decoding the predictable trailing images based on the leading images". How this was done is however unclear to me. For each leading image decoding the predictable trailing images should be equivalent to decoding validity (as there were only 2 possible trailing image categories: 1 valid, 1 invalid). How is it then possible that the analysis is performed separately for valid and invalid trials? If the authors simply decode which leading image category was shown, but combine L1+L2 and L4+L5 into one class respectively, the resulting decoder would in my opinion not decode prediction, but instead dissociate the representation of L1+L2 from L4+L5, which may also explain why the time-course of the prediction peaks during the leading image stimulus-response, which is rather different compared to previous studies decoding predictions (e.g. Kok et al. 2017). Instead for the prediction analysis to be informative about the prediction, the decoder ought to decode the representation of the trailing image during the leading image and inter-stimulus interval. Therefore I am at present not convinced that the utilized analysis approach is informative about predictions.

In this analysis, we attempted to decode ( from the response to leading images) which trailing categories ought to be presented. The analysis was split between trials where the expected category was indeed presented (valid) vs. those in which it was not (invalid). The separation of valid vs invalid trials in the prediction decoding analysis served as a sanity check as no information about trial validity was yet available to participants. However, as mentioned above, we have decided to remove the “prediction decoding” analysis based on leading images as we cannot disentangle prediction decoding from category decoding.

(3) I may be misunderstanding the reported statistics or analyses, but it seems unlikely that >10  of the reported contrasts have the exact same statistic of Tmax= 2.76 . Similarly, it seems implausible, based on visual inspection of Figure 2, that the Tmax for the invalid condition decoding (reported as Tmax = 14.903) is substantially larger than for the valid condition decoding (reported as Tmax = 2.76), even though the valid condition appears to have superior peak decoding performance. Combined these details may raise concerns about the reliability of the reported statistics.

Thank you for bringing this to our attention. This copy error has now been rectified.

(4) The reported analyses and results do not seem to support the conclusion of early learning resulting in dampening and later stages in sharpening. Specifically, the authors appear to base this conclusion on the absence of a decoding effect in some time-bins, while in my opinion a contrast between time-bins, showing a difference in decoding accuracy, is required. Or better yet, a non-zero slope of decoding accuracy over time should be shown ( not contingent on post-hoc and seemingly arbitrary binning).

Thank you for the helpful suggestion. We have performed an additional analysis to address this issue, we calculated the trial-by-trial time-series of the decoding accuracy benefit for valid vs. invalid for each participant and averaged this benefit across time points for each of the two significant time windows. Based on this, we fitted a logarithmic model to quantify the change of this benefit over trials, then found the trial index for which the change of the logarithmic fit was < 0.1% (i.e., accuracy was stabilized). Given the results of this analysis and to ensure a sufficient number of trials, we focussed our further analyses on bins 1-2 to directly assess the effects of learning. This is explained in more detail in the revised manuscript .

(5) The present results both within and across trials are difficult to reconcile with previous studies using MEG (Kok et al., 2017; Han et al., 2019), single-unit and multi-unit recordings (Kumar et al., 2017; Meyer & Olson 2011), as well as fMRI (Richter et al., 2018), which investigated similar questions but yielded different results; i.e., no reversal within or across trials, as well as dampening effects with after more training. The authors do not provide a convincing explanation as to why their results should differ from previous studies, arguably further compounding doubts about the present results raised by the methods and results concerns noted above.

The discussion of these findings has been expanded in the revised manuscript . In short, the experimental design of the above studies did not allow for an assessment of these effects prior to learning. Several of them also used repeated stimuli (albeit some studies changed the pairings of stimuli between trials), potentially allowing for RS to confound their results.

Recommendations for the Authors:

Reviewer 1 (Recommendations for the authors):

(1) On a first read, I was initially very confused by the statement on p.7 that each stimulus was only presented once - as I couldn't then work out how expectations were supposed to be learned! It became clear after reading the Methods that expectations are formed at the level of stimulus category (so categories are repeated multiple times even if exemplars are not). I suspect other readers could have a similar confusion, so it would be helpful if the description of the task in the 'Results' section (e.g., around p.7) was more explicit about the way that expectations were generated, and the (very large) stimulus set that examples are being drawn from.

Following your suggestion, we have clarified the paradigm by adding details about the categories and the manner in which expectations are formed.

(2) p.23: the authors write that their 1D decoding images were "subjected to statistical inference amounting to a paired t-test between valid and invalid categories". What is meant by 'amounting to' here? Was it a paired t-test or something statistically equivalent? If so, I would just say 'subjected to a paired t-test' to avoid any confusion, or explaining explicitly which statistic inference was done over.

We have rephrased this as “subjected to (1) a one-sample t-test against chance-level, equivalent to a fixed-effects analysis, and (2) a paired t-test”.

Relatedly, this description of an analysis amounting to a 'paired t-test' only seems relevant for the sensory decoding and memory decoding analyses (where there are validity effects) rather than the prediction decoding analysis. As far as I can tell the important thing is that the expected image category can be decoded, not that it can be decoded better or worse on valid or invalid trials.

In the previous version of the manuscript, the comparison of prediction decoding between valid and invalid trials was meant as a sanity check. However, in response to the other Reviewers’ comments we have decided to remove the prediction decoding analysis from the revised manuscript due to confounds.

It would be helpful if authors could say a bit more about how the statistical inferences were done for the prediction decoding analyses and the 'condition against baseline' contrasts (e.g., when it is stated that decoding accuracy in valid trials *,in general,* is above 0 at some cluster-wise corrected value). My guess is that this amounts to something like a one-sample t-test - but it may be worth noting that one-sample t-tests on information measures like decoding accuracy cannot support population-level inference, because these measures cannot meaningfully be below 0 (see Allefeld et al, 2016).

When testing for decoding accuracy against baseline, we used one-sample t-tests against chance level (rather than against 0) throughout the manuscript. We now clarify in the manuscript that this corresponds to a fixed-effects analysis (Allefeld et al., 2016). In contrast, when testing for differences in decoding accuracy between valid and invalid conditions, we used paired-sample t-tests. As mentioned above, the prediction decoding analysis has been removed from the analysis.

(3) By design, the researchers focus on implicit predictive learning which means the expectations being formed are ( by definition) task-irrelevant. I thought it could be interesting if the authors might speculate in the discussion on how they think their results may or may not differ when predictions are deployed in task-relevant scenarios -  particularly given that some studies have found sharpening effects do not seem to depend on task demands ( e.g., Kok et al, 2012 ; Yon et al, 2018)  while other studies have found that some dampening effects do seem to depend on what the observer is attending to ( e.g., Richter et al, 2018) . Do these results hint at a possible explanation for why this might be? Even if the authors think they don't, it might be helpful to say so!

Thank you for the interesting comment. We have expanded on this in the revised manuscript.

Reviewer 2  (Recommendations for the authors):

Methods/results

(1) The goal of this study is the assessment of expectation effects during statistical learning while controlling for repetition effects, one of the common confounds in prediction suppression studies (see, Feuerriegel et al., 2021). I agree that this is an important aspect and I assume that this was the reason why the authors introduced the P=0.5 neutral condition (Figure 1B, L3). However, I completely missed the analyses of this condition in the manuscript. In the figure caption of Figure 1C, it is stated that the reaction times of the valid, invalid, and neutral conditions are shown, but only data from the valid and invalid conditions are depicted. To ensure that participants had built up expectations and had learned the pairing, one would not only expect a difference between the valid and invalid conditions but also between the valid and neutral conditions. Moreover, it would also be important to integrate the neutral condition in the multivariate EEG analysis to actually control for repetition effects. Instead, the authors constructed another control condition based on the arbitrary pairings. But why was the neutral condition not compared to the valid and invalid prediction decoding results? Besides this, I also suggest calculating the ERP for the neutral condition and adding it to Figure 2A to provide a more complete picture.

As mentioned above, we have included the neutral condition in the behavioural analysis, as outlined in the revised manuscript. We have also included a repeated measures ANOVA on all 3 conditions. The purpose of the neutral condition was not to avoid RS, but rather to provide a control condition. We avoided repetition by using individual, categorised stimuli. Figure 1C has been amended to include the neutral condition). In response to the remaining comments, we have decided to remove the prediction decoding analysis from the manuscript.

(2) One of the main results that is taken as evidence for the OPT is that there is higher decoding accuracy for valid trials (indicate sharpening) early in the trial and higher decoding accuracy for invalid trials (indicate dampening) later in the trial. I would have expected this result for prediction decoding that surprisingly showed none of the two effects. Instead, the result pattern occurred in sensory decoding only, and partly (early sharpening) in memory decoding. How do the authors explain these results? Additionally, I would have expected similar results in the ERP; however, only the early effect was observed. I missed a more thorough discussion of this rather complex result pattern. The lack of the opposing effect in prediction decoding limits the overall conclusion that needs to be revised accordingly.

Since sharpening vs. dampening rests on the comparison between valid and invalid trials, evidence for sharpening vs. dampening could only be obtained from decoding based on responses to trailing images. In prediction decoding (removed from the current version), information about the validity of the trial is not yet available. Thus, our original plan was to compare this analysis with the effects of validity on the decoding of trailing images (i.e. we expected valid trials to be decoded more accurately after the trailing image than before). The results of the memory decoding did mirror the sensory decoding of the trailing image in that we found significantly higher decoding accuracy of the valid trials from 123-180 ms. As with the sensory decoding, there was a tendency towards a later flip (280-296 ms) where decoding accuracy of invalid trials became nominally higher, but this effect did not reach statistical significance in the memory decoding.

(3) To increase the comprehensibility of the result pattern, it would be helpful for the reader to clearly state the hypotheses for the ERP and multivariate EEG analyses. What did you expect for the separate decoding analyses? How should the results of different decoding analyses differ and why? Which result pattern would (partly, or not) support the OPT?

Our hypotheses are now stated in the revised manuscript.

(4) I was wondering why the authors did not test for changes during learning for prediction decoding. Despite the fact that there were no significant differences between valid and invalid conditions within-trial, differences could still emerge when the data set is separated into bins. Please test and report the results.

As mentioned above, we have decided to remove the prediction decoding analysis from the current version of the manuscript.

(5) To assess the effect of learning the authors write: 'Given the apparent consistency of bins 2-4, we focused our analyses on bins 1-2.' Please explain what you mean by 'apparent consistency'. Did you test for consistency or is it based on descriptive results? Why do the authors not provide the complete picture and perform the analyses for all bins? This would allow for a better assessment of changes over time between valid and invalid conditions. In Figure 3, were valid and invalid trials different in any of the QT3 or QT4 bins in sensory or memory encoding?

We have performed an additional analysis to address this issue. The reasoning behind the decision to focus on bins 1-2 is now explained in the revised manuscript. In short, fitting a learning curve to trial-by-trial decoding estimates indicates that decoding stabilizes within <50% of the trials. To quantify changes in decoding occurring within these <50% of the trials while ensuring a sufficient number of trials for statistical comparisons, we decided to focus on bins 1-2 only.

(6) Please provide the effect size for all statistical tests.

Effect sizes have now been provided.

(7) Please provide exact p-values for non-significant results and significant results larger than 0.001.

Exact p-values have now been provided.

(8) Decoding analyses: I suppose there is a copy/paste error in the T-values as nearly all T-values on pages 11 and 12 are identical (2.76) leading to highly significant p-values (0.001) as well as non-significant effects (>0.05). Please check.

Thank you for bringing this to our attention. This error has now been corrected.

(9) Page 12:  There were some misleading phrases in the result section. To give one example: 'control analyses was slightly above change' - this sounds like a close to non-significant effect, but it was indeed a highly significant effect of p<0.001. Please revise.

This phrase was part of the prediction decoding analysis and has therefore been removed.

(10) Sample size: How was the sample size of the study be determined (N=31)? Why did only a subgroup of participants perform the behavioral categorization task after the EEG recording? With a larger sample, it would have been interesting to test if participants who showed better learning (larger difference in reaction times between valid and invalid conditions) also showed higher decoding accuracies.

This has been clarified in the revised manuscript. In short, the larger sample size of N=31 was based on previous research; ten participants were initially tested as part of a pilot which was then expanded to include the categorisation task.

(11) I assume catch trials were removed before data analyses?

We have clarified that catch trials were indeed removed prior to analyses.

(12) Page 23, 1st line: 'In each, the decoder...' Something is missing here.

Thank you for bringing this to our attention, this sentence has now been rephrased as “In both valid and invalid analyses” in the revised manuscript.

Discussion

(1) The analysis over multiple trials showed dampening within the first 15 min followed by sharpening. I found the discussion of this finding very lengthy and speculative (page 17). I recommend shortening this part and providing only the main arguments that could stimulate future research.

Thank you for the suggestion. Since Reviewer 3 has requested additional details in this part of the discussion, we have opted to keep this paragraph in the manuscript. However, we have also made it clearer that this section is relatively speculative and the arguments provided for the across trials dynamics are meant to stimulate further research.

(2) As this task is purely perceptual, the results support the OPT for the area of visual perception. For action, different results have been reported. Suppression within-trial has been shown to be larger for expected than unexpected features of action targets and suppression even starts before the start of the movement without showing any evidence for sharpening ( e.g., Fuehrer et al., 2022, PNAS). For suppression across trials, it has been found that suppression decreases over the course of learning to associate a sensory consequence to a specific action (e.g., Kilteni et al., 2019, ELife). Therefore, expectation suppression might function differently in perception and action (an area that still requires further research). Please clarify the scope of your study and results on perceptual expectations in the introduction, discussion, and abstract.

We have clarified the scope of the study in the revised manuscript.

Figures

(1) Figure 1A: Add 't' to the arrow to indicate time.

This has been rectified.

(2) Figure 3:  In the figure caption, sensory and memory decoding seem to be mixed up. Please correct. Please add what the dashed horizontal line indicates.

Thank you for bringing this to our attention, this has been rectified.

Reviewer 3  (Recommendations for the authors):

I applaud the authors for a well-written introduction and an excellent summary of a complicated topic, giving fair treatment to the different accounts proposed in the literature. However, I believe a few additional studies should be cited in the Introduction, particularly time-resolved studies such as Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011. This would provide the reader with a broader picture of the current state of the literature, as well as point the reader to critical time-resolved studies that did not find evidence in support of OPT, which are important to consider in the interpretation of the present results.

The introduction has been expanded to include the aforementioned studies in the revised manuscript.

Given previous neuroimaging studies investigating the present phenomenon, including with time-resolved measures (e.g. Kok et al., 2017; Han et al., 2019; Kumar et al., 2017; Meyer & Olson 2011), why do the authors think that their data, design, or analysis allowed them to find support for OPT but not previous studies? I do not see obvious modifications to the paradigm, data quantity or quality, or the analyses that would suggest a superior ability to test OPT predictions compared to previous studies. Given concerns regarding the data analyses (see points below), I think it is essential to convincingly answer this question to convince the reader to trust the present results.

The most obvious alteration to the paradigm is the use of non-repeated stimuli. Each of the above time-resolved studies utilised repeated stimuli (either repeated, identical stimuli, or paired stimuli where pairings are changed but the pool of stimuli remains the same), allowing for RS to act as a confound as exemplars are still presented multiple times. By removing this confound, it is entirely plausible that we may find different time-resolved results given that it has been shown that RS and ES are separable in time (Todorovic & de Lange, 2012). We also test during learning rather than training participants on the task beforehand. By foregoing a training session, we are better equipped to assess OPT predictions as they emerge. In our across-trial results, learning appears to take place after approximately 15 minutes or 432 trials, at which point dampening reverses to sharpening. Had we trained the participants prior to testing, this effect would have been lost.

What is actually decoded in the "prediction decoding" analysis? The authors state that it is "decoding the predictable trailing images based on the leading images" (p.11). The associated chance level (Figure 2E) is indicated as 50%. This suggests that the classes separated by the SVM are T6 vs T7. How this was done is however unclear. For each leading image decoding the predictable trailing images should be equivalent to decoding validity (as there are only 2 possible trailing images, where one is the valid and the other the invalid image). How is it then possible that the analysis is performed separately for valid and invalid trials? Are the authors simply decoding which leading image was shown, but combine L1+L2 and L4+L5 into one class respectively? If so, this needs to be better explained in the manuscript. Moreover, the resulting decoder would in my opinion not decode the predicted image, but instead learn to dissociate the representation of L1+L2 from L4+L5, which may also explain why the time course of the prediction peaks during the leading image stimulus-response, which is rather different compared to previous studies decoding (prestimulus) predictions (e.g. Kok et al. 2017). If this is indeed the case, I find it doubtful that this analysis relates to prediction. Instead for the prediction analysis to be informative about the predicted image the authors should, in my opinion, train the decoder on the representation of trailing images and test it during the prestimulus interval.

As mentioned above, the prediction decoding analysis has been removed from the manuscript. The prediction decoding analysis was intended as a sanity check, as validity information was not yet available to participants.

Related to the point above, were the leading/trailing image categories and their mapping to L1, L2, etc. in Figure 1B fixed across subjects? I.e. "'beach' and 'barn' as 'Leading' categories would result in 'church' as a 'Trailing' category with 75% validity" (p.20) for all participants? If so, this poses additional problems for the interpretation of the analysis discussed in the point above, as it may invalidate the control analyses depicted in Figure 2E, as systematic differences and similarities in the leading image categories could account for the observed results.

Image categories and their mapping were indeed fixed across participants. While this may result in physical differences and similarities between images influencing results, counterbalancing categories across participants would not have addressed this issue. For example, had we swapped “beach” with “barn” in another participant, physical differences between images may still be reflected in the prediction decoding. On the other hand, counterbalancing categories across trials was not possible given our aim of examining the initial stages of learning over trials. Had we changed the mappings of categories throughout the experiment for each participant, we would have introduced reversal learning and nullified our ability to examine the initial stages of learning under flat priors. In any case, the prediction decoding analysis has been removed from the manuscript, as outlined above.

Why was the neutral condition L3 not used for prediction decoding? After all, if during prediction decoding both the valid and invalid image can be decoded, as suggested by the authors, we would also expect significant decoding of T8/T9 during the L3 presentation.

In the neutral condition, L3 was followed by T8 vs. T9 with 50% probability, precluding prediction decoding. While this could have served as an additional control analysis for EEG-based decoding, we have opted for removing prediction decoding from the analysis. However, in response to the other Reviewers’ comments, the neutral condition has now been included in the behavioral analysis.

The following concern may arise due to a misunderstanding of the analyses, but I found the results in Figures 2C and 2E concerning. If my interpretation is correct, then these results suggest that the leading image itself can only be decoded with ~33% accuracy (25% chance; i.e. ~8% above chance decoding). In contrast, the predicted (valid or invalid) image during the leading image presentation can be decoded with ~62% accuracy (50% chance; i.e. ~12% above chance decoding). Does this seem reasonable? Unless I am misinterpreting the analyses, it seems implausible to me that a prediction but not actually shown image can be better decoded than an on-screen image. Moreover, to my knowledge studies reporting decoding of predictions can (1) decode expectations just above chance level (e.g. Kok et al., 2017; which is expected given the nature of what is decoded) and (2) report these prestimulus effects shortly before the anticipated stimulus onset, and not coinciding with the leading image onset ~800ms before the predicted stimulus onset. For the above reasons, the key results reported in the present manuscript seem implausible to me and may suggest the possibility of problems in the training or interpretation of the decoding analysis. If I misunderstood the analyses, the analysis text needs to be refined. If I understood the analyses correctly, at the very least the authors would need to provide strong support and arguments to convince the reader that the effects are reliable (ruling out bias and explaining why predictions can be decoded better than on-screen stimuli) and sensible (in the context of previous studies showing different time-courses and results).

As explained above, we have addressed this concern by performing an additional analysis, implementing decoding based on image pixel values. Indeed we could not rule out the possibility that “prediction” decoding reflected stimulus differences between leading images.

Relatedly, the authors use the prestimulus interval (-200 ms to 0 ms before predicted stimulus onset) as the baseline period. Given that this period coincides with prestimulus expectation effects ( Kok et al., 2017) , would this not result in a bias during trailing image decoding? In other words, the baseline period would contain an anticipatory representation of the expected stimulus ( Kok et al., 2017) , which is then subtracted from the subsequent EEG signal, thereby allowing the decoder to pick up on this "negative representation" of the expected image. It seems to me that a cleaner contrast would be to use the 200ms before leading image onset as the baseline.

The analysis of trailing images aimed at testing specific hypotheses related to differences between decoding accuracy in valid vs. invalid trials. Since the baseline was by definition the same for both kinds of trials (since information about validity only appears at the onset of the trailing image), changing the baseline would not affect the results of the analysis. Valid and invalid trials would have the same prestimulus effect induced by the leading image.

Again, maybe I misunderstood the analyses, but what exactly are the statistics reported on p. 11 onward? Why is the reported Tmax identical for multiple conditions, including the difference between conditions? Without further information this seems highly unlikely, further casting doubts on the rigor of the applied methods/analyses. For example: "In the sensory decoding analysis based on leading images, decoding accuracy was above chance for both valid (Tmax= 2.76, pFWE < 0.001) and invalid trials (Tmax= 2.76, pFWE < 0.001) from 100 ms, with no significant difference between them (Tmax= 2.76, pFWE > 0.05) (Fig. 2C)" (p.11).

Thank you for bringing this to our attention. As previously mentioned, this copy error has been rectified in the revised manuscript.

Relatedly, the statistics reported below in the same paragraph also seem unusual. Specifically, the Tmax difference between valid and invalid conditions seems unexpectedly large given visual inspection of the associated figure: "The decoding accuracy of both valid (Tmax = 2.76, pFWE < 0.001) and invalid trials (Tmax = 14.903, pFWE < 0.001)" (p.12). In fact, visual inspection suggests that the largest difference should probably be observed for the valid not invalid trials (i.e. larger Tmax).

This copy error has also been rectified in the revised manuscript.

Moreover, multiple subsequent sections of the Results continue to report the exact same Tmax value. I will not list all appearances of "Tmax = 2.76" here but would recommend the authors carefully check the reported statistics and analysis code, as it seems highly unlikely that >10 contrasts have exactly the same Tmax. Alternatively, if I misunderstand the applied methods, it would be essential to better explain the utilized method to avoid similar confusion in prospective readers.

This error has also now been rectified. As mentioned above the prediction decoding analysis has been removed.

I am not fully convinced that Figures 3A/B and the associated results support the idea that early learning stages result in dampening and later stages in sharpening. The inference made requires, in my opinion, not only a significant effect in one-time bin and the absence of an effect in other bins. Instead to reliably make this inference one would need a contrast showing a difference in decoding accuracy between bins, or ideally an analysis not contingent on seemingly arbitrary binning of data, but a decrease ( or increase) in the slope of the decoding accuracy across trials. Moreover, the decoding analyses seem to be at the edge of SNR, hence making any interpretation that depends on the absence of an effect in some bins yet more problematic and implausible.

Thank you for the helpful suggestion. As previously mentioned we fitted a logarithmic model to quantify the change of the decoding benefit over trials, then found the trial index for which the change of the logarithmic fit was < 0.1 %. Given the results of this analysis and to ensure a sufficient number of trials, we focussed our further analyses on bins 1-2 . This is explained in more detail in the revised manuscript.

Relatedly, based on the literature there is no reason to assume that the dampening effect disappears with more training, thereby placing more burden of proof on the present results. Indeed, key studies supporting the dampening account (including human fMRI and MEG studies, as well as electrophysiology in non-human primates) usually seem to entail more learning than has occurred in bin 2 of the present study. How do the authors reconcile the observation that more training in previous studies results in significant dampening, while here the dampening effect is claimed to disappear with less training?

The discussion of these findings has been expanded on in the revised manuscript. As previously outlined, many of the studies supporting dampening did not explicitly test the effect of learning as they emerge, nor did they control for RS to the same extent.

The Methods section is quite bare bones. This makes an exact replication difficult or even impossible. For example, the sections elaborating on the GLM and cluster-based FWE correction do not specify enough detail to replicate the procedure. Similarly, how exactly the time points for significant decoding effects were determined is unclear (e.g., p. 11). Relatedly, the explanation of the decoding analysis, e.g. the choice to perform PCA before decoding, is not well explained in the present iteration of the manuscript. Additionally, it is not mentioned how many PCs the applied threshold on average resulted in.

Thank you for this suggestion, we have described our methods in more detail.

To me, it is unclear whether the PCA step, which to my knowledge is not the default procedure for most decoding analyses using EEG, is essential to obtain the present results. While PCA is certainly not unusual, to my knowledge decoding of EEG data is frequently performed on the sensor level as SVMs are usually capable of dealing with the (relatively low) dimensionality of EEG data. In isolation this decision may not be too concerning, however, in combination with other doubts concerning the methods and results, I would suggest the authors replicate their analyses using a conventional decoding approach on the sensory level as well.

Thank you for this suggestion, we have explained our decision to use PCA in the revised manuscript.

Several choices, like the binning and the focus on bins 1-2 seem rather post-hoc. Consequently, frequentist statistics may strictly speaking not be appropriate. This further compounds above mentioned concerns regarding the reliability of the results.

The reasoning behind our decision to focus on bins 1-2 is now explained in more detail in the revised manuscript.

A notable difference in the present study, compared to most studies cited in the introduction motivating the present experiment, is that categories instead of exemplars were predicted.

This seems like an important distinction to me, which surprisingly goes unaddressed in the Discussion section. This difference might be important, given that exemplar expectations allow for predictions across various feature levels (i.e., even at the pixel level), while category predictions only allow for rough (categorical) predictions.

The decision to use categorical predictions over exemplars lies in the issue of RS, as it is impossible to control for RS while repeating stimuli over many trials. This has been discussed in more detail in the revised manuscript.

While individually minor problems, I noticed multiple issues across several figures or associated figure texts. For example: Figure 1C only shows valid and invalid trials, but the figure text mentions the neutral condition. Why is the neutral condition not depicted but mentioned here? Additionally, the figure text lacks critical information, e.g. what the asterisk represents. The error shading in Figure 2 would benefit from transparency settings to not completely obscure the other time-courses. Increasing the figure content and font size within the figure (e.g. axis labels) would also help with legibility (e.g. consider compressing the time-course but therefore increasing the overall size of the figure). I would also recommend using more common methods to indicate statistical significance, such as a bar at the bottom of the time-course figure typically used for cluster permutation results instead of a box. Why is there no error shading in Figure 2A but all other panels? Fig 2C-F has the y-axis label "Decoding accuracy (%)" but certainly the y-axis, ranging roughly from 0.2 to 0.7, is not in %. The Figure 3 figure text gives no indication of what the error bars represent, making it impossible to interpret the depicted data. In general, I would recommend that the authors carefully revisit the figures and figure text to improve the quality and complete the information.

Thank you for the suggestions. Figure 1C now includes the neutral condition. Asterisks denote significant results. The font size in Figure 2C-E has been increased. The y-axis on Figure 2C-E has been amended to accurately reflect decoding accuracy in percentage. Figure 2A has error shading, however, the error is sufficiently small that the error shading is difficult to see. The error bars in Figure 3 have been clarified.

Given the choice of journal (eLife), which aims to support open science, I was surprised to find no indication of (planned) data or code sharing in the manuscript.

Plans for sharing code/data are now outlined in the revised manuscript.

While it is explained in sufficient detail later in the Methods section, it was not entirely clear to me, based on the method summary at the beginning of the Results section, whether categories or individual exemplars were predicted. The manuscript may benefit from clarifying this at the start of the Results section.

Thank you for this suggestion, following this and suggestions from other reviewers, the experimental paradigm and the mappings between categories has been further explained in the revised manuscript, to make it clearer that predictions are made at the categorical level.

"Unexpected trials resulted in a significantly increased neural response 150 ms after image onset" (p.9). I assume the authors mean the more pronounced negative deflection here. Interpreting this, especially within the Results section as "increased neural response" without additional justification may stretch the inferences we can make from ERP data; i.e. to my knowledge more pronounced ERPs could also reflect increased synchrony. That said, I do agree with the authors that it is likely to reflect increased sensory responses, it would just be useful to be more cautious in the inference.

Thank you for the interesting comment, this has been rephrased as a “more pronounced negative deflection” in the revised manuscript.

Why was the ERP analysis focused exclusively on Oz? Why not a cluster around Oz? For object images, we may expect a rather wide dipole.

Feuerriegel et al (2021) have outlined issues questioning the robustness of univariate analyses for ES, as such we opted for a targeted ROI approach on the channel showing peak amplitude of the visually evoked response (Fig. 2B). More details on this are in the revised manuscript.           

How exactly did the authors perform FWE? The description in the Method section does not appear to provide sufficient detail to replicate the procedure.

FWE as implemented in SPM is a cluster-based method of correcting for multiple comparisons using random field theory. We have explained our thresholding methods in more detail in the revised manuscript.

If I misunderstand the authors and they did indeed perform standard cluster permutation analyses, then I believe the results of the timing of significant clusters cannot be so readily interpreted as done here (e.g. p.11-12); see: Maris & Oostenveld 2007; Sassenhagen & Dejan 2019.

All statistics were based on FWE under random field theory assumptions (as implemented in SPM) rather than on cluster permutation tests (as implemented in e.g.  Fieldtrip)

Why did the authors choose not to perform spatiotemporal cluster permutation for the ERP results?

As mentioned above, we opted to target our ERP analyses on Oz due to controversies in the literature regarding univariate effects of ES (Feuerriegel et al., 2021).

Some results, e.g. on p.12 are reported as T29 instead of Tmax. Why?

As mentioned above, prediction decoding analyses have been removed from the manuscript.

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Según ese paper y estrategia son 3 modelos? no 4? configural, + thresholds, + cargas pero y los errores no?

Reviewer #2 (Public review):

The revised manuscript by Altan et al. includes some real improvements to the visualizations and explanations of the authors' thesis statement with respect to fMRI measurements of pRF sizes. In particular, the deposition of the paper's data has allowed me to probe and refine several of my previous concerns. While I still have major concerns about how the data are presented in the current draft of the manuscript, my skepticism about data quality overall has been much alleviated. Note that this review focuses almost exclusively on the fMRI data as I was satisfied with the quality of the psychophysical data and analyses in my previous review.

Major Concerns

(I) Statistical Analysis

In my previous review, I raised the concern that the small sample size combined with the noisiness of the fMRI data, a lack of clarity about some of the statistics, and a lack of code/data likely combine to make this paper difficult or impossible to reproduce as it stands. The authors have since addressed several aspects of this concern, most importantly by depositing their data. However their response leaves some major questions, which I detail below.

First of all, the authors claim in their response to the previous review that the small sample size is not an issue because large samples are not necessary to obtain "conclusive" results. They are, of course, technically correct that a small sample size can yield significant results, but the response misses the point entirely. In fact, small samples are more likely than large samples to erroneously yield a significant result (Button et al., 2013, DOI:10.1038/nrn3475), especially when noise is high. The response by the authors cites Schwarzkopf & Huang (2024) to support their methods on this front. After reading the paper, I fail to see how it is at all relevant to the manuscript at hand or the criticism raised in the previous review. Schwarzkopf & Huang propose a statistical framework that is narrowly tailored to situations where one is already certain that some phenomenon (like the adaptation of pRF size to spatial frequency) either always occurs or never occurs. Such a framework is invalid if one cannot be certain that, for example, pRF size adapts in 98% of people but not the remaining 2%. Even if the paper were relevant to the current study, the authors don't cite this paper, use its framework, or admit the assumptions it requires in the current manuscript. The observation that a small dataset can theoretically lead to significance under a set of assumptions not appropriate for the current manuscript is not a serious response to the concern that this manuscript may not be reproducible.

To overcome this concern, the authors should provide clear descriptions of their statistical analyses and explanations of why these analyses are appropriate for the data. Ideally, source code should be published that demonstrates how the statistical tests were run on the published data. (I was unable to find any such source code in the OSF repository.) If the effects in the paper were much stronger, this level of rigor might not be strictly necessary, but the data currently give the impression of being right near the boundary of significance, and the manuscript's analyses needs to reflect that. The descriptions in the text were helpful, but I was only able to approximately reproduce the authors analyses based on these descriptions alone. Specifically, I attempted to reproduce the Mood's median tests described in the second paragraph of section 3.2 after filtering the data based on the criteria described in the final paragraph of section 3.1. I found that 7/8 (V1), 7/8 (V2), 5/8 (V3), 5/8 (V4), and 4/8 (V3A) subjects passed the median test when accounting for the (40) multiple comparisons. These results are reasonably close to those reported in the manuscript and might just differ based on the multiple comparisons strategy used (which I did not find documented in the manuscript). However, Mood's median test does not test the direction of the difference-just whether the medians are different-so I additionally required that the median sigma of the high-adapted pRFs be greater than that of the low-adapted pRFs. Surprisingly, in V1 and V3, one subject each (not the same subject) failed this part of the test, meaning that they had significant differences between conditions but in the wrong direction. This leaves 6/8 (V1), 7/8 (V2), 4/8 (V3), 5/8 (V4), and 4/8 (V3A) subjects that appear to support the authors' conclusions. As the authors mention, however, this set of analyses runs the risk of comparing different parts of cortex, so I also performed Wilcox signed-rank tests on the (paired) vertex data for which both the high-adapted and low-adapted conditions passed all the authors' stated thresholds. These results largely agreed with the median test (only 5/8 subjects significant in V1 but 6/8 in in V3A, other areas the same, though the two tests did not always agree which subjects had significant differences). These analyses were of course performed by a reviewer with a reviewer's time commitment to the project and shouldn't be considered a replacement for the authors' expertise with their own data. If the authors think that I have made a mistake in these calculations, then the best way to refute them would be to publish the source code they used to threshold the data and to perform the same tests.

Setting aside the precise values of the relevant tests, we should also consider whether 5 of 8 subjects showing a significant effect (as they report for V3, for example) should count as significant evidence of the effect? If one assumes, as a null hypothesis, that there is no difference between the two conditions in V3 and that all differences are purely noise, then a binomial test across subjects would be appropriate. Even if 6 of 8 subjects show the effect, however (and ignoring multiple comparisons), the p-value of a one-sided binomial test is not significant at the 0.05 level (7 of 8 subjects is barely significant). Of course, a more rigorous way to approach this question could be something like an ANOVA, and the authors use an ANOVA analysis of the medians in the paragraph following their use of Mood's median test. However, ANOVA assumes normality, and the authors state in the previous paragraph that they employed Mood's median test because "the distribution of the pRF sizes is zero-bounded and highly skewed" so this choice does not make sense. The Central Limits Theorem might be applied to the medians in theory, but with only 8 subjects and with an underlying distribution of pRF sizes that is non-negative, the relevant data will almost certainly not be normally distributed. These tests should probably be something like a Kruskal-Wallis ANOVA on ranks.

All of the above said, my intuition about the data is currently that there are significant changes to the adapted pRF size in V2. I am not currently convinced that the effects in other visual areas are significant, and I suspect that the paper would be improved if authors abandoned their claims that areas other than V2 show a substantial effect. Importantly, I don't think this causes the paper to lose any impact-in fact, if the authors agree with my assessments, then the paper might be improved by focusing on V2. Specifically, the authors' already discuss psychophysical work related to the perception of texture on pages 18 and 19 and link it to their results. V2 is also implicated in the perception of texture (see, for example, Freeman et al., 2013; DOI:10.1038/nn.3402; Ziemba et al., 2016, DOI:10.1073/pnas.1510847113; Ziemba et al., 2019; DOI:10.1523/JNEUROSCI.1743-19.2019) and so would naturally be the part of the visual cortex where one might predict that spatial frequency adaptation would have a strong effect on pRF size. This neatly connects the psychophysical and imaging sides of this project and could make a very nice story out of the present work.

(II) Visualizations

The manuscript's visual evidence regarding the pRF data also remains fairly weak (but I found the pRF size comparisons in the OSF repository and Figure S1 to be better evidence-more in the next paragraph). The first line of the Results section still states, "A visual inspection on the pRF size maps in Figure 4c clearly shows a difference between the two conditions, which is evident in all regions." As I mentioned in my previous review, I don't agree with this claim (specifically, that it is clear). My impression when I look at these plots is of similarity between the maps, and, where there is dissimilarity, of likely artifacts. For example, the splotch of cortex near the upper vertical meridian (ventral boundary) of V1 that shows up in yellow in the upper plot but not the lower plot also has a weirdly high eccentricity and a polar angle near the opposite vertical meridian: almost certainly not the actual tuning of that patch of cortex. If this is the clearest example subject in the dataset, then the effect looks to me to be very small and inconsistently distributed across the visual areas. That said, I'm not convinced that the problem here is the data-rather, I think it's just very hard to communicate a small difference in parameter tuning across a visual area using this kind of side-by-side figure. I think that Figure S2, though noisy (as pRF maps typically are), is more convincing than Figure 4c, personally. For what it's worth, when looking at the data myself, I found that plotting log(𝜎(H) / 𝜎(L)), which will be unstable when noise causes 𝜎(H) or 𝜎(L) to approach zero, was less useful than plotting plotting (𝜎(H) - 𝜎(L)) / (𝜎(H) + 𝜎(L)). This latter quantity will be constrained between -1 and 1 and shows something like a proportional change in the pRF size (and thus should be more comparable across eccentricity).

In my opinion, the inclusion of the pRF size comparison plots in the OSF repository and Figure S1 made a stronger case than any of the plots of the cortical surface. I would suggest putting these on log-log plots since the distribution of pRF size (like eccentricity) is approximately exponential on the cortical surface. As-is, it's clear in many plots that there is a big splotch of data in the compressed lower left corner, but it's hard to get a sense for how these should be compared to the upper right expanse of the plots. It is frequently hard to tell whether there is a greater concentration of points above or below the line of equality in the lower left corner as well, and this is fairly central to the paper's claims. My intuition is that the upper right is showing relatively little data (maybe 10%?), but these data are very emphasized by the current plots.
The authors might even want to consider putting a collection of these scatter-plots (or maybe just subject 007, or possible all subjects' pRFs on a single scatter-plot) in the main paper and using these visualizations to provide intuitive supporting for the main conclusions about the fMRI data (where the manuscript currently use Figure 4c for visual intuition).

Minor Comments

(1) Although eLife does not strictly require it, I would like to see more of the authors' code deposited along with the data (especially the code for calculating the statistics that were mentioned above). I do appreciate the simulation code that the authors added in the latest submission (largely added in response to my criticism in the previous reviews), and I'll admit that it helped me understand where the authors were coming from, but it also contains a bug and thus makes a good example of why I'd like to see more of the authors' code. If we set aside the scientific question of whether the simulation is representative of an fMRI voxel (more in Minor Comment 5, below), Figures 1A and the "AdaptaionEffectSimulated.png" file from the repository (https://osf.io/d5agf) imply that only small RFs were excluded in the high-adapted condition and only large RFs were excluded in the low-adapted condition. However, the script provided (SimlatePrfAdaptation.m: https://osf.io/u4d2h) does not do this. Lines 7 and 8 of the script set the small and large cutoffs at the 30th and 70th percentiles, respectively, then exclude everything greater than the 30th percentile in the "Large RFs adapted out" condition (lines 19-21) and exclude anything less than the 70th percentile in the "Small RFs adapted out" condition (lines 27-29). So the figures imply that they are representing 70% of the data but they are in fact representing only the most extreme 30% of the data. (Moreover, I was unable to run the script because it contains hard-coded paths to code in someone's home directory.) Just to be clear, these kinds of bugs are quite common in scientific code, and this bug was almost certainly an honest mistake.

(2) I also noticed that the individual subject scatter-plots of high versus low adapted pRF sizes on the OSF seem to occasionally have a large concentration of values on the x=0 and y=0 axes. This isn't really a big deal in the plots, but the manuscript states that "we denoised the pRF data to remove artifactual vertices where at least one of the following criteria was met: (1) sigma values were equal to or less than zero ..." so I would encourage the authors to double-check that the rest of their analysis code was run with the stated filtering.

(3) The manuscript also says that the median test was performed "on the raw pRF size values". I'm not really sure what the "raw" means here. Does this refer to pRF sizes without thresholding applied?

(4) The eccentricity data are much clearer now with the additional comments from the authors and the full set of maps; my concerns about this point have been met.

(5) Regarding the simulation of RFs in a voxel (setting aside the bug), I will admit both to hoping for a more biologically-grounded situation and to nonetheless understanding where the authors are coming from based on the provided example. What I mean by biologically-grounded: something like, assume a 2.5-mm isotropic voxel aligned to the surface of V1 at 4{degree sign} of eccentricity; the voxel would span X to Y degrees of eccentricity, and we predict Z neurons with RFs in this voxel with a distribution of RF sizes at that eccentricity from [reference], etc. eventually demonstrating a plausible pRF size change commensurate to the paper's measurements. I do think that a simulation like this would make the paper more compelling, but I'll acknowledge that it probably isn't necessary and might be beyond the scope here.

Author Response:

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

Reviewer #1 (Public Review):

We thank the reviewer for their careful evaluation and positive comments. 

Adaptation paradigm

“why is it necessary to use an *adaptation* paradigm to study the link between SF tuning and pRF estimation? Couldn't you just use pRF bar stimuli with varying SFs?” 

We thank the reviewer for this question. First, by using adaptation we can infer the correspondence between the perceptual and the neuronal adaptation to spatial frequency. We couldn’t draw any inference about perception if we only varied the SF inside the bar. More importantly, while changing the SF inside the bar might help drive different neuronal populations, this is not guaranteed. As we touched on in our discussion, responses obtained from the mapping stimuli are dominated by complex processing rather than the stimulus properties alone. A considerable proportion of the retinotopic mapping signal is probably simply due to spatial attention to the bar (de Haas & Schwarzkopf, 2018; Hughes et al., 2019). So, adaptation is a more targeted way to manipulate different neuronal populations.

Other pRF estimates: polar angle and eccentricity 

We included an additional plot showing the polar angle for both adapter conditions (Figure S4), as well as participant-wise scatter plots comparing raw pRF size, eccentricity, and polar angle between two adapter conditions (available in shared data repository). In line with previous work on the reliability of pRF estimates (van Dijk, de Haas, Moutsiana, & Schwarzkopf, 2016; Senden, Reithler, Gijsen, & Goebel, 2014), both polar angle and eccentricity maps are very stable between the two adaptation conditions. 

Variability in pRF size change

As the reviewer pointed out, the pRF size changes show some variability across eccentricities, and ROIs (Figure 5A and 5B). It is likely that the variability could relate to the varying tuning properties of different regions and eccentricities for the specific SF we used in the mapping stimulus. So one reason V2 is most consistent could be that the stimulus is best matched for the tuning there. However, what factors contribute to this variability is an interesting question that will require further study. 

Other recommendations

We have addressed the other recommendations of the reviewer with one exception. The reviewer suggested we should comment on the perceived contrast decrease after SF adaptation (as seen in Figure 6B) in the main text. However, since we refer the readers to the supplementary analyses (Supplementary section S8) where we discuss this in detail, we chose to keep this aspect unchanged to avoid overcomplicating the main text.

Reviewer #2 (Public Review):

We thank the reviewer for their comments - we improved how we report key findings which we hope will clarify matters raised by the reviewer.

RF positions in a voxel

The reviewer’s comments suggest that they may have misunderstood the diagram (Figure 1A) illustrating the theoretical basis of the adaptation effect, likely due to us inadvertently putting the small RFs in the middle of the illustration. We changed this figure to avoid such confusion.

Theoretical explanation of adaptation effect

The reviewer’s explanation for how adaptation should affect the size of pRF averaging across individual RFs is incorrect. When selecting RFs from a fixed range of semi-uniformly distributed positions (as in an fMRI voxel), the average position of RFs (corresponding to pRF position) is naturally near the center of this range. The average size (corresponding to pRF size) reflects the visual field coverage of these individual RFs. This aggregate visual field coverage thus also reflects the individual sizes. When large RFs have been adapted out, this means the visual field coverage at the boundaries is sparser, and the aggregate pRF is therefore smaller. The opposite happens when adapting out the contribution of small RFs. We demonstrate this with a simple simulation at this OSF link: https://osf.io/ebnky/. The pRF size of the simulated voxels illustrate the adaptation effect should manifest precisely as we hypothesized.

Figure S2

It is not actually possible to compare R² between regions by looking at Figure S2 because it shows the pRF size change, not R². Therefore, the arguments Reviewer #2 made based on their interpretation of the figure are not valid. Just as the reviewer expected, V1 is one of the brain regions with good pRF model fits. We included normalized and raw R² maps to make this more obvious to the readers.

V1 appeared essentially empty in that plot primarily due to the sigma threshold we selected, which was unintentionally more conservative than those applied in our analyses and other figures. We apologize for this mistake. We corrected it in the revised version by including a plot with the appropriate sigma threshold.

Thresholding details 

Thresholding information was included in our original manuscript; however, we included more information in the figure captions to make it more obvious.

2D plots replaced histograms

We thank the reviewer for this suggestion. The original manuscript contained histograms showing the distribution of pRF size for both adaptation conditions for each participant and visual area (Figure S1). However, we agree that 2D plots better communicate the difference in pRF parameters between conditions. So we moved the histogram plots to the online repository, and included scatter plots with a color scheme revealing the 2D kernel density.

We chose to implement 2D kernel density in scatter plots to display the distribution of individual pRF sizes transparently.

(proportional) pRF size-change map 

The reviewer requests pRF size difference maps. Figure S2 in fact demonstrates the proportional difference between the pRF sizes of the two adaptation conditions. Instead of simply taking the difference, we believe showing the proportional change map is more sensible because overall pRF size varies considerably between visual regions. We explained this more clearly in our revision. 

pRF eccentricity plot 

“I suspect that the difference in PRF size across voxels correlates very strongly with the difference in eccentricity across voxels.”

Our original manuscript already contained a supplementary plot (Figure S4 B, now Figure S4 C) comparing the eccentricity between adapter conditions, showing no notable shift in eccentricities except in V3A - but that is a small region and the results are generally more variable. In addition, we included participant-wise plots in the online repository, presenting raw comparisons of pRF size, eccentricity, and polar angle estimates between adaptation conditions. These 2D plots provide further evidence that the SF adapters resulted in a change in pRF size, while eccentricity and polar angle estimates did not show consistent differences.  

To the reviewer’s point, even if there were an appreciable shift in eccentricity between conditions (as they suggest may have happened for the example participant we showed), this does not mean that the pRF size effect is “due [...] to shifts in eccentricity.” Parameters in a complex multi-dimensional model like the pRF are not independent. There is no way of knowing whether a change in one parameter is causally linked with a change in another. We can only report the parameter estimates the model produces. 

In fact, it is conceivable that adaptation causes both: changes in pRF size and eccentricity. If more central or peripheral RFs tend to have smaller or larger RFs, respectively, then adapting out one part of the distribution will shift the average accordingly. However, as we already established, we find no compelling evidence that pRF eccentricity changes dramatically due to adaptation, while pRF size does.

Other recommendations

We have addressed the other recommendations of the reviewer, except for the y-axis alignment. Different regions in the visual hierarchy naturally vary substantially in pRF size. Aligning axes would therefore lead to incorrect visual inferences that (1) the absolute pRF sizes between ROIs are comparable, and (2) higher regions show the effect most

prominently. However, for clarity, we now note this scale difference in our figure captions. Finally, as mentioned earlier, we also present a proportional pRF size change map to enable comparison of the adaptation effect between regions.

Reviewer #3 (Public Review):

We thank the reviewer for their comments.

pRF model

Top-up adapters were not modelled in our analyses because they are shared events in all TRs, critically also including the “blank” periods, providing a constant source of signal. Therefore modelling them separately cannot meaningfully change the results. However, the reviewer makes a good suggestion that it would be useful to mention this in the manuscript, so we added a discussion of this point in Section 3.1.5.

pRF size vs eccentricity

We added a plot showing pRF size in the two adaptation conditions (in addition to the pRF size difference) as a function of eccentricity.

Correlation with behavioral effect

In the original manuscript, we pointed out why the correlation between the magnitude of the behavioral effect and the pRF size change is not an appropriate test for our data. First, the reviewer is right that a larger sample size would be needed to reliably detect such a between-subject correlation. More importantly, as per our recruitment criteria for the fMRI experiment, we did not scan participants showing weak perceptual effects. This limits the variability in the perceptual effect and makes correlation inapplicable.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity (Required)):*

As stated by the authors in the introduction, the RNA-binding protein Sxl is foundational to understanding sex determination in Drosophila. Sxl has been extensively studied as the master regulator of female sex determination in the soma, where it is known to initiate an alternative splicing cascade leading to the expression of DsxF. Additionally, Sxl has been shown to be responsible for keeping X chromosome dosage compensation off in females, while males hyperactivate their X chromosome. While these roles have been well defined, the authors explore an aspect of Sxl that is quite separate from its role as master regulator of female fate. They describe Sxl-RAC, a Sxl isoform that is expressed in the male and female nervous system. Using several genomic techniques, the authors conclude that the Sxl-RAC isoform associates with chromatin in a similar pattern to the RNA polymerase II/III subunit, Polr3E, and Sxl depends on Polr3E for chromatin-association. Further, neuronal loss of Sxl causes changes in lifetime and geotaxis in a similar manner as loss of Polr3E. The work is thorough and significant and should be appropriate for publication if a few issues can be addressed.

Major Concerns:*

* 1) How physiological is the Sxl chromatin-association assay? As binding interactions are concentration-dependent, how similar is Sxl-DAM expression to wt Sxl expression in neurons? In addition, does the Sxl-DAM protein function as a wt Sxl protein? Does UAS-Sxl-DAM rescue any Sxl loss phenotypes?*

Author response:

As Reviewer 3 correctly notes, Targeted DamID relies on ribosomal re-initiation (codon slippage) to produce only trace amounts of the Dam-fusion protein. By design, this results in expression levels that are significantly lower than those of the endogenous protein. As such, the experiment can be interpreted within a near–wild-type context, rather than as an overexpression model. The primary aim of this experiment was to determine whether Sxl associates with chromatin, and our dataset provides clear evidence supporting such binding.

2) Is Polr3E chromatin-association also dependent on Sxl? They should do the reciprocal experiment to their examination of Sxl chromatin-association in Polr3E knockdown. This might also help address point 1-if wt Sxl is normally required for aspects of Polr3E chromatin binding, then concerns about whether the Sxl-DAM chromatin-association is real or artifactual would be assuaged.

Author response:

This is an interesting thought, however, if Sxl were required for Polr3E recruitment to RNA Pol III, then, in most male Drosophila melanogaster cells, Polr3E would not be incorporated, and males would not be viable (as it is essential for Pol III activity). While it is possible that there could be a subtle effect on Polr3E recruitment, such an experiment, would not alter the central conclusion of our study - that Sxl is recruited to chromatin (accessory to the Pol III complex) via Polr3E.

Minor concerns:

* The observed Sxl loss of function phenotypes are somewhat subtle (although perhaps any behavior phenotype at all is a plus). Did they try any other behaviour assays-courtship, learning/memory, anything else at all to test nervous system function?*

Author response:

Given the exploratory nature of this study, we focused on broader behavioural and transcriptional assays.

While well written, it is sometimes difficult to understand how the experiment was performed or what genotypes were used without looking into the methods sections. One example is they should describe the nature of the Sxl-DAM fusion protein clearly in the results.

Author response:

We will revise these sections to improve clarity and ensure there is no confusion.

* Reviewer #1 (Significance (Required)):

This manuscript represents a dramatic change in our thinking about the action of the Sex-lethal protein. Previously, Sxl was known as the master regulator of both sex determination and dosage compensation, and performed these roles as an RNA-binding protein affecting RNA splicing and translational regulation. Here, the authors describe a sex-non-specific role of Sxl in the male and female nervous system. Further, this activity appears independent of Sxl's RNA binding activity and instead Sxl functions as a chromatin-associating protein working with the RNA pol2/3 factor Polr3E to regulate gene expression. Thus, this represents a highly significant finding. *

Reviewer #2 (Evidence, reproducibility and clarity (Required)):*

Summary: In this paper, the authors report on an unexpected activity for Sex lethal (Sxl) (a known splicing regulator that functions in sex determination and dosage compensation) in binding to chromatin. They show, using DamID, that Sxl binds to approximately the same chromatin regions as Polr3E (a subunit of RNA Pol III). They show that this binding to chromatin is unaffected by mutations in the RNA binding domains or by deletions of either N or C terminal regions of the Sxl protein. This leads the authors to conclude that Sxl must bind to chromatin through some interacting protein working through the central region of the Sxl protein. They show that Sxl binding is dependent on Polr3E function. They show that male-specific neuronal knockdown of Sxl gives similar phenotypes to knockdown of Polr3E in terms of lethality and improved negative geotaxis. They show gene expression changes with knockdown of Sxl in male adult neurons - mainly that metabolic and pigmentation genes go down in expression. They also show that expression of a previously discovered male adult specific form of Sxl (that does not have splicing activity) in the same neurons also leads to changes in gene expression, including more upregulated than downregulated tRNAs. But they don't see (or don't show) that the same tRNA genes are down with knockdown of Sxl. Nonetheless, based on these findings, they suggest that Sxl plays an important role in regulating Pol III activity through the Polr3E subunit.

Major comments:

*

*To be honest, I'm not convinced that the conclusions drawn from this study are correct. The fact that every mutant form of Sxl shows the same result from the DamID labelling is a little concerning. I would like to see independent evidence of the SxlRac protein binding chromatin. *

Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

__Author Response: __

Regarding the reviewer’s overall concerns about the legitimacy of the Sxl binding data:

1. i) The fold differences between Dam-Sxl-mutants and the Dam-only control are very robust (up to 9 log2 fold change (500-fold change)), which is higher than what we observe with most transcription factors using Targeted DamID.

2. ii) We observed that Sxl binding was significantly reduced upon knockdown of Polr3E, confirming that the signal we observe is biologically specific and not due to technical noise or background. iii) If the concern relates to potential Sxl binding in non-neuronal tissues such as salivary glands, we would like to clarify that all DamID constructs were expressed under elav-GAL4, a pan-neuronal driver. Furthermore, dissections were performed to isolate larval brains, with salivary glands carefully removed. This ensures that chromatin profiles were derived from neuronal tissue exclusively.

3. iv) Salivary gland polytene chromosome staining with a Sxl antibody in a closely related species (Drosophila virilis) show __binding of Sxl to chromatin __in both sexes (Bopp et al., 1996). We will include more text in the revised manuscript to emphasise these points.

Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

Author Response:

Prior work in Drosophila virilis (where Sxl is also required for sex determination and Sxl-RAC is conserved) has already demonstrated Sxl-chromatin association (using a full-length Sxl antibody) in salivary glands using polytene chromosome spreads (Bopp et al., 1996). Binding is observed in both sexes and across the genome, reflecting our observations. We will incorporate this into the revised discussion to support the chromatin-binding role of Sxl across species.

There is a clear and long-overlooked precedent for Sxl's alternative, sex-independent roles, findings that have been largely overshadowed by the gene’s canonical function. Our study not only validates and extends these observations but also brings much-needed attention to this understudied aspect of fundamental biology.

Bopp D, Calhoun G, Horabin JI, Samuels M, Schedl P. Sex-specific control of Sex-lethal is a conserved mechanism for sex determination in the genus Drosophila. Development. 1996 Mar;122(3):971-82. doi: 10.1242/dev.122.3.971. PMID: 8631274.

I would like to see independent evidence of the SxlRac protein binding chromatin.

* *__Author Response: __

We do not believe this is necessary:

1. i) Our data demonstrated that a large N-terminal truncation of Sxl (removing far more of the N-terminal region than is absent in Sxl-RAC) does not impair chromatin binding.
2. ii) Our deletion experiments show that it is the central domain __of Sxl that is required for chromatin association (as removal of the N-or C-terminal domain has no effect). This central domain is __unaffected in Sxl-RAC. iii) Independent Y2H experiments have shown that it is exclusively the__ RBD-1 __(RNA binding domain 1) of the central domain of Sxl that interacts with Polr3E (Dong et al., 1999). Sxl-RAC contains this region, therefore will be recruited by Polr3E.

iv) Review 3 also believes that this is not necessary (see cross-review below) and highlights the robustness of the Y2H experiments performed by Dong et al., 1999.

• *

Also, given that their DamID experiments reveal that Sxl binds half of the genes encoded in the Drosophila genome, finding that it binds around half of the tRNA genes is perhaps not surprising.

__Author Response: __

Our data show that Sxl binds to a range of Pol III-transcribed loci, and this binding pattern supports the proposed model that Sxl plays a broader regulatory role in Pol III activity. Within these Pol III targets, tRNA genes represent a specific and biologically relevant subset. The emphasis on tRNAs is not to suggest they are the exclusive or primary targets of Sxl, but rather to__ highlight a functionally important class of Pol III-transcribed elements__ that align with the model we are proposing. We will revise the text to better reflect this framing and avoid any confusion regarding the scope of Sxl’s binding profile.

*I would like to see evidence beyond citing a 1999 yeast two-hybrid study that Sxl and Polr3E directly interact with one another. *

Author response:

We do not believe this is necessary (these points were also mentioned above):

1. i) The Dong et al., 1999 study was highly comprehensive in its characterisation of Sxl binding to Polr3E.
2. ii) Our DamID data provide strong complementary evidence for this interaction: knockdown of Polr3E robustly reduces Sxl’s recruitment to chromatin, strongly supporting the relevance of the interaction in vivo. iii) Review 3 highlights the robustness of the Y2H experiments performed by Dong et al., 1999.

In my opinion, the differences in lethality observed with loss of Sxl versus control are unlikely to be meaningful given the different genetic backgrounds. The similar defects in negative geotaxis could be meaningful, but I'm unsure how often this phenotype is observed. What other class of genes affect negative geotaxis? It's a little unclear why having reduced expression of metabolic and pigment genes or of tRNAs would improve neuronal function.

Author response:

While the differences in survival were indeed subtle, they were statistically significant and thus warranted inclusion. Our primary aim in this section was to demonstrate that knockdown of Sxl or Polr3E results in comparable behavioural and transcriptional phenotypes, suggesting overlapping functional roles. In this context, we believe the data were presented transparently and effectively support our interpretation.

Regarding the negative geotaxis phenotype, we appreciate the reviewer’s interest and agree that it is both intriguing and atypical. For this reason, we performed the assay multiple times, particularly in Polr3e knockdowns, to confirm the robustness of the result. To address potential confounding variables, we carefully selected control lines that account for genetic background and transgene insertion site, including KK controls and attP40-matched lines. We also employed multiple independent RNAi lines targeting Sxl to validate the phenotype across different genetic backgrounds.

Although the observed improvement in climbing is unexpected, it is not without precedent in the RNA polymerase III field. Notably, Malik et al. (2024) demonstrated that heterozygous Polr3DEY/+ mutants exhibit a significantly delayed decline in climbing ability with age. We allude to this in the discussion and will revise the text to emphasise this connection more explicitly.

Finally, while we recognise that negative geotaxis is a relatively broad assay and thus does not pinpoint the precise cellular mechanisms involved, we interpret the phenotype as suggesting a neural basis and a functional role for Sxl in the nervous system.

One would expect that not just the same classes of genes would be affected by loss and overexpression of Sxl, but the same genes would be affected - are the same genes changing in opposite directions in the two experiments or just the same classes of genes. Likewise, are the same genes changing expression in the same direction with both Sxl and the Polr3E loss? Also, why are tRNA genes not also affected with Sxl loss. Finally, they describe the changes in gene expression as being in male adult neurons, but the sequencing was done of entire heads - so no way of knowing which cell type is showing differential gene expression.

Author response:

While we do examine gene classes, our approach also includes pairwise correlation analyses of gene expression changes between specific genotypes. Notably, we observed a significant positive correlation between Polr3e knockdowns and Sxl knockdowns, and a significant negative correlation between Sxl-RAC–expressing flies and Sxl knockdowns. Furthermore, we examined Sxl-DamID target genes within our RNA-seq datasets and found a consistent relationship between Sxl targets and genes differentially expressed in Polr3e knockdowns.

Regarding the Pol III qPCR results, we note that tRNA expression changes may require a longer duration of RNAi induction (e.g., beyond 4 days) to become apparent, especially given that phenotypic effects such as changes in lifespan and negative geotaxis only emerge after 20 days or more. It is also plausible that Sxl knockdown leads to a partial reduction in Pol III efficiency, which may not be readily detectable through bulk Pol III qPCRs. We are willing to repeat Pol III qPCRs at later timepoints to further investigate this trend.

Finally, we infer that gene expression changes observed in our RNA-seq data are of neuronal origin, as all knockdown and overexpression constructs used in this study were driven pan-neuronally using elav-/nSyb-GAL4. While we acknowledge that bulk RNA-seq does not provide cell-type resolution, tissue-specific assumptions are widely used in the field when driven by a relevant promoter.

I'm also not sure what I'm supposed to be seeing in panel 5F (or in the related supplemental figure) and if it has any meaning - If they are using the Sxl-T2A-Gal4 to drive mCherry, I think one would expect to see expression since Sxl transcripts are made in both males and in females. Also, one would expect to see active protein expression (OPP staining) in most cells of the adult male brain and I think that is what is observed, but again, I'm not sure what I'm supposed to be looking at given the absence of any arrows or brackets in the figures.

Author Response:

Due to the presence of the T2A tag and the premature stop codon in exon 3 of early male Sxl transcripts, GAL4 expression is not expected in males unless the head-specific SxlRAC isoform is produced. The aim of panel 5F is to demonstrate the spatial overlap between SxlRAC expression (as we are examining male brains) and regions of elevated protein synthesis, as detected by OPP staining.

To quantitatively assess this relationship, we performed colocalisation analysis using ImageJ, which showed a positive correlation between Sxl and OPP signal intensity, supporting this interpretation. It is also evident from our images that regions with lower levels of protein synthesis (such as the neuropil - as shown in independent studies Villalobos-Cantor et al., 2023) concurrently lack Sxl-related signal. We have highlighted regions in Fig. 5 exhibiting higher/lower levels of Sxl/OPP signal to better illustrate this relationship. We can also test the effects of knockdown/overexpression on general protein synthesis if required.

Villalobos-Cantor S, Barrett RM, Condon AF, Arreola-Bustos A, Rodriguez KM, Cohen MS, Martin I. Rapid cell type-specific nascent proteome labeling in Drosophila. Elife. 2023 Apr 24;12:e83545. doi: 10.7554/eLife.83545. PMID: 37092974; PMCID: PMC10125018.

Minor comments:

* Line 223 - 225 - I believe that it is expected that Sxl transcripts would be broadly expressed in the male and female adult, given that it is only the spliced form of the transcript that is female specific in expression. *

As explained above, the only isoform that will be ‘trapped’ by the T2A-GAL4 in males is the Sxl-RAC isoform (as the other isoforms contain premature stop codons). Our immunohistochemistry data indicate that Sxl-RAC is expressed in the male brain, specifically in neurons. Therefore, knockdown experiments in males will reduce all mRNA isoforms, of which, Sxl-RAC is the only one producing a protein.

Line 236 - 238 - Sentence doesn't make sense.

We have addressed and clarified this.

Reviewer #2 (Significance (Required)):

It would be significant to discover that a gene previously thought to function in only sex determination and dosage compensation also moonlights as a regulator of RNA polymerase III activity. Unfortunately, I am not convinced by the work presented in this study that this is the case.

My expertise is in Drosophila biology, including development, transcription, sex determination, morphogenesis, genomics, transcriptomics, DNA binding

Reviewer #3 (Evidence, reproducibility and clarity (Required)):*

Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Drosophila Sxl, widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species, is also a chromatin factor that can stimulate transcription by Pol III and Pol II of genes involved with metabolism and protein homeostasis, specifically some encoding tRNAs.

The evidence for the tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments. I have a few specific comments below, all minor.*

Scientific points: - The approach taken for the evaluation of Sxl DNA-binding activity in Fig2 is not entirely clear. I assume these are crosses of elav-Gal4 x different UAS- lines, then using males or females for UAS-Sxl-Full-Length. But what about the others? Were the experiments done in males only? This is hinted at in the main text but not explicitly indicated in the figure or the methods (at least, that I could easily find). And is this approach extended to all other experiments? Longevity? Climbing assays? Considering the role of Sxl, it may be helpful to be fastidiously systematic with this.

Author Response:

We have revised the wording to ensure greater clarity. Males were used for all survival and behavioural experiments (as only males can be leveraged for knocking down Sxl-RAC without affecting the canonical Sxl-F isoform).

- In the discussion, lines 360-61, the authors say: Indeed, knockdown of Polr3E leads to a loss of Sxl binding to chromatin, suggesting a cooperative mechanism. Maybe I am misunderstanding the authors, but when I read "cooperation" in this context I think of biochemical cooperative binding. This is possible, but I do not think a simple 'requirement' test can suggest specifically that this mechanistic feature of biochemical binding is at play. I would expect, for starters, a reciprocal requirement for binding (which is not tested), and some quantitative features that would be difficult to evaluate in vivo. I do not think cooperative binding needs to be invoked anyway, as the authors do not make any specific point or prediction about it. But if they do think this is going on, I think it would need to be referred to as a speculation.

Author Response:

We appreciate that the original wording may have been unclear and will revise the text to more accurately reflect a functional relationship, rather than implying direct cooperation.

- In lines 428-432, the authors discuss the ancestral role of Sxl and make a comparison with ELAV, in the context of an RNA-binding protein that has molecular functions beyond those of a splicing factor, considering the functions of ELAV in RNA stability and translation, and finishing with "suggesting that similar regulatory mechanisms may be at play". I do not understand this latter sentence. Which mechanisms are these? Are the authors referring to the molecular activities of ELAV and SXL? But what would be the similarity? SXL seems to have a dual capacity to bind RNA and protein interactors, which allows it to work both in chromatin-level regulation as well as post-transcriptionally in splicing; but ELAV seems rather to take advantage of its RNA binding function to make it work in multiple RNA-related contexts, all post-transcriptional. I do not see an obvious parallel beyond the fact that RNA binding proteins can function at different levels of gene expression regulation -- but I would not say this parallel are "similar regulatory mechanisms", so I find the whole comparison a bit confusing.

Author Response:

We have reduced this section, as it is largely speculative and intended to highlight potential, though indirect, links in higher organisms. Our goal was primarily to illustrate the possibility that Sxl may have an ancestral role distinct from its well-characterised function, and to suggest a potential avenue for future research into ELAV2’s involvement in chromatin or Pol III regulation.

- One aspect of the work that I find is missing in the discussion is the possibility that the simultaneous capacity of Sxl for RNA binding and Polr3E binding: are these mutually exclusive? if so, are they competitive or hierarchical? how would they be coordinated anyway?

Author Response:

This is an interesting point, and we have expanded on it further in the Discussion section.

- The only aspect of the paper where I found that one could make an experimental improvement is the claim that Sxl induces the expression of genes that have the overall effect of stimulating protein synthesis. The OPP experiment shows a correlation between the expression of Sxl and the rate of protein synthesis initiation. However, a more powerful experiment would be, rather obviously, to introduce Sxl knock-down in the same experiment, and observe whether in Sxl-expressing neurons the incorporation of OPP is reduced. I put this forth as a minor point because the tenet of the paper would not be affected by the results (though the perception of importance of the newly described function could be reinforced).

• *

Author Response:

This could be a valid experiment and we are prepared to perform it if required.

- In a similar way, it would be interesting to know whether the recruitment of Polr3E and Sxl to chromatin is co-dependent or Sxl follows Polr3E. This is also a minor point because this would possibly refine the mechanism of recruitment but does not alter the main discovery.

Author Response:

We have addressed a similar point for Reviewer 2 (see below) and will include a Discussion point for this:

If Sxl were required for Polr3E recruitment to RNA Pol III, then, in most male Drosophila melanogaster cells, Polr3E would not be incorporated, and males would not be viable (as it is essential for Pol III activity). While it is possible that there could be a subtle effect on Polr3E recruitment, such an experiment, would not alter the central conclusion of our study - that Sxl is recruited to chromatin (accessory to the Pol III complex) via Polr3E.

* Figures and reporting:

• In Figure 2, it would be helpful to see the truncation coordinate for the N and C truncations.

• In Figure 3D, genomic coordinates are missing.

• In Figure 3E, the magnitude in the Y axis is not entirely clear (at least not to me). How is the amount of binding across the genome quantified? Is this the average amplitude of normalised TaDa signal across the genome? Or only within binding intervals?

• Figure S3E-F: it would be interesting to show the degree of overlap between the downregulated genes that are also binding targets (regardless of the outcome).

• Figure 5C-E: similarly to Figure S3, it would be interesting to know how the transcriptional effects compare with the binding targets.

• Authors use Gehan-Breslow-Wilcoxon to test survival, which is a bit unusual, as it gives more weight to the early deaths (which are rare in most Drosophila longevity experiments). Is there any rationale behind this? It may be even favour their null hypothesis.*

Author response:

Thank you for the detailed feedback on our figures. We have__ incorporated__ the suggested changes.

We agree that examining the overlap between Sxl binding sites and transcriptional changes is valuable, and we aimed to highlight this in the pie charts shown in Figures S3 and S5. If the reviewer is suggesting a more explicit quantification of the proportion of Sxl-Dam targets with significant transcriptomic changes, we are happy to include this analysis in the final version of the manuscript.

As noted in the Methods, both Gehan–Breslow–Wilcoxon (GBW) and Kaplan–Meier tests were used. The significance in Figure 4a is specific to the GBW test, which we indicated by describing the effect as mild. Our focus here is not on the magnitude of survival differences, but on the consistent trends observed in both Polr3e and Sxl knockdowns.

Writing and language:*

• Introduction finishes without providing an outline of the findings (which is fine by me if that is what the authors wanted).

• In lines 361-5, the authors say "We speculate that this interaction not only facilitates Pol III transcription but may also influence chromatin architecture and RNA Pol II-driven transcription as observed with Pol III regulation in other organisms". "This interaction" refers to Polr3E-Sxl-DNA interaction and with "Pol III transcription" I presume the authors refer to transcription executed by Pol III. I am not clear about the meaning of the end of the sentence "as observed with Pol III regulation in other organisms". What is the observation, exactly? That Pol III modifies chromatin in Pol II regulated loci, or that Pol III interactors change chromatin architecture?

• DPE abbreviation is not introduced (and only used once).

• A few typos: Line 41 ...splicing of the Sxl[late] transcripts, which is [ARE?] constitutively transcribed (Keyes et al.,... Line 76 ...sexes but appears restricted to the nervous system [OF] male pupae and adults (Cline et Line 289 ...and S41). To assess any effect [ON]translational output, O-propargyl-puromycin (OPP)o Line 323 ...illustrating that the majority (72%) changes in tRNA levels [ARE] due to upregulation...hi Line 402 ...it was discovered [WE DISCOVERED] Line 792 ...Sxl across chromosomes X, 2 L/R, 3 L/R and 4. The y-axis represents the log[SYMBOL] ratio... This happens in other figure legends as well.*

Author response:

Thank you for the detailed feedback, we have clarified and incorporated the suggested changes.

**Referee Cross-commenting***

Reviewer 1 asks how physiological is the Sxl chromatin-association assay. I think the loss of association in Polr3E knock-down and the lack of association of other splicing factors goes a long way into answering this question. It is true that having positive binding data specifically for Sxl-RAC and negative binding data for a deletion mutant of the RMM domain would provide more robust conclusions (see below), but I am not sure it is completely necessary -- though this will depend on which journal the authors want to send the paper to.

I think that the comment of reviewer 1 about the levels of expression of Sxl-DAM does not apply here because of the way TaDa works - it relies on codon slippage to produce minimal amounts of the DAM fusion protein, so by construction it will be expressed at much lower levels than the endogenous protein.

Reviewer 1 also asks whether Polr3E chromatin-association is also dependent on Sxl, to round up the model and also as a way to address whether Sxl association to chromatin is real. While I agree with this on the former aim (this would be a nice-to-have), I think I disagree on the latter; there is no need for Polr3E recruitment to depend on Sxl for Sxl association to chromatin to be physiologically relevant. Polr3E is a peripheral component of Pol III and unlikely to depend on a factor of restricted expression like Sxl to interact with chromatin. The recruitment of Sxl could well be entirely 'hierarchical' and subject to Polr3E.

Revewer 2 is concerned with the fact that every mutant form of Sxl shows the same result from the DamID labelling. I have to agree with this to a point. A deletion mutant of RMM domains would address this. Microscopy evidence in salivary glands would be nice, certainly, but the system may not lend itself to this particular interaction, which might be short-lived and/or weak. I do not immediately see the relevance of the chromatin binding capacity of non-Drosophilidae Sxl -- though it might indicate that the impact of the discovery is less likely to go beyond this group.

Reviewer 2 does not find surprising that some tRNA genes (less than half) are regulated by Sxl. I think the value of that observation is just qualitative, as tRNAs are Pol III-produced transcripts, but their point is correct. A hypergeometric test could settle this.

Reviewer 2 is concerned that the evidence of direct interaction between Sxl and Polr3E is a single 1999 two-hybrid study. But that paper contains also GST pull-downs that narrow down the specific domains that mediate binding, and perform the binding in competitive salt conditions. I think it is enough. The author team, I think, are not biochemists, so finding the right collaborators and performing these experiments would take time that I am not sure is warranted.

Reviewer 2 is also concerned that the longevity assays may not be meaningful due to the difference in genetic backgrounds. This is a very reasonable concern (which I would extend to the climbing assays - any quantitative phenotype is sensitive to genetic background). However, I think the authors here may have already designed the experiment with this in mind - the controls express untargeted RNAi constructs, but I lose track of which one is control of which. This should be clarified in Methods.

Other comments are in line, I think, with what I have pointed out and I generally agree with everything else that has been said.

Reviewer #3 (Significance (Required)):

Drosophila Sxl is widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species. It is a favourite example of how splicing factors and alternative can have profound influence in biology and used cleverly in the molecular circuitry of the cell to enact elegant regulatory decisions.

In this work, Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Sxl is also a chromatin factor with an sex-independent, neuron-specific role in stimulating transcription by Pol III and Pol II, of genes involved with metabolism and protein homeostasis, including some encoding tRNAs.

This opens a large number of interesting biological questions that range from biochemistry, gene regulation or neurobiology to evolution. How is the simultaneous capacity of binding RNA and chromatin (with the same protein domain, RRM) regulated/coordinated? How did this dual activity evolve and which one is the ancestral one? How many other RRM-containin RNA-binding proteins can also bind chromatin? How is Sxl recruited to chromatin to both Pol II and Pol III targets and are they functionally related? If so, how is the coordination of cellular functions activated through different RNA polymerases taking place and what is the role of Sxl in this? What are the functional consequences to neuronal biology? Does this affect similarly all Sxl-expressing neurons?

The evidence for the central tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments.*

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

*The convincing analysis demonstrates a role for the Drosophila Sex determining gene sex lethal in controlling aspects of transcription in the nervous system independent of its role in splicing. Interaction with an RNA Pol III subunit mediating Sxl association with chromatin and similar knockdown phenotypes strongly support the role of Sxl in the regulation of neuronal metabolism. Given that Sxl is an evolutionary recent acquisition for sex determination, the study may reveal an ancestral role for Sxl.

The conclusions are well justified by the datasets presented and I have no issues with the study or the interpretation. Throughout the work is well referenced, though perhaps the authors might take a look at Zhang et al (2014) (PMID: 24271947) for an interesting evolutionary perspective for the discussion.*

Author Response:

Thank you for the thoughtful suggestion. We will be sure to incorporate the findings from Zhang et al. regarding the evolution of the sex determination pathway.

*I have some minor comments for clarification:

There is no Figure 2b, should be labelled 2 or label TaDa plots as 2b

Clarify if Fig 2 data are larval or adult *

*Larval

Fig 3d - are these replicates or female and male?

Please elaborate on tub-GAL80[ts] developmental defects

Fig 4e, are transcriptomics done with the VDRC RNAi line? The VDRC and BDSC RNAi lines exhibit different behaviours - former has "better" survival and Better negative geotaxis, the latter seems to have poorer survival but little geotaxis effect?*

*Fig S3 - volcano plot for Polr3E?

Fig S4a - legend says downregulated genes?

The discussion should at least touch on the fact that Sxl amorphs (i.e. Sxl[fP7B0] are male viable and fertile, emphasising that the newly uncovered role is not essential.*

Author Response:

We agree with the suggestions outlined in the comments and have made the appropriate revisions.

Reviewer #4 (Significance (Required)):*

A nonessential role for Sxl in the nervous system independent of sex-determination contributes to better understanding a) the evolution of sex determining mechanisms, b) the role of RNA PolIII in neuronal homeostasis and c) more widely to the neuronal aging field. I think this well-focused study reveals a hitherto unsuspected role for Sxl.*

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Referee #3

Evidence, reproducibility and clarity

Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Drosophila Sxl, widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species, is also a chromatin factor that can stimulate transcription by Pol III and Pol II of genes involved with metabolism and protein homeostasis, specifically some encoding tRNAs.

The evidence for the tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments. I have a few specific comments below, all minor.

Scientific points:

• The approach taken for the evaluation of Sxl DNA-binding activity in Fig2 is not entirely clear. I assume these are crosses of elav-Gal4 x different UAS- lines, then using males or females for UAS-Sxl-Full-Length. But what about the others? Were the experiments done in males only? This is hinted at in the main text but not explicitly indicated in the figure or the methods (at least, that I could easily find). And is this approach extended to all other experiments? Longevity? Climbing assays? Considering the role of Sxl, it may be helpful to be fastidiously systematic with this.
• In the discussion, lines 360-61, the authors say: Indeed, knockdown of Polr3E leads to a loss of Sxl binding to chromatin, suggesting a cooperative mechanism. Maybe I am misunderstanding the authors, but when I read "cooperation" in this context I think of biochemical cooperative binding. This is possible, but I do not think a simple 'requirement' test can suggest specifically that this mechanistic feature of biochemical binding is at play. I would expect, for starters, a reciprocal requirement for binding (which is not tested), and some quantitative features that would be difficult to evaluate in vivo. I do not think cooperative binding needs to be invoked anyway, as the authors do not make any specific point or prediction about it. But if they do think this is going on, I think it would need to be referred to as a speculation.
• In lines 428-432, the authors discuss the ancestral role of Sxl and make a comparison with ELAV, in the context of an RNA-binding protein that has molecular functions beyond those of a splicing factor, considering the functions of ELAV in RNA stability and translation, and finishing with "suggesting that similar regulatory mechanisms may be at play". I do not understand this latter sentence. Which mechanisms are these? Are the authors referring to the molecular activities of ELAV and SXL? But what would be the similarity? SXL seems to have a dual capacity to bind RNA and protein interactors, which allows it to work both in chromatin-level regulation as well as post-transcriptionally in splicing; but ELAV seems rather to take advantage of its RNA binding function to make it work in multiple RNA-related contexts, all post-transcriptional. I do not see an obvious parallel beyond the fact that RNA binding proteins can function at different levels of gene expression regulation -- but I would not say this parallel are "similar regulatory mechanisms", so I find the whole comparison a bit confusing.
• One aspect of the work that I find is missing in the discussion is the possibility that the simultaneous capacity of Sxl for RNA binding and Polr3E binding: are these mutually exclusive? if so, are they competitive or hierarchical? how would they be coordinated anyway?
• The only aspect of the paper where I found that one could make an experimental improvement is the claim that Sxl induces the expression of genes that have the overall effect of stimulating protein synthesis. The OPP experiment shows a correlation between the expression of Sxl and the rate of protein synthesis initiation. However, a more powerful experiment would be, rather obviously, to introduce Sxl knock-down in the same experiment, and observe whether in Sxl-expressing neurons the incorporation of OPP is reduced. I put this forth as a minor point because the tenet of the paper would not be affected by the results (though the perception of importance of the newly described function could be reinforced).
• In a similar way, it would be interesting to know whether the recruitment of Polr3E and Sxl to chromatin is co-dependent or Sxl follows Polr3E. This is also a minor point because this would possibly refine the mechanism of recruitment but does not alter the main discovery.

Figures and reporting:

• In Figure 2, it would be helpful to see the truncation coordinate for the N and C truncations.
• In Figure 3D, genomic coordinates are missing.
• In Figure 3E, the magnitude in the Y axis is not entirely clear (at least not to me). How is the amount of binding across the genome quantified? Is this the average amplitude of normalised TaDa signal across the genome? Or only within binding intervals?
• Figure S3E-F: it would be interesting to show the degree of overlap between the downregulated genes that are also binding targets (regardless of the outcome).
• Figure 5C-E: similarly to Figure S3, it would be interesting to know how the transcriptional effects compare with the binding targets.
• Authors use Gehan-Breslow-Wilcoxon to test survival, which is a bit unusual, as it gives more weight to the early deaths (which are rare in most Drosophila longevity experiments). Is there any rationale behind this? It may be even favour their null hypothesis.

Writing and language:

• Introduction finishes without providing an outline of the findings (which is fine by me if that is what the authors wanted).
• In lines 361-5, the authors say "We speculate that this interaction not only facilitates Pol III transcription but may also influence chromatin architecture and RNA Pol II-driven transcription as observed with Pol III regulation in other organisms". "This interaction" refers to Polr3E-Sxl-DNA interaction and with "Pol III transcription" I presume the authors refer to transcription executed by Pol III. I am not clear about the meaning of the end of the sentence "as observed with Pol III regulation in other organisms". What is the observation, exactly? That Pol III modifies chromatin in Pol II regulated loci, or that Pol III interactors change chromatin architecture?
• DPE abbreviation is not introduced (and only used once).
• A few typos: Line 41 ...splicing of the Sxl[late] transcripts, which is [ARE?] constitutively transcribed (Keyes et al.,... Line 76 ...sexes but appears restricted to the nervous system [OF] male pupae and adults (Cline et Line 289 ...and S41). To assess any effect [ON]translational output, O-propargyl-puromycin (OPP)o Line 323 ...illustrating that the majority (72%) changes in tRNA levels [ARE] due to upregulation...hi Line 402 ...it was discovered [WE DISCOVERED] Line 792 ...Sxl across chromosomes X, 2 L/R, 3 L/R and 4. The y-axis represents the log[SYMBOL] ratio... This happens in other figure legends as well.

Referee Cross-commenting

Reviewer 1 asks how physiological is the Sxl chromatin-association assay. I think the loss of association in Polr3E knock-down and the lack of association of other splicing factors goes a long way into answering this question. It is true that having positive binding data specifically for Sxl-RAC and negative binding data for a deletion mutant of the RMM domain would provide more robust conclusions (see below), but I am not sure it is completely necessary -- though this will depend on which journal the authors want to send the paper to.

I think that the comment of reviewer 1 about the levels of expression of Sxl-DAM does not apply here because of the way TaDa works - it relies on codon slippage to produce minimal amounts of the DAM fusion protein, so by construction it will be expressed at much lower levels than the endogenous protein.

Reviewer 1 also asks whether Polr3E chromatin-association is also dependent on Sxl, to round up the model and also as a way to address whether Sxl association to chromatin is real. While I agree with this on the former aim (this would be a nice-to-have), I think I disagree on the latter; there is no need for Polr3E recruitment to depend on Sxl for Sxl association to chromatin to be physiologically relevant. Polr3E is a peripheral component of Pol III and unlikely to depend on a factor of restricted expression like Sxl to interact with chromatin. The recruitment of Sxl could well be entirely 'hierarchical' and subject to Polr3E.

Revewer 2 is concerned with the fact that every mutant form of Sxl shows the same result from the DamID labelling. I have to agree with this to a point. A deletion mutant of RMM domains would address this. Microscopy evidence in salivary glands would be nice, certainly, but the system may not lend itself to this particular interaction, which might be short-lived and/or weak. I do not immediately see the relevance of the chromatin binding capacity of non-Drosophilidae Sxl -- though it might indicate that the impact of the discovery is less likely to go beyond this group.

Reviewer 2 does not find surprising that some tRNA genes (less than half) are regulated by Sxl. I think the value of that observation is just qualitative, as tRNAs are Pol III-produced transcripts, but their point is correct. A hypergeometric test could settle this.

Reviewer 2 is concerned that the evidence of direct interaction between Sxl and Polr3E is a single 1999 two-hybrid study. But that paper contains also GST pull-downs that narrow down the specific domains that mediate binding, and perform the binding in competitive salt conditions. I think it is enough. The author team, I think, are not biochemists, so finding the right collaborators and performing these experiments would take time that I am not sure is warranted.

Reviewer 2 is also concerned that the longevity assays may not be meaningful due to the difference in genetic backgrounds. This is a very reasonable concern (which I would extend to the climbing assays - any quantitative phenotype is sensitive to genetic background). However I think the authors here may have already designed the experiment with this in mind - the controls expres untargeted RNAi constructs, but I lose track of which one is control of which. This should be clarified in Methods.

Other comments are in line, I think, with what I have pointed out and I generally agree with everything else that has been said.

Significance

Drosophila Sxl is widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species. It is a favourite example of how splicing factors and alternative can have profound influence in biology and used cleverly in the molecular circuitry of the cell to enact elegant regulatory decisions.

In this work, Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Sxl is also a chromatin factor with an sex-independent, neuron-specific role in stimulating transcription by Pol III and Pol II, of genes involved with metabolism and protein homeostasis, including some encoding tRNAs.

This opens a large number of interesting biological questions that range from biochemistry, gene regulation or neurobiology to evolution. How is the simultaneous capacity of binding RNA and chromatin (with the same protein domain, RRM) regulated/coordinated? How did this dual activity evolve and which one is the ancestral one? How many other RRM-containin RNA-binding proteins can also bind chromatin? How is Sxl recruited to chromatin to both Pol II and Pol III targets and are they functionally related? If so, how is the coordination of cellular functions activated through different RNA polymerases taking place and what is the role of Sxl in this? What are the functional consequences to neuronal biology? Does this affect similarly all Sxl-expressing neurons?

The evidence for the central tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments.

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Reply to the reviewers

1. General Statements

• This manuscript represents a full revision incorporating all reviewer recommendations; the additional follow-up experiments and expanded analyses will be presented in dedicated subsequent manuscripts.
• Congenital dyserythropoietic anemia type I (CDA-I) is a rare hereditary disease characterized by ineffective erythropoiesis and mutations in Codanin1 and CDIN1.
• Our study reveals the structural and functional dynamics of the CDIN1-Codanin1 complex, shedding light on the molecular mechanisms of protein-protein interactions implicated in CDA-I pathology.
• The main goal of our study was to examine the interaction between CDIN1 and the C‑terminal binding domain of Codanin1 using complementary biophysical approaches.
• We quantified binding and identified interacting regions of Codanin1 and CDIN1.
• We found that CDA-I-associated mutations in interacting regions disturb CDIN1‑Codanin1 complex.
• We proposed a hypothetical molecular model of CDIN1-Codanin1 role in CDA-I hallmarks development.
• Our initial studies on BioRxiv (2023) have been cited by leading publications in the field (Jeong, Frater et al. 2025, Sedor and Shao 2025, Nature Communications) and prompted further research on this topic.

2. Point-by-point description of the revisions

*Here we provide a point-by-point reply describing the revisions already carried out and included in the transferred manuscript. *

Reply to the reviewers

Reviewer #1 – Evidence, reproducibility and clarity

This is a rigorous biophysical characterization of a protein-protein interaction relevant to CDA-1 disease. The two proteins were purified in an E. coli host but CD and DLS was performed to ensure that the purified protein is well folded. An impressive native protein EMSA was used to show a 1:1 complex. While common for protein-nucleic acid complexes, EMSAs are much more challenging with protein complexes. A higher-running complex, likely a heterotetramer was implied at higher protein concentrations. These results were supported with SEC-MALS analysis and analytic ultracentrifugation analysis. Thermophoresis and ITC were used to report a nanomolar affinity of the proteins for each other. SEC-SAXS supported the conclusions about stoichiometry and composition inferred from the earlier methods and suggested that the dimerization interface comes from CDIN1. Next HDX-MS was used to identify putative interface residues, which were then mutated in each of the proteins and assessed for binding using coimmunoprecipitation. This study uses at least 10 orthogonal biophysical and/or biochemical methodologies to characterize an important protein-protein interaction and the analysis is clear and so is the writing. I couldn't (reading it once) find any grammatical or other errors in the text or figures. This manuscript is top-quality and suitable for publication.

__Reviewer #1 – Significance __

Such detailed structural and mechanistic studies are greatly lacking in many clinical conditions for which mutations are known (unless they cause cancer, neurodegenerative disease, and so on). We need more such studies on disease topics! This study will be of interest to the hematologic diseases community.

1. Response – ____Significance

We thank Reviewer #1 for the thoughtful and encouraging evaluation of our work. We are particularly grateful for recognizing the significance of studying protein-protein interaction in the context of CDA-I disease, as well as the rigor and clarity of our biophysical and biochemical characterization.

We appreciate the reviewer's acknowledgment of the challenges associated with native protein EMSAs. We are pleased that our use of multiple orthogonal techniques was recognized as a strength of the study. We are gratified that the comprehensiveness and coherence of our data and the manuscript's clarity were well received.

We thank the reviewer for noting the broader impact of our findings on the hematologic disease community. As highlighted, there is a pressing need for a mechanistic understanding of non-oncologic, non-neurodegenerative diseases, and our studies address this gap.

We are honored by the reviewer's endorsement of our manuscript as "top-quality and suitable for publication". We value the reviewer's highly supportive and motivating feedback.

__Reviewer #2 – 1. Evidence, reproducibility and clarity __

This manuscript presents structural and biochemical characterization of the interaction between CDIN1 and the C-terminal domain of Codanin1, shedding light on a complex implicated in Congenital Dyserythropoietic Anemia Type I (CDA-I). While the authors provide valuable structural insights and identify disease-associated mutations that impair CDIN1-Codanin1 binding, I think several important concerns should be addressed to strengthen both the mechanistic claims and their functional relevance.

Contradiction Between Stoichiometry Models:

The authors propose that CDIN1 and Codanin1Cterm primarily form a heterodimer in vitro. However, this appears to contradict previous reports indicating a tetra-heteromeric arrangement. Additionally, while CDIN1 homodimerize seems confusing to me, do the authors suggest it is stable without Codanin1? This seems contrary to findings that CDIN1 is unstable in the absence of Codanin1 (Sedor, S.F., Shao, S. nature comm 2025, Swickley, G., Bloch, Y., Malka, L. et al 2020 BMC Mol and Cell Biol). These inconsistencies raise concerns about whether the observed stoichiometries are physiologically relevant or artifacts of in vitro reconstitution, especially since full-length Codanin1 was not studied.

2.1 Response ____– Consistent stoichiometry of Codanin1Cterm

We thank Reviewer #2 for raising critical points regarding the stoichiometry and physiological relevance of the CDIN1-Codanin1 interaction. The following response clarifies the rationale and interpretation in relation to previous findings.

Stoichiometry of CDIN1-Codanin1Cterm complex:

Recent Cryo-EM studies of full-length Codanin1 (Jeong, Frater et al. 2025, Sedor and Shao 2025) suggest independent internal dimerization domains (452-798 and 841-1000 amino acid residue) driving homodimer formation, with each Codanin1 monomer binding one CDIN1 via the C-terminal region (1005-1227 amino acid residue), resulting in a tetra-heteromeric complex. Therefore, the complete assembly appears as a dimer of heterodimers in the full-length context.

In our study, Codanin1 was truncated to retain only the CDIN1-binding C-terminus (1005-1227 amino acid residues), eliminating the homodimerization ability of Codanin1. Hence, in the case of truncated Codanin1Cterm, the minimal complex we observe is a 1:1 heterodimer of CDIN1-Codanin1Cterm, which is fully consistent with the equimolar stoichiometry of CDIN1-Codanin1 complex seen in the full-length structure.

Stability and oligomeric state of CDIN1 in the absence of Codanin1:

We concur with the reviewer that Sedor et al. (2025) and Swickley et al. (2020) reported decreased CDIN1 levels in cells lacking Codanin1, implying in vivo dependence of CDIN1 on Codanin1 partner for stability (Swickley, Bloch et al. 2020, Sedor and Shao 2025). The purified CDIN1 is monodisperse (Supplementary Figure 2D), exhibits thermal stability with a melting temperature of 48 °C (Supplementary Figure 2E), and displays proper folding as indicated by CD measurements (Supplementary Figure 2B). Additionally, SAXS profiles of CDIN1 correspond to AlphaFold predictions (Fig. 2B). Together, our findings indicate that the recombinant CDIN1 forms a stable conformation in vitro without Codanin1. To the best of our knowledge, no previous research has directly identified the endogenous oligomeric states of CDIN1 within cellular content.

We fully acknowledge that future analysis of the full-length Codanin1-CDIN1 assembly in a cellular context will be necessary for understanding physiological stoichiometries. As outlined in the General statements, our study focuses on the C-terminus of Codanin1 to describe the binding interface and complex biophysical properties of the CDIN-Codanin1Cterm complex.

__Reviewer #2 – ____2. Unvalidated Functional Claims: __

The manuscript identifies several CDA-I-associated mutations that disrupt CDIN1-Codanin1 interaction. However, the authors do not test how these mutations affect the biological function of the complex, particularly its role in ASF1 sequestration or histone trafficking. Given the central importance of this axis in their disease model, functional validation (e.g., ASF1 localization, histone deposition assays) is necessary to support these mechanistic conclusions.

2.2 Response – ____Hypothetical model as discussion merit

We thank the reviewer for the comment regarding the functional implications of CDA-I-associated mutations and their potential impact on ASF1 sequestration and histone trafficking hypothesized within the Discussion. We fully agree that understanding the downstream biological consequences of disrupted CDIN1-Codanin1 interaction is critical for elucidating the full molecular basis of CDA-I pathogenesis.

In the Future research directions of the Discussion, we have acknowledged and emphasized the need for follow-up studies using erythroblast cell lines to determine whether specific disease-associated mutations disrupt CDIN1-Codanin1 binding, leading to functional defects relevant to erythropoiesis and nuclear architecture typical for CDA-I disease.

However, as we respectfully note in General Statements, the main aim of the present study was to provide a rigorous biophysical characterization of the CDIN1-Codanin1Cterm interaction. Proposed cellular experiments, though relevant, are beyond the conceptual scope of the presented studies.

Reviewer #2 – ____3. Speculative and Potentially Contradictory Model:

The proposed model suggests that CDIN1 competes with ASF1 for Codanin1 binding, thereby indirectly promoting histone delivery to the nucleus. However, emerging data indicate that Codanin1, CDIN1, and ASF1 can form a stable ternary complex, calling into question this competitive binding hypothesis (Sedor, S.F., Shao, S. nature comm 2025). The authors do not acknowledge or discuss these findings, and the model in its current form may therefore be oversimplified or inaccurate.

2.3 Response – ____Hypothetical model fully aligned with current knowledge

We fully acknowledged and discussed in the current manuscript the recent findings demonstrating that Codanin1, CDIN1, and ASF1 can form a ternary complex (Sedor, S.F., Shao, S. Nature Comm. 2025; Jeong, T. K. et al. Nature Comm. 2025). Our revised model was updated accordingly to reflect the collaborative binding of Codanin1, CDIN1, and ASF1, and is presented in alignment with published data.

While earlier versions of our work published on the BioRxiv server (May 26, 2023) proposed a competitive hypothesis, the current manuscript incorporates recent literature and prior reviewer feedback to offer a refined model. We believe that the updated hypothesis suggests a plausible mechanism for how CDIN1 modulates Codanin1 function, which will be further tested in future cellular studies.

Reviewer #2 – 4. Significance:

Overall, the study adds to our structural understanding of CDIN1 and Codanin1 interactions, but the functional interpretations are currently speculative, and in some cases in conflict with existing literature. The manuscript would benefit significantly from addressing these discrepancies, incorporating relevant data on ASF1, and clarifying whether the observed assemblies reflect physiological complexes.

__2.4 Response – Significance __

We thank Reviewer #2 for the constructive feedback. As noted in General Statements, our current manuscript is primarily dedicated to defining the molecular architecture and interactions of the CDIN1–Codanin1Cterm core interface. We agree that follow-up ASF1‑dependent functional assays will be critical to fully validate observed assemblies, but these experiments lie outside the scope of the present study and are ongoing in our laboratory.

To address the reviewer's concern about possible speculative interpretation, we have:

• Used cautious language in Results and Discussion to prevent overstatement (e.g., page 31, line 754, “leads” exchanged to “may contribute” in legend of Fig. 4).
• Described in the Discussion how our results enhance and add understanding to the body of published structural data of CDIN1–Codanin1Cterm.
• Updated our hypothetical model in Fig. 4 to be fully in line with published data.
• Clearly stated that the working hypothesis is connected with a subset of CDA-I mutations (p. 31, l. 758-759, “The proposed model represents a working hypothesis relating to a subset of CDA-I mutations and is not currently substantiated by experimental evidence at the cellular level.”)
• Stated in Future research directions of Discussion that functional validation, including ASF1, will motivate future critical studies, p. 32, l. 771-773: “The ability of Codanin1 to interact with both CDIN1 and ASF1 motivates further investigation of how CDIN1 and ASF1 affect the function of full-length Codanin1, which even recent cryo-EM data has not addressed yet.”
• Highlighted the necessity of complementary in vivo studies in erythroblast cell lines to determine if CDA-I-related mutations in CDIN1-Codanin1 interaction region cause typical CDA-I phenotypes, aiming to clarify the molecular mechanisms of inherited CDA-I anemia. We state in Future research directions in Discussion, p. 32, l. 774-780: “…follow-up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding also affect ASF1 localization and cause a phenotype typical of CDA-I. In future work, additional Codanin1 mutations, including those outside the C-terminal region, should be evaluated to determine how the mutations affect ASF1’s nuclear concentration and subcellular localization. The proposed research directions will provide additional deeper insights into the underlying mechanisms of the molecular origin of inherited anemia CDA-I.” We believe that the revisions objectively clarify the significance and the limits of the current work and set the stage for the detailed functional studies to follow.

__Reviewer #3 – Evidence, reproducibility and clarity: __

Congenital Dyserythropoietic Anemia Type I (CDA I) is an autosomal recessive disorder characterized by ineffective erythropoiesis and distinctive nuclear morphology ("Swiss cheese" heterochromatin) in erythroblasts. CDA I is caused by mutations in CDAN1 and CDIN1. Codanin1, encoded by CDAN1, is part of the cytosolic ASF1-H3.1-H4-Importin-4 complex, which regulates histone trafficking to the nucleus. CDIN1 has been shown to bind the C-terminal domain of Codanin-1, but until now, pathogenic mutations had not been directly linked to the disruption of this interaction.

In this study, the authors used biophysical techniques to characterize the interaction between Codanin-1's C-terminal region (residues 1005-1227) and CDIN1, demonstrating high-affinity, equimolar binding. HDX-MS identified interaction hotspots, and disease-associated mutations in these regions disrupted complex formation. The authors propose that such disruption prevents ASF1 sequestration in the cytoplasm, thereby reducing nuclear histone levels and contributing to the chromatin abnormalities seen in CDA I.

Major Comments:

1. Use of Codanin-1 Fragment:

Most experiments were conducted using only the C-terminal 223 amino acids of Codanin-1. While this region is known to bind CDIN1, it is unclear whether its conformation is maintained in the context of the full-length protein. This could affect binding properties and structural interpretations. The authors should discuss how structural differences between the isolated C-terminus and the full-length Codanin-1 may influence the conclusions.

Response of authors ____#3

3.1 Response: Use of Codanin-1 Fragment as biding part to CDIN1

We thank the reviewer for the important observation regarding the use of the C-terminal fragment of Codanin1. As noted in the manuscript (e.g., p. 30, line 721 and p. 32, line 761), we fully acknowledge that the truncation of Codanin1 may influence its conformational dynamics or contextual folding relative to the full-length protein.

However, several lines of evidence suggest that the C-terminal 223 amino acid residues—responsible for CDIN1 binding—are structurally autonomous and have minimal intramolecular contacts with upstream regions. Published cryo-EM and biochemical data (Jeong, Frater et al. 2025, Sedor and Shao 2025), in conjunction with AlphaFold structural predictions (Fig. 2D) and our co-immunoprecipitation assays (Fig. 3F), consistently support a model wherein the CDIN1-binding region is flexible and spatially isolated from the core structural domains of Codanin1. Additionally, results from our co-immunoprecipitation assay (Fig. 3F) indicate that full-length Codanin1 and truncated Codanin1Cterm interact with CDIN1 similarly, further supporting the isolated manner of the C-terminal fragment. The available data together imply that the C-terminal fragment used in our study retains its native conformation and binding properties when expressed independently.

While our findings are confined to the interaction domain and do not reflect full-length Codanin1’s architecture, we believe the use of the C-terminal minimal fragment of Codanin1 enables precise dissection of the CDIN1-binding interface and yields mechanistic insights without introducing significant structural artifacts.

We agree with the reviewer that future work incorporating full-length Codanin1, especially in a cellular context, will be instrumental to fully characterize higher-order assembly and regulatory functions.

__Reviewer #3 – 2. ____Graphical Abstract and Domain Independence: __

The graphical abstract presents the Codanin-1 C-terminus as an independent domain, but no direct evidence is provided to support its structural autonomy in vivo.

The authors should clarify whether the C-terminal region functions as a distinct domain in the context of the full-length protein.

__3.2 Response –____ Independent C-terminal domain __

We thank the reviewer for bringing up the question of the independence of the C-terminal domain. Although direct in vivo proof of C-terminal autonomy is not yet available, published cryo-EM structures of full-length Codanin1, our biophysical characterization, and AlphaFold models all consistently indicate that the C-terminal 223 amino acid residues of Codanin1 form a structurally independent binding module. In the graphical abstract, we illustrated the C‑terminal domain as a loosely connected part of Codanin1 to highlight its independence and to emphasize the specific focus of our studies.

To articulate limitations of our studies focused on the C-terminal part of Codanin1, we stated in the Functional implications of CDA-I-related mutations in the Discussion, p. 30, l. 721-724: “However, our measurements do not exclude the possible role of the disordered regions in full-length Codanin1. For example, CDIN1 could potentially stabilize full-length Codanin1 by rearranging the disordered regions into a more condensed structure, thereby augmenting the structural stability of Codanin1.”

Reviewer #3 – 3.____Pathogenic Mutations Beyond the Binding Site:

The study highlights a triplet mutation that impairs CDIN1 binding. However, most CDA I‑associated mutations in CDAN1 are dispersed across the entire protein and may not affect CDIN1 interaction directly.

The authors should discuss alternative mechanisms by which mutations in other regions of Codanin-1 might cause disease.

3.3 Response – Pathogenic mutations outside the binding site – alternative mechanisms

We appreciate the reviewer noting that most CDA-I-associated CDAN1 mutations are outside the CDIN1-Codanin1 binding site and suggesting alternative mechanisms. In the revised Discussion, we added a paragraph on alternative pathogenic models, p. 29, l. 702-713:

"Our study centers on the CDIN1-binding C-terminus, however, most CDA-I-associated CDAN1 mutations lie elsewhere and probably act through alternative mechanisms. Mutations such as P672L and F868I in the LOBE2 (452-798 amino acid residue) and F868I in the coiled-coil (841-1000 amino acid residue) domains may disturb Codanin1 homodimerization and higher-order complex assembly, directly affecting ASF1 sequestration (Jeong, T. K. et al. Nature Comm. 2025). Other mutant variants may also interfere with ASF1 sequestration, nuclear targeting, or chromatin-remodeling functions, while destabilizing mutations may induce misfolding and proteasomal degradation. Moreover, CDA-I-associated mutations, such as R714W and R1042W, might compromise the interaction between Codanin1 and ASF1 (Ask, Jasencakova et al. 2012). Collectively, the complementary alternative pathogenic mechanisms associated with Codanin1 mutations in distal regions and mutations in CDIN1‑binding C-terminus of Codanin1 may contribute to erythroid dysfunction in CDA-I."

Reviewer #3 – 4. ____Contradictory Functional Models:

Ask et al. (EMBO J, 2012) reported that Codanin-1 depletion increases nuclear ASF1 and accelerates DNA replication. This contrasts with the current hypothesis that disruption of the Codanin-1/CDIN1 complex reduces nuclear ASF1.

The authors should attempt to reconcile this apparent contradiction, possibly by proposing a context-specific or dual-function model for Codanin-1 in histone trafficking.

3.4 Response – ____Clarified explanation of hypothetical functional model

We thank the reviewer for raising this point, which improved the clarity of our work. There is no real discrepancy between Ask et al. and our findings; both agree that Codanin1 restrains ASF1 in the cytoplasm. Ask et al. examined the complete loss of Codanin1, which abolishes cytoplasmic ASF1 sequestration and thus leads to maximal nuclear accumulation. We suggest the CDA-I-associated mutations selectively disrupt the CDIN1-Codanin1 interface, releasing ASF1 from the cytoplasm into the nucleus.

To enhance clarity, we now state in the legend of Figure 4 describing the hypothesis (p. 31, l. 752-753): "…CDA-I-associated mutations prevent CDIN1-Codanin1 complex formation, thus prevent ASF1 sequestration to cytoplasm; ASF1 remains accumulated in nucleus."

Reviewer #3 – 5. ____Conclusions and Claims:

The proposed model of CDA I pathogenesis (Fig. 4) is plausible but not yet fully supported by the available data. The authors suggest that disruption of the Codanin-1/CDIN1 interaction leads to nuclear histone depletion, but this has not been experimentally confirmed.

Claims about the general pathogenesis of CDA I should be clearly qualified as hypothetical and applicable to a subset of mutations. The presence and localization of ASF1 in the nucleus following disruption of the Codanin-1/CDIN1 complex should be tested experimentally.

3.5 Response – __Tempered ____conclusions and claims: __

We thank the reviewer for underscoring the need to temper our conclusions and to distinguish hypotheses from available results. We fully agree that our Fig. 4 model—linking disruption of the Codanin1-CDIN1 interface to nuclear histone imbalance—remains a working hypothesis, currently supported by indirect biochemical and structural data.

Accordingly, we have:

• Revised the text to explicitly state that this model is hypothetical and pertains to a subset of CDA-I-associated CDAN1 mutations. Specifically, we

• Added to the last paragraph of the section Functional implications of CDA-I-related mutations in Discussion (p. 31, l. 744-749): “In considering functional implications of our findings within available data, it is essential to qualify that mechanistic claims regarding the general pathogenesis of CDA-I remain hypothetical and are restricted to a specific subset of mutations. Furthermore, direct experimental validation, such as immunolocalization or live-cell imaging, to assess ASF1’s nuclear presence and distribution following disruption of the CDIN1-Codanin1 complex is required to substantiate the proposed model.”

• Included in the legend of Fig. 4: ”The proposed model represents a working hypothesis relating to a subset of CDA-I mutations and is not currently substantiated by experimental evidence at the cellular level.”
• Replaced any associated definitive language (e.g., “leads to”) with qualified phrasing (e.g., “may contribute to”) in the legend of Fig. 4.
• Clarified in the Discussion that direct measurement of nuclear ASF1 redistribution and histone levels following interface disruption has not yet been performed. Specifically, we added to the section Functional implications of CDA-I-related mutations in Discussion (p. 30, l. 734-735): “It should be noted, however, that direct quantification of nuclear ASF1 redistribution and histone levels after CDIN1-Codanin1 disruption has not yet been conducted.” Although experimental verification of nuclear ASF1 localization upon CDIN1-Codanin1 complex disruption falls beyond the current manuscript’s scope, we acknowledge its importance and have emphasized the need for such studies in future work within the Future research directions of the Discussion. Specifically, we concluded by stating (p. 32, l. 774-776): “Finally, follow‑up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding, also affect ASF1 localization and cause a phenotype typical of CDA-I.”

__Reviewer #3 – 6.____Broader Mutation Analysis and ASF1 Localization: __

To strengthen the link between Codanin-1/CDIN1 disruption and disease pathogenesis, it would be important to test the effects of additional CDAN1 mutations, including those outside the C-terminal region. Similarly, the impact on ASF1 nuclear concentration and localization should be directly assessed. These experiments would significantly bolster the central hypothesis. If feasible, they should be pursued or at least acknowledged as important future directions.

3.6 Response – Broader mutation analysis and ASF1 localization in future directions

We thank Reviewer #3 for emphasizing the value of a broader mutation survey and direct ASF1 localization studies. As noted above, our current manuscript is centered on delineating the molecular architecture of the CDIN1-Codanin1Cterm core interface; comprehensive mutational analyses outside the C-terminal binding region and ASF1-dependent functional assays will be critical to extend these findings but fall beyond the scope of the present work and will be the objective of our following studies. To address the reviewer’s concern, we have:

• Expanded the Future Directions section to specify that additional CDA-I-linked CDAN1 variants, including non-C-terminal mutations, and quantitative assessments of ASF1 nuclear localization will be the subject of ongoing and planned investigations. Specifically, we added (p. 32, l. 776-778):” In future work, additional Codanin1 mutations, including those outside the C-terminal region, should be evaluated to determine how the mutations affect ASF1’s nuclear concentration and subcellular localization.”

• Emphasized the need for complementary in vivo validation in erythroblast models to confirm whether the disturbance of CDIN1-Codanin1 binding recapitulates CDA-I phenotypes. We acknowledged the need for cell-line studies in future work within the Future research directions of Discussion (p. 32, l. 774-776): “Finally, follow-up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding, also affect ASF1 localization and cause a phenotype typical of CDA-I.” We believe these changes more precisely delimit the scope and significance of the current study while laying out a clear roadmap for the essential follow-up experiments.

Reviewer #3 – 7. ____Rigor and Presentation and Cross-commenting

__Minor Comments: __

• Methods and Reproducibility:

The experimental methods are well described, and the results appear reproducible.

• Presentation:

The text and figures are clear and well organized.

Referee Cross-commenting

I agree with reviewer 1 that the paper presents detailed structure study of Codanin-1 and CDIN1 protein. However, as reviewer 2 claims functional studies are missing and therefore the hypothesis regarding the pahtogenesis of CDAI is speculaltive especially with no studies regarding ASF1.

3____.7 Response ____–____ Rigor and Presentation and Cross-commenting:

We thank the reviewers for their positive appraisal of our results' reproducibility, presentation, and method descriptions. We also appreciate the cross-comment that, while our structural analysis of the CDIN1-Codanin1 complex is thorough, functional validation, particularly regarding ASF1, remains to be addressed.

As outlined above, we have revised the manuscript to:

• Emphasize that pathogenic hypotheses drawn from structural data are provisional (refer to Responses 2.2, 2.3, and 3.5).
• Include follow-up studies for ASF1 localization assays and broader mutation profiling in our Future Directions (refer to Responses 2.4, 3.5, 3.6).
• Integrate cautious language throughout to clearly delineate verified findings from model-based speculation (refer to Responses 2.4, 3.5, 3.6). The implemented adjustments ensure that the current work is positioned as a detailed structural and interaction foundation, upon which the essential functional studies will build. We believe that all extensions and clarifications fully satisfy the reviewers’ collective recommendations.

__Reviewer #3 –____ Significance: __

Nature and Significance of the Advance:

This study extends prior work (e.g., Swickley et al., BMC Mol Cell Biol 2020; Shroff et al., Biochem J 2020) on Codanin-1/CDIN1 interaction by applying high-resolution biophysical techniques to identify mutations that disrupt this complex. It provides a plausible cellular mechanism by which specific mutations may lead to CDA I through impaired histone trafficking.

Nevertheless, key question remains: How do mutations outside the Codanin-1 C-terminus contribute to the pathology?

3.8 Response – Significance:

• We thank Reviewer #3 for this important point. Although our work specifically dissects the C-terminal CDIN1-binding domain of Codanin1, we fully acknowledge that CDA-I-associated mutations throughout Codanin1 may operate via additional mechanisms. To address the additional mechanisms, we have added a new paragraph describing other possible pathogenic models to the Discussion (please refer to Response 3.3).
• We also fully acknowledged the need for systematic functional assays of non-C-terminal mutations and their impact on ASF1 localization (please refer to Response 3.6).

• We revised the text to clarify how mutations beyond the C-terminus may contribute to CDA-I pathogenesis and present the significance of our current structural analyses, biophysical characterizations, and molecular insights as a foundation for future research (please refer to Response 3.6). __Audience: __

• Molecular and cellular biologists investigating nuclear-cytoplasmic trafficking mechanisms

• Hematologists and geneticists studying rare red cell disorders
• Clinicians managing CDA I patients and researchers exploring targeted therapies __Reviewer Expertise: __

Pediatric hematologist with over 20 years of research experience in CDA I, including the initial identification of CDAN1 and the elucidation of Codanin-1's role in embryonic erythropoiesis. Not a specialist in the biophysical techniques used in this study.

References

Ask, K., Z. Jasencakova, P. Menard, Y. Feng, G. Almouzni and A. Groth (2012). "Codanin-1, mutated in the anaemic disease CDAI, regulates Asf1 function in S-phase histone supply." The EMBO Journal 31(8): 2013–2023.

Jeong, T.-K., R. C. M. Frater, J. Yoon, A. Groth and J.-J. Song (2025). "CODANIN-1 sequesters ASF1 by using a histone H3 mimic helix to regulate the histone supply." Nature Communications 16(1): 2181.

Sedor, S. F. and S. Shao (2025). "Mechanism of ASF1 engagement by CDAN1." Nature Communications 16(1): 2599.

Swickley, G., Y. Bloch, L. Malka, A. Meiri, S. Noy-Lotan, A. Yanai, H. Tamary and B. Motro (2020). "Characterization of the interactions between Codanin-1 and C15Orf41, two proteins implicated in congenital dyserythropoietic anemia type I disease." Molecular and Cell Biology 21(1).

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Referee #2

Evidence, reproducibility and clarity

This manuscript presents structural and biochemical characterization of the interaction between CDIN1 and the C-terminal domain of Codanin1, shedding light on a complex implicated in Congenital Dyserythropoietic Anemia Type I (CDA-I). While the authors provide valuable structural insights and identify disease-associated mutations that impair CDIN1-Codanin1 binding, I think several important concerns should be addressed to strengthen both the mechanistic claims and their functional relevance.

Contradiction Between Stoichiometry Models:

The authors propose that CDIN1 and Codanin1Cterm primarily form a heterodimer in vitro. However, this appears to contradict previous reports indicating a tetra-heteromeric arrangement. Additionally, while CDIN1 homodimerize seems confusing to me, do the authors suggest it is stable without Codanin1? This seems contrary to findings that CDIN1 is unstable in the absence of Codanin1(Sedor, S.F., Shao, S. nature comm 2025, Swickley, G., Bloch, Y., Malka, L. et al 2020 BMC Mol and Cell Biol). These inconsistencies raise concerns about whether the observed stoichiometries are physiologically relevant or artifacts of in vitro reconstitution, especially since full-length Codanin1 was not studied.

Unvalidated Functional Claims:

The manuscript identifies several CDA-I-associated mutations that disrupt CDIN1-Codanin1 interaction. However, the authors do not test how these mutations affect the biological function of the complex, particularly its role in ASF1 sequestration or histone trafficking. Given the central importance of this axis in their disease model, functional validation (e.g., ASF1 localization, histone deposition assays) is necessary to support these mechanistic conclusions.

Speculative and Potentially Contradictory Model:

The proposed model suggests that CDIN1 competes with ASF1 for Codanin1 binding, thereby indirectly promoting histone delivery to the nucleus. However, emerging data indicate that Codanin1, CDIN1, and ASF1 can form a stable ternary complex, calling into question this competitive binding hypothesis (Sedor, S.F., Shao, S. nature comm 2025). The authors do not acknowledge or discuss these findings, and the model in its current form may therefore be oversimplified or inaccurate.

Significance

Overall, the study adds to our structural understanding of CDIN1 and Codanin1 interactions, but the functional interpretations are currently speculative, and in some cases in conflict with existing literature. The manuscript would benefit significantly from addressing these discrepancies, incorporating relevant data on ASF1, and clarifying whether the observed assemblies reflect physiological complexes.

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Reply to the reviewers

Reply to the Reviewers

I would like to thank the reviewers for their comments and interest in the manuscript and the study.

Reviewer #1

1. I would assume that there are RNA-seq and/or ChIP-seq data out there produced after knockdown of one or more of these DBPs that show directional positioning.

The directional positioning of CTCF-binding sites at chromatin interaction sites was analyzed by CRISPR experiment (Guo Y et al. Cell 2015). We found that the machine learning and statistical analysis showed the same directional bias of CTCF-binding motif sequence and RAD21-binding motif sequence at chromatin interaction sites as the experimental analysis of Guo Y et al. (lines 229-253, Figure 3b, c, d and Table 1). Since CTCF is involved in different biological functions (Braccioli L et al. Essays Biochem. 2019 ResearchGate webpage), the directional bias of binding sites may be reduced in all binding sites including those at chromatin interaction sites (lines 68-73). In our study, we investigated the DNA-binding sites of proteins using the ChIP-seq data of DNA-binding proteins and DNase-seq data. We also confirmed that the DNA-binding sites of SMC3 and RAD21, which tend to be found in chromatin loops with CTCF, also showed the same directional bias as CTCF by the computational analysis.

__2. Figure 6 should be expanded to incorporate analysis of DBPs not overlapping CTCF/cohesin in chromatin interaction data that is important and potentially more interesting than the simple DBPs enrichment reported in the present form of the figure. __

Following the reviewer's advice, I performed the same analysis with the DNA-binding sites that do no overlap with the DNA-binding sites of CTCF and cohesin (RAD21 and SMC3) (Fig. 6 and Supplementary Fig. 4). The result showed the same tendency in the distribution of DNA-binding sites. The height of a peak on the graph became lower for some DNA-binding proteins after removing the DNA-binding sites that overlapped with those of CTCF and cohesin. I have added the following sentence on lines 435 and 829: For the insulator-associated DBPs other than CTCF, RAD21, and SMC3, the DNA-binding sites that do not overlap with those of CTCF, RND21, and SMC3 were used to examine their distribution around interaction sites.

3. Critically, I would like to see use of Micro-C/Hi-C data and ChIP-seq from these factors, where insulation scores around their directionally-bound sites show some sort of an effect like that presumed by the authors - and many such datasets are publicly-available and can be put to good use here.

As suggested by the reviewer, I have added the insulator scores and boundary sites from the 4D nucleome data portal as tracks in the UCSC genome browser. The insulator scores seem to correspond to some extent to the H3K27me3 histone marks from ChIP-seq (Fig. 4a and Supplementary Fig. 3). We found that the DNA-binding sites of the insulator-associated DBPs were statistically overrepresented in the 5 kb boundary sites more than other DBPs (Fig. 4d). The direction of DNA-binding sites on the genome can be shown with different colors (e.g. red and green), but the directionality of insulator-associated DNA-binding sites is their overall tendency, and it may be difficult to notice the directionality from each binding site because the directionality may be weaker than that of CTCF, RAD21, and SMC3 as shown in Table 1 and Supplementary Table 2. We also observed the directional biases of CTCF, RAD21, and SMC3 by using Micro-C chromatin interaction data as we estimated, but the directionality was more apparent to distinguish the differences between the four directions of FR, RF, FF, and RR using CTCF-mediated ChIA-pet chromatin interaction data (lines 287 and 288).

 I found that the CTCF binding sites examined by a wet experiment in the previous study may not always overlap with the boundary sites of chromatin interactions from Micro-C assay (Guo Y et al. *Cell* 2015). The chromatin interaction data do not include all interactions due to the high sequencing cost of the assay, and include less long-range interactions due to distance bias. The number of the boundary sites may be smaller than that of CTCF binding sites acting as insulators and/or some of the CTCF binding sites may not be locate in the boundary sites. It may be difficult for the boundary location algorithm to identify a short boundary location. Due to the limitations of the chromatin interaction data, I planned to search for insulator-associated DNA-binding proteins without using chromatin interaction data in this study.

 I discussed other causes in lines 614-622: Another reason for the difference may be that boundary sites are more closely associated with topologically associated domains (TADs) of chromosome than are insulator sites. Boundary sites are regions identified based on the separation of numerous chromatin interactions. On the other hand, we found that the multiple DNA-binding sites of insulator-associated DNA-binding proteins were located close to each other at insulator sites and were associated with distinct nested and focal chromatin interactions, as reported by Micro-C assay. These interactions may be transient and relatively weak, such as tissue/cell type, conditional or lineage-specific interactions.

 Furthermore, I have added the statistical summary of the analysis in lines 372-395 as follows: Overall, among 20,837 DNA-binding sites of the 97 insulator-associated proteins found at insulator sites identified by H3K27me3 histone modification marks (type 1 insulator sites), 1,315 (6%) overlapped with 264 of 17,126 5kb long boundary sites, and 6,137 (29%) overlapped with 784 of 17,126 25kb long boundary sites in HFF cells. Among 5,205 DNA-binding sites of the 97 insulator-associated DNA-binding proteins found at insulator sites identified by H3K27me3 histone modification marks and transcribed regions (type 2 insulator sites), 383 (7%) overlapped with 74 of 17,126 5-kb long boundary sites, 1,901 (37%) overlapped with 306 of 17,126 25-kb long boundary sites. Although CTCF-binding sites separate active and repressive domains, the limited number of DNA-binding sites of insulator-associated proteins found at type 1 and 2 insulator sites overlapped boundary sites identified by chromatin interaction data. Furthermore, by analyzing the regulatory regions of genes, the DNA-binding sites of the 97 insulator-associated DNA-binding proteins were found (1) at the type 1 insulator sites (based on H3K27me3 marks) in the regulatory regions of 3,170 genes, (2) at the type 2 insulator sites (based on H3K27me3 marks and gene expression levels) in the regulatory regions of 1,044 genes, and (3) at insulator sites as boundary sites identified by chromatin interaction data in the regulatory regions of 6,275 genes. The boundary sites showed the highest number of overlaps with the DNA-binding sites. Comparing the insulator sites identified by (1) and (3), 1,212 (38%) genes have both types of insulator sites. Comparing the insulator sites between (2) and (3), 389 (37%) genes have both types of insulator sites. From the comparison of insulator and boundary sites, we found that (1) or (2) types of insulator sites overlapped or were close to boundary sites identified by chromatin interaction data.

4. The suggested alternative transcripts function, also highlighted in the manuscripts abstract, is only supported by visual inspection of a few cases for several putative DBPs. I believe this is insufficient to support what looks like one of the major claims of the paper when reading the abstract, and a more quantitative and genome-wide analysis must be adopted, although the authors mention it as just an 'observation'.

According to the reviewer's comment, I performed the genome-wide analysis of alternative transcripts where the DNA-binding sites of insulator-associated proteins are located near splicing sites. The DNA-binding sites of insulator-associated DNA-binding proteins were found within 200 bp centered on splice sites more significantly than the other DNA-binding proteins (Fig. 4e and Table 2). I have added the following sentences on lines 405 - 412: We performed the statistical test to estimate the enrichment of insulator-associated DNA-binding sites compared to the other DNA-binding proteins, and found that the insulator-associated DNA-binding sites were significantly more abundant at splice sites than the DNA-binding sites of the other proteins (Fig 4e and Table 2; Mann‒Whitney U test, p value 5. Figure 1 serves no purpose in my opinion and can be removed, while figures can generally be improved (e.g., the browser screenshots in Figs 4 and 5) for interpretability from readers outside the immediate research field.

I believe that the Figure 1 would help researchers in other fields who are not familiar with biological phenomena and functions to understand the study. More explanation has been included in the Figures and legends of Figs. 4 and 5 to help readers outside the immediate research field understand the figures.

6. Similarly, the text is rather convoluted at places and should be re-approached with more clarity for less specialized readers in mind.

Reviewer #2's comments would be related to this comment. I have introduced a more detailed explanation of the method in the Results section, as shown in the responses to Reviewer #2's comments.

Reviewer #2

1. Introduction, line 95: CTCF appears two times, it seems redundant.

On lines 91-93, I deleted the latter CTCF from the sentence "We examine the directional bias of DNA-binding sites of CTCF and insulator-associated DBPs, including those of known DBPs such as RAD21 and SMC3".

2. Introduction, lines 99-103: Please stress better the novelty of the work. What is the main focus? The new identified DPBs or their binding sites? What are the "novel structural and functional roles of DBPs" mentioned?

Although CTCF is known to be the main insulator protein in vertebrates, we found that 97 DNA-binding proteins including CTCF and cohesin are associated with insulator sites by modifying and developing a machine learning method to search for insulator-associated DNA-binding proteins. Most of the insulator-associated DNA-binding proteins showed the directional bias of DNA-binding motifs, suggesting that the directional bias is associated with the insulator.

 I have added the sentence in lines 96-99 as follows: Furthermore, statistical testing the contribution scores between the directional and non-directional DNA-binding sites of insulator-associated DBPs revealed that the directional sites contributed more significantly to the prediction of gene expression levels than the non-directional sites. I have revised the statement in lines 101-110 as follows: To validate these findings, we demonstrate that the DNA-binding sites of the identified insulator-associated DBPs are located within potential insulator sites, and some of the DNA-binding sites in the insulator site are found without the nearby DNA-binding sites of CTCF and cohesin. Homologous and heterologous insulator-insulator pairing interactions are orientation-dependent, as suggested by the insulator-pairing model based on experimental analysis in flies. Our method and analyses contribute to the identification of insulator- and chromatin-associated DNA-binding sites that influence EPIs and reveal novel functional roles and molecular mechanisms of DBPs associated with transcriptional condensation, phase separation and transcriptional regulation.

3. Results, line 111: How do the SNPs come into the procedure? From the figures it seems the input is ChIP-seq peaks of DNBPs around the TSS.

On lines 121-124, to explain the procedure for the SNP of an eQTL, I have added the sentence in the Methods: "If a DNA-binding site was located within a 100-bp region around a single-nucleotide polymorphism (SNP) of an eQTL, we assumed that the DNA-binding proteins regulated the expression of the transcript corresponding to the eQTL".

4. Again, are those SNPs coming from the different cell lines? Or are they from individuals w.r.t some reference genome? I suggest a general restructuring of this part to let the reader understand more easily. One option could be simplifying the details here or alternatively including all the necessary details.

On line 119, I have included the explanation of the eQTL dataset of GTEx v8 as follows: " The eQTL data were derived from the GTEx v8 dataset, after quality control, consisting of 838 donors and 17,382 samples from 52 tissues and two cell lines". On lines 681 and 865, I have added the filename of the eQTL data "(GTEx_Analysis_v8_eQTL.tar)".

5. Figure 1: panel a and b are misleading. Is the matrix in panel a equivalent to the matrix in panel b? If not please clarify why. Maybe in b it is included the info about the SNPs? And if yes, again, what is then difference with a.

The reviewer would mention Figure 2, not Figure 1. If so, the matrices in panels a and b in Figure 2 are equivalent. I have shown it in the figure: The same figure in panel a is rotated 90 degrees to the right. The green boxes in the matrix show the regions with the ChIP-seq peak of a DNA-binding protein overlapping with a SNP of an eQTL. I used eQTL data to associate a gene with a ChIP-seq peak that was more than 2 kb upstream and 1 kb downstream of a transcriptional start site of a gene. For each gene, the matrix was produced and the gene expression levels in cells were learned and predicted using the deep learning method. I have added the following sentences to explain the method in lines 133 - 139: Through the training, the tool learned to select the binding sites of DNA-binding proteins from ChIP-seq assays that were suitable for predicting gene expression levels in the cell types. The binding sites of a DNA-binding protein tend to be observed in common across multiple cell and tissue types. Therefore, ChIP-seq data and eQTL data in different cell and tissue types were used as input data for learning, and then the tool selected the data suitable for predicting gene expression levels in the cell types, even if the data were not obtained from the same cell types.

6. Line 386-388: could the author investigate in more detail this observation? Does it mean that loops driven by other DBPs independent of the known CTCF/Cohesin? Could the author provide examples of chromatin structural data e.g. MicroC?

As suggested by the reviewer, to help readers understand the observation, I have added Supplementary Fig. S4c to show the distribution of DNA-binding sites of "CTCF, RAD21, and SMC3" and "BACH2, FOS, ATF3, NFE2, and MAFK" around chromatin interaction sites. I have modified the following sentence to indicate the figure on line 501: Although a DNA-binding-site distribution pattern around chromatin interaction sites similar to those of CTCF, RAD21, and SMC3 was observed for DBPs such as BACH2, FOS, ATF3, NFE2, and MAFK, less than 1% of the DNA-binding sites of the latter set of DBPs colocalized with CTCF, RAD21, or SMC3 in a single bin (Fig. S4c).

 In Aljahani A et al. *Nature Communications* 2022, we find that depletion of cohesin causes a subtle reduction in longer-range enhancer-promoter interactions and that CTCF depletion can cause rewiring of regulatory contacts. Together, our data show that loop extrusion is not essential for enhancer-promoter interactions, but contributes to their robustness and specificity and to precise regulation of gene expression. Goel VY et al. *Nature Genetics* 2023 mentioned in the abstract: Microcompartments frequently connect enhancers and promoters and though loss of loop extrusion and inhibition of transcription disrupts some microcompartments, most are largely unaffected. These results suggested that chromatin loops can be driven by other DBPs independent of the known CTCF/Cohesin.

I added the following sentence on lines 569-577: The depletion of cohesin causes a subtle reduction in longer-range enhancer-promoter interactions and that CTCF depletion can cause rewiring of regulatory contacts. Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently. Furthermore, the loop extrusion is not essential for enhancer-promoter interactions, but contributes to their robustness and specificity and to precise regulation of gene expression.

 FOXA1 pioneer factor functions as an initial chromatin-binding and chromatin-remodeling factor and has been reported to form biomolecular condensates (Ji D et al. *Molecular Cell* 2024). CTCF have also found to form transcriptional condensate and phase separation (Lee R et al. *Nucleic acids research* 2022). FOS was found to be an insulator-associated DNA-binding protein in this study and is potentially involved in chromatin remodeling, transcription condensation, and phase separation with the other factors such as BACH2, ATF3, NFE2 and MAFK. I have added the following sentence on line 556: FOXA1 pioneer factor functions as an initial chromatin-binding and chromatin-remodeling factor and has been reported to form biomolecular condensates.

7. In general, how the presented results are related to some models of chromatin architecture, e.g. loop extrusion, in which it is integrated convergent CTCF binding sites?

Goel VY et al. Nature Genetics 2023 identified highly nested and focal interactions through region capture Micro-C, which resemble fine-scale compartmental interactions and are termed microcompartments. In the section titled "Most microcompartments are robust to loss of loop extrusion," the researchers noted that a small proportion of interactions between CTCF and cohesin-bound sites exhibited significant reductions in strength when cohesin was depleted. In contrast, the majority of microcompartmental interactions remained largely unchanged under cohesin depletion. Our findings indicate that most P-P and E-P interactions, aside from a few CTCF and cohesin-bound enhancers and promoters, are likely facilitated by a compartmentalization mechanism that differs from loop extrusion. We suggest that nested, multiway, and focal microcompartments correspond to small, discrete A-compartments that arise through a compartmentalization process, potentially influenced by factors upstream of RNA Pol II initiation, such as transcription factors, co-factors, or active chromatin states. It follows that if active chromatin regions at microcompartment anchors exhibit selective "stickiness" with one another, they will tend to co-segregate, leading to the development of nested, focal interactions. This microphase separation, driven by preferential interactions among active loci within a block copolymer, may account for the striking interaction patterns we observe.

 The authors of the paper proposed several mechanisms potentially involved in microcompartments. These mechanisms may be involved in looping with insulator function. Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently (Hsieh TS et al. *Nature Genetics* 2022). Among the identified insulator-associated DNA-binding proteins, Maz and MyoD1 form loops without CTCF (Xiao T et al. *Proc Natl Acad Sci USA* 2021 ; Ortabozkoyun H et al. *Nature genetics* 2022 ; Wang R et al. *Nature communications* 2022). I have added the following sentences on lines 571-575: Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently. I have included the following explanation on lines 582-584: Maz and MyoD1 among the identified insulator-associated DNA-binding proteins form loops without CTCF.

 As for the directionality of CTCF, if chromatin loop anchors have some structural conformation, as shown in the paper entitled "The structural basis for cohesin-CTCF-anchored loops" (Li Y et al. *Nature* 2020), directional DNA binding would occur similarly to CTCF binding sites. Moreover, cohesin complexes that interact with convergent CTCF sites, that is, the N-terminus of CTCF, might be protected from WAPL, but those that interact with divergent CTCF sites, that is, the C-terminus of CTCF, might not be protected from WAPL, which could release cohesin from chromatin and thus disrupt cohesin-mediated chromatin loops (Davidson IF et al. *Nature Reviews Molecular Cell Biology* 2021). Regarding loop extrusion, the 'loop extrusion' hypothesis is motivated by in vitro observations. The experiment in yeast, in which cohesin variants that are unable to extrude DNA loops but retain the ability to topologically entrap DNA, suggested that in vivo chromatin loops are formed independently of loop extrusion. Instead, transcription promotes loop formation and acts as an extrinsic motor that extends these loops and defines their final positions (Guerin TM et al. *EMBO Journal* 2024). I have added the following sentences on lines 543-547: Cohesin complexes that interact with convergent CTCF sites, that is, the N-terminus of CTCF, might be protected from WAPL, but those that interact with divergent CTCF sites, that is, the C-terminus of CTCF, might not be protected from WAPL, which could release cohesin from chromatin and thus disrupt cohesin-mediated chromatin loops. I have included the following sentences on lines 577-582: The 'loop extrusion' hypothesis is motivated by in vitro observations. The experiment in yeast, in which cohesin variants that are unable to extrude DNA loops but retain the ability to topologically entrap DNA, suggested that in vivo chromatin loops are formed independently of loop extrusion. Instead, transcription promotes loop formation and acts as an extrinsic motor that extends these loops and defines their final positions.

 Another model for the regulation of gene expression by insulators is the boundary-pairing (insulator-pairing) model (Bing X et al. *Elife* 2024) (Ke W et al. *Elife* 2024) (Fujioka M et al. *PLoS Genetics* 2016). Molecules bound to insulators physically pair with their partners, either head-to-head or head-to-tail, with different degrees of specificity at the termini of TADs in flies. Although the experiments do not reveal how partners find each other, the mechanism unlikely requires loop extrusion. Homologous and heterologous insulator-insulator pairing interactions are central to the architectural functions of insulators. The manner of insulator-insulator interactions is orientation-dependent. I have summarized the model on lines 559-567: Other types of chromatin regulation are also expected to be related to the structural interactions of molecules. As the boundary-pairing (insulator-pairing) model, molecules bound to insulators physically pair with their partners, either head-to-head or head-to-tail, with different degrees of specificity at the termini of TADs in flies (Fig. 7). Although the experiments do not reveal how partners find each other, the mechanism unlikely requires loop extrusion. Homologous and heterologous insulator-insulator pairing interactions are central to the architectural functions of insulators. The manner of insulator-insulator interactions is orientation-dependent.

8. Do the authors think that the identified DBPs could work in that way as well?

The boundary-pairing (insulator-pairing) model would be applied to the insulator-associated DNA-binding proteins other than CTCF and cohesin that are involved in the loop extrusion mechanism (Bing X et al. Elife 2024) (Ke W et al. Elife 2024) (Fujioka M et al. PLoS Genetics 2016).

 Liquid-liquid phase separation was shown to occur through CTCF-mediated chromatin loops and to act as an insulator (Lee, R et al. *Nucleic Acids Research* 2022). Among the identified insulator-associated DNA-binding proteins, CEBPA has been found to form hubs that colocalize with transcriptional co-activators in a native cell context, which is associated with transcriptional condensate and phase separation (Christou-Kent M et al. *Cell Reports* 2023). The proposed microcompartment mechanisms are also associated with phase separation. Thus, the same or similar mechanisms are potentially associated with the insulator function of the identified DNA-binding proteins. I have included the following information on line 554: CEBPA in the identified insulator-associated DNA-binding proteins was also reported to be involved in transcriptional condensates and phase separation.

9. Also, can the authors comment about the mechanisms those newly identified DBPs mediate contacts by active processes or equilibrium processes?

Snead WT et al. Molecular Cell 2019 mentioned that protein post-transcriptional modifications (PTMs) facilitate the control of molecular valency and strength of protein-protein interactions. O-GlcNAcylation as a PTM inhibits CTCF binding to chromatin (Tang X et al. Nature Communications 2024). I found that the identified insulator-associated DNA-binding proteins tend to form a cluster at potential insulator sites (Supplementary Fig. 2d). These proteins may interact and actively regulate chromatin interactions, transcriptional condensation, and phase separation by PTMs. I have added the following explanation on lines 584-590: Furthermore, protein post-transcriptional modifications (PTMs) facilitate control over the molecular valency and strength of protein-protein interactions. O-GlcNAcylation as a PTM inhibits CTCF binding to chromatin. We found that the identified insulator-associated DNA-binding proteins tend to form a cluster at potential insulator sites (Fig. 4f and Supplementary Fig. 3c). These proteins may interact and actively regulate chromatin interactions, transcriptional condensation, and phase separation through PTMs.

10. Can the author provide some real examples along with published structural data (e.g. the mentioned micro-C data) to show the link between protein co-presence, directional bias and contact formation?

Structural molecular model of cohesin-CTCF-anchored loops has been published by Li Y et al. Nature 2020. The structural conformation of CTCF and cohesin in the loops would be the cause of the directional bias of CTCF binding sites, which I mentioned in lines 539 - 543 as follows: These results suggest that the directional bias of DNA-binding sites of insulator-associated DBPs may be involved in insulator function and chromatin regulation through structural interactions among DBPs, other proteins, DNAs, and RNAs. For example, the N-terminal amino acids of CTCF have been shown to interact with RAD21 in chromatin loops.

 To investigate the principles underlying the architectural functions of insulator-insulator pairing interactions, two insulators, Homie and Nhomie, flanking the *Drosophila even skipped *locus were analyzed. Pairing interactions between the transgene Homie and the eve locus are directional. The head-to-head pairing between the transgene and endogenous Homie matches the pattern of activation (Fujioka M et al. *PLoS Genetics* 2016).

Reviewer #3

Major Comments:

1. Some of these TFs do not have specific direct binding to DNA (P300, Cohesin). Since the authors are using binding motifs in their analysis workflow, I would remove those from the analysis.

When a protein complex binds to DNA, one protein of the complex binds to the DNA directory, and the other proteins may not bind to DNA. However, the DNA motif sequence bound by the protein may be registered as the DNA-binding motif of all the proteins in the complex. The molecular structure of the complex of CTCF and Cohesin showed that both CTCF and Cohesin bind to DNA (Li Y et al. Nature 2020). I think there is a possibility that if the molecular structure of a protein complex becomes available, the previous recognition of the DNA-binding ability of a protein may be changed. Therefore, I searched the Pfam database for 99 insulator-associated DNA-binding proteins identified in this study. I found that 97 are registered as DNA-binding proteins and/or have a known DNA-binding domain, and EP300 and SIN3A do not directory bind to DNA, which was also checked by Google search. I have added the following explanation in line 257 to indicate direct and indirect DNA-binding proteins: Among 99 insulator-associated DBPs, EP300 and SIN3A do not directory interact with DNA, and thus 97 insulator-associated DBPs directory bind to DNA. I have updated the sentence in line 20 of the Abstract as follows: We discovered 97 directional and minor nondirectional motifs in human fibroblast cells that corresponded to 23 DBPs related to insulator function, CTCF, and/or other types of chromosomal transcriptional regulation reported in previous studies.

2. I am not sure if I understood correctly, by why do the authors consider enhancers spanning 2Mb (200 bins of 10Kb around eSNPs)? This seems wrong. Enhancers are relatively small regions (100bp to 1Kb) and only a very small subset form super enhancers.

As the reviewer mentioned, I recognize enhancers are relatively small regions. In the paper, I intended to examine further upstream and downstream of promoter regions where enhancers are found. Therefore, I have modified the sentence in lines 929 - 931 of the Fig. 2 legend as follows: Enhancer-gene regulatory interaction regions consist of 200 bins of 10 kbp between -1 Mbp and 1 Mbp region from TSS, not including promoter.

3. I think the H3K27me3 analysis was very good, but I would have liked to see also constitutive heterochromatin as well, so maybe repeat the analysis for H3K9me3.

Following the reviewer's advice, I have added the ChIP-seq data of H3K9me3 as a truck of the UCSC Genome Browser. The distribution of H3K9me3 signal was different from that of H3K27me3 in some regions. I also found the insulator-associated DNA-binding sites close to the edges of H3K9me3 regions and took some screenshots of the UCSC Genome Browser of the regions around the sites in Supplementary Fig. 3b. I have modified the following sentence on lines 974 - 976 in the legend of Fig. 4: a Distribution of histone modification marks H3K27me3 (green color) and H3K9me3 (turquoise color) and transcript levels (pink color) in upstream and downstream regions of a potential insulator site (light orange color). I have also added the following result on lines 356 - 360: The same analysis was performed using H3K9me3 marks, instead of H3K27me3 (Fig. S3b). We found that the distribution of H3K9me3 signal was different from that of H3K27me3 in some regions, and discovered the insulator-associated DNA-binding sites close to the edges of H3K9me3 regions (Fig. S3b).

4. I was not sure I understood the analysis in Figure 6. The binding site is with 500bp of the interaction site, but micro-C interactions are at best at 1Kb resolution. They say they chose the centre of the interaction site, but we don't know exactly where there is the actual interaction. Also, it is not clear what they measure. Is it the number of binding sites of a specific or multiple DBP insulator proteins at a specific distance from this midpoint that they recover in all chromatin loops? Maybe I am missing something. This analysis was not very clear.

The resolution of the Micro-C assay is considered to be 100 bp and above, as the human nucleome core particle contains 145 bp (and 193 bp with linker) of DNA. However, internucleosomal DNA is cleaved by endonuclease into fragments of multiples of 10 nucleotides (Pospelov VA et al. Nucleic Acids Research 1979). Highly nested focal interactions were observed (Goel VY et al. Nature Genetics 2023). Base pair resolution was reported using Micro Capture-C (Hua P et al. Nature 2021). Sub-kilobase (20 bp resolution) chromatin topology was reported using an MNase-based chromosome conformation capture (3C) approach (Aljahani A et al. Nature Communications 2022). On the other hand, Hi-C data was analyzed at 1 kb resolution. (Gu H et al. bioRxiv 2021). If the resolution of Micro-C interactions is at best at 1 kb, the binding sites of a DNA-binding protein will not show a peak around the center of the genomic locations of interaction edges. Each panel shows the number of binding sites of a specific DNA-binding protein at a specific distance from the midpoint of all chromatin interaction edges. I have modified and added the following sentences in lines 593-597: High-resolution chromatin interaction data from a Micro-C assay indicated that most of the predicted insulator-associated DBPs showed DNA-binding-site distribution peaks around chromatin interaction sites, suggesting that these DBPs are involved in chromatin interactions and that the chromatin interaction data has a high degree of resolution. Base pair resolution was reported using Micro Capture-C.

Minor Comments:

1. PIQ does not consider TF concentration. Other methods do that and show that TF concentration improves predictions (e.g., ____https://www.biorxiv.org/content/10.1101/2023.07.15.549134v2____or ____https://pubmed.ncbi.nlm.nih.gov/37486787____/). The authors should discuss how that would impact their results.

The directional bias of CTCF binding sites was identified by ChIA-pet interactions of CTCF binding sites. The analysis of the contribution scores of DNA-binding sites of proteins considering the binding sites of CTCF as an insulator showed the same tendency of directional bias of CTCF binding sites. In the analysis, to remove the false-positive prediction of DNA-binding sites, I used the binding sites that overlapped with a ChIP-seq peak of the DNA-binding protein. This result suggests that the DNA-binding sites of CTCF obtained by the current analysis have sufficient quality. Therefore, if the accuracy of prediction of DNA-binding sites is improved, although the number of DNA-binding sites may be different, the overall tendency of the directionality of DNA-binding sites will not change and the results of this study will not change significantly.

 As for the first reference in the reviewer's comment, chromatin interaction data from Micro-C assay does not include all chromatin interactions in a cell or tissue, because it is expensive to cover all interactions. Therefore, it would be difficult to predict all chromatin interactions based on machine learning. As for the second reference in the reviewer's comment, pioneer factors such as FOXA are known to bind to closed chromatin regions, but transcription factors and DNA-binding proteins involved in chromatin interactions and insulators generally bind to open chromatin regions. The search for the DNA-binding motifs is not required in closed chromatin regions.

2. DeepLIFT is a good approach to interpret complex structures of CNN, but is not truly explainable AI. I think the authors should acknowledge this.

In the DeepLIFT paper, the authors explain that DeepLIFT is a method for decomposing the output prediction of a neural network on a specific input by backpropagating the contributions of all neurons in the network to every feature of the input (Shrikumar A et al. ICML 2017). DeepLIFT compares the activation of each neuron to its 'reference activation' and assigns contribution scores according to the difference. DeepLIFT calculates a metric to measure the difference between an input and the reference of the input.

 Truly explainable AI would be able to find cause and reason, and to make choices and decisions like humans. DeepLIFT does not perform causal inferences. I did not use the term "Explainable AI" in our manuscript, but I briefly explained it in Discussion. I have added the following explanation in lines 623-628: AI (Artificial Intelligence) is considered as a black box, since the reason and cause of prediction are difficult to know. To solve this issue, tools and methods have been developed to know the reason and cause. These technologies are called Explainable AI. DeepLIFT is considered to be a tool for Explainable AI. However, DeepLIFT does not answer the reason and cause for a prediction. It calculates scores representing the contribution of the input data to the prediction.

 Furthermore, to improve the readability of the manuscript, I have included the following explanation in lines 159-165: we computed DeepLIFT scores of the input data (i.e., each binding site of the ChIP-seq data of DNA-binding proteins) in the deep leaning analysis on gene expression levels. DeepLIFT compares the importance of each input for predicting gene expression levels to its 'reference or background level' and assigns contribution scores according to the difference. DeepLIFT calculates a metric to measure the difference between an input and the reference of the input.

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